Oncology Clinical Trials: Successful Design, Conduct, and Analysis

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Oncology Clinical Trials

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Oncology Clinical Trials

Wm. Kevin Kelly, DO Associate Professor Medicine and Surgery Yale School of Medicine Director of the Clinical Research Services Co-director of Prostate and Urologic Malignancy Yale Comprehensive Cancer Center New Haven, Connecticut

Susan Halabi, PhD Associate Professor Department of Biostatistics and Bioinformatics Duke University Medical Center Duke University Durham, North Carolina

New York

Acquisitions Editor: Richard Winters Cover Design: Steve Pisano Compositor: Publications Services Inc. Printer: King Printing Visit our website at www.demosmedpub.com

© 2010 Demos Medical Publishing, LLC. All rights reserved. This book is protected by copyright. No part of it may be reproduced, stored in a retrieval system, or transmitted in any form or by any means, electronic, mechanical, photocopying, recording, or otherwise, without the prior written permission of the publisher. Medicine is an ever-changing science. Research and clinical experience are continually expanding our knowledge, in particular our understanding of proper treatment and drug therapy. The authors, editors, and publisher have made every effort to ensure that all information in this book is in accordance with the state of knowledge at the time of production of the book. Nevertheless, the authors, editors, and publisher are not responsible for errors or omissions or for any consequences from application of the information in this book and make no warranty, express or implied, with respect to the contents of the publication. Every reader should examine carefully the package inserts accompanying each drug and should carefully check whether the dosage schedules mentioned therein or the contraindications stated by the manufacturer differ from the statements made in this book. Such examination is particularly important with drugs that are either rarely used or have been newly released on the market.

The views expressed in this book are solely those of the contributors and do not represent those of the organizations or of the universities that the authors are affiliated with. In addition the authors accept all responsibility for any errors or omissions in this work.

Library of Congress Cataloging-in-Publication Data Oncology clinical trials / [edited by] William Kevin Kelly, Susan Halabi. p. ; cm. Includes bibliographical references and index. ISBN 978-1-933864-38-9 (hardcover) 1. Cancer—Research—Statistical methods. 2. Clinical trials. I. Kelly, William Kevin. II. Halabi, Susan. [DNLM: 1. Neoplasms—drug therapy. 2. Clinical Trials as Topic. QZ 267 O578 2010] RC267.O53 2010 362.196’994061—dc22 2009044203

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Contents

Foreword Preface Contributors

1. Introduction: What Is a Clinical Trial?

ix xi xiii

1

Susan Halabi and Wm. Kevin Kelly

2. Historical Perspectives of Oncology Clinical Trials

5

Ada H. Braun and David M. Reese

3. Ethical Principles Guiding Clinical Research

11

Sandra L. Alfano

4. Preclinical Drug Assessment

21

Cindy H. Chau and William Douglas Figg

5. Formulating the Question and Objectives

29

Lauren C. Harshman, Sandy Srinivas, James Thomas Symanowski, and Nicholas J. Vogelzang

6. Choice of Endpoints in Cancer Clinical Trials

35

Wenting Wu and Daniel Sargent

7. Design, Testing, and Estimation in Clinical Trials

43

Barry Kurt Moser

8. Design of Phase I Trials

57

Anatasia Ivanova and Leslie A. Bunce

v

vi

CONTENTS

9. Design of Phase II Trials

65

Hongkun Wang, Mark R. Conaway, and Gina R. Petroni

10. Randomization

73

Susan Groshen

11. Design of Phase III Trials

83

Stephen L. George

12. Multiple Treatment Arm Trials

93

Susan Halabi

13. Noninferiority Trials in Oncology

101

Suzanne E. Dahlberg and Robert J. Gray

14. Bayesian Designs in Clinical Trials

109

Gary L. Rosner and B. Nebiyou Bekele

15. The Trials and Tribulations of Writing an Investigator Initiated Clinical Study

119

Nicole P. Grant, Melody J. Sacatos, and Wm. Kevin Kelly

16. Data Collection

131

Eleanor H. Leung

17. Reporting of Adverse Event

141

Carla Kurkjian and Helen X. Chen

18. Toxicity Monitoring: Why, What, When?

151

A. Dimitrios Colevas

19. Interim Analysis of Phase III Trials

163

Edward L. Korn and Boris Friedlin

20. Interpretation of Results: Data Analysis and Reporting of Results

179

Donna Niedzwiecki and Donna Hollis

21. Statistical Considerations for Assessing Prognostic Factors in Cancer

189

Susan Halabi

22. Pitfalls in Oncology Clinical Trial Designs and Analysis

197

Stephanie Green

23. Biomarkers and Surrogate Endpoints in Clinical Trials

215

Marc Buyse and Stefan Michiels

24. Use of Genomics in Therapeutic Clinical Trials

227

Richard Simon

25. Imaging in Clinical Trials Binsheng Zhao and Lawrence H. Schwartz

239

vii

CONTENTS

26. Pharmacokinetic and Pharmacodynamic Monitoring in Clinical Trials: When Is It Needed?

251

Ticiana Leal and Jill M. Kolesar

27. Practical Design and Analysis Issues of Health Related Quality of Life Studies in International Randomized Controlled Cancer Clinical Trials

261

Andrew Bottomley, Corneel Coens, Murielle Mauer

28. Clinical Trials Considerations in Special Populations

267

Susan Burdette-Radoux and Hyman Muss

29. A Critical Reader’s Guide to Cost-Effectiveness Analysis

277

Greg Samsa

30. Systemic Review and Meta-Analysis

285

Steven M. Brunelli, Angela DeMichelle, James Guevara, and Jesse A. Berlin

31. Regulatory Affairs: The Investigator-Initiated Oncology Trial

299

Maria Mézes and Harvey M. Arbit

32. The Drug Evaluation Process in Oncology: FDA Perspective

307

Steven Lemery, Patricia Keegan, and Richard Pazdur

33. Industry Collaboration in Cancer Clinical Trials

315

Linda Bressler

34. Defining the Roles and Responsibilities of Study Personnel

321

Fred De Pourcq

35. Writing a Consent Form

327

Christine Grady

36. How Cooperative Groups Function

335

Edward L. Trimble and Alison Martin

37. Adaptive Clinical Trial Design in Oncology

343

Elizabeth Garrett-Mayer

38. Where Do We Need to Go with Clinical Trials in Oncology?

357

Andrea L. Harzstark and Eric J. Small Index

363


Foreword

C

linical trials are the engine of progress in the development of new drugs and devices for the detection, monitoring, prevention and treatment of cancer. A well conceived, carefully designed and efficiently conducted clinical trial can produce results that change clinical practice overnight, deliver new oncology drugs and diagnostics to the marketplace, and expand the horizon of contemporary thinking about cancer biology. A poorly done trial does little to advance the field or guide clinical practice, consumes precious clinical and financial resources and challenges the validity of the ethical contract between investigators and the volunteers who willingly give their time and effort to benefit future patients. Critical elements of clinical trials are those that address the scientific, ethical, technical and regulatory

aspects of human subjects research. What are we trying to learn? What clinical trial design will best address our objectives? How do we identify, recruit and protect the population of interest? How do we assure the quality of our data and the validity of our results? What regulatory standards must be met to obtain marketing approval for the drug or device we are studying? How do we maximize the information obtained from every trial so as to have the greatest impact on advancing science and improving care? Richard L. Schilsky, MD Professor of Medicine University of Chicago Chairman, Cancer and Leukemia Group B ASCO President 2008–2009

ix


Preface

I

n 2006, a group of colleagues were discussing the days events at ASCO and the topic turned to people that were retiring at the end of the year or changing career directions. Many of us were initially taken back, yet, also excited, to learn that some of our long time colleagues were turning a new leaf in their lives. These individuals were giants in the field who had not only helped shape modern oncology, but also had long and generously provided guidance to us. Many had been our mentors and we always felt that they would be there to ask: “How did you design this pivotal trial in colon cancer? Why did you use this endpoint for this lung trial? Can we really use this as a surrogate marker?” They were always were a voice of reason which reflected years of experience in doing clinical research and they played a vital role in our own scientific and intellectual development. Having the benefit of their experience underscored the importance, and declining prevalence, of mentoring the next generation of clinical trialists. Many of us have now inherited these perilous challenges.

This book is a collaborative effort and is based on the knowledge and expertise of leading oncologists, statisticians and clinical trial professionals from academia, industry and government who have years of experience in designing, conducting, analyzing, and reporting clinical trials in cancer. This collective experience was created to allow these seasoned investigators to pass on their knowledge to those who are entering the field. In so doing, our mission is to enhance the successful design, development, management and analysis of oncology clinical trials for the next generation. While this book focuses on oncology clinical trials, the fundamental concepts and basic principles are applicable to all trials in many medical disciplines. We hope that this work will aid the junior investigator’s academic, industry or government career in order to improve the quality of clinical trials. In so doing, their discoveries can be quickly and efficiently translated into improved patients outcomes and future care. Wm. Kevin Kelly Susan Halabi

xi


Contributors

Sandra L. Alfano, PharmD Chair, Human Investigational Committee Associate Research Scientist Department of Internal Medicine Yale University School of Medicine New Haven, Connecticut

Andrew Bottomley, PhD Assistant Director Head, Quality of Life Department European Organization for Research and Treatment of Cancer Brussels, Belguim

Harvey M. Arbit, BS Pharm, PharmD, MBA Director IND/IDE Assistance Program Clinical and Translation Science Institute Academic Health Center University of Minnesota Minneapolis, Minnesota

Ada H. Braun, MD, PhD Clinical Research Medical Director Department of Hematology/Oncology Amgen, Inc. Thousand Oaks, California

B. Nebiyou Bekele, PhD Associate Professor Department of Biostatistics The University of Texas MD Anderson Cancer Center Houston, Texas Jesse A. Berlin, ScD Vice President Department of Epidemiology Johnson & Johnson Pharmaceutical Research and Development Titusville, New Jersey

Linda Bressler, PharmD Director of Regulatory Affairs Cancer and Leukemia Group B Chicago, Illinois Steven M. Brunelli, MD, MSCE Assistant Professor Associate Physician Renal Division Brigham and Women’s Hospital Harvard Medical School Boston, Massachusetts

xiii

xiv

Leslie A. Bunce, MD Consultant Leslie A. Bunce, LLC Chapel Hill, North Carolina Susan Burdette-Radoux, MD Associate Professor of Medicine Hematology/Oncology Unit Vermont Cancer Center University of Vermont Burlington, Vermont Marc Buyse, ScD Chairman International Drug Development Institute Louvain-la-Neuve, Belgium Associate Professor of Biostatistics Hasselt University Hasselt, Belgium Cindy H. Chau, PharmD, PhD Medical Oncology Branch National Cancer Institute National Institutes of Health Bethesda, Maryland Helen X. Chen, MD Associate Chief Investigational Drug Branch Cancer Therapy Evaluation Program National Cancer Institute Bethesda, Maryland Corneel Coens, MSc Quality of Life Department European Organization for Research and Treatment of Cancer Brussels, Belgium A. Dimitrios Colevas, MD Associate Professor Department of Medicine Stanford University Stanford, California Mark R. Conaway, PhD Professor Public Health Services University of Virginia Charlottesville, Virginia

CONTRIBUTORS

Suzanne E. Dahlberg, PhD Reserach Scientist Department of Biostatistics and Computational Biology Dana-Farber Cancer Institute Havard School of Public Health Boston, Massachusetts Angela DeMichele, MD, MSCE Associate Professor of Medicine and Epidemiology Department of Medicine, Biostatistics and Epidemiology University of Pennsylvania Philadelphia, Pennsylvania William Douglas Figg, PharmD, MBA Medical Oncology Branch National Cancer Institute National Institutes of Health Bethesda, Maryland Boris Friedlin, PhD Mathematical Statistician Biometric Research Branch Division of Cancer Treatment and Diagnosis National Cancer Institute Bethesda, Maryland Stephen L. George, PhD Professor of Biostatistics and Bioinformatics Duke University School of Medicine Durham, North Carolina Christine Grady, MSN, PhD Acting Chief and Head of Section on Human Subjects Research Department of Bioethics National Institutes of Health Clinical Center Bethesda, Maryland Nicole P. Grant, BS Director, Protocol Development Office Yale Cancer Center New Haven, Connecticut Robert J. Gray, PhD Professor of Biostatistics Department of Biostatistics and Computational Biology Dana-Farber Cancer Institute Havard School of Public Health Boston, Massachusetts

CONTRIBUTORS

Stephanie Green, PhD Senior Director Clinical Biostatistics Pfizer, Inc. New London, Connecticut Susan Groshen, PhD Professor Department of Preventive Medicine Keck School of Medicine University of Southern California Los Angeles, California James Guevara, MD, MPH Associate Professor Department of Pediatrics University of Pennsylvania School of Medicine University of Pennsylvania Philadelphia, Pennsylvania Susan Halabi, PhD Associate Professor Department of Biostatistics and Bioinformatics Duke University Medical Center Duke University Durham, North Carolina Lauren C. Harshman, MD Instructor of Medicine Department of Medicine Division of Oncology Stanford University School of Medicine Stanford, California Andrea L. Harzstark, MD Assistant Clinical Professor Department of Medicine Univerisity of California, San Francisco San Francisco, California Donna Hollis, MS Senior Statistician Duke Comprehensive Cancer Center Duke University Durham, North Carolina Anastasia Ivanova, PhD Associate Professor Department of Biostatistics The University of North Carolina at Chapel Hill Chapel Hill, North Carolina

Patricia Keegan, MD Division Director Division of Biologic Oncology Products Office of Oncology Drug Products Center for Drug Evaluation and Research Food and Drug Administration Silver Spring, Maryland Wm. Kevin Kelly, DO Associate Professor Medicine and Surgery Yale School of Medicine Director of the Clinical Research Services Co-director of Prostate and Urologic Malignancy Yale Comprehensive Cancer Center New Haven, Connecticut Jill M. Kolesar, PharmD Professor School of Pharmacy University of Wisconsin-Madison Madison, Wisconsin Edward L. Korn, PhD Mathematical Statistician Biometric Research Branch Division of Cancer Treatment and Diagnosis National Cancer Institute Bethesda, Maryland Carla Kurkjian, MD Assistant Professor Department of Internal Medicine Section of Hematology/Oncology University of Oklahoma Health Sciences Center Oklahoma City, Oklahoma Ticiana Leal, MD Clinical Assistant Professor Department of Medical Oncology Carbone Cancer Center University of Wisconsin Madison, Wisconsin Steven Lemery, MD Medical Officer OODP/CDER Food and Drug Administration Silver Spring, Maryland

xv

xvi

CONTRIBUTORS

Eleanor H. Leung, PhD Data Coordinator Cancer and Leukemia Group B Statistical Center Duke University Durham, North Carolina

Donna Niedzwiecki, PhD Assistant Professor Biostatics and Bioinformatics Duke University Durham, North Carolina

Alison Martin, MD President and CEO Melanoma Research Alliance Washington, District of Columbia

Richard Pazdur, MD Director Office of Oncology Drug Products Food and Drug Administration Silver Spring, Maryland

Murielle Mauer, PhD Biostatistician Quality of Life Department European Organization for Research and Treatment of Cancer Brussels, Belgium Elizabeth Garrett-Mayer, PhD Associate Professor Department of Medicine Division of Biostatistics and Epidemiology Medical University of South Carolina Charleston, South Carolina Maria Mézes, BA, BEd Director INDMSU and Connecticut Clinical Trials Network Coordinator Yale Comprehensive Cancer Center Yale University School of Medicine New Haven, Connecticut Stefan Michiels, PhD Unit of Biostatistics and Epidemiology Institut Gustave Roussy Villejuif, France Barry Kurt Moser, PhD Associate Research Professor Department of Biostatistics and Bioinformatics Duke University Medical Center Duke University Durham, North Carolina Hyman B. Muss, MD Professor of Medicine University of North Carolina Director of Geriatric Oncology Lineberger Comprehensive Cancer Center Chapel Hill, North Carolina

Gina R. Petroni, PhD Professor Public Health Services University of Virginia Charlottesville, Virginia Fred De Pourcq, MS Special Projects Administrator Yale Center for Clinical Investigations Yale University New Haven, Connecticut David M. Reese, MD Executive Medical Director Hematology/Oncology Medical Sciences Amgen, Inc. Thousand Oaks, California Gary L. Rosner, ScD Professor Department of Biostatistics The University of Texas MD Anderson Cancer Center Houston, Texas Melody J. Sacatos, BA Yale Center for Clinical Investigation Yale University School of Medicine New Haven, Connecticut Greg Samsa, PhD Associate Professor Department of Biostatistics and Bioinformatics Duke University School of Medicine Duke University Durham, North Carolina

CONTRIBUTORS

Daniel Sargent, PhD Professor of Biostatistics Department of Health Sciences Research Mayo Clinic Rochester, Minnesota Lawrence H. Schwartz, MD James Picker Professor of Radiology Chairman, Department of Radiology Columbia University College of Physicians and Surgeons New York, New York Richard Simon, DSc Chief Biometric Research Branch National Cancer Institute Bethesda, Maryland Eric J. Small, MD Professor Department of Medicine University of California, San Francisco San Francisco, California Sandy Srinivas, MD Associate Professor of Medicine Department of Medicine Division of Oncology Stanford University of Medicine Stanford, California James Thomas Symanowski, PhD Head of Biostatistics Department of Biostatistics Nevada Cancer Institute Las Vegas, Nevada

Edward L. Trimble, MD, MPH Head, Gynecologic Cancer Therapeutics and Quality of Cancer Care Therapeutics Clinical Investigations Branch Cancer Therapy Evaluation Program Division of Cancer Treatment and Diagnosis National Cancer Institute Bethesda, Maryland Nicholas J. Vogelzang, MD Chair and Medical Director Developmental Therapies Department of Medical Oncology Comprehensive Cancer Center of Nevada Las Vegas, Nevada Hongkun Wang, PhD Assistant Professor Public Health Services University of Virginia Charlottesville, Virginia Wenting Wu, PhD Assistant Professor of Biostatistics Department of Health Sciences Research Mayo Clinic Rochester, Minnesota Binsheng Zhao, DSc Associate Professor Department of Radiology Columbia University College of Physicians and Surgeons New York, New York

xvii


1

Introduction to Clinical Trials

Susan Halabi Wm. Kevin Kelly

“Learn from yesterday, live for today, hope for tomorrow. The important thing is to not stop questioning” —Albert Einstein, 1879–1955 The number of cancer cases diagnosed daily continues to increase around the world, and we urgently need to develop more effective therapies for this disease. Although there are a plethora of new agents that have shown promise in preclinical cancer models, clinical trials in patients remain the hallmark for clinical research in oncology and the key to developing more effective therapies for patients with cancer. We define clinical trials as scientific investigations that evaluate the safety and\or particular outcome(s) of a therapeutic or nontherapeutic intervention in a defined group of patients. According to ClinicalTrials.gov, “a clinical trial is a research study to answer specific questions about vaccines or new therapies or new ways of using known treatments.” Clinical trials (also called medical research, or research studies) are used to determine whether new drugs or treatments are both safe and effective; and they comprise the main conduit the Federal Drug Agency (FDA) uses to approve agents for use in humans. Over the last several decades, clinical trial methodology has evolved from simple, small, prospective studies to large, sophisticated studies that incorporate many correlative-science and quality-of-

life objectives. Although studies have become more complex, they still can be broken down broadly into four categories or phases: “phase I tests a new drug or treatment in a small group to evaluate dose and safety; phase II expands the study to a larger group of similar patients with a defined treatment or intervention; phase III expands the study to an even larger group of people; and phase IV takes place after the drug or treatment has been licensed and marketed.” (1) Phase III clinical trials are usually the definitive trials providing evidence for or against a new experimental therapy, and they have become the gold standard in assessing the efficacy of a new experimental arm or a device (2, 3). Friedman et al., define a phase III clinical trial as “a prospective controlled evaluation of an intervention for some disease or condition in human beings” (2). There are generally three purposes of randomized phase III trials: (i) to determine the efficacy of a new treatment compared to an observation/placebo arm, (ii) to determine the efficacy of a new treatment versus a standard therapy, or (iii) to test whether a new treatment is more effective relative to a standard therapy, but is associated with less morbidity (3). The main objectives of a clinical trial are to obtain reliable answers to important clinical questions and, more importantly, to change medical practice. Results from a single phase III trial are not sufficient for the intervention to be considered definitive or to change medical practice. When considering strength of evidence

1

2

ONCOLOGY CLINICAL TRIALS

1. Anecdotal case reports 2. Case series without controls 3. Series with literature controls 4. Analyses using computer databases 5. “Case-control” observational studies 6. Series based on historical control groups 7. Single randomized controlled clinical trials 8. Confirmed randomized controlled clinical trials

FIGURE 1.1 Hierarchy of strength of evidence. Printed with permission from Green & Byar, Statistics in Medicine, Vol. 3, 1984

of data, investigators should interpret data from other sources including other phase III trials and results from epidemiologic and other meta-analyses. As presented in Figure 1.1, Green and Byar argued that confirmed randomized controlled phase III trials form the strongest evidence of support for an intervention (4). The basic principles of design are to minimize bias and increase precision of the treatment effect, which will improve the delivery of treatment and eventually improve care for oncology patients.

SCOPE The landscape of conducting clinical trials in oncology is quickly changing, and many investigators are now exposed to clinical trials without a deep appreciation for or understanding of the basic principles and practical issues of conducting clinical research. Although historically this knowledge has been passed down from mentor to student, that practice is increasingly not the case in today’s educational environment. The goal of this book is to provide an understanding of and a sound foundation for clinical trials and to pass on the decades of experience from seasoned investigators concerning a wide range of topics that are critical to formulate, write, conduct, and report clinical trials. This book is intended for investigators with minimal or some experience in clinical trials in oncology, who are interested in pursuing a career in academia or industry. In this sense, it seeks to be a guide, if not a mentor. In addition, this book provides a comprehensive, integrated presentation of principles and methodologies for clinical trials to enable readers to become active, competent investigators. Clinical trials are expensive and time-consuming, and a lot of thought goes into their planning, execution, and reporting. The time involved from concept

development to study activation varies, depending on the phase of the trial and whether it is a single or multiinstitutional study. In recent reports, Dilts et al., indicated that there were 296 processes from concept inception to study activation in phase III trials sponsored by the Cancer Therapy Evaluation Program (CTEP), and the median time that the trials were activated was 602 days (interquartile range, 454 to 861 days) (5-7). This shows the complexity of clinical trials and highlights the fact that there are many areas where insufficiency and errors can occur if one does not have the experience, the guidance, or the appropriate personnel to aid in trial development and execution. The development and conduct of a trial require a multidisciplinary approach that involves physician, scientists, biostatisticians, research nurses, experts in regulatory affairs and contract negotiations, data coordinators, and research technicians, who are all critical for the success of the study. In particular, biostatisticians play a central role in clinical trials, and collaborating with biostatisticians in the early design stage ensures that the trial will yield valid and interpretable results. Close collaboration with biostatisticians results in trials with clearly defined objectives, study designs well-suited to address the hypotheses being posited, and appropriate analyses. This book is unique because it has contributions from a broad range of members of the multidisciplinary team, who provide their experience and expertise to guide investigators to a successful study. Altman describes the general sequence of steps in a research project as follows: planning, design, execution (data collection), data processing, data analysis, presentation, interpretation, and publication (8). The book is arranged in similar order, and it focuses on studies in humans, with emphasis on safety consideration in trial design. The early chapters discuss historical perspectives, along with ethical issues that have been raised with oncology clinical trials, which give one a basis for understanding the evolution that has occurred over the last several decades. The next several chapters deal with the most difficult obstacles that a new investigator encounters. The first such obstacle is choosing the correct agents to study. Chau and collogues review preclinical drug assessment. That chapter highlights the technological advances and preclinical models used to determine the pharmacological profile of the drugs, which are critical as you design your trial. Once your agents are chosen, defining the questions, objectives, and endpoints of the trial are crucial, and these aspects of planning often do not receive the critical consideration they deserve. The chapters by Stark et al., and Wu et al., provide first-hand experience from multiple, seasoned clinical investigators on their approach to these issues.

3

1 INTRODUCTION TO CLINICAL TRIALS

Input from biostatisticians is important at each stage of the process of protocol development, and the next series of chapters highlights basic statistical concepts, such as estimation, hypothesis testing, and design considerations for phase I through III trials. Throughout these chapters, the authors provide their extensive experience in trial design and provide actual examples to demonstrate their points. More advanced statistical issues such as multiple arm trials, noninferiority trials, Bayesian designs, meta-analysis, and adaptive design are discussed later in the book. In the past, there were few standards for writing a protocol, but through immense work from CTEP and other agencies, writing a protocol has been greatly simplified by the use of standardized templates. Although these templates have simplified the writing of a study, there is an art to writing a study, and there are many obstacles that investigators need to consider. Grant et al., take you through the writing of an investigatorinitiated study, and Leung highlights important issue in data collection; Kurkjian et al., describe the reporting of adverse events, and Colevas outlines the intricacies of toxicity reporting. Once the study is underway and near completion, Korn and Friedlin discuss the importance of interim analysis, and Niedzwiecki and Hollis give us an overview on how to interpret study results. There are many pitfalls that can be encountered in conducting and interpreting a clinical trial, which is well illustrated by Green; and Halabi discusses the importance of assessing prognostic factors in cancer studies. In the past decade, there has been increased emphasis in decreasing the time for a new drug to be approved. Thus, biomarkers, surrogate endpoints, novel imaging techniques, pharmacokinetic and pharmacodynamic assessments, genetics, and intensive quality-of-life monitoring have been incorporated into investigational studies to help move the development of drugs along. The authors of these chapters update the reader on the pros and cons of these approaches. Burdette-Radoux and Muss identify that there are populations of patients who have special clinical trial considerations, and Samsa gives us a dose of reality by guiding us through the cost analysis of investigational studies. At times a single trial may not give enough information to make a conclusive result, and Brunelli and colleagues review the advantages and limitations of performing a meta-analysis. The last several chapters are dedicated to some of the more practical issues that novice investigators encounter, but for which they cannot always get a straight answer. These include chapters that describe the requirements of regulatory affairs in studies: how does the FDA review and approve new agents; how

should one interact with industry; how do we define the role of study personnel; how ought we to write an informed consent form; or how do the cooperative oncology groups operate? Developing an understanding of all these issues is imperative for successful clinical trialists. Finally, Harzstark and Small look into the future to give us an idea of where we should be in the next decade and how clinical trials will evolve further.

RESOURCES Several books that have been written on clinical trials have focused on randomized phase III trials (9–12). The available books emphasize statistical or clinical principles and concepts, whereas in this book we present a balanced perspective on clinical trials. Our intention is to enhance statistical thinking and understanding among a wider professional audience. Unlike other books that focus only on randomized phase III clinical trials, we include topics that emerge earlier in the traditional paradigm, such as preclinical drug assessment (Chapter 4), design of phase I trials (Chapter 8), and phase II trials (Chapter 9). There are many resources dedicated to clinical trials. These include web-based resources for clinical trials. The list is not inclusive but we present some valuable links in Table 1.1. In addition, the Society of Clinical Trials (www.sctweb.org) is an organization dedicated to the study, design, and analysis of clinical trials, with a peer reviewed journal (Controlled Trials). There are other educational resources, including workshops, offered to junior faculty members in academic centers, such as the ASCO workshops, with the

TABLE 1.1

Web-Based Resources. http://www.cancer.gov/ www.cochrane.org www.clinicaltrials.gov www.consort-statement.org www.controlled-trials.com http://grants.nih.gov/grants/guide/notice-files/not 98-084.html http://deainfo.nci.nih.gov/grantspolicies/datasafety .htm http://www.emea.eu.int/pdfs/human/ewp/587203en .pdf http://www.acrpnet.org/chapters/belg/whotdr _guidelines.doc

4


purpose of training junior faculty members in the United States and around the world.

SUMMARY There is an ever increasing need for educational resources and this book will serve as a roadmap for the next generation of clinical trialists in oncology. The objective is to enable the reader to understand the different stages involved in the design, conduct, and analysis of clinical trials. In addition, this book can be used as an aid in teaching clinical fellows in clinical training programs complemented by lectures and discussion. This book may be of interest for public health students and public health workers and for contract research organizations and departments of medicine, where people are involved with clinical trials. Our hope is that the reader will find this book valuable, especially the practical issues we have encountered in doing clinical trials exemplified by citing real life examples of clinical trial failures and success. Rigorous clinical trials can address important questions relevant to a patient population in which one can make valid inferences about the therapy being tested. Such studies should be designed starting with a hypothesis, an explicit definition of endpoints, appropriate identification and selection of the patient population, and a sufficiently large sample size with high power to detect small to moderate clinical effect sizes. In addition, these studies should be monitored for terminating a trial early so that patients can benefit from

a promising treatment or are spared from a harmful regimen.

References 1. www.clinicaltrials.gov. 2. Friedman LM, Furberg CD, DeMets DL. Fundamentals of Clinical Trials. 3rd ed. New York, Springer-Verlag; 1998. 3. Simon RS. Design and conduct of clinical trials, in DeVita VT, Hellman S, Rosenberg SA (eds.). Cancer: Principles and Practice of Oncology. Philadelphia, PA, J.B. Lippincott, 1993; pp 418–440. 4. Green SB, Byar DP. Using observational data from registries to compare treatments: The fallacy of omnimetrics (with discussion). Statistics in Medicine, 1984;3:361–373. 5. Dilts DM, Sandler A, Cheng S, Crites J, Ferranti L, Wu A, Gray R, MacDonald J, Marinucci D, Comis R. Development of clinical trials in a cooperative group setting: the eastern cooperative oncology group. Clin Cancer Res. 2008;14:3427–3433. 6. Dilts DM, Sandler A, Cheng S, Crites J, Ferranti L, Wu A, Gray R, MacDonald J, Marinucci D, Comis R. Processes to activate phase III clinical trials in a cooperative oncology group: the case of cancer and leukemia group B. J Clin Oncol 2006;24: 4553–4557. 7. Dilts DM, Sandler AB, Cheng SK, Crites JS, Ferranti LB, Wu AY, Finnigan S, Friedman S, Mooney M, Abrams J. Steps and time to process clinical trials at the Cancer Therapy Evaluation Program. J Clin Oncol 2009;27:1761–1766. 8. Altman, DG. Practical Statistics for Medical Research. 1st ed. p. 1–9. London; New York: Chapman and Hall; 1991. 9. Everitt BS, Pickles A. Statistical Aspects of the Design and Analysis of Clinical Trials (2nd ed.). London, Imperial College Press; 2004. 10. Green S, Benedetti J, Crowley J. Clinical Trials in Oncology (2nd ed.). New York, Chapman and Hall; 2002. 11. Piantadosi S: Clinical Trials. A Methodologic Perspective (2nd ed.). New York, John Wiley & Sons; 2005. 12. Spiegelhalter DJ, Abrams KR, Myles JP. Bayesian Approaches to Clinical Trials and Health-Care Evaluation. Wiley & Sons; 2004.

2

Historical Perspectives of Oncology Clinical Trials

Ada H. Braun David M. Reese

ORIGINS OF ONCOLOGY: ANTIQUITY, GREECE, AND ROME Cancer is older than human life, and in fact it is intrinsic to terrestrial biology. The first evidence of tumors was found in bones from dinosaurs of the Jurassic period that lived some 200 million years ago (1). All vertebrate and many invertebrate species can develop cancer (2). Early human evidence of neoplasia includes both primary tumors and metastatic lesions; this evidence spans over 5,000 years, from predynastic Egyptian mummies to early Christian times, and over multiple continents, from the Far East to South America (3–5). The Babylonian “Code of Hammurabi” (1750 BCE), Chinese folklore (“Rites of the Zhou Dynasty”; 1100–400 BCE), as well as medical documents from India (“Ramayana”; 500 BCE) and Egypt, attest to the early recognition of cancer. Perhaps most famously, the George Ebers and Edwin Smith papyri (Egypt, ca. 1550 and 1600 BCE) describe several tumor ailments and their treatment. The Ebers papyrus, which may be considered the oldest textbook of medicine, recommends operations for certain accessible tumors and outlines palliative treatment for inoperable disease, including topical applications (6). The Smith papyrus provides more prosaic case reports; portraying what is likely a tumor of the breast, the scribe annotates, “there is no treatment” (7).

Although these ancient documents describe what we now recognize as malignant tumors, for millennia there was no attempt to study cancer systematically, until Greek physicians founded what we consider Western medicine. These doctors regarded all diseases—cancer included—as having natural (as opposed to supernatural) causes. Traditionally, Hippocrates (ca. 460 to 377 BCE) first described cancer as a biological process, a disease entity with both local and distant consequences. Based on observation of the growth patterns of tumors directly visualizable, such as breast cancers, he coined the term karkinoma, from the Greek word for crab; the term was later Latinized to the familiar carcinoma. According to legend, Galen of Pergamon (ca. 129 to 200 CE) thought the disease was “so called because it appears at length with turgid veins shooting out from it, so as to resemble the figure of a crab; or as others say, because like a crab, where it has once got, it is scarce possible to drive it away” (8). If Hippocratic physicians laid the foundation of empiric medicine by replacing supernatural concepts of disease with meticulous observation and logical inference, Galen has been recognized as the founder of experimental science. The last prominent physician of the Greco-Roman school, he combined results of animal dissections, experiments in physiology, and clinical observation to construct models of human physiology and disease, which he recorded and taught systematically (9).

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Following the Hippocratic physicians, Galen surmised that cancer originated in an imbalance of the four humors: specifically, an excess of melan chole (black bile) over yellow bile, phlegm, and blood was thought to drive the formation of malignant tumors. Because excess black bile was the cause of cancer, efforts to remove black bile were the logical treatment. Bloodletting, purgatives, and emetics thus entered the armamentarium of physicians attempting to treat the disease. No one as yet, however, thought to systematically record the results of treatment in a group of patients, or to directly compare one cancer treatment (or no treatment at all) with another. These astute healers did understand that most of their therapies were ineffective, though, and one teaching summarized a view dating to the time of Hippocrates: superficial tumors could sometimes be treated with surgery, but deep-seated tumors should be left alone, as patients often died more quickly with treatment compared with when they were left alone (8). When he died, Galen left behind a formidable literary legacy comprising over 10,000 pages of authoritative treatises. These were a combination of science blended with Greek philosophy, and they profoundly influenced medicine for 1,500 years, cancer medicine included. The eminent Canadian doctor Sir William Osler (1849 to 1919) best described what followed: “fifteen centuries stopped thinking and slept, until awakened by the De Fabrica of Vesalius” (10). Cancer medicine slumbered with the rest of the profession.

THE DAWN OF CANCER SCIENCE: ADVANCES IN PATHOLOGY In the sixteenth century, advances in anatomy heralded a new era of empiricism. Physicians such as Antonio Benivieni (1443 to 1502; Florence) pioneered the use of autopsy to understand the causes of death, correlating clinical conditions with postmortem findings. In 1543, based on hundreds of dissections, Andreas Vesalius of Brussels (1514 to 1564) published “De Humani Corporis Fabrica” (On the Fabric of the Human Body), a groundbreaking first complete depiction of human anatomy, lavishly illustrated with detailed drawings of the body. Within another century, Italy’s Giovanni Battista Morgagni (1682 to 1771) inaugurated the field of pathological anatomy with his masterpiece “De Sedibus et Causis Morborum per Anatomen Indagatis” (The Seats and Causes of Diseases Investigated by Anatomy). Thereafter, a succession of investigators used increasingly specialized technology to localize disease with an ever-increasing clarity. Marie François Xavier Bichat (1771 to 1802;

France) identified tissues underlying recognizable organ systems with the naked eye, thus laying the groundwork for histology. With the introduction of improved microscopes in the 1800s, Rudolf Virchow (1821 to 1902; Germany) honed in on the newly discovered building blocks of life: the cell. Cell theory revolutionized the understanding of cancer, making possible for the first time the systematic study of the disease in the laboratory and the clinic. Virchow defined cancer as a disease of abnormal cells emanating from other cells through division. As he famously stated, “from every cell a cell” (omnis cellula e cellula) (11). Early in his career, Virchow described an abnormal proliferation of malignant white blood cells in a patient. Based on this case study, he coined the term “leukemia” (‘white blood’; from Greek leukos, white, and aima, blood), shortly after Thomas Hodgkin (1798 to 1866; Great Britain) characterized the proliferation of malignant cells in lymph glands as “lymphoma” (12). In 1863, the German pathologist Wilhelm von Waldeyer-Hartz (1836 to 1921) further outlined the fundamentals of malignant transformation and carcinogenesis. He postulated that cancer cells originate from normal cells, multiply by cell division, and metastasize (spread to distant sites; from Greek methistanai, to place away) through lymph or blood (13). Observing a nonrandom pattern of metastatic growth in hundreds of autopsy records, Stephen Paget (1855 to 1926) subsequently proposed that the predilection of cancer cells to metastasize to certain organs was “not a matter of chance.” In 1889, the British surgeon planted the groundbreaking “seed and soil” hypothesis that prevails to date: “when a plant [cancer] goes to seed, its seeds [the cancer cells] are carried in all directions; but they can live and grow only if they fall on congenial soil [a conducive organ microenvironment]” (14). Another hundred years passed before experimental evidence substantiated the theory. Indeed, though nineteenth-century pathology provided an increasingly accurate description of cancer, it offered little pathobiologic insight. The transition of oncology from a largely descriptive art to an experimental science finally occurred around the turn of the twentieth century.

ONCOLOGY IN THE MODERN ERA: A VERY BRIEF OVERVIEW The 20th century opens as the experimental era with the systematic study of tumors throughout the animal kingdom, and it . . . promises to widely separate many neoplastic

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diseases formerly held to be closely related. It may thereby prove to be the era of successful therapeutics and prophylaxis. —James Ewing, 1919 The notion that cancer is not a single entity but rather hundreds of biologically distinct illnesses really dates to James Ewing’s (1866 to 1943, United States) monumental textbook Neoplastic Diseases, in which he classified tumors according to the tissue they arose from or resembled (15). Ewing, who became the first director of what is now Memorial Sloan-Kettering, tirelessly catalogued tumor cells according to their microscopic features, but he was more than a brilliant laboratory researcher. He recognized the substantial clinical implications his work could have, and he wrote in the preface to the third edition of his text, Up to a very recent time the practical physician or surgeon has been content to regard all fibromas, sarcomas, or cancers [carcinomas] as equivalent conditions . . . and on this theory to treat the members of each class alike. Upon this theory it was also legitimate to conceive of a universal causative agent of malignant tumors and thus to subordinate many very obvious differences which clinical experience has established in the origin and behavior of different related tumors” (16). Ewing’s insight that different tumor types might arise from distinct sources and might require specific treatment approaches represented a breakthrough in thinking about cancer. In essence, it envisioned targeted treatment and personalized medicine. Ewing’s achievement arose in an era of great excitement about the promise of scientific medicine. Claude Bernard (1813 to 1878; France) had propagated a stringent scientific method and, through intricate experiments in live animals (vivisection), achieved major advances in physiology (17). The fields of radiology and radiation therapy were born with the fortuitous discovery of X-rays by Wilhelm Conrad Röntgen in 1895, and the discovery of natural radioactivity by Henri Becquerel and Pierre and Marie Curie (18). Surgery matured, spurred by technical improvements and, foremost, by innovations in aseptic techniques and anesthesiology (19). Nursing became a skilled profession and a key component in the fight against disease (20). Alongside and contributing to these advances, hospitals were transformed from charitable asylums for the sick to medical institutions (21). All of these developments together helped lay the scientific groundwork

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for clinical research as we have come to practice it today.

THE ORIGINS OF ONCOLOGY CLINICAL TRIALS Although there are references to what may be loosely considered clinical studies dating back at least to Biblical times, the first true medical trials depended on a specific breakthrough in medical thinking, namely the acceptance of quantitative methods as a fundamental component of clinical research. The notion that simple counting could be a useful tool in medical research arose, as with so many other things, with the ancient Greeks. Epidemiology (from the Greek epi demios, among the people) began with Hippocrates and other Greek physicians, who made rudimentary generalizations about infectious epidemics, such as their seasonal nature. Understanding was limited, however, as the number of cases of specific diseases in defined populations was not collected. The birth of modern epidemiology can be traced to the haberdasher John Graunt (1620 to 1674; Great Britain), who among his varied pursuits studied patterns of death among residents of various London parishes, using numbers and causes reported in the parish clerks’ weekly burial lists (22). By tracking outbreaks of fever and other common causes of death, Graunt demonstrated in stark terms the uses to which simple statistics could be put. Quantitative observation was first introduced to experimental medicine by the groundbreaking work of William Harvey (1578 to 1657) in the seventeenth century, with the description of the circulation of blood on observational and mathematical grounds (23). One of the reasons Harvey’s arguments carried such great weight—were ultimately irresistible—was because of simple calculations he made. Based on the anatomy of the heart (the volume of the left ventricle) and the normal heart rate, Harvey estimated that the average person pumped approximately 540 pounds of blood in an hour. By simple inference, Galen’s theory that the blood supply was replenished daily in the liver could not be true. What human could manufacture, in a 24-hour period, the staggering amount of blood required? A little bit of arithmetic put the lie to 1,500 years of dogma. The first use of simple statistics in a clinical-trial setting occurred in the eighteenth century. Anecdotal reports dating to the 1600s had suggested that citrus fruits could prevent scurvy, which was extraordinarily common among sailors undertaking long ocean voyages. Drawing on his personal observations, the

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Scottish naval surgeon James Lind determined to test the hypothesis that citrus fruits were effective antiscorbutics. In 1854, on board the HMS Salisbury, he selected 12 patients with scurvy, and applied to them sets of two various treatments, including oil of vitriol, vinegar, sea water, oranges and lemons, cider, and a combination of garlic, radish, balsam, and myrrh. Those receiving the fruit recovered within a week (24). Once the Navy adopted these findings and began issuing lemon juice to all its sailors, scurvy was essentially eliminated from the fleet. Despite successes as pioneered by Lind, it was not until well into the twentieth century that the randomized clinical trial—enshrined as the gold standard by which medical therapies are assessed—was formally introduced. The landmark study that launched the modern era of clinical trials evaluated the effectiveness of streptomycin as an antituberculosis agent, and owed its design and execution in large part to the efforts of a statistician who wanted to introduce physicians gently to the concepts of randomization and experimental design, as outlined by colleagues such as Fisher. Austin Bradford Hill, a professor at the London School of Tropical Medicine and Hygiene, was the primary driver behind the study and later the author of a landmark textbook of medical statistics. At the time of the study, there was a limited amount of streptomycin available in Great Britain. This drug scarcity, coupled with the variable natural history of the disease, led Hill and his coinvestigators to believe that a randomized study in which half of the patients would not receive the experimental medication could be ethically justified. Anticipating our contemporary studies, the trial had strict eligibility criteria, including bilateral, progressive lung infiltrates, bacteriologically documented disease, and age between 15 and 30 years. Patients were randomly assigned to bed rest (standard therapy) or streptomycin. Standardized case reports were developed and used, and radiologists were blinded to treatment assignment–assessed serial chest X-rays. When the data were examined, the results could not have been more clear-cut. Substantially greater numbers of patients receiving streptomycin experienced radiographic improvement, and at the end of the 6-month observation period only 8% of those receiving the antibacterial had died, compared with 51% in the bed-rest arm of the study (25). The feasibility and practical utility of a randomized trial had been demonstrated beyond a shadow of a doubt. Additional evidence for the utility of a statistical approach in medicine came from the field of cancer itself, with the publication in the 1950s of the landmark studies correlating smoking with the development of lung cancer. As early as 1761, a linkage between the

development of cancer and exposure to an external agent (a carcinogen) was first postulated, when the London physician and polymath John Hill issued his pamphlet “Cautions Against the immoderate Use of Snuff: Founded on the known Qualities of the Tobacco Plant; and the Effects it must produce when this Way taken into the Body: and Enforced by Instances of Persons who have perished miserably of Diseases, occasioned, or rendered incurable by its Use.” Hill associated heavy snuff use with nasal tumors and, bucking the tide of medical opinion, recommended against its use (26). It was not until the middle of the twentieth century, however, with the development of sophisticated statistical techniques, that the causative relationship between tobacco and cancer became irrefutable. Commissioned by the British Medical Research Council in 1947, Austin Bradford Hill and Richard Doll analyzed potential causes for the dramatically rising mortality from lung cancer. Their comprehensive case-control study of over 2,400 patients identified unequivocally that “smoking is a factor, and an important factor, in the lung” (27). Ernst Wynder and Evarts Graham in the United States published a similar, large survey in over twelve hundred patients the same year, again identifying “tobacco smoking as a possible etiologic factor in bronchiogenic carcinoma” (28). Finally, in the 1960s, the link between smoking and cancer was officially recognized. The streptomycin trial, along with the lung cancer epidemiologic studies, powerfully established the value of a statistical approach to medical research. How was this new thinking incorporated into the justdeveloping field of oncology? In the remainder of this chapter we briefly review the rise of clinical studies in cancer medicine, with a particular emphasis on the development of chemotherapy as illustrative of the wholesale adoption of controlled trials. The notion that chemicals might control cancer actually has an ancient history. Hippocratic doctors treated superficial tumors with ointments containing toxic copper compounds. Later, in the first century BCE, the physician and compounder Dioscorides, one of the patron saints of pharmacy, employed autumn crocus, which has as an active ingredient colchicine, later shown to be possessed of mild antitumor effects. Arsenicals in particular enjoyed widespread use, mostly as topical applications, from ancient Egypt, through Galen and Falloppio, until the early nineteenth century (29). The first successful systemic cancer chemotherapy was published by Heinrich Lissauer, who reported remissions in two patients with leukemia using Fowler’s solution, a then common cure-all based on arsenic (30). In spite of these anecdotal reports, though, and given a profound lack of evidence to support the use of drugs

2 HISTORICAL PERSPECTIVES OF ONCOLOGY CLINICAL TRIALS

or chemicals, standard treatment for cancer in the early twentieth century remained either surgery or radiation therapy. The terminology and concept of modern chemotherapy, the use of chemicals to treat disease, was coined by Paul Ehrlich (1854 to 1915) in the early 1900s. Ehrlich introduced the use of laboratory animals to screen chemicals for their potency against diseases, leading to the development of arsenicals to treat syphilis and trypanosomiasis. He investigated aniline dyes and the first alkylating agents as potential drugs to treat cancer, and summarized his observations in what is known to be the first textbook of chemotherapy (31). In experimental oncology, in the first four decades of the twentieth century, the development of adequate models for cancer drug screening then took center stage (32). A major breakthrough was achieved by George Clowes of Roswell Park Memorial Institute, who developed the first transplantable tumor systems in rodents, allowing for standardized testing of a larger number of drugs (33). Initiation of clinical studies of modern chemotherapy can be traced to World Wars I and II. Use of mustard gas in WW I and an accidental spill of sulfur mustards (Bari Harbor, Italy) in WW II were observed to cause severe lymphoid hypoplasia and myelosuppression in exposed soldiers (34, 35). In 1942, Alfred Gilman and Louis S. Goodman were commissioned by the U.S. State Department to examine the potential therapeutic use of toxic agents developed for chemical warfare (36). When they observed marked regression of lymphoid tumors in mice, they convinced their colleague, thoracic surgeon Gustav Lindskog, to treat a patient with non-Hodgkin’s lymphoma (NHL) with a closely related compound, nitrogen mustard. Significant, albeit temporary, tumor remission was observed. The investigators and colleagues went on to treat several dozen more patients, with variable success. Although nitrogen mustard was clearly no magic bullet for hematologic malignancies, for the first time in history a systemic chemical agent had been shown, under controlled clinical conditions, to combat cancer cells. The principle was established that cancer cells may be more susceptible to certain toxins than are normal cells. In 1946, after wartime secrecy restrictions had been lifted, the clinical data were published, and the era of cancer chemotherapy had arrived (37, 38). In the two decades that followed, improved alkylating agents were developed (e.g., cyclophosphamide, chlorambucil) that became key components of leukemia and lymphoma treatment regimens. More chemotherapeutic approaches were to follow. Sydney Farber observed that folic acid, the vitamin deficient in megaloblastic anemia, stimulated proliferation

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of acute lymphoblastic leukemia (ALL) cells in children. In collaboration with industry, antifolates (aminopterin, amethopterin [methotrexate]) were synthesized and were the first drugs to induce remissions in children with ALL (39). Methotrexate displayed activity against a variety of other malignancies, including breast cancer, ovarian cancer, and head and neck cancer. Most remarkably, single-agent methotrexate was found to be the first chemotherapy agent to cure a solid tumor, choriocarcinoma, a germ cell malignancy originating in the placenta. Methotrexate was also the first agent to demonstrate benefit of adjuvant chemotherapy treatment—to prevent recurrence of osteosarcoma following surgery. Additional anticancer drugs entered clinical trials in the 1950s, including the inhibitor of adenine metabolism 6-mercaptopurine (6-MP), vinca alkaloids, and 5-fluorouracil, an inhibitor of DNA synthesis (32). Natural products such as taxanes (e.g., paclitaxel; 1964; from the bark of the Pacific Yew tree) or camptothecins (e.g., irinotecan; 1966; from a Chinese ornamental tree) were developed under the auspices of C. Gordon Zubrod at the NCI (40). Many more were to follow, including platinum compounds (e.g., cisplatin, carboplatin) or topoisomerase II inhibitors (e.g., anthracyclines or epipodophyllotoxins). In the development of all of these drugs, controlled clinical studies were essential to establish their effectiveness, and it can be argued that oncology has more systematically used the randomized study than any other field in medicine. It has been only 150 years since cancer was recognized as a disease of cells, and a mere six decades since the introduction of the randomized clinical trial. Today, multimodality treatment, often incorporating molecular markers or targeted therapy, has become standard treatment for many malignancies. Our task for the future will be to retain the essential features of the randomized study, while developing new clinical trial methodologies that allow the most efficient investigation of novel therapeutics.

References 1. Greaves MF. Cancer: The Evolutionary Legacy. Oxford; New York: Oxford University Press; 2000. 2. Huxley J. Biological Aspects of Cancer. London: Allen & Unwin; 1958. 3. Urtega OB, Pack GT. On the antiquity of melanoma. Cancer and Metastasis Reviews 1966;19:607–10. 4. Strouhal E. Tumors in the remains of ancient Egyptians. Am J Physical Anthropol 1976;45:613–20. 5. Weiss L. Observations on the antiquity of cancer and metastasis. Cancer and Metastasis Reviews 2000;19(3–4): 193–204. 6. Bryan CP. The Papyrus Ebers. New York: Appleton; 1931. 7. Breasted JH. The Edwin Smith Surgical Papyrus. Special ed. Chicago, Ill.: University of Chicago Press; 1930.

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8. Kardinal CG, Yarbro JW. A conceptual history of cancer. Sem Oncol 1979;6(4):396–408. 9. Siegel RE, Galen. Galen’s System of Physiology and Medicine. Basel, New York: Karger; 1968. 10. Osler W, Camac CNB. Counsels and Ideals from the Writings of William Osler. Boston: Houghton Mifflin; 1906. 11. Rather LJ. Rudolf Virchow’s views on pathology, pathological anatomy, and cellular pathology. Arch Pathol 1966;82:197–204. 12. Hodgkin T, Lister JJ. Notice of some microscopic observations of the blood and animal tissues. Philos Mag 1827;2:130–8. 13. Triolo VA. Nineteenth century foundations of cancer research: advances in tumor pathology, nomenclature, and theories of oncogenesis. Cancer Res 1965;25:75–106. 14. Paget S. The distribution of secondary growths in cancer of the breast. Lancet 1889;133(3421):571–3. 15. Ewing J. Neoplastic Diseases: A Treatise on Tumors. Philadelphia and London: W.B. Saunders Company; 1919. 16. Ewing J, Raney RB. Neoplastic Diseases: A Treatise on Tumors. 3d ed. rev. and enl., with 546 illustrations. Philadelphia, London: W.B. Saunders; 1928. 17. Bernard C. Introduction à l’étude de la médecine expérimentale. Paris: Baillière; 1865. 18. Hayter CR. The clinic as laboratory: the case of radiation therapy, 1896–1920. Bull Hist Med 1998;72(4):663–88. 19. Wangensteen OH, Wangensteen SD. The Rise of Surgery: From Empiric Craft to Scientific Discipline. Minneapolis: University of Minnesota Press; 1978. 20. Maggs C. A General History of Nursing: 1800—1900. In: Bynum WF, Porter R, eds. Companion Encyclopedia of the History of Medicine. London: Routledge; 1993:1300–20. 21. Risley M. House of Healing: The Story of the Hospital. New York: Doubleday, 1961. 22. Rothman KJ. Lessons from John Graunt. Lancet 1996;347 (8993):37–9. 23. Harvey W. An Anatomical Disputation Concerning the Movement of the Heart and Blood in Living Creatures. Oxford: Blackwell Scientific; 1976. 24. Porter R. The Greatest Benefit to Mankind: A Medical History of Humanity. New York: Norton; 1997. 25. Medical Research Council Investigation. Streptomycin treatment of tuberculosis. Br Med J 1948;2:769–782.

26. Petrakis NL. Historic milestones in cancer epidemiology. Sem Oncol 1979;6:433–44. 27. Doll R, Hill AB. Smoking and carcinoma of the lung: preliminary report. Br Med J 1950;2:739–48. 28. Wynder EL, Graham EA. Tobacco smoking as a possible etiologic factor in bronchiogenic carcinoma: a study of 684 proved cases. JAMA 1950;143:329–36. 29. Burchenal JH. The historical development of cancer chemotherapy. Sem Oncol 1977;4:135–46. 30. Lissauer H. Zwei Fälle von Leucaemie. Berl Klin Wochenschr 1865;2:403–5. 31. Ehrlich P. Beiträge zur experimentellen Pathologie und Chemotherapie. Leipzig: Akademischer Verlag; 1909. 32. DeVita VT, Jr., Chu E. A history of cancer chemotherapy. Cancer Res 2008;68:8643–53. 33. Clowes GHA. A study of the influence exerted by a variety of physical and chemical forces on the virulence of carcinoma in mice. Br Med J 1906:1548–54. 34. Krumbhaar EB, Krumbhaar HD. The blood and bone marrow in yellow cross gas poisoning. Journal of Medical Research 1919;40:497–506. 35. Einhorn J. Nitrogen mustard: the origin of chemotherapy for cancer. Int J Radiation Oncol Biol Physics 1985;11:1375–8. 36. Gilman A. The initial clinical trial of nitrogen mustard. American J Surg 1963;105:574–8. 37. Goodman LS, Wintrobe MM, Dameshek W, Goodman MJ, Gilman A, McLennan MT. Nitrogen mustard therapy. Use of methyl-bis(beta-chloroethyl)amine hydrochloride and tris (beta-chloroethyl)amine hydrochloride for Hodgkin’s disease, lymphosarcoma, leukemia and certain allied and miscellaneous disorders. JAMA 1946;132:126–32. 38. Gilman A, Philips FS. The biological actions and therapeutic applications of the B-chloroethyl amines and sulfides. Science 1946;103:409–36. 39. Farber S, Diamond LK, Mercer RD, Sylvester RF, Wolff JA. Temporary remissions in acute leukemia in children produced by folic acid antagonist, 4-aminopteroyl-glutamic acid (aminopterin). N Engl J Med 1948;238:787–93. 40. Chabner BA, Roberts TG. Chemotherapy and the War on Cancer. Nature Rev Cancer 2005;5:65–72.

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Ethical Principles Guiding Clinical Research

Sandra L. Alfano

HISTORICAL PERSPECTIVES

ETHICAL PRINCIPLES

Research involving humans is recognized as essential to the advancement of the practice of medicine. Particularly in oncology, the need for new and innovative treatments remains high, necessitating robust, sound scientific exploration of new treatments. With this fundamental need comes a corollary need: to value and protect the humans who participate in this research, and to pursue sound, ethical research which incorporates that protection. Over the past century, and even into this new millennium, there have been numerous examples of researchers compromising ethical principles in their pursuit of new knowledge. Striking examples, such as the World War II Nazi medical experiments on detainees, the U.S. Public Health Service’s Tuskegee Syphilis Experiment, and the death of Jesse Gelsinger in a gene transfer study have been summarized and analyzed elsewhere (1, 2). As a result of these numerous events, governments and professional organizations have developed codes of conduct or guiding documents to remind us of moral obligations and factors that must be considered when involving humans in research experiments. In particular, for biomedical research, three guidance documents are often referred to in providing a frame of reference for researchers, regulators, and research participants alike.

The Nuremberg Code (3) was generated in 1949 from the Trials of War Criminals before the Nuremberg Military Tribunals in response to worldwide outrage at the use of World War II concentration camp prisoners in cruel human experiments. This simple code reflects a belief that voluntary consent of the human subject is absolutely essential. The fundamental concept of voluntariness was articulated as necessary because detainees had been forced to take part in the experiments, and often put in grave danger, and this was viewed as entirely unacceptable. From this basic concept flows the need for informed decision making, necessitating that the volunteer must be competent, and of sound mind. This requirement for informed consent directly from the subject or volunteer is the foundation of the Nuremberg Code. In 1964, the World Medical Association issued the first Declaration of Helsinki (4), which is intended to be a broader document encompassing obligations of biomedical researchers in the world community. Especially in international clinical research trials, this code provides guidance for ethical conduct of medical research in a variety of clinical settings. The Declaration is regularly revisited and updated, with the latest complete update conducted in 2008.

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In 1974, in response to national outrage in the United States about revelations of the Tuskegee Syphilis Experiment, the U.S. government enacted the National Research Act, which established the Institutional Review Board (IRB) system for regulating research in the United States. IRBs were thus charged with responsibility for protecting the rights and welfare of human subjects participating in research studies, and for ensuring that research is conducted in accordance with accepted ethical standards. The Act also established the “National Commission for Protection of Human Subjects of Biomedical and Behavioral Research.” This national commission met over several years and ultimately issued, in 1979, the Report of the National Commission for the Protection of Human Subjects of Research, which is referred to as the Belmont Report (5). The Belmont Report contains the ethical principles upon which the U.S. federal regulations for protection of human subjects are based: respect for persons, beneficence, and justice. Each of these fundamental principles will be explored in depth in the following sections of this chapter, as they are the underpinnings of our work with human subjects of research. The Belmont Report was used as guidance to Congress in enacting regulations for the protection of human subjects. These regulations, codified in the Code of Federal Regulations (CFR), at 45 CFR 46, “Protection of Human Subjects,” govern the review of research, and are known as the Common Rule (6). The reader should note that there is controversy about how we should refer to the people that enroll in our studies. Table 3.1 provides an overview of this controversy.

RESPECT FOR PERSONS The guiding ethical principle of respect for persons sets out the belief that individuals should be treated as autonomous agents, and that they have the right to selfdetermination. This belief, that subjects have the right to choose what will or will not happen to them, entails the concepts of informed consent and voluntariness. A corollary principle is that those with diminished autonomy should be protected. This introduces the concept of vulnerable subjects (which is explored below), and leaves us with the need to understand that the vulnerability of a given population or person can change over time, depending on the context and situation. This principle is demonstrated through the process of informed consent, requiring attention to capacity, information, comprehension, and voluntariness. There should be thoughtful planning of the process of consent, with the intent of incorporating four elements: informing (conveying information), assessing comprehension, assessing autonomy (capacity to make one’s own decisions), and getting consent (agreement to be a subject). The essence of consent, and the resultant consent form that is used, should be information sharing. Researchers should keep in mind that the intent of a consent form is not to serve as a legal document, but rather to inform the participant. Thus efforts should be made to avoid the use of legalese— contract based terms that serve to focus on legal issues and may tend to diminish comprehension. The process of consent should be conducted as a collaborative dialogue, a negotiation, a give and take, that is intended to facilitate understanding. This of course involves discussion as an educational interchange (not simply

TABLE 3.1

How Should We Refer to Those Who Enroll in Clinical Trials? Harkening back to the National Commission, and the attitudes about research in the 1970s, Belmont and the resultant regulations refer to human subjects. In contrast, perhaps in light of wanting to be more politically correct, some now advocate for referring to those enrolled as participants or volunteers. While some research entails negotiation and collaboration between researchers and those who participate, classic biomedical clinical trials largely do not. There are relative power relationships, with researchers designing and driving the research protocols, and the enrollees agreeing to follow directions. Especially in oncology clinical trials, the person enrolled does not share in development of the protocol nor in research activities in a participatory sense; rather, they are the subjects of the research techniques and the outcomes they endure are the measures of the research. So it is argued that, if we are honest, we should refer to these persons in a truer sense, without establishing or crediting them with more than they are allotted, hence referring to them as human subjects. There is, however, general agreement that those who enroll in clinical trials should not be referred to as patients, in an endeavor to remind all team members that the researcher-subject relationship is quite different than the physician-patient relationship. It is also best to remember that the individual agreeing to enroll in a study must demonstrate a willingness to assume the role; it seems best to be clear about what that role is.

3 ETHICAL PRINCIPLES GUIDING CLINICAL RESEARCH

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TABLE 3.2

How to Conduct the Consent Discussion. · Ensure autonomy. Begin with an invitation to participate, and ensure there is no coercion or undue influence (remove any impediments). · Allow ample time for a considered response. Typically, it is best to solicit consent in advance of commencing research activities, when at all possible. The consent form is not a confidential document; encourage that it be taken home, and shared with family and providers. · Consider breaking up the material into multiple sessions. · Verify understanding, comprehension, and pay attention to verbal and nonverbal cues. · Use witnesses or consent monitors, if necessary. · Consider use of a quiz. · Provide a copy of the signed consent form for the subject to keep; the document may be viewed as a reference. · Consent forms should be written at a 6th or 8th grade reading level and written in the second person (first person language is more contract-oriented).

handing the person the form to read). Efforts should be made to avoid using jargon and medical acronyms which may not be understood by a lay person. There is not universal agreement about the amount of information that should be shared. Too much information may overwhelm the subject and obscure meaningful information. Too little may leave researchers open to criticism for failure to disclose. Perhaps a compromise is to follow the reasonable person standard. The reasonable person is a hypothetical, rational, reasonably intelligent individual who is intended to represent a sort of average citizen. When writing a consent form, it might be helpful to ask, “What would a reasonable person want to know?” The process of consent should be described in the protocol, including a description of where the session will take place, how much time is allotted for consideration, and who will conduct the session. Table 3.2 provides some practical tips on conducting the consent discussion and additional information about the consent document itself, while Table 3.3 emphasizes the ongoing nature of consent. The required elements of consent are detailed in Table 3.4. Obtaining truly informed consent can be challenging, especially when dealing with special

populations, such as children, non-English speaking individuals, and those with decisional impairment. For children, we largely rely on permission granted by the parent(s), but should also demonstrate respect for the child by soliciting their assent in most cases. For older children, or for long-term studies, a plan should also be developed to re-negotiate their personal consent upon reaching the age of majority. Non-English speaking individuals present a challenge, and researchers are reminded that there is a need for initial consent, as well as ongoing communication in a language understood by the subject. This applies to both verbal and written communication, hence leading to the requirement to provide a translated version of the consent document. For verbal translation, it is recommended to avoid using family members who themselves may not understand very well, or who may filter the information to the subject. For the decisionally impaired, generally surrogate consent is solicited from a legally authorized representative (LAR). However, because this situation involves someone other than the participant deciding about enrollment, the decision to allow surrogate consent must be based on degree of risk of harm and probability of direct benefit.

TABLE 3.3

Ongoing Nature of Consent, and Obligation to Share New Information. · Consent process continues throughout study participation. · An informed subject is better able to comply with/complete the study. · Share new information as it becomes available, and renegotiate consent with existing subjects (use consent addendum to direct attention to whatever new information is being shared). · Ask, “Do you want to continue to participate?” · After completion of the study, inform subjects of the results.

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TABLE 3.4

Required Elements of Consent. · Explain that the proposal is research. Describe the purpose, the expected duration of participation, and the required procedures in lay terms (differentiating between standard of care and research). · Describe reasonably foreseeable risks/discomforts. · Describe potential benefits (compensation is not a benefit). · Disclose alternatives, if any. · Promise confidentiality/describe limits (who will have access to study records). · Explain provisions in case of injury, if applicable. · Identify whom to contact with questions. · Explain voluntary participation and right to withdraw (no waiver of rights, no effect on relationships). · Address economic considerations, number of subjects to be enrolled, etc.

BENEFICENCE The second fundamental ethical principle of beneficence tells us that persons are treated in an ethical manner not only by respecting their decisions and protecting them from harm, but also by making efforts to secure their well-being. This Belmont principle generally encompasses two rules: (1) do not harm, and (2) maximize possible benefits/minimize possible harms. This principle translates into a focus on the risk/benefit relationship that is encompassed in the clinical trial. Researchers and their IRBs must make decisions about the currently unknown: when is it justifiable to seek certain benefits despite the risks involved, versus when are the potential benefits insufficient because of the risks? In developing a clinical trial protocol, the researcher should continually ask, “Are the risks presented justified?” This must be addressed both in the initial analysis as part of the development and approval of the proposed protocol, as well as through ongoing monitoring of risks and benefits throughout the study (via a data and safety monitoring plan). An acceptable risk/benefit relationship must exist for a protocol to be approved, and in order for the research to be allowed to continue. Examining the risk side of the relationship requires understanding fundamentally that research by its very nature involves risk; all must accept that subjects may be exposed to risk and may be harmed. The principle reminds us that we have an obligation to minimize the probability of harm, to maximize the potential benefits and to never knowingly cause (permanent) injury. Investigators must identify risks and objectively estimate magnitude and likelihood, both in the protocol for IRB review, as well as in the consent form for potential subjects. The risk/benefit analysis should be presented to prospective subjects in the consent form. A difficult issue to address is the level of

detail required in the consent form when presenting risks. What should be disclosed? One view is that all possible risks, anything that has been seen in trials to date, should be listed in the spirit of full disclosure. Another view is that emphasis should be placed on the most common, most important, most serious risks, so that subjects will be careful in their decision making. A possible compromise is to list at least what a reasonable person would find important to make a decision (see earlier discussion of the Reasonable Person Theory.) Safety of human subjects is of paramount importance; researchers address this through development of appropriate research design, establishment of inclusion/exclusion criteria, and feedback from subjects throughout the study. Despite best efforts, however, it must be acknowledged that not all potential risks are known. Every research protocol should have a data and safety monitoring plan (DSMP) for how data will be reviewed, how safety will be monitored, and how reporting and stopping rules will be accomplished. The plan should be commensurate with risks, size, and complexity of the protocol. Researchers should provide an explicit statement of risk along with the rationale (supported by previous work done). There should be an adverse event grading and attribution scheme that is developed prior to study onset. There must be a plan for reporting unanticipated serious adverse events to appropriate persons/bodies, within an established (prompt) time frame. And there should be an adequate plan for regular safety and data review and reporting. In some instances, a Data and Safety Monitoring Board (7) (DSMB) (also referred to as a Data Monitoring Committee [DMC]) may be established, primarily to provide a broad context for safety monitoring. A DSMB usually looks at global data, including all adverse event reports either completely unblinded or categorized by treatment arm. As such, the DSMB is able to determine whether a clear effect exists in one


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TABLE 3.5

Designing a Sound Scientific and Ethical Research Study. · · · · · · · ·

Start with a highly competent research team. Use a good design, plan for data and safety monitoring, and select least susceptible subjects. Identify opportunities for risk exposure and procedures for minimizing risks. Utilize research procedures that have the least likelihood of harm. Ensure adequate monitoring so that adverse events are quickly identified, managed, and reported. Ensure privacy and confidentiality are protected. Maximize benefits, including direct, indirect, and societal benefits. Goal of all research is to produce generalizable knowledge.

arm of the study versus the other(s). The DSMB is thus able to apply stopping rules, either because of emerging toxicity or because of futility concerns. There are no universal requirements for DSMBs, but they are required by the National Institutes of Health (NIH) for all phase III trials. They may be appropriate for phase I or phase II trials if there are multiple sites, the study is blinded, there are high risks, or vulnerable populations are involved. They may also be required by the IRB if a potential for conflict of interest exists. The benefit assessment is equally challenging, and must be reasonable in relation to the phase of the trial, and what is known to date about effects of the intervention. There may be potential direct benefits to the enrolled subjects, or there may be future benefits to society. There may also be indirect benefits that accrue from participation in research in general. While all types of benefits are legitimate, and may weigh in the risk/benefit assessment, researchers must be careful to avoid overstating potential benefits. Table 3.5 provides considerations in the design of a research study, to emphasize sound scientific design in ethical research.

JUSTICE The Belmont Report tells us, “An injustice occurs when some benefit to which a person is entitled is denied without good reason or when some burden is imposed unduly. . . .” This sets up an ethical obligation: the fair sharing of burdens and benefits, with the corresponding requirement to ensure equitable selection of research subjects. This is manifest in fairness in inclusion and exclusion criteria, asking the questions, “Does the research involve individuals who are unlikely to benefit from the results of the research?” and “Who is likely to benefit? What connection do they have to the research subjects?” It is important to note that when the Belmont Report was written, there was a national

attitude of protectionism, which focused on the potential risks or burdens of research, and the need to protect subjects from the unfair burden of research. In the late 1980s, there began a movement that focused more on fairness in access to the potential benefits as a justice issue. There was attention given to expanded access to clinical trials and earlier access to investigational agents, which continues today. Researchers need to be attuned to both sides of this issue, ensuring appropriate inclusion to distribute possible benefits, while also avoiding targeting one group to bear the risks that will offer benefits to others. A critical aspect of the principle of justice focuses on development of inclusion and exclusion criteria for the clinical trial. These criteria embody the attributes necessary to accomplish the purpose of the research. Well defined criteria will increase the likelihood of producing reliable and reproducible results, decrease the likelihood of harm, and guard against exploitation of vulnerable populations. The concept of vulnerability deserves some consideration. Federal regulations define such subjects as: [V]ulnerable to coercion or undue influence, such as children, prisoners, pregnant women, mentally disabled persons, or economically or educationally disadvantaged persons . . . [and require that] . . . additional safeguards have been included in the study to protect the rights and welfare of these subjects. Protections that must be in place for the aforementioned groups are specified in special subparts of the federal regulations. But it is important to recognize that vulnerability extends beyond these defined groups, and really reflects a condition in which there is a substantial inability to protect one’s own interests. This condition thus interferes with autonomy or decision-making capacity, and may involve personal circumstances which expose subjects

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TABLE 3.6

IRB Approval Considerations, in the Context of Ethical Principles. · · · · · · ·

Is the risk/benefit relationship reasonable? Are risks minimized? Is selection of subjects equitable? Is appropriate informed consent planned? Will the data collected be adequately monitored? Are there adequate provisions to protect privacy and maintain confidentiality of data? Are there additional safeguards, if needed (children, prisoners, decisionally impaired, etc.)?

to intimidation or exploitation. Examples of potentially vulnerable populations include children, prisoners, pregnant women, critically ill, decisionally impaired (beyond those with cognitive deficits, consider those with brain metastases, those who have just received a devastating diagnosis), homeless who need money, and some clinic populations. Researchers should consider implementing additional safeguards for these populations. For example, the researcher or the IRB may place limits on level of risk to which such subjects may be exposed, or may require or allow surrogate consent, or use of a consent monitor, subject advocate, or quizzes to assess comprehension. Some would also advocate introduction of a delay in the consenting process, to allow adequate time for decision making, and for some populations it could be useful to consider use of an independent evaluator, or incorporation of a DSMB. Recruitment of subjects is an important activity which starts the subject selection process, and thus must be sound and ethical. The IRB must review and approve methodology and content, since this activity is considered the beginning of the consent process. Methodologies might include advertisements, internet postings, registries, use of targeted letters, phone calls, and so forth. Efforts must be in place to ensure that recruitment activities are accurate and truthful, and do not overemphasize benefits or payments, and do not underestimate possible risks.

IRB APPROVAL ISSUES The IRB is responsible for protecting the rights and welfare of human subjects participating in research studies and ensuring that research is conducted in accordance with accepted ethical standards. Table 3.6 and Table 3.7 review approval considerations for research protocols, and focus on evaluation of the protocol application and the consent form. For initial IRB review, there will be scrutiny of the risk profile, the plan

for data and safety monitoring, and the consent process. For continuing IRB review, the focus will be on whether there is any new information which might alter the risk/benefit ratio, and whether unanticipated problems have occurred. Accrual will also be examined, to be certain the trial is proceeding according to plan, and to allow project completion and generation of reliable results. SPECIAL TOPICS FOR CONSIDERATION Ethical Issues with Phase I Oncology Trials In biomedical research, the early work that is done in translation of laboratory (preclinical) research into the clinical arena in humans is referred to as phase I research. It is important to recognize that the major objective of a phase I study is to characterize the investigational agent’s toxicity profile, and to determine a dose and schedule appropriate for phase II testing.

TABLE 3.7

How Are the Principles Applied? · Careful review of the protocol, especially the · Research hypothesis, scientific rationale, and study design · Inclusion/exclusion criteria · DSMP and stopping rules · Risks/benefits · Consent process · Confidentiality provisions · In case of injury section · Careful review of the consent form, ensuring that the · Purpose and research procedures are well described · Risks and anticipated benefits are reasonable · Confidentiality and privacy are addressed · Alternative treatments are explained · Voluntariness is stressed


While traditional phase I studies use healthy volunteers, phase I oncology trials typically use patients with cancer who have exhausted standard therapy. This approach, which is deemed scientifically appropriate, and which is intended to minimize toxicity exposure for healthy volunteers, may nonetheless be ethically suspect. Concerns center on design (designed to characterize toxicity), benefit (little to no benefit to participants), and risks (unknown risks, often felt therefore to be potentially high risk.) Indeed, older data estimates that the benefit, as measured by response rate, is only about 1.5% to 5%, while the risk of toxicity is substantial, with an actual mortality rate of approximately 0.5% (8). The relatively low clinical benefit coupled with a small but definite risk of death and serious but unquantified adverse effects leads to concerns over the risk/benefit balance being too heavily weighted on the risk side. These concerns are compounded by the need for a substantial time commitment from participants, often at the end of life. And there are concerns that perhaps informed consent is given under the cloud of the therapeutic misconception. This is a misunderstanding that participating in research is the same as receiving individualized treatment from a physician. Research subjects fail to appreciate that the aim of research is to obtain scientific knowledge, and that any benefit that may accrue is a by-product of the research. The question is, if a cancer patient really knew/understood the intentions of a phase I trial, how could they possibly agree to participate in a phase I oncology trial? There are concerns with deficient disclosure, exaggeration of benefits, and minimization of risks. Critics argue that these people either are not given accurate information, or fail to understand the information they are provided. Most patients have deficient understanding of the objectives of phase I research, as cancer patients legitimately hope for stabilization, improvement, or even cure. Being potentially vulnerable subjects, their thinking may be clouded, and some say they may be unable to make their own decisions. In addition to concerns about adequate consent, there are ethical concerns about the risk/benefit balance. Is there risk? Certainly, but hopefully it is minimized to the greatest extent possible. Is there benefit? Maybe, but certainly it is minimal due to study design. So, how do we assess the risk/benefit ratio? What standard is used to calculate the answer? Who gets to decide? Several authors have turned to more recent data to try to answer these questions. Roberts et al. (9) examined American Society of Clinical Oncology (ASCO) data from 1991 to 2002, and found results

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supportive of the older data mentioned above. There were 243 objective responses among 6,474 patients (3.8% response rate), 137 deaths from any cause, 35 of which were classified as fatal toxicity (0.54%) and 670 nonfatal serious grade 3 or 4 toxic events (for an overall serious toxicity rate of 10.3%). Adding a different perspective, however, was the review by Horstmann and colleagues (10) which examined Cancer Therapy Evaluation Program (CTEP) data from the National Cancer Institute (NCI) from 1991 to 2002. They reported a 10.6% response rate (7.5% partial, 3.1% complete), and also noted that 34.1% had stable disease or less-than-partial response. This response was accompanied by 58/11,935 deaths (0.49%) at least possibly related, but 18 definitely related and 7 probably related (0.21% fatal toxicity), and 14.3% had grade 4 toxic effects in a subset of studies, but overall, 5,251 grade 4 toxic effects were reported in 11,935 participants (44%). So certainly there are risks such as death due to the agent being tested (fatal toxicity) as well as grade 4 serious adverse events and a substantial time commitment at end of life. But, these significant risks might be considered offset by the better response proportions noted in the Horstmann review. In addition, there truly are several different types of benefits, as described by Glannon (11): Direct benefit: direct physiologic effect from the intervention; Collateral (indirect) benefit: inclusional benefit from participating in the research, and Aspirational benefit: benefit to society and future patients from results of the study. Glannon describes rationality and decision making, contrasting the therapeutic misconception (a belief in a direct benefit without much, if any, consideration of risk) against rational therapeutic optimism (weighing low probable benefit against risk when one is facing death). Agrawal et al. (12) described four areas of the decision-making process in phase I oncology trials: how subjects perceive their options and alternatives, what pressures they feel, how they understand the purpose and risks, and how they assess benefits. They interviewed 163 subjects who had enrolled in a phase I oncology trial, and found that the majority were well aware of alternatives but largely did not consider them. Subjects did not feel a lot of pressure to participate from researchers or family, but 75% felt pressure because their cancer was growing. They reported that the research purpose to kill cancer cells was most important in their decision making, and that even a 10% chance of death would not dissuade their participation. These authors went on to conclude that these phase I participants might be viewed as therapeutic optimists: they hoped to benefit although they recognized that others would not. So it seems that while

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there may be ethical concerns with phase I oncology trials, limited empirical data support the continued practice of enrolling end-stage oncology patients rather than healthy volunteers. Ethical Issues with Tissue and Data Banking Biomedical research is increasingly recognizing the value of the samples and the data that are collected as part of clinical trials. This has led to a push in recent years to bank samples in various repositories to allow continued future research use. Several ethical concerns arise when considering repositories, involving concerns that touch all three ethical principles: · Respect for persons concerns involve adequacy of informed consent, ensuring autonomy, ensuring the right to withdrawal, and privacy and confidentiality of the information. Recommendations are that the purpose of future research be specified in the consent process to the extent possible. Donors should be told who will have access to their information, and what identifiers will be associated with the sample. Where human genetic research is anticipated, the consent form must describe the possible consequences. Consents should specify conditions whereby subjects may withdraw their participation, and whether this will involve destruction of the samples or simple anonymization. · Beneficence concerns arise, as it is agreed that there is generally no direct benefit for the donor, but only indirect or societal benefit, thus necessitating attention to minimizing risk. The main risks involve a potential breach of confidentiality, along with a perceived fear of harm of discrimination, and a possible effect on access to or retention of benefits or entitlements (health or life insurance, employability, etc.). Also feared are possible stigmatization and the possibility of altered family relationships. These risks may be minimized by coding or de-identifying samples, using secure storage and computerized systems that utilize secure servers or encryption. · Justice concerns are centered primarily on ownership issues (13). In the limited cases to date, it seems the courts say that subjects forfeit ownership upon donation (signing informed consent) and voluntary withdrawal from the research (repository) does not equate to directing use or transferring ownership. It is, however, recognized that proprietary rights belong to the subject if the cells are still within the subject. The ownership and justice issues are not resolved yet and may evolve over time. Guidance for managing all of these issues has been developed by the NIH (14)

and the Office for Human Research Protections (OHRP) (15). Conflict of Interest Increasing national scrutiny is being given to those situations in which financial or other personal considerations may compromise, or appear to compromise, the investigator’s professional judgment in conducting or reporting research. It is thought that financial interests held by those conducting research may compromise or appear to compromise the fulfillment of ethical obligations regarding the well-being of the research subjects. Obviously, other issues beyond financial matters may affect conduct, such as seeking prestige, promotion, publication, or prizes. But it is typically the financial interests which garner the most attention and scrutiny, and which may undermine the credibility of the research. When conflicts of interest do arise, they must be recognized, disclosed, and either eliminated or properly managed. Disclosure is a key concept. Financial interests determined to be a conflict of interest may be managed by eliminating them or mitigating their impact. A variety of methods (or combinations) may be effective to minimize risks to subjects. Consider, “Would the rights and welfare of human subjects be better protected by any (or a combination) of the following”: Reduction or elimination of the financial interest; disclosure of the financial interest to the prospective subject; separation of responsibilities; additional oversight or monitoring of the research; modification of the roles of particular research personnel; or change in location of specific research related activities? Unsettled issues remain, and may be explored through the following questions: Is it enough to inform human subjects of the investigator’s financial or potential financial interests? Will disclosing the information to a research volunteer affect their decision to participate? Will it make the process any safer for them? Can financial conflicts be managed in a way that doesn’t adversely affect patient safety or influence the objectivity of the research conclusions? It is critical to recognize that conflicts of interest reflect a situation, not a behavior, nor an indictment. Current approaches involve disclosure, followed by elimination, or mitigation, and management.


FUTURE ISSUES The IRB system as described in this chapter has been in place for decades, and some call for a major overhaul of the system. Some advocate for a system of regional or national review, in lieu of the local institutional review system that predominates now. The National Cancer Institute has developed the Central IRB (CIRB). Information is available at its Web site, http://www .ncicirb.org. Institutions wishing to use this mechanism must enter into an agreement with the National Cancer Institute (NCI). While there may be criticism of the current IRB system, another perspective calls for heightened scrutiny of conflicts and enhancement of existing protections for human subjects. The tension between too much and too little oversight is likely to continue to grow in a regulated industry such as clinical research. Another future issue will be the tailoring of protocols to small molecule targets, or genetics of receptors, which may raise new ethical issues that clinical researchers will need to grapple with in developing appropriate research designs. Finally, there already is a strong advocacy for registration of clinical trials in a public forum, such as the NIH Web site (http://clinicaltrials.gov). In coming years, this registration will evolve to a requirement for the posting of results, in an effort to better disseminate the results of research.

References 1. Levine RJ. Ethics and regulation of clinical research. 2nd ed. Baltimore: Urban and Schwarzenberg; 1986. 2. Dunn CM, Chadwick GL. Protecting study volunteers in research. 3rd ed. Boston: Thomson Centerwatch; 2004.

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3. Nuremberg Code. Trials of War Criminals before the Nuremberg Military Tribunals under Control Council Law No. 10, Vol. 2, pp. 181–182. Washington, D.C.: U.S. Government Printing Office, 1949. (Accessed August 15, 2008, at http://www.hhs.gov/ohrp/references/nurcode.htm.) 4. World Medical Association. Declaration of Helsinki: Ethical Principles for Medical Research Involving Human Subjects. Adopted by the 18th WMA General Assembly, Helsinki, Finland, June 1964, and as revised by the 52nd WMA General Assembly, Edinburgh, Scotland, October 2000. (Accessed June 16, 2008, at http://www.wma.net/e/policy/b3.htm.) 5. The National Commission for the Protection of Human Subjects of Biomedical and Behavioral Research. The Belmont Report, Ethical Principles and Guidelines for the Protection of Human Subjects of Research, April 18, 1979. (Accessed August 15, 2008 at http://www.hhs.gov/ohrp/humansubjects/ guidance/belmont.htm.) 6. Code of Federal Regulations. Title 45 Public Welfare Department of Health and Human Services; Part 46 Protection of Human Subjects, June 23, 2005. (Accessed August 15, 2008, at http://www.hhs.gov/ohrp/humansubjects/guidance/45cfr46.htm.) 7. Slutsky AS, Lavery JV. Data and safety monitoring boards. N Engl J Med. 2004;350:1143–1147. 8. Decoster G, Stein G, Holdener EE. Responses and toxic deaths in phase I clinical trials. Ann Oncol. 1990;1:175–181. 9. Roberts TG, Goulart BH, Squitieri L, et al. Trends in the risks and benefits to patients with cancer participating in phase 1 clinical trials. JAMA. 2004;292:2130–2140. 10. Horstmann E, McCabe MS, Grochow L, et al. Risks and benefits of phase 1 oncology trials, 1991–2002. NEJM. 2005;352:895–904. 11. Glannon W. Phase I oncology trials: why the therapeutic misconception will not go away. J Med Ethics. 2006;32:252–255. 12. Agrawal M, Grady C, Fairclough DL, Meropol NJ, Maynard K, Emanuel EJ. Patients’ decision-making process regarding participation in phase I oncology research. J Clin Onc. 2006;24:4479–4484. 13. Charo RA. Body of research-ownership and use of human tissue. N Engl J Med. 2006;355:1517–1519. 14. Research Involving Private Information or Biological Specimens. (Accessed June 16, 2008, at http://grants.nih.gov/ grants/policy/hs/PrivateInfoOrBioSpecimensDecisionChart.pdf.) 15. Issues to Consider in the Research Use of Stored Data or Tissues November 7, 1997. (Accessed June 16, 2008, at http://www.hhs .gov/ohrp/humansubjects/guidance/reposit.htm.)


4

Preclinical Drug Assessment

Cindy H. Chau William Douglas Figg

The oncology drug development process spans from the discovery and screening phase to preclinical and clinical testing (Fig. 4.1). Preclinical drug assessment remains one of the most important aspects of a successful drug development program. Preclinical research must show that a drug candidate not only possesses therapeutic benefit but also establish that it will not expose humans to unreasonable risks when used in limited, early-stage clinical testing. Well-designed pharmacology, toxicology, and pharmacokinetic studies are important to support safe use conditions for human trials with oncology drugs. An investigational new drug (IND) exemption (which includes information on animal pharmacology and toxicology studies, manufacturing information, and clinical protocols and investigator information) is filed with the Food and Drug Administration (FDA) before an experimental drug might proceed to human studies. The regulatory aspect (which includes details of the IND application) of the drug development process will be discussed in a separate chapter. The focus of this chapter will be on preclinical testing, which includes a discussion of various technological advances and preclinical models used to determine the pharmacological profile of the drug and evaluate the acute and short-term toxicity of the drug in at least two species of animals. Recent advances in drug discovery programs have identified a large number of drug targets utilizing sophisticated methods such as genomic/proteomic

analyses, high-throughput compound screening, and structure-based drug design. Developing appropriate preclinical models that are predictive of human malignancies will enable the selection of potential drug candidates for further clinical investigation. One of the challenges lies in overcoming the issue where agents that looked promising in the preclinical phase of development ultimately failed in pivotal phase 3 clinical trials. In this regard there is a critical need for better approaches to preclinical drug assessment so that only the most promising agents are advanced for further clinical evaluation. Preclinical models theoretically should define whether a particular potential therapy has activity against tumors with the appropriate drug target, and whether or not activity might be expected in patients at tolerated doses. The interpretation of data from preclinical models is often perceived as a bottleneck in drug development, and it is hoped that the selection of appropriate animal models with reproducible activity can portend to a subsequent successful clinical development pathway. Existing models that have been used in the development of traditional cytotoxic drugs will need to be reevaluated and refined for the newer molecularly targeted drugs. Indeed the emergence of targeted therapy has resulted in a shift in preclinical drug assessment strategies in an attempt to bridge the gap between preclinical models and clinical efficacy. This chapter will describe recent

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Preclinical Drug Assessment

Phase of Development

Primary Objectives

Discovery

Target identification & validation; screening; lead discovery & optimization

Clinical Drug Assessment

Preclinical

Clinical Trials

Testing

Post-marketing Surveillance

Laboratory & animal studies; assess safety & biological activity

Determine safety & efficacy in Phase 0-3 studies

Monitor for safety & side effects in Phase 4 studies

FIGURE 4.1 Stages of the drug discovery and development process.

technological advances in in vitro and in vivo models used in cancer drug development that enable drug assessment at the preclinical phase and evaluate their strengths and weaknesses. The chapter will address how preclinical drug assessment can be best implemented to make the drug development process more efficient and accurate.

UNDERSTANDING TECHNOLOGICAL ADVANCES IN CANCER DRUG DISCOVERY AND DEVELOPMENT The availability of complete genome sequence information and most recently the first report of the cancer genome (1) have provided an abundance of new opportunities for discovering novel cancer-related gene expressions and/or mutations. This pioneering work sets the stage for the use of a more comprehensive, genome-wide approach to unravel the genetic basis of cancer and is the foundation for developing more effective therapies for cancer treatment. These advances have become the basis in preclinical research for a variety of high-throughput screens to identify potential drug targets, for lead optimization, and to determine the extent to which lead compounds affect particular molecular pathways. Perhaps the roots of much of the progress and promise in cancer drug discovery programs lies in the advent of gene expression microarray analyses and related technologies such as genomics and proteomics (2). Indeed, the integration of various technologies proves pivotal to not only target identification, characterization, and validation, but also lead to

optimization. In fact, the platform applied in target discovery can also be further developed and used in analytical validation, such as in the case for biomarker discovery and validation platforms. Target measurements can be assessed at different molecular and biological levels with different technologies. Selection of an appropriate assay largely depends on the feasibility of preclinical data interpretation and the limitations of the respective technology. A genomics approach consists of various methods that measure gene expression analysis, such as in microarrays, which has become the standard technology used for target identification and validation. Reverse transcription-polymerase chain reaction is a very sensitive, reproducible technology and often times used to validate microarray-generated data. Comparative genomic hybridization can be used to detect chromosomal alterations associated with certain cancers. Proteomics involves global protein profiling to provide information about protein abundance, location, modification, and protein-protein interactions, as well as to determine the functional relationships among these proteins and how protein complexes are altered in cancer cells or in response to therapy. As such, proteomics provide researchers with valuable information much more rapidly than traditional methods (e.g., cloning and sequencing of genes) for establishing functional relationships among proteins (3). While proteomics is a discovery technology, immunoassays are routinely used for protein assessments due to its straightforward clinical application and translation into a potential diagnostic assay. The multiplexing of protein assays can increase the throughput for simultaneous analysis of several proteins;

4 PRECLINICAL DRUG ASSESSMENT

however, it is limited by the need to standardize assay conditions, the loss of sensitivity over single assays, and the quality control of each analyte in the complete multiplex panel (4). Metabonomics (or metabolomics) is the profiling of endogenous metabolites in biofluids or tissue for characterization of the metabolic phenotype. The analytical platforms used are based on nuclear magnetic resonance spectroscopy and the combination of liquid chromatography with mass spectroscopy. It is principally used in drug discovery, although by definition it is the ultimate end-point measurement of biological events. Yet the technology is limited by the lack of comprehensive metabolite databases and throughput both of which affect data analysis and interpretation. The integration of these technologies lends to a new field that blends molecular biology and computer science, or bioinformatics, where linking expression data derived from genomic/proteomic approaches to target biological pathways can provide a comprehensive understanding of the disease biology and further validating the molecular target (5). Progress in both genomics and proteomics research has resulted in the need for bioinformatics research to develop increasingly sophisticated analytical software, powerful statistical methods, and user interfaces for database management and experimental data mining. Screening of drug candidates may rely on improved and accelerated methods for determining structure-activity relationships that involve both traditional and modified high-throughput screening of very large combinatorial libraries of compounds as well as in silico molecular modeling (or rational drug design). To further identify or validate therapeutic targets, and to assess drug efficacy and toxicity in in vitro or in vivo systems, researchers may employ animal models with precisely defined genetic backgrounds. The creation of gene knockouts in a wide variety of organisms can be achieved by using RNA interference technology. A knockout enables scientists to examine experimental animals without the gene of interest under various experimental conditions, and reveal what would happen if an agent against that target were completely effective. As such, the advent of new technology (genomics, proteomics, etc.), combinatorial chemistry, and highthroughput screening for the identification of potential lead compounds has markedly expanded the cancer drug pipeline. Progress in understanding the genetic and molecular basis of cancer has intensified efforts to identify more selective and targeted anticancer compounds; hence, altering the preclinical models and methods used during the evaluation process of these drugs.

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PRECLINICAL EVALUATION PROCESS Proper preclinical evaluation of drug candidates can improve the predictive value, lessen the time and cost of launching new products, and accelerate the drug development process. The preclinical phase of drug development ranges from lead candidate selection, to establishing proof of concept and toxicity testing, to the selection of the first human doses. The preclinical evaluation process includes establishing safety and toxicity endpoints, the selection of relevant species, pharmacological characterization, and appropriate analysis and interpretation of preclinical data. Current preclinical safety assessments vary among cytotoxics, small molecules, and biologics. Preclinical efficacy testing occurs in various in vivo models of cancer to evaluate anticancer activity and preclinical oncology assessments of drug candidates. These animal models include the traditional syngeneic and human tumor xenografts, as well as the orthotopic and transgenic tumor models. The application of imaging technologies makes all of these model systems more quantitative, particularly enhancing the efficiency of orthotopic and transgenic models. Additional functional imaging studies provide an integrated and quantitative correlation of drug efficacy with mechanism of action.

PRECLINICAL MODELS IN CANCER DRUG DISCOVERY AND DEVELOPMENT Preclinical screening of anticancer drugs involves testing in two different types of systems: in vitro biochemical screens, cell-based assays, or tissue culture systems, and in vivo animal models. The National Cancer Institute (NCI) has been involved in the discovery and development of many anticancer agents over the years. To support the preclinical development of novel therapeutic modalities for cancer, NCI established the Developmental Therapeutics Program (DTP) to provide in vitro and in vivo screening services to select and advance active agents in preclinical models toward clinical evaluation. The next section describes various preclinical models used to advance drug candidates from preclinical to clinical testing. The NCI Human Tumor Cell Line (60-Cell) Screen DTP initiated an in vitro screen for potential anticancer drugs utilizing a panel of 60 human tumor cell lines derived from various tissue types, representing

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leukemia, melanoma, and cancers of the lung, colon, brain, ovary, breast, prostate, and kidney (6). Natural products collected in an NCI repository are also a major source of chemical entities screened. The aim of the screen is to aid in the selection of a lead compound or for further development of a particular class of synthetic or natural compounds that demonstrate selective growth inhibition or cell killing of particular tumor cell lines. For a given compound, a dose response data set is produced that gives a biological response pattern that can be utilized in pattern recognition algorithms to either assign a putative mechanism of action or to determine that the response pattern is unique. Compounds with similar mechanisms of action tend to have similar patterns of growth inhibition in the 60 cell line screen (7). The pattern of response of the cell lines as a group can be used to rank a compound according to the likelihood of sharing common mechanisms. The COMPARE computer algorithm quantifies this pattern (8), and COMPARE searches the database of screened agents to compile a list of the compounds that are most similar (9). This approach has been used to identify novel tubulin-interacting compounds and topoisomerase poisons (10, 11). Moving beyond growth inhibition and cell killing to characterizing mechanisms of action through the expression of molecular targets in the 60 cell lines (8), NCI has developed collaborations with the cancer research community to establish a Molecular Targets database. Following characterization of various molecular targets in the 60 cell lines, it may also be possible to select compounds most likely to interact with a specific molecular target using the COMPARE algorithm. Data available in the database include mutation status of genes important in cancer, quantitation of proteins, and RNA levels within cells, enzyme activity, and microarray data measuring the baseline expression of thousands of genes (7). While the DTP databases are resourceful to the discovery and screening process, it is important to emphasize that any correlations generated with COMPARE analysis or between compounds and Molecular Targets need to be verified experimentally. Additionally, a potential weakness in the use of human tumor cell lines used in the discovery and characterization of new therapeutic drugs is that they may have lost the important properties originally possessed in vivo. In fact, cellular differences in biological properties were demonstrated in a comparison of human tumor cell lines and of primary cultures of tumor material taken directly at surgery from cancer patients (12). Therefore, it is especially important to identify cell lines that preserve potential targets and hence research using primary cultures and early-passage cell lines may prove useful in drug discovery.

Nonetheless, NCI is also reclassifying the cells in the panel according to the types of genetic defects the cells carry. This would enable drugs that address the specific defects or targets to be identified and theoretically be matched to a patient’s tumor cell makeup. This should prove useful and important in the current era of personalized medicine. Hollow Fiber Technology Once compounds are identified as possessing some evidence of anti-proliferative activity in in vitro assays, further evaluation in in vivo models would be the next step. However, the cost and time of running the laborintensive conventional xenograft models with empirical dosing strategies for all possible lead compounds would greatly reduce the rate at which compounds could be evaluated. A short term in vivo assay, the hollow fiber model, was developed by NCI given the fact that in vitro screening efforts exceeded the available capacity for traditional xenograft model testing. These assays used semipermeable hollow fibers implanted in animals. The fibers allow tumor cells to grow in contact with each other, and more than one tumor can be implanted into a single animal providing greater efficiencies than would be obtained through a single in vivo experiment (13). A standard panel of 12 tumor cell lines is used for the routine hollow-fiber screening of compounds with in vitro activity, and alternate lines can be used for specialized testing on a nonroutine basis. The premise of this technique is that advancing potential anticancer agents identified in an in vitro screen to preclinical development requires a demonstration of in vivo efficacy in one or more animal models (14). Hollow fiber screens can indeed define compounds that go on to show evidence of in vivo activity in traditional xenograft models and appear to correlate well with clinical results (15). The hollow fiber assay is not intended to replace detailed biological models such as transgenic or knockout models. Rather it is used as an initial point of triage to determine and prioritize compounds that should be further studied in detailed in vivo models for further pharmacological and mechanistic studies.

Human Tumor Xenografts Human tumor xenografts grown subcutaneouly (s.c.) in nude or in mice with severe combined immunodeficiency representing all major tumor types have played a significant role in preclinical anticancer drug development testing in vivo. Their use has been validated for


cytotoxics as predictive indicators of probable clinical activity, playing a pivotal role in late preclinical agent optimization and guiding the selection of candidates for phase I trials (15). In parallel with efficacy determinations, the xenograft model is useful in determining the agent’s pharmacokinetic and pharmacodynamic markers of response for subsequent clinical applications in that it provides a renewable and readily accessible source of target human tumor cells. Limitations to this model system include the time and expense (relative to the hollow fiber assay and in vitro testing), ethical issues around animal experimentation, a general lack of metastatic spread from primary s.c. implanted xenografts and thus not a good model for studying anti-metastatic strategies, and instances where the model is inappropriate as a likely predictor of clinical outcome (16). Orthotopic Model Systems Orthotopic models of cancer were developed in attempt to address one of the major drawbacks of s.c. tumor xenografts in that they do not reproduce the primary site of the common human cancers, nor do they represent the common sites of metastasis. Considerable effort has been made to develop more clinically relevant models by using orthotopic transplantation of tumors in rodents from a variety of tumor types into the appropriate anatomical site and often these tumors will metastasize in a similar manner as the same tumor type will in human cancer. It is now clear that the process of metastasis is more efficient in orthotopically implanted tumors and mimics human metastasis (17). A number of clinically relevant targets will be better represented by orthotopic model systems that mimic the morphology, microenvironment, and growth and metastatic patterns of human cancer. Limitations to orthotopic models include the technical aspect of the procedures, which are more difficult and time-consuming, and, hence, more expensive than conventional s.c. models. In addition, the endpoints for determining the therapeutic effects are more complex than the normal tumor measurements in s.c. models (18). Although imaging studies have indicated the potential for monitoring tumor growth noninvasively, it is still unclear whether the use of orthotopic versus s.c. tumors results in a better prediction of clinical response. For example, the matrix metalloproteinase inhibitor Batimastat was shown to reduce tumor progression in an orthotopic model of colon cancer (19), but this compound has subsequently failed clinical testing; thus, orthotopic tumors may overestimate potential clinical efficacy.

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Spontaneous and Genetically Engineered Animal Models Alternatives to tumor transplantation models are animals that naturally develop cancers with features relevant to human disease. These models include mice that are genetically engineered to develop cancer and companion (pet) animals that naturally develop cancers. A detailed discussion of the strengths and weaknesses of these models and their appropriate use in integrated drug development programs is reviewed in Hansen and Khanna (20). Briefly, genetically engineered mice are generally immunocompetent, and the tumors they develop are genetically mouse and localized in the usual sites. Limitations of these models include the requirements for breeding the animals that make these models high cost and the tumors usually develop late in the animal’s lifespan; so these models are slow in developing. There are few tumor types available, hence making it difficult to obtain enough animals to establish reliable statistics. Moreover, very few of these models have been validated as representative of human disease. IMAGING TECHNOLOGY Advances in novel imaging approaches have profound implications for drug development, especially imaging methods that are suitable for rodents as they offer opportunities for anticancer efficacy models. The application of imaging makes these in vivo model systems more quantitative, particularly enhancing the efficiency of orthotopic and transgenic models. Molecular and functional imaging technologies are used to assess cell proliferation and apoptosis (e.g., 18F-fluoro-L-thymidine and 99mTc-annexin imaging), cellular metabolism (e.g., 18 F-fluorodeoxyglucose positron emission tomography), and angiogenesis and vascular dynamics (e.g., dynamic contrast-enhanced computed tomography and magnetic resonance imaging). In addition to assessment of anticancer activity, additional functional imaging studies provide an integrated and quantitative correlation of drug efficacy with mechanism of action. Bioluminescence offers an opportunity to develop rodent models for efficacy evaluations that are more sensitive, more specific and of shorter duration than those traditionally used as well as with sensitive endpoints in the luciferase read-out (21, 22). These include models using orthotopic implant sites that were previously difficult to monitor for tumor growth. Transgenic mice bearing a luciferase reporter mechanism can be used to monitor the tumor microenvironment and to signal when transforming events occur. The limitation to using bioluminescence as an endpoint in efficacy studies is the requirement for tumor cell lines that

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express luciferase, although some commercial sources of luciferase-expressing tumor cell lines are slowly becoming available (22).

TOXICOLOGY EVALUATION The Toxicology and Pharmacology Branch of the NCI performs pharmacological and toxicological evaluations of new oncology agents. Once a compound of interest is identified, animal models are critical to assess preclinical toxicology. The FDA requires that preclinical toxicology studies be conducted in two species, a rodent and a nonrodent for all small molecules, with the determination of maximum tolerated dose and drug behavior in the animal (pharmacokinetics) in both species (23). This requirement for safety/toxicity data results in a variety of studies (pharmacokinetics, pharmacodynamics, range-finding toxicity, IND-enabling toxicity studies) usually being conducted in rats and dogs for most new chemical entities (NCE). Mice, while favored for preclinical efficacy studies, are not typically used as the rodent species for toxicology studies because they tend to be poorer predictors of human toxicity, and their small size precludes serial blood sampling (24, 25). For both traditional cytotoxic and molecular target-based NCEs, there is the need to develop sensitive methodology to determine pharmacokinetics in various species, including plasma protein binding as well as determine whether metabolism is important and to identify metabolic pathways. If possible, appropriate biomarkers are selected to assess target modulation and develop sensitive methodology to determine the impact of drug treatment on targets in tumors and selected normal tissues. Finally, there is the need to determine the maximal tolerated doses and dose limiting toxicities in single dose studies in both a rodent and nonrodent using abbreviated study designs as a prelude to other repeated dose range-finding studies or definitive IND-enabling studies (26). In the current era of molecular target-based therapies, methodology to determine whether modulating the tumor molecular target is also responsible for toxicity is developed by correlating plasma drug levels and/or biomarkers with safety and toxicity across species.

incorporation of target or molecular endpoints in early clinical trials to follow logically from the preclinical experience. More safety testing would be required for those compounds that proceed to phase I clinical trials using the biological, pharmacological, and toxicological properties to define the optimal dose and schedule conditions for human studies. The question that remains to be addressed is how do we optimize the preclinical/clinical interface to ensure smoother transitions as the drug candidate moves from the preclinical to clinical phase of development (Fig. 4.1). The increasing number of molecularly targeted agents has called for better preclinical models to facilitate the development of biomarkers that may make predictive correlations with early clinical endpoints. Optimal evaluation of these molecularly targeted drugs requires the integration of PD (pharmacodynamic) assays into early phase trials. The incorporation of the exploratory phase 0 or target-development clinical trial design that focuses on extensive compound characterization and target assay development (including molecular imaging studies) in a limited number of patients could expedite the drug development process for these targeted agents. For the purposes of this chapter in discussing preclinical drug assessments, our interest lies in the preclinical modeling of the phase 0 trial. Basic standards of a phase 0 trial include: (a) validating targets or biomarkers in preclinical models and then in human tissue prior to initiating the clinical trial; (b) defining standard operating procedures for handling of tissues and biospecimens prior to initiating the clinical trial; (c) demonstrating drug target or biomarker effect in preclinical models; and (d) determining the relationship between the pharmacodynamics and the pharmacokinetics (27). Essential to this process is the pharmacodynamic assay that has been validated for analytical performance and proven to be therapeutically relevant in preclinical studies. An example is the qualification of a PD assay of poly (ADP-Ribose) polymerase (PARP) in tumor biopsies of mouse xenografts that has facilitated the design of a phase 0 trial of ABT888, a PARP inhibitor, and serving as a model for developing proof-of-principle clinical trials of molecularly targeted drugs (28).

CONCLUSIONS NEW APPROACHES TO CANCER DRUG DEVELOPMENT: PRECLINICAL MODELING OF THE PHASE 0 TRIAL An effect on the particular molecular target becomes a constant signal after which pharmacologic, scheduling, and toxicologic studies follow, allowing for the

Recent advances in cancer drug discovery have resulted in the increasingly rapid identification of therapeutic targets and improvements in validating these targets through refined in vitro systems and more sophisticated in vivo models of cancer provide an important foundation for developing anticancer agents with the


potential to be highly specific, potent, and nontoxic. Adapting to advancements in novel technologies and cancer science requires modifying drug screens, developing new in vitro and in vivo models and exploring more effective toxicological evaluations. Thus, there will always be a critical need to find better approaches to preclinical drug assessment so that only the most promising agents are advanced for further clinical evaluation. Caution should be taken when halting developmental programs prematurely due to lack of efficacy in available preclinical models, thereby discarding potentially useful agents in the process. The focus on how preclinical development can be improved to reduce the number of false positives and/or false negatives remains a challenge to oncology drug development. Despite the progress that has been made in every stage of cancer drug discovery and development, the success rate for oncology agents remains disappointing. There is a growing need to improve the efficiency in moving agents from the preclinical phase to the market with more efficient and rational translational approaches and close collaboration between laboratory and clinical scientists.

10. 11.

12. 13. 14. 15.

16. 17. 18. 19.

References 1. Ley TJ, Mardis ER, Ding L, et al. DNA sequencing of a cytogenetically normal acute myeloid leukaemia genome. Nature. 2008;456:66–72. 2. Clarke PA, te Poele R, Wooster R, Workman P. Gene expression microarray analysis in cancer biology, pharmacology, and drug development: progress and potential. Biochem Pharmacol. 2001;62:1311–1336. 3. Petricoin EF, Zoon KC, Kohn EC, Barrett JC, Liotta LA. Clinical proteomics: translating benchside promise into bedside reality. Nat Rev Drug Discov. 2002;1:683–695. 4. Kingsmore SF. Multiplexed protein measurement: technologies and applications of protein and antibody arrays. Nat Rev Drug Discov. 2006;5:310–320. 5. Ilyin SE, Belkowski SM, Plata-Salaman CR. Biomarker discovery and validation: technologies and integrative approaches. Trends Biotechnol. 2004;22:411–416. 6. Monks A, Scudiero D, Skehan P, et al. Feasibility of a high-flux anticancer drug screen using a diverse panel of cultured human tumor cell lines. J Natl Cancer Inst. 1991;83:757–766. 7. Holbeck SL. Update on NCI in vitro drug screen utilities. Eur J Cancer. 2004;40:785–793. 8. Monks A, Scudiero DA, Johnson GS, Paull KD, Sausville EA. The NCI anti-cancer drug screen: a smart screen to identify effectors of novel targets. Anticancer Drug Des. 1997;12: 533–541. 9. Paull KD, Shoemaker RH, Hodes L, et al. Display and analysis of patterns of differential activity of drugs against human

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tumor cell lines: development of mean graph and COMPARE algorithm. J Natl Cancer Inst. 1989;81:1088–1092. Leteurtre F, Sackett DL, Madalengoitia J, et al. Azatoxin derivatives with potent and selective action on topoisomerase II. Biochem Pharmacol. 1995;49:1283–1290. Solary E, Leteurtre F, Paull KD, Scudiero D, Hamel E, Pommier Y. Dual inhibition of topoisomerase II and tubulin polymerization by azatoxin, a novel cytotoxic agent. Biochem Pharmacol. 1993;45:2449–2456. Baguley BC, Marshall ES. In vitro modelling of human tumour behaviour in drug discovery programmes. Eur J Cancer. 2004;40:794–801. Decker S, Hollingshead M, Bonomi CA, Carter JP, Sausville EA. The hollow fibre model in cancer drug screening: the NCI experience. Eur J Cancer. 2004;40:821–826. Hollingshead MG, Alley MC, Camalier RF, et al. In vivo cultivation of tumor cells in hollow fibers. Life Sci. 1995;57: 131–141. Johnson JI, Decker S, Zaharevitz D, et al. Relationships between drug activity in NCI preclinical in vitro and in vivo models and early clinical trials. Br J Cancer. 2001;84: 1424–1431. Kelland LR. Of mice and men: values and liabilities of the athymic nude mouse model in anticancer drug development. Eur J Cancer. 2004;40:827–836. Killion JJ, Radinsky R, Fidler IJ. Orthotopic models are necessary to predict therapy of transplantable tumors in mice. Cancer Metastasis Rev. 1998;17:279–284. Bibby MC. Orthotopic models of cancer for preclinical drug evaluation: advantages and disadvantages. Eur J Cancer. 2004;40:852–857. Wang X, Fu X, Brown PD, Crimmin MJ, Hoffman RM. Matrix metalloproteinase inhibitor BB-94 (batimastat) inhibits human colon tumor growth and spread in a patient-like orthotopic model in nude mice. Cancer Res. 1994;54:4726–4728. Hansen K, Khanna C. Spontaneous and genetically engineered animal models; use in preclinical cancer drug development. Eur J Cancer. 2004;40:858–880. Contag CH, Spilman SD, Contag PR, et al. Visualizing gene expression in living mammals using a bioluminescent reporter. Photochem Photobiol. 1997;66:523–531. Hollingshead MG, Bonomi CA, Borgel SD, et al. A potential role for imaging technology in anticancer efficacy evaluations. Eur J Cancer. 2004;40:890–898. DeGeorge JJ, Ahn CH, Andrews PA, et al. Regulatory considerations for preclinical development of anticancer drugs. Cancer Chemother Pharmacol. 1998;41:173–185. Grieshaber CK, Marsoni S. Relation of preclinical toxicology to findings in early clinical trials. Cancer Treat Rep. 1986;70: 65–72. Olson H, Betton G, Robinson D, et al. Concordance of the toxicity of pharmaceuticals in humans and in animals. Regul Toxicol Pharmacol. 2000;32:56–67. Tomaszewski JE. Multi-species toxicology approaches for oncology drugs: the US perspective. Eur J Cancer. 2004;40: 907–913. Kummar S, Kinders R, Rubinstein L, et al. Compressing drug development timelines in oncology using phase ‘0’ trials. Nat Rev Cancer. 2007;7:131–139. Kinders RJ, Hollingshead M, Khin S, et al. Preclinical modeling of a phase 0 clinical trial: qualification of a pharmacodynamic assay of poly (ADP-ribose) polymerase in tumor biopsies of mouse xenografts. Clin Cancer Res. 2008;14:6877–6885.


5

Formulating the Question and Objectives

Lauren C. Harshman Sandy Srinivas James Thomas Symanowski Nicholas J. Vogelzang

There are no bad anticancer agents, only bad clinical trial designs. —DD Von Hoff, MD Formulating a relevant question and designing a clinical trial can be daunting to the young investigator. Most interesting questions arise from the ability to identify deficiencies in treatment whether it be in the therapies for a particular type of patient, such as colorectal cancer patients with an activating mutation in the KRAS (v-Ki-ras2—Kirsten rat sarcoma viral oncogene homolog) gene, or in the line of treatment such as the treatment of refractory pancreatic cancer, where randomized controlled trials have been notably lacking (1, 2). The ability to identify unmet needs is enhanced by experience, which equates to time in the field, a trait most young investigators aspire to but do not yet possess. This chapter will delineate some of the key steps in formulating a clear, succinct question with answerable objectives. Common criticisms of clinical trials are failure to define a transparent question with clear objectives or to develop a strategy that has achievable outcomes. A central theme throughout this chapter will be to eliminate ambiguity. Unambiguous descriptions of objectives and outcomes will produce more interpretable and reproducible results that can be readily applied to clinical practice. The goals of clinical trials

are manifold, but generally include answering a question that will change clinical practice in terms of therapy, diagnosis, or the utility of a prognostic or predictive surrogate marker of response. Without a thoughtful trial design, the primary question may not be properly answered and could result in erroneous acceptance that a therapy is successful (a type I error) or in failure to show that a good therapy works (failing to reject the null hypothesis, a type II error.) The terms question, objectives, and endpoints or outcomes can become muddled in the young investigator’s mind as they develop a clinical trial. To define the question, first determine the nature of the answer sought. Does the study aim to evaluate a drug’s efficacy or is the goal to assess the utility of a surrogate biomarker or imaging study? The objectives, in turn, will delineate what needs to be accomplished in order to answer the question. The endpoints or outcomes can be deduced from this approach, and might more understandably be described as “how the objectives will be achieved or measured.” The fundamental components of formulating a good clinical question, answering it, and changing practice (i.e., making it relevant) include: · Thorough background knowledge of the disease, therapy, and/or biomarkers (or correlative study endpoints) that pertain to the primary question · Clearly defined objectives

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· · · ·

Early consultation with a biostatistician Statistically sound trial design A suitable and accessible patient population to study A rationale drug or combination, dose, surrogate markers or imaging studies · Appropriate endpoints that will measure the objectives · Proper statistical analysis · Effective communication and dissemination of the results

THE IMPORTANCE OF BACKGROUND KNOWLEDGE When evaluating a new therapy or determining the proper use of a new molecular marker or imaging study, a comprehensive review of the background on the disease or patient population is critical. Review prior investigations and studies that have determined the current standard treatment. Evaluate past unsuccessful trials and assess the reasons for failure. This systematic appraisal will highlight deficiencies in existing treatments, biomarkers, or imaging modalities for the disease. By thoroughly understanding the mechanism of action of a new drug or the etiological pathway that triggers the disease, you may identify the right intervention to investigate. In addition to confirmation that your question is relevant, this review of the background of the disease, intervention, biomarkers, or other secondary or correlative study endpoints may elicit additional questions that require resolution. Further, the appropriate dosing or process to study can be ascertained by discussion with the company owning the rights to the drug or process, speaking with other investigators who have worked with the agent or process, evaluation of the preclinical data, and review of the results of phase I studies. Finally, in the case of rare diseases, review of the background data or lack thereof may highlight a potential niche for the young investigator, or offer the opportunity for a translational project when no prior clinical studies have been performed.

CLEARLY DEFINE THE OBJECTIVES The objectives assert the goals of the study. Objectives should be clearly defined such that they can be investigated by a quantitative assessment of appropriate outcomes (3). Gebski and colleagues devised a checklist for objectives in clinical trials (3, 4): · Are the intervention and control (e.g., usual care) described in detail?

· Has the target patient population been specified? · Has the degree of benefit from the intervention on a particular outcome, and the time frame, been specified? · Have any secondary outcomes been prespecified in similar detail? Avoid Ambiguity Ambiguous objectives should be avoided as they can lead to skepticism about trial results. Vague objectives may cause reviewers to wonder if definitions have been created post hoc and adjusted to fit the data (3). The need for clear definitions is especially important in the era of the targeted agents, where controversy has arisen regarding what constitutes appropriate objectives and endpoints and how best to assess them. Speaking with respect to second line therapy for hormone refractory prostate cancer, Dahut asked what is a meaningful measure of clinical benefit? (W.L. Dahut, American Society of Clinical Oncology Annual Meeting 2008). He asserted that it is tumor growth that causes morbidity and mortality, not the lack of tumor response. As such, perhaps oncologists should only stop therapy for objective progression, not for a lack of tumor response. This concept is somewhat difficult to reconcile with the historic goal of “shrinking the tumor” or “making it disappear.” While such goals have been validated as surrogate endpoints for many types of cancers, such as leukemia, lymphoma, and germ cell tumors, and have been formalized using the accepted Response Evaluation Criteria in Solid Tumors (RECIST) method of determining response (RECIST defines therapeutic success in terms of either partial or complete responses) (5), the vast majority of solid tumors do not disappear when treated with chemotherapy. Rather, radiologically and clinically they appear to stabilize or slow down. This dilemma of how to appropriately characterize clinical efficacy is further exemplified by the use of surrogate biomarkers (e.g., PSA, LDH, Ca19–9) and the cytostatic targeted agents. With both surrogate biomarkers and the cytostatic agents, using RECIST to assess response has come under question. RECIST does not include biomarker response, but it is generally agreed that normalization or decreases in these markers can aid in identifying therapeutic efficacy. In terms of the cytostatic agents, which tend to stabilize disease rather than dramatically decrease tumor size, the concept of incorporating clinical benefit (CB) as a measure of response has arisen. Here, clinical benefit incorporates disease stabilization (SD) in addition to partial response (PR) and complete response (CB) (CB = SD + PR + CR) as a measure of therapeutic success.

5 FORMULATING THE QUESTION AND OBJECTIVES

Proponents of including CB as a measure of response propose that SD is an acceptable and achievable goal when managing incurable diseases that are refractory to cytotoxic agents. In summary, in formulating an unambiguous question, be certain to evaluate carefully the role of endpoints with biomarkers versus endpoints with clinical or radiological examinations, and clearly define what constitutes clinical efficacy. This topic will be discussed in more detail in Chapters 6 and 7. Primary versus Secondary Objectives A study often has one primary objective and several secondary objectives. On rare occasions there can be co-primary endpoints. The primary objective is the focus of the study and directs the answer to the question or hypothesis, whereas the secondary objectives are often derivative or ancillary. In order for a study to be clinically meaningful and lead to a change in clinical practice, it must achieve its primary objective. Secondary objectives are certainly important; they can enhance the robustness of the results observed for the primary objective and can lead to additional studies, but are not of the same level of importance as that of answering the primary question. Safety assessment is a notable exception to this general rule (3). Even when safety is listed as a secondary objective, it is of equal importance to that of the primary objective in human subjects. In addition, be cautious not to overload the study with too many secondary objectives and methods of assessment as it may dilute the impact of the study and confuse the Institutional Review Board (IRB), Federal Drug Agency (FDA), and your eventual reviewers and readers. Determination of the primary and secondary objectives also depends on the type of trial planned. There are some common objectives that distinguish phase I trials versus those of phase II or phase III trials. In a phase I study of a new agent, the primary objective might be to define the maximally tolerated dose (MTD) or the optimal biological dose. In the United States, the MTD is generally the dose below that which induced dose-limiting toxicity at an unacceptably high rate and is the dose that will be investigated in the phase II study. Secondary objectives of a phase I trial commonly include describing the toxicities and pharmacokinetics of the agent. In phase II trials, assessing whether a drug or intervention has antitumor activity or can stabilize disease in the form of response or progression-free survival is commonly the primary objective, whereas safety or prolongation of overall survival might be rational secondary objectives. The goal of phase III trials is often to determine which therapy or intervention

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is more clinically effective. The investigational arm is usually compared to a control arm in the form of the current standard of care intervention, or, if none, best supportive care or placebo. When assessing whether the new therapy is more effective, the primary objective can be statistically designed to determine whether the new therapy is superior, equivalent, or not inferior. Noninferiority designs can be utilized if it is hypothesized that the experimental interval has similar primary clinical efficacy (usually in the form of overall survival) and additionally has secondary advantages such as a better safety profile or a more convenient drug administration. This primary objective is frequently measured using endpoints of prolongation of overall survival or progression-free survival. In phase II and phase III trials, the study will be powered to prove the primary objective, so it is especially important to distinguish between the primary and secondary objectives. Choose Feasible Objectives Understand whether the objectives of the study are feasible. For example, evaluating improvement in survival using a new therapy in locally advanced prostate cancer is rarely practical as patients may live 5 to 10 years after diagnosis. In these cases, a primary objective other than survival should be pursued. For example, a molecular endpoint using tissue from the resected specimen or a change in biomarkers, such as prostate-specific antigen (PSA) or circulating tumor cells, may be more reasonable. Also, a clear understanding of the number of patients who are potentially eligible to enroll in the trial from your site or cooperative group will be necessary. Seek assistance in developing accurate assessments of patients likely to be eligible and willing to enter the trial from the tumor registrar and the clinical trials office at your institution. Only by taking the time to adequately assess the available patient resources for the trial will your question be answered effectively. Choose Pharmaceutical Company— and FDA—Pleasing Objectives It is important to understand what the FDA and the pharmaceutical industry consider important when evaluating a therapy or intervention for approval. In some disease states, especially when there is a surfeit of agents for one indication, demonstrating an improvement in response rate is insufficient, and, instead, proof that the agent prolongs overall survival is required. In disease states where it is not feasible to demonstrate an improvement in overall survival, proof that the agent prolongs progression-free survival may be the basis of approval, provided that improvement is recognized as

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a clinical benefit to patients. In other rarer, more treatment-resistant diseases, such as renal cell carcinoma (RCC), where no therapy existed that consistently improved overall survival, two of the three drugs approved since 2005 were approved based on prolongation of progression-free survival (6–8). The recent demonstration of improvements in overall survival with temsirolimus and sunitinib (granted that the survival benefit for sunitinib had a p value of 0.051) portends that the standard for future FDA approvals for RCC therapies will be higher (7, 9).

TRIAL DESIGN AND BIOSTATISTICAL INPUT Perhaps of paramount importance in designing a good clinical trial is early consultation with a biostatistician. It is essential to clearly communicate the hypothesis and background information supporting your assumptions, objectives, and outcome measures to your biostatistical colleague. A good biostatistician will verify the assumptions by evaluating pre-existing data and in the context of phase II and phase III trials calculate the necessary sample size required to achieve the primary objective or endpoint. Once an appropriate sample size has been determined, confirm whether your institution has adequate patient numbers to successfully accrue to the study. If insufficient, a change in the trial design or the primary objective upon which the study is powered may be necessary. Collaboration with other institutions may permit larger sample sizes and enhance the generalizability of your study. In the case of randomized trials, the biostatistician will ensure that adequate baseline factors are incorporated into the randomization scheme in order to minimize bias and variability as it pertains to treatment group comparisons. The statistician will provide an a priori plan for the statistical analysis of the objectives and trial. It is critical to ensure that the trial design is statistically sound and, when applicable, adequately powered to answer your question and objectives. As discussed above, phase III trials often appraise efficacy of a new agent by assessing whether it is equivalent, superior, or not inferior to the standard of care therapy. These three different primary objectives of equivalency, superiority, or noninferiority require different statistical analyses and sample sizes. A second example of a primary objective necessitating different trial designs is whether the purpose is to evaluate response to an agent or whether the goal is to assess prolongation of progression-free survival. In this case, a randomized design should be considered for assessment of a benefit in progression-free survival, whereas, a single-arm

design may be sufficient for investigating a primary objective of response. In the latter case, a Simon Two Stage design may be utilized as it exposes fewer patients to the investigational agent and halts the trial if a prespecified number of patients do not meet response criteria. A third example that highlights the importance of choosing an appropriate trial design would be with efficacy studies of agents such as histone deacetylase inhibitors (HDACi, e.g. vorinostat) or DNA methyltransferase I inhibitors (DNMTi, e.g. decitabine). It may not be of interest to show antitumor activity or disease stabilization with these agents as monotherapies, but rather to determine whether they act synergistically with standard of care agents or radiation. Trial design will be discussed more thoroughly later in this book.

CHOOSING THE RIGHT PATIENT POPULATION When crafting the question and objectives, a target patient population should be clearly defined. Which patients with what disease will your drug or intervention treat? What line of therapy are you evaluating (e.g., treatment-naïve versus refractory)? Understand the population available in your clinic or institution and what questions can be adequately answered in that milieu. While it may be interesting to study a third line treatment for colorectal cancer with a novel targeted agent in combination with standard chemotherapy, such as irinotecan and 5-Fluorouracil, if the standard first and second line treatments at your center include irinotecan, this is not an ideal population to target. In some instances, the appropriate patient population may arise after identification of a signal of efficacy in a particular tumor type during a phase I study where several different types of solid tumors were treated with the same drug. The novel drug should then be assessed further in a phase II study in a larger population of patients with the responsive disease. Other times, the right patient population may be identified translationally whereby a known chromosomal mutation exists in a certain disease, and a novel agent that targets this mutation is available for human investigation. The reverse concept (or bedside to bench) example could be to identify a rare disease in which there are few treatment options and investigate a rationale agent based on the pathophysiology of the disease. Once the appropriate patient population is identified and the sample size for accrual is reasonable from the standpoint of your clinic, institution, multi-institution collaboration, or cooperative group, the next step is to establish eligibility criteria for the study with

5 FORMULATING THE QUESTION AND OBJECTIVES

the goal of optimizing the number of patients who can be accrued while maintaining generalizability. This goal requires a fine balance. If criteria are too relaxed, patients with complicated medical issues or unusual disease pathology may confound the study results, whereas homogenous criteria may result in limited generalizability.

CHOOSING APPROPRIATE ENDPOINTS Clearly defining a question and objectives requires forward thinking of achievable endpoints or outcome measures. These measures are often referred to as hard and surrogate endpoints. Examples of hard or objective endpoints include response rate as defined by RECIST criteria, progression-free survival, or overall survival. Surrogate endpoints tend to be more tangible and easily attainable measures than direct assessment of response or survival for a particular disease that may have a long latency to achievable hard endpoints. Examples of surrogate endpoints include blood or tissue biomarkers and imaging correlates. Surrogate endpoints are especially useful in chronic diseases such as prostate cancer, where primary endpoints using survival may take 10 or more years, or when evaluating cytostatic targeted therapies that may not be best assessed by traditional criteria. As mentioned above, it is recognized that antiangiogenic agents such as the VEGF antibodies and tyrosine kinase inhibitors evoke less tumor regression and more stabilization of disease. Use of endpoints that require traditional anatomic-based assessment such as RECIST might recognize these agents as failures in terms of percentage of PR and CR, when in fact they may elicit a significant clinical benefit in terms of disease stabilization and progression-free survival. Other novel and potentially more useful methods of efficacy assessment for these cytostatic agents include metabolic- or perfusion-based criteria and are the objects of current investigations, especially with the antiangiogenic agents (10). When defining objectives and how they will be achieved using certain endpoints, keep in mind the individual limitations of the outcome measures involved. Overall survival may be confounded by treatment with multiple subsequent agents, whereas time to progression (TTP) or response rate can cloud the fact that although the intervention is effective in the short term, it may not prolong survival (11). The latter may be acceptable in some instances where no generalizable agent exists that prolongs survival. For example, gemcitabine was approved for platinum-sensitive, refractory ovarian cancer by prolonging progression-free survival despite the fact that overall survival was not

33

extended, because extending the progression-free survival interval was viewed as a clinical benefit in this patient population (12). Endpoints will be more thoroughly discussed in later chapters but are germane to this chapter as they are critical to the big picture of forming your question and objectives.

APPRECIATE THE END GOAL: FDA APPROVAL Understand the FDA approval process a priori when devising your question, objectives, and trial design. The FDA has specific regulations for initiating clinical trials that assess new agents or interventions on human subjects and generally requires that the primary objective is proven in order to approve the intervention. Often the FDA will agree with the importance of the question but has reservations about the design and whether it will achieve the desired objectives. The Prostate Cancer Clinical TrialsWorking Group 2 recommendations are a good example of consensus guidelines that do not have teeth because the FDA has not affirmed the validity of the endpoints, for instance, PSA (13).

SUMMARY In conclusion, the transparency of the question and objectives in combination with achievable outcomes and a statistically sound trial design are essential to accomplishing a superior clinical trial whether it be molecular, radiological, or therapeutic. Unambiguous descriptions of your objectives and outcomes will produce more interpretable results that can be more easily applied to clinical practice.

References 1. Boeck S, Heinemann V. Second-line therapy in gemcitabinepretreated patients with advanced pancreatic cancer. J Clin Oncol. 2008;26:1178–1179. 2. Kulke MH, Blaszkowsky LS, Ryan DP, et al. Capecitabine plus erlotinib in gemcitabine-refractory advanced pancreatic cancer. J Clin Oncol. 2007;25:4787–4792. 3. Gebski V, Marschner I, Keech AC. Specifying objectives and outcomes for clinical trials. Med J Aust. 2002;176:491–492. 4. Moher D, Schulz KF, Altman D. The CONSORT statement: revised recommendations for improving the quality of reports of parallel-group randomized trials. JAMA. 2001;285:1987–1991. 5. Therasse P, Arbuck SG, Eisenhauer EA, et al. New guidelines to evaluate the response to treatment in solid tumors. European Organization for Research and Treatment of Cancer, National Cancer Institute of the United States, National Cancer Institute of Canada. J Natl Cancer Inst. 2000;92:205–216. 6. Escudier B, Eisen T, Stadler WM, et al. Sorafenib in advanced clear-cell renal-cell carcinoma. N Engl J Med. 2007;356:125–134.

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7. Hudes G, Carducci M, Tomczak P, et al. Temsirolimus, interferon alfa, or both for advanced renal-cell carcinoma. N Engl J Med. 2007;356:2271–2281. 8. Motzer RJ, Hutson TE, Tomczak P, et al. Sunitinib versus interferon alfa in metastatic renal-cell carcinoma. N Engl J Med. 2007;356:115–124. 9. Figlin RA, Hutson TE, Tomczak P, et al. Overall survival with sunitinib versus interferon (IFN)-alfa as first-line treatment of metastatic renal cell carcinoma (mRCC). J Clin Oncol 26: 2008 (May 20 suppl; abstr 5024). 10. Jaffe CC. Response assessment in clinical trials: implications for sarcoma clinical trial design. Oncologist. 2008;13(suppl 2):S14–S18.

11. Schiller JH. Clinical trial design issues in the era of targeted therapies. Clin Cancer Res. 2004;10:4281s–4282s. 12. Pfisterer J, Plante M, Vergote I, et al. Gemcitabine plus carboplatin compared with carboplatin in patients with platinumsensitive recurrent ovarian cancer: an intergroup trial of the AGO-OVAR, the NCIC CTG, and the EORTC GCG. J Clin Oncol. 2006;24:4699–4707. 13. Scher HI, Halabi S, Tannock I, et al. Design and end points of clinical trials for patients with progressive prostate cancer and castrate levels of testosterone: recommendations of the prostate cancer clinical trials working group. J Clin Oncol. 2008;26:1148–1159.

6

Choice of Endpoints in Cancer Clinical Trials

Wenting Wu Daniel Sargent

A critical element to the success of any clinical trial is the choice of the appropriate endpoint(s). In the context of a clinical trial, an endpoint is defined as a characteristic of a patient that is assessed by a protocol specified mechanism. Examples of endpoints commonly assessed in cancer clinical trials include adverse events, measures of tumor growth or shrinkage, or time-related endpoints such as overall survival. The choice of the endpoint for any given trial depends primarily on the trial’s objectives. In this chapter we will first present general considerations related to the choice of an endpoint for a trial, and then focus on specific endpoints that may be appropriate for various trial types, specifically phase I, phase II, or phase III trials.

GENERAL CONSIDERATIONS Each clinical trial should specify a single, primary endpoint. This endpoint is the patient characteristic that will most directly capture whether the therapy being tested is having the desired (or undesired, in the case of an adverse event) effect on the patient. The primary endpoint also typically determines the trial’s sample size, through the process of specifying what effect on the primary endpoint is desired to be detected in the trial to a prespecified degree of accuracy. The primary endpoint must be appropriately justified, and typ-

ically should be a well-defined and commonly accepted endpoint in that cancer type and/or study phase. Once a primary endpoint has been determined, typically multiple additional endpoints, known as secondary endpoints, are specified. Secondary endpoints should be variables that are of interest to study investigators, such that the examination of these endpoints will enhance the utility of the trial to address clinically or biologically relevant questions. Formally, statistical testing for treatment-related effects on these secondary endpoints should only occur if there is a statistically significant effect on the primary endpoint. In practice, these endpoints are typically examined regardless of the primary endpoint results. When considering possible endpoints for a clinical trial, an important distinction exists between clinical and surrogate endpoints. A clinical endpoint is one with direct clinical and patient relevance, such as patient quality of life or survival. In most cases, if possible and feasible, a clinical endpoint should be preferred for a protocol. However, in many cases, the optimal clinical endpoint may take very long to assess (such as patient survival), require a costly procedure (such as imaging), or be too invasive to be practical or ethical (such as requiring a patient biopsy). In such cases, a surrogate endpoint is often considered. A surrogate endpoint is defined as an endpoint obtained more quickly, at lower cost, or less invasively than the true clinical endpoint of interest (1). The practice of

35

36


validating, or confirming the accuracy, of a surrogate endpoint is challenging, and there are many examples of endpoints that were considered promising surrogates only to be subsequently shown to have a poor or even negative association with the true endpoint of interest (2). The topic of surrogate endpoints is addressed in depth in a later chapter (3); we do not consider this further here.

ENDPOINTS FOR PHASE I TRIALS Historically, cancer therapies have been designed to act as cytotoxic, or cell killing, agents. The fundamental assumption regarding the dose-related activity of such agents is that there exists a monotone nondecreasing dose-response curve, meaning that as the dose increases, tumor shrinkage will also increase, which should translate into increasing clinical benefit. Under this assumption, both toxicity and the clinical benefit of the agent under study will increase with increasing dose, and an appropriate goal of a phase I trial will be to find the highest dose with acceptable toxicity. Since the monotone nondecreasing dose-response curve has been observed for most cytotoxic therapies, toxicity has historically been used as the primary endpoint to identify the dose that has the greatest chance to be effective in subsequent testing. In this context, the typical goal for phase I clinical trials has been to determine the maximum tolerated dose (MTD); which has been traditionally defined as the highest dose level where only one of six patients experiences unacceptable or dose-limiting toxicity (DLT). More generally, the highest dose that can be administered with an acceptable toxicity profile is referred to as the MTD. The use of toxicity as an endpoint and thus defining the MTD as the primary goal of a phase I trial has considerable appeal. This endpoint is clinically relevant, is straightforward to observe, easy to explain, has clear intuitive rationale, and considerable historical precedent. However, particularly with newer agents as discussed below, the use of toxicity as the primary endpoint poses increasing challenges in modern clinical trials. A first challenge to toxicity as the primary endpoint is that it may require a long time and many patients to reach the MTD, with many patients treated at suboptimal doses. Goldberg et al. (4) conducted a phase I study to determine the MTD and DLT of CPT-11 in the regimen of CPT-11/5-FU/LV for patients with metastatic or locally advanced cancer, where CPT-11 was administered on day 1 and 5-FU/LV was administered on days 2 to 5 of a 21-day cycle. Fifty-six patients were accrued during a period of 38 months and 13 dose

levels were studied. A different design coupled with a different endpoint may have been able to significantly shorten the study duration. A more significant obstacle to the use of toxicity as a phase I endpoint is posed by noncytotoxic therapies. In cancer therapeutics, many novel targets are currently being pursued. At the level of the cell, targets in cytoplasmic and cell-surface signaling molecules, processes of cell-cycle control and mutations or lack of expression of suppressor genes have all yielded multiple new agents for evaluation. At the extra cellular level, there are large numbers of novel drugs designed to limit tumor penetration and metastasis and agents which directly inhibit angiogenesis. Vaccines to overcome immune tolerance of cancer are also being developed. These cytostatic or targeted therapies, many of which seem to be nontoxic at doses that achieve concentrations with desired biologic effects, have become more common as the biology of cancer has become better understood. In these cases, a dose-escalation trial incorporating a biologic endpoint specific for the agent in addition to toxicity might be appropriate (5, 6). In considering a dose-escalation scheme for a trial with a nontoxicity endpoint, it is important to consider the need to reduce the assumptions about the shape of the dose outcome curve. In theory, the dose response could be monotone nondecreasing, quadratic, or increasing with a plateau. As such, the assumption that increasing dose will always lead to increasing efficacy that is appropriate for cytotoxic agents is not reasonable for such an agent, thus one may want to consider using a dose escalation design that is based not only on occurrence of toxicity, but also based on other endpoints. In a phase I trial with such an agent, an appropriate goal is to estimate the biologically optimal dose (BOD); that is, the dose that has maximal efficacy, with acceptable toxicity (7). As such, the trial must incorporate both toxicity and efficacy as endpoints while estimating the BOD. Several endpoints that could serve as efficacy endpoints to supplement toxicity as the single endpoint for trials of cytostatic/targeted therapies are discussed below. The use of this kind of endpoint should have reproducible assays available, and optimally be shown to correlate with a clinical endpoint, such as tumor response, in human or at minimum animal models. An ideal efficacy endpoint in this setting would be an endpoint that represents a measurement of the effect of the agent on the molecular target. However, in practice, several challenges exist for such an endpoint. These include that a reliable assay for measurement of the drug effect must be available, that the relevant tissue in which to measure target inhibition is readily available, that serial tumor sampling is usually invasive

6 CHOICE OF ENDPOINTS IN CANCER CLINICAL TRIALS

and associated with sampling error, and that at this early stage of a drug’s development it may be difficult to define the appropriate measure of achieved target effects for a specific drug. The issue of ready availability of tissue may be addressed by restricting patient enrollment to those with accessible disease for assessment of the drug effect on the tumor, but this may severely restrict the number of patients eligible for the trial. Other possible measurements for activity of an agent, and thus potential endpoints, include pharmacokinetic analysis, which would be appropriate if sufficient preclinical data exist demonstrating a convincing pharmacokinetic-pharmacodynamic relationship. More specifically, an endpoint of assessing whether the minimum effective blood concentration level of the agent has been attained could be considered. Again, such an endpoint would require preclinical data that have demonstrated that the target blood or serum level correlates with clinically relevant efficacy. To date, few published phase I trials have used nontoxicity endpoints such as we have described, for both biologic and practical reasons. First, at this point in an agent’s development, it may be difficult to define the desired target biological effect. Even if the target is known and an effect level known, it may be difficult to define and validate an appropriate measurement for that endpoint. Practical difficulties in measuring target levels once they have been defined include the lack of reliable, real-time assays and the difficulty in obtaining the required tumor specimens. The real-time nature of the assay is critical, as if dosing decisions are to be made based on the endpoint, turnaround must be rapid, and batch processing is not likely acceptable. Finally, statistical trial designs for identifying a dose that maximizes the biologic response would likely require more patients than are typically studied in phase I trials.

ENDPOINTS FOR PHASE II AND III TRIALS Phase II and phase III clinical trials, as opposed to phase I trials, are designed to obtain a preliminary (phase II) or definitive (phase III) determination of a new agent’s efficacy. As such, the endpoints for these trials tend to be clinical in nature, designed to directly assess the impact of a therapy on a patient-relevant phenomena. The four endpoints most commonly used in phase II and phase III oncology trials are tumor response rate, patient progression-free survival (PFS) (in the advanced disease setting)/disease-free survival (DFS) (in the adjuvant setting), overall survival (OS), and quality of life (QOL). Historically, response rate has been the most common endpoint for phase II trials, and overall

37

survival for phase III trials. However, in the last 5 to 10 years, both PFS/DFS and OS have been used increasingly as an endpoint in the phase II setting. Thus, in this section we discuss these endpoints, as they are relevant for both phase II and phase III trials. Response Rate The response rate in a trial is defined as the proportion of responders (complete or partial) among all eligible patients. Since the establishment of the Response Evaluation Criteria in Solid Tumors (RECIST) Criteria in 2000 (8), this standard has become widely accepted as the preferred method to assess tumor shrinkage. Under RECIST, all measurable lesions up to a maximum of 10 are identified as target lesions and the baseline measurements for these lesions are recorded. During treatment, for target lesions, complete response (CR) is defined as the disappearance of all target lesions, and partial response (PR) as a decrease of at least 30% in the sum of the longest diameter (LD) of target lesions, taking as reference the baseline sum of the LD. Progressive disease (PD) is defined as at least a 20% increase in the sum of the LD of target lesions, taking as reference the smallest sum LD recorded since the treatment started or the appearance of one or more new lesions. Stable disease (SD) is defined as neither sufficient shrinkage to qualify for PR nor sufficient increase to qualify for PD, taking as reference the smallest sum LD since the treatment started. Lesions that are not measurable per RECIST (typically due to poorly defined dimensions) are classified as nontarget lesions. For nontarget lesions, CR is defined as the disappearance of all nontarget lesions. Incomplete Response/Stable Disease (SD) is defined as the persistence of one or more nontarget lesions or/and maintenance of tumor marker level above the normal limits, with PD defined as appearance of one or more new lesions and/or unequivocal progression of existing nontarget lesions. Under RECIST, the best overall response at the patient level is the best response recorded from the start of the treatment until disease progression/recurrence, and it is evaluated as per Table 6.1. To be assigned a status of PR or CR per RECIST, changes in tumor measurements must be confirmed by repeat assessment performed no less than 4 weeks after the criteria for response are first met. Response rate has been the major primary endpoint for phase II trials in the last 40 years. The use of response rate as a primary endpoint has substantial biological plausibility: as tumors rarely shrink by themselves, a tumor response can be considered as a clear signal of activity of a new therapy. In addition, in most solid tumors, response occurs quickly after the

38


TABLE 6.1

Patient Overall Response Based on Target Lesions, Nontarget Lesions, and New Lesions. TARGET LESIONS CR CR PR SD PD Any Any

NONTARGET LESIONS

NEW LESIONS

CR Incomplete response/SD Non-PD Non-PD Any PD Any

No No No No Yes or No Yes or No Yes

initiation of therapy, most often within 3 months. As such, tumor response provides an endpoint that can be assessed rapidly, allowing a timely determination of whether an agent is sufficiently promising to warrant phase III testing. In the last 5 to 10 years, the appropriateness of tumor response as a trial endpoint has been challenged (9, 10, 11). The RECIST criteria for response were designed primarily to assess cytotoxic agents. For drugs that might be active in slowing the cancer disease process, but without consistent achievement of tumor shrinkage, such as the epidermal growth factor tyrosine kinase inhibitors (gefitinib and erlotinib), or the multiple new agents targeting the vascular endothelial growth factor pathway (bevacizumab and sorafenib), the tumor response endpoint does not consider durable modest regressions or prolonged disease stability as activity, which we now know is an effect of those agents. For example, consider a randomized trial of bevacizumab, an anti-vascular endothelial growth factor antibody, in the setting of metastatic renal cancer (12). This randomized, double-blind, phase II trial was conducted comparing placebo with bevacizumab at doses of 3 and 10 mg/kg of body weight with time to disease progression and response rate as primary endpoints. In this trial, only 4 out of 116 patients demonstrated tumor response (all PRs), and all of them were in the high dose arm. However, the time to progression of disease in the high-dose group was significantly superior to that in the placebo group, with a median TTP of 4.8 versus 2.5 months, p ⎥ (Eqn. 7-12), σˆ 2(1 − ρˆ ) / n ⎥⎦ ⎢⎣ or equivalently,

TABLE 7.1

Powers Associated with the Two-sided a Level Test Procedure (Eqn. 7-11) for Various Mean Detectable Differences d and Correlations r Given a = 0.05, n = 45, and s = 17.5. ABSOLUTE MEAN DETECTABLE DIFFERENCE d CORRELATION r 0 0.1 0.5

5

7

9

11

0.273 0.475 0.684

0.298 0.516 0.730

0.483 0.765 0.932

0.858 0.989 >0.999

The sample size of n = 45 for this trial was set to accommodate the power calculations of the primary objective of the study, not to accommodate the power calculations of the microvessel density analysis, which was a secondary objective. However, by solving (Eqn. 7-13) for n, it is possible to calculate the sample size required to attain a specified power for an a level two-sided test for the hypothesis H0 : m1 − m2 = 0 versus H1 : m1 − m2 ≠ 0 for a specified correlation r. The resulting equation is: n=

2σ 2 (1 − ρ)(zα / 2 + zβ )

(Eqn. 7-14), δ2 where the specified power equals 1 − b. From (Eqn. 7-14) for an a = 0.05 two-sided test of H0 : m1 − m2 = 0 versus H1 : m1 − m2 ≠ 0 with s = 17.5, the sample size required to achieve a power of 0.80 is provided in Table 7.2 for various absolute mean detectable differences d and correlations r.

MS(Pre/Post) ⎤ ⎡ p-value = P ⎢ F1,n −1 > MS(Patient*Pre/Post) ⎥⎦ , ⎣ where MS(Pre/Post) and MS(Patient*Pre/Post) are the analysis of variance (ANOVA) mean square due to the pre/post effect and the mean square due to interaction of patients by the pre/post effect, respectively. For any detectable absolute difference under the alternative hypothesis |m1 − m2| = d > 0, the power of the (Eqn. 7-11) procedure is given by: ⎡ ⎤ δ power = 1 − P ⎢ N (0, 1) < zα / 2 − ⎥ σ 2(1 − ρ ) / n ⎥⎦ ⎢⎣ (Eqn. 7-13). Table 7.1 provides powers for various r and d given a = 0.05, n = 45, and s = 17.5.

TABLE 7.2

Sample Sizes (n) Required to Attain a Power of 0.80 Associated with the Two-Sided Hypothesis Test (Eqn. 7-12) for Various Mean Detectable Differences d and Correlations r Given a = 0.05. and s = 17.5. ABSOLUTE MEAN DETECTABLE DIFFERENCE d CORRELATION r 0 0.1 0.5

5

7

9

11

192 98 59

173 88 53

96 49 30

38 20 12

48


For a one-sided a level test where the alternative hypothesis is either H1 : m1 − m2 > 0 or H1 : m1 − m2 < 0, equations (Eqn. 7-13) and (Eqn. 7-14) still hold provided a/2 is replaced by a and d continues to represent the absolute difference |m1 − m2 | = d > 0 under the alternative hypothesis. Note that under a normal distribution assumption, the test criterion (Eqn. 7-11), the p-value (Eqn. 7-12), the power function (Eqn. 7-13), and the sample size function (Eqn. 7-14) can also be applied to two independent samples by setting r = 0 Testing, Estimation, and Confidence Intervals Although this trial closed due to poor accrual, Table 7.3 provides simulated pre and post microvessel density data for 45 patients. The observed mean difference between the postand pre-microvessel density averaged over the 45 patients was y1 − y2 = 61.13 − 57.33 = 3.8. The ANOVA mean square for the patients effect with 44 degrees of freedom was 426.7, the ANOVA mean square due to the pre/post time effect with 1 degree of freedom was 324.9, and the ANOVA mean square due to the patient by pre/post time interaction effect with 44 degrees of freedom was 135.3. The mean square due to patients and the mean square due to the patient by pre/post time interaction are ANOVA estimates of s 2(1 + r) and s 2(1 − r), respectively. Setting the s 2(1 + r) equal to 426.7 and s 2(1 − r) equal to 135.3 and solving for s 2, r, we obtain σˆ 2 = 281.3 (σˆ = 16.772) and r = 0.519. Therefore the p-value of the test on H0 : m1 − m2 > 0 versus H1 : m1 − m2 ≠ 0 equals: ⎡ ⎤ | 3.8 | p-value = 2P ⎢ N(0, 1) > ⎥ 16.772 ⋅ 2 ⋅ (1 − 0.519)/45 ⎥⎦ ⎢⎣ = 2P ⎡⎣ N (0, 1) > 1.56 ⎤⎦ = 0.12

(Eqn. 7-15),

or equivalently, 324.9 ⎤ ⎡ p-value = P ⎢ F1,n −1 > = P[ F1,n −1 > 2.4] = 0.12 . 135 .3 ⎥⎦ ⎣ An unbiased estimate of the mean difference m1 − m2 is provided by y1 − y2 = 3.8. Furthermore, a 100(1 − a)% confidence interval on m1 − m2 is given by: y1 − y2 ± zα / 2σˆ 2(1 − ρˆ ) / n

(Eqn. 7-16).

For this example using (Eqn. 7-16), 95% confidence bounds on m1 − m2 are given by (−1.01, 8.61). EXAMPLE 7-4 A randomized phase III trial of gemcitabine plus bevacizumab versus gemcitabine plus placebo in patients with advanced pancreatic cancer.

Discussion The primary objective of the trial was to determine if gemcitabine plus bevacizumab achieved superior overall survival compared to gemcitabine plus placebo in patients with advanced pancreatic cancer. As a secondary objective, the toxicity rates between the two treatment arms were compared. Design and Hypothesis Test To address the primary objective of comparing the overall survival of the two treatments, the patients were randomized with equal probability to the treatment gemcitabine plus bevacizumab or gemcitabine plus placebo. The assumed total enrollment rate was 20 patients per month. For an a = 0.05 two-sided test, the trial was powered to distinguish a difference in the

TABLE 7.3

Pre- and Post-Treatment Microvessel Density Simulated Data on 45 Patients. Patient Pre Post

1 64 36

2 59 67

3 52 72

4 70 78

5 81 64

6 64 56

7 28 42

8 72 75

9 29 56

10 68 50

11 67 66

12 38 46

13 110 68

14 43 62

15 57 39

Patient Pre Post

16 47 13

17 53 44

18 60 47

19 54 45

20 56 99

21 72 89

22 83 73

23 70 65

24 67 64

25 40 33

26 27 43

27 71 64

28 70 57

29 40 54

30 89 57

Patient Pre Post

31 78 75

32 52 53

33 71 64

34 73 71

35 55 46

36 55 45

37 57 47

38 61 54

39 63 56

40 58 64

41 49 53

42 70 44

43 56 40

44 104 91

45 48 53

49

7 DESIGN, TESTING, AND ESTIMATION IN CLINICAL TRIALS

survival curves of the two treatments when the median survival of the gemcitabine plus bevacizumab arm was 6 months and the median survival of the gemcitabine plus placebo arm was 8.1 months, producing a 1.35 hazard ratio under an exponential event-time assumption. Using results from George and Desu (2) and Rubenstein et al. (3) (calculated by a computer program DSTPLAN downloaded from http:// biostatistics.mdanderson.org/SoftwareDownload/Single Software.aspx?Software_Id = 41, an enrollment of n = 528 patients was required with a 26.4 months enrollment period (at a 20 patient enrolled/month) and a 12 month follow-up period to attain a 90% power to detect a hazard rate of 1.35 using a two-sided log-rank test. During the enrollment and follow-up period, 470 events were expected. The secondary objective of the trial was to test whether the toxicity rates of the two treatment arms were equal or differed by Δ or more, assuming the toxicity rate of the gemcitabine plus placebo treatment was 0.10. Formally, this comparison can be written as the hypotheses: H0 : p1 − p2 = 0 versus H1 : p1 − p2 = Δ > 0 where p1, p2 are the population toxicity rates of the gemcitabine plus bevacizumab and gemcitabine plus placebo treatment, respectively. Since the sample sizes in each treatment arm are large, an approximate normal arcsin transformation procedure was used to test the hypothesis. Under this assumption, arcsinn( pˆ 1 ) , arcsinn( pˆ 2 ) are independent normal random variables with means arcsinn( p1 ) , arcsinn( p2 ) , and variances 1/(4n1), 1/(4n2), respectively, where n1, n2, are the sample sizes and pˆ 1 , pˆ 2 are the observed toxicity rates for the gemcitabine plus bevacizumab and gemcitabine plus placebo, respectively. The criterion to test this hypothesis is: Reject H0 : p1 − p2 = 0 in favor of H1 : p1 − p2 = Δ > 0 if arcsin( pˆ 1 ) − arcsin( pˆ 2 ) ≥ zα 1 / (4n1) + 1 / (4n2 ) (Eqn. 7-17). If it is of interest to provide a p-value rather than an a level test criterion then the p-value of the onesided test is given by: ⎡ ⎤ ⎢ ⎥ arcsin pˆ 1 − arcsin pˆ 2 ⎥ p-value = P ⎢⎢ N (0, 1) > ⎥ 1 1 ⎢ ⎥ + 4n1 4n2 ⎢⎣ ⎥⎦ (Eqn. 7-18).

TABLE 7.4

Powers Associated with the One-sided a Level Test Procedure (Eqn. 7-17) for Various Combinations of p1 and Δ = p1 − p2 for a = 0.05 and n1 = n2 = n/2 = 264. P1

P2

POWER

0.18 0.20 0.22 0.28 0.30 0.32 0.38 0.40 0.42 0.48 0.50 0.52

0.10 0.10 0.10 0.20 0.20 0.20 0.30 0.30 0.30 0.40 0.40 0.40

0.848 0.947 0.985 0.696 0.846 0.935 0.617 0.779 0.892 0.583 0.748 0.870

For any values of p1, p2 under H1 : p1 − p2 = Δ > 0, the power of the (Eqn. 7-17) procedure is given by: ⎡ arcsin( p1 ) − arcsin( p2 ) ⎤ ⎥ Power = 1 − P ⎢N (0, 1) < zα − 1 / (4n1) + 1 / (4n2 ) ⎢⎣ ⎥⎦ (Eqn. 7-19).

From (Eqn. 7-19), Table 7.4 provides powers for combinations of p1 = 0.10, 0.20, 0.30, 0.40 and Δ = 0.08, 0.10, 0.12 for a one-sided α = 0.05 test with n1 = n2 n/2 = 264. The sample size of n = 528 for this trial was set to accommodate the power calculations of the primary objective of the study, not to accommodate the power calculations of the toxicity rate comparison, which was a secondary objective. However, for equal allocation to each treatment (i.e., n1 = n2 = n/2), it is possible from (Eqn. 7-19) to calculate the sample size n required to attain a specified power for an a level one-sided test for the hypothesis H0 : p1 − p2 = 0 versus H1 : p1 − p2 = Δ > 0. The resulting equation is: n=

(zα + zβ )2 [arcsin( p1 ) − arcsin( p2 )]2

(Eqn. 7-20),

where the specified power equals 1 − b. So from (Eqn. 7-20) for an a = 0.05 one-sided test of H0 : p1 − p2 = 0 versus H1 : p1 − p2 = Δ > 0, the sample size required to achieve a power of 0.80 is provided in Table 7.5 for combinations of p1 = 0.10, 0.20, 0.30, 0.40 and Δ = 0.08, 0.10, 0.12.

50


EXAMPLE 7-5

TABLE 7.5

Sample Size Required to Attain a Power of 0.80 Associated with the One-Sided Hypothesis Test (Eqn. 7-17) for Various Values of p1 and p2 Given a = 0.05. p1

p2

0.18 0.20 0.22 0.28 0.30 0.32 0.38 0.40 0.42 0.48 0.50 0.52

0.10 0.10 0.10 0.20 0.20 0.20 0.30 0.30 0.30 0.40 0.40 0.40

n 456 307 223 700 460 326 864 560 393 950 610 424

For a two-sided a level test where the alternative hypothesis is H1 : p1 − p2 ≠ 0, equations (Eqn. 7-19) and (Eqn. 7-20) still hold provided a/2 is replaced by a and in (Eqn. 7-19) arcsin(p1) − arcsin(p2) is replaced by | arcsin(p1) − arcsin(p2)|. Testing, Estimation, and Confidence Intervals Testing and estimation of the primary endpoint, overall survival will not be examined for this example since the log-rank and Kaplan-Meier analysis procedure will be examined in detail in the next Example 7-5. Instead, in this example we will use the secondary objective to examine the difference in grade 4 and 5 maximum hematologic toxicity rates between the two treatment arms. The number of patients with grade 4 and 5 hematologic toxic events (8) was x1 = 30 and x2 = 21 from samples of size n1 = 263 and n2 = 277 in the bevacizumab and placebo arms, respectively. Therefore, the observed toxicity rates for the bevacizumab and placebo arms were pˆ1 = 30/263 = 0.1141 and pˆ2 = 21/277 = 0.0758. From (Eqn. 7-18), the p-value to test the one-sided hypothesis H0 : p1 − p2 = 0 versus H1 : p1 − p2 = Δ > 0 is given by: ⎡ ⎤ ⎢ ⎥ arcsin 0.1141 − arcsin 0.00758 ⎥ p-value = P ⎢ N(0, 1) > ⎢ ⎥ 1 1 + ⎢ ⎥ 4(263) 4(277) ⎣ ⎦

= 0.0639

(Eqn. 7-21).

A randomized phase III trial of induction (daunorubicin/ cytarabine) and consolidation (high dose cytarabine) plus midostaurin or placebo in newly diagnosed FLT3 mutated AML patients.

Discussion The primary objective of the trial was to determine if the addition of midostaurin to daunorubicin/cytarabine induction, high dose cytarabine consolidation, and continuation therapy improves overall survival in mutant FLT3 AML patients. A secondary objective was to determine if the addition of midostaurin to daunorubicin/cytarabine induction, high dose cytarabine consolidation, and continuation therapy improves disease free survival (DFS) in mutant FLT3 AML patients. Design and Hypothesis Test To address the primary objective of comparing the overall survival of the two treatments in newly diagnosed FLT3 mutated AML patients, the patients were randomized with equal probability to the two treatments: (1) induction (daunorubicin/cytarabine) and consolidation (high dose cytarabine) plus midostaurin, and (2) induction (daunorubicin/ cytarabine) and consolidation (high dose cytarabine) plus placebo. A formal one-sided hypothesis to compare whether the midostaurin arm improves overall survival is: H0 : l = 1 versus H0 : l > 1 where l is the hazard ratio of the two survival curve. Assuming exponential event times l = mM /mP where mM, mP are the median survival times of the midostaurin and placebo patient populations, respectively. The assumed total enrollment rate was 25 patients per month. For an a = 0.05 one-sided test, the trial was powered to distinguish a difference in the survival curves of the two treatments when the median survival of the daunorubicin/cytarabine plus midostaurin arm was 21 months and the median survival of the daunorubicin/cytarabine plus placebo arm was 15 months, producing a 1.4 hazard ratio under an exponential event time assumption. Using results from George and Desu (2) and Rubenstein et al. (3), an enrollment of n = 514 patients was required with a 20.5 months enrollment period and a 24-month follow-up period to attain a 90% power to detect a hazard rate of 1.4 using a onesided log-rank test. During the enrollment and followup period, 374 survival events were expected. The secondary objective of the trial was to compare the DFS between patients in the midostaurin and placebo arms. Among patients who achieved complete remission after the induction phase DFS time is the

51

7 DESIGN, TESTING, AND ESTIMATION IN CLINICAL TRIALS

period from complete remission to relapse or death, whichever comes first. Seventy-nine percent of the FLT3 mutated patients were expected to achieve complete remission in each treatment arm after the induction phase, producing 406 patients (=0.79*514) to investigate DFS. Assuming a median DFS time of 11 months in the placebo arm provides an 87% power (2, 3) to detect an increase to 15.4 months in the midostaurin arm. During the post induction enrollment period and the follow-up period, 335 DFS events are expected. The comparison of overall survival between the two treatment arms and the comparison between the DFS between the two treatment arms can both be performed through the log-rank test. Therefore the logrank test will be discussed relative to overall survival time and a comparable application can be made to the disease free survival time. An excellent discussion of the log-rank test is provided by Collett (6). Suppose that there are r distinct death times occurring in either arm and let tj represent the times when the deaths occurred for j = 1, 2,..., r and t1 < t2 χ12,α (0) (Eqn. 7-24), 2 where χ v,α (0) is the 100(1 − a) percentile of a central chi-square distribution with v degrees of freedom. The p-value for the two-sided test is given by:

p-value = P[ χ12 (0) > RL2 ]

2 where χ v (0) is a central chi-square random variable with v degrees of freedom. An estimate of the survivor curve Si(t) in the ith arm can be generated through a Kaplan-Meier curve for i = 1, 2. The Kaplan-Meier survival curve estimate Sî (t) for any time t in the interval tk to tk+1, k = 1, 2,...r where tr+1 is defined to be ∞ is given by: k ⎛n −d ⎞ ij ij Sî (t) = ∏ ⎜ ⎟ nj ⎠ j =1 ⎝

(Eqn. 7-26),

for arms i = 1, 2. The standard error of the KaplanMeier estimate of the survival function is given by the Greenwood formula: 1/ 2

⎫⎪ dij ⎪⎧ k s.e.{Sî (t)} ≈ [ Sî (t)] ⎨∑ ⎬ ⎩⎪ j =1 nij (nij − dij ) ⎭⎪

(Eqn. 7-27),

for tk ≤ t < tk+1. Therefore, a 100(1 − a)% confidence interval on the survival curve Si(t) at time tk ≤ t < tk+1 for treatment i = 1, 2 is given by

Reject H0 : l = 1 in favor of H1 : l > 1 if RL > za (Eqn. 7-22),

Sî (t) ± zα / 2s.e.{Sî (t)}

(Eqn. 7-28).

However, confidence intervals (Eqn. 7-28) are symmetric and therefore can produce confidence intervals outside the range (0,1) for values of Sî (t) near 0 or 1. To correct this situation, an alternative confidence interval on Si(t) produced through a logistic transformation on Si(t) is given by:

where RL =

(Eqn. 7-25),

UL VL r

UL = ∑ (d1 j − e1 j ) j =1

⎡ Sˆ (t)exp[ zα / 2s.e.{log[ − log Sî (t )]}] , Sˆ (t)exp[ − zα / 2s.e.{log[ − log Sî (t )]}] ⎤ i ⎣ i ⎦

r

VL = ∑ v1 j j =1

v1 j =

(Eqn. 7-29),

n1 j n2 j d j (n j − d j ) n 2j (n j − 1)

where . var{log[ − log Sî (t)]} =

The p-value for the one-sided test is given by: p-value = P[Ν(0,1) > RL]

(Eqn. 7-23).

k dij 1 (Eqn. 7-30), ∑ 2 ˆ [log S(t)] j =1 (nij − dij )

{

}

ˆ ˆ and s.e.{ log[ − log Si (t)]} = var{log[ − log Si (t)]}

1/ 2

.

52


Testing, Estimation, and Confidence Intervals Although this trial was just opened to enrollment at the time of this writing, Table 7.6 provides representative death times tj and values of d1j, n1j, d2j, n2j, dj, nj, e1j, and v1j, for a total enrollment of 514 patients. The times are grouped in tenths of year increments so there will be a manageable number of death times to demonstrate the numerical calculations.

From Table 7-6 UL = 38.2903 and VL = 86.5266. Therefore, RL = 38.5266/ 86.5266 = 4.14

(Eqn. 7-31),

and from (Eqn. 7-23) the p-value 0.25, STOP. · If SCORE ≥ 0.35, STOP. The estimated MTD is the highest dose level with observed SCORE less than or equal to 0.25. A more

complex trial with many toxicity types and grades is described in the work of Bekele and Thall (9).

TRIALS WITH LONG FOLLOW-UP As we have seen earlier a lot of dose finding problems in oncology can be addressed by designs similar to the 3 + 3 design. However, there are challenges that require different approaches. One such challenge is the dose-finding trial with long follow-up. Since many oncology trials are comprised of multiple cycles of study drug administered over extended duration, there is often a need to follow subjects for DLTs for a long period of time. For example, radiation therapy trials often require long follow-up since long-term toxicities are likely to occur. Consider this slightly modified example of an actual trial of a new cytotoxic drug used in conjunction with other drugs for prophylaxis of graft-verses-host disease in patients undergoing stem cell transplantation. The goal is to identify the MTD defined as a dose with DLT rate of 0.25. The DLT is defined as any irreversible grade 3 toxicity or any grade 4 nonhematologic toxicity related to study drug observed during the first 42 days following stem cell infusion. Late treatmentrelated toxicities, such as veno-occlusive disease of the liver, pulmonary fibrosis, or neurotoxicity, can also count as DLTs if they occur within 60 months after study drug initiation. A protocol based upon the 3 + 3 design, with each cohort followed for 60 months, will result in a trial of very long duration. One possible approach is to use the 3 + 3 design and to base decisions regarding dose escalation on the 42-day follow-up period. Then, one asks how to take into account late toxicities that occur beyond 42 days but within 60 months of the start of study drug administration. One possible design solution is described below. The idea is to have a blend of two designs: first, the design similar to the 3 + 3 scheme used in the beginning of the trial, which we will refer to as a start-up rule, and secondly, an up-and-down type design that is invoked after the first DLT is observed. In the start-up rule clinical trial subjects are assigned to cohorts of three. During this start-up phase subjects are monitored for the potential emergence of AEs including an AE that might develop into a DLT. If no DLTs are observed to occur in a cohort during the first 42 days after study drug initiation, then the next cohort of three subjects is assigned to the next higher dose level of study drug. If the study investigator chooses to enroll any additional subjects prior to the completion of the most recent cohort’s first 42 days

63

8 DESIGN OF PHASE I TRIALS

of study drug exposure at the current highest dose, then any additional subject could be given the lower tried-and-tested dose level for which there has already been the protocol-required 42-day minimum dose exposure experience of 3 patients without occurrence of a DLT. All study subjects continue to be monitored for AEs during the entire span of the 60-month study period. The start-up would continue until the first DLT is seen in any of the subjects, at which point the dosing assignments follow the upand-down design starting from the dose associated with the newly documented DLT. In the up-and-down design, the goal is to assign each new subject to the dose that is believed to be the MTD based on the data available so far. Let q be the estimated DLT rate at the time when a patient is ready for assignment. We will illustrate later how to compute this estimate. Assume that the most recent subject is assigned to dose dj. Then the dose for the next subject is determined based on the following algorithm: · if q ≤ Γ − Δ, the next patient is assigned to dose dj+1 · if q ≥ Γ+ Δ, the next patient is assigned to dose dj-1 · if Γ − Δ < q < Γ + Δ, the next patient is assigned to dose dj Special provisions are in place in case the lowest dose appears to have high rate of DLT. To make the decision rules in the up-and-down design similar to the 3 + 3 design, Γ = 0.26 and design parameter Δ = 0.09 are used. For example, if a DLT is observed at a dose, the dose can be escalated according to the up-and-down design if six patients are assigned to this dose with only one DLT observed. More details about the design and recommendations regarding the choice of the design parameter can be found in the review by Ivanova, Flournoy, and Chung (10). For example, for Γ between 0.1 and 0.25, Δ = 0.09 is recommended; for Γ between 0.30 and 0.35, Δ = 0.10 is recommended; for Γ = 0.40, Δ = 0.12 is recommended; and for Γ between 0.45 and 0.5, Δ = 0.13 is recommended. The DLT rate at each dose is estimated using all DLT information available at that dose so far. Let T be the follow up time, T = 60 months. Assume that a DLT time is uniformly distributed in (0,T), that is, the DLT is as equally likely to occur at any time during follow-up. At the time of analysis for subject i, define wi = min{(follow-up time)/T, 1}, the proportion of time a subject has been followed so far; and DLT indicator yi = 0, if no DLT so far, or yi = 1, if DLT. The weight wi is set to 1, if a subject had a DLT. The estimate of DLT rate at the dose q can be computed using the following iterative algorithm:

Step 0. θ = ∑ i =1 yi / ∑ i =1 wi n

Step 1. ai =

n

1 , i = 1,..., n 1 − wiθ

Step 2. θ new = ∑ i =1 ai yi / ∑ i =1 ai wi n

n

Then iterate between Steps 1 and 2. Mathematically speaking θ maximized the likelihood n

L(θ ) = ∏ ( wiθ ) i (1 − wiθ ) i =1

y

1− yi

,

and the algorithm described above finds θ that maximizes L(q ). For example, if the data at a dose are Subject 1: DLT (y1 = 1, w1 = 1); Subject 2: no DLT, follow-up time = T (y2 = 0, w2 = 1); Subject 3: no DLT so far, follow-up time = T/2 (y3 = 0, w3 = 0.5); The estimate q we use iterative algorithm described above Step 0. θ = (1 + 0 + 0) / (1 + 1 + .5) = 0.40 1 1 = 1.67, a2 = = 1.67, Step 1. a1 = 1 − 1 × 0.4 1 − 1 × 0.4 1 a3 = = 1.25 1 − 0.5 × 0.4 Step 2. θ new = (1.67 × 1 + 1.67 × 0 + 1.25 × 0) / (1.67 × 1 + 1.67 × 1 + 1.25 × .5) = 0.42 1 1 = 1.72, a2 = = 1.72, 1 − 1 × 0.42 1 − 1 × 0.42 1 = 1.27 a3 = 1 − 0.5 × 0.42 Step 2. θ new = (1.72 × 1 + 1.72 × 0 + 1.27 × 0) /

Step 1. a1 =

(1.72 × 1 + 1.72 × 1 + 1.27 × .5) = 0.42 The value of θ is the same in the last two iterations, indicating that the algorithm converged and the estimated DLT rate is q = 0.42. At the end of the trial, the dose with the estimated DLT rate closest to 0.25 is declared the MTD. The design described in this section allows for the trial to occur relatively quickly, provides flexibility in assignment of subjects, and will likely result in assigning many subjects to the MTD. The total sample size for the trial has to be specified in advance, and is usually 20 to 30 patients. It is recommended to run simulations using plausible dose-toxicity models to see if the

64


proposed total sample size yields high likelihood of selecting the right dose at the MTD. DISCUSSION Numerous designs have been developed for phase I trials in oncology. We only reviewed and presented designs that are easy to implement without a computer. Among others, the design that should be mentioned is the Continual Reassessment Method (CRM). The CRM (11) was developed with the goal of bringing experimentation close to the MTD as soon as possible and assigning as many subjects as possible to the MTD. The CRM uses a working model as a tool allowing for the utilization of all information available in the trial to derive the best dose assignment that is closest to the MTD for the next subject. We focused our attention on dose-finding trials with a single anticancer agent. Almost every oncology trial nowadays involves a combination of anticancer therapies. Methods have been developed that allow one to fully evaluate the space created by multiple doses, instead of changing one dose at a time. These include methods described by Thall et al., and by Ivanova and Wang (12, 13). Similar design problems arise in trials in which subjects can be stratified before the trial into two (or more) subpopulations according to their susceptibility to toxicity. For example, patients can be divided into two subpopulations using genetic information available before the trial. One has to run two different dose-finding trials, one for each subpopulation; however, the study can be made more efficient if the two trials exchange information (14, 15).

References 1. Rosenberger WF, Haines LM. Competing designs for phase I clinical trials: a review. Statistics in Medicine. 2002;21: 2757–2770. 2. Storer BE. Design and analysis of phase I clinical trials. Biometrics. 1989;45:925–937. 3. Korn EL, Midthune D, Chen TT, Rubinstein LV, Christian MC, Simon RM. A comparison of two phase I trial designs. Statistics in Medicine. 1994;13:1799–1806. 4. Kang SH, Ahn C. The expected toxicity rate at the maximum tolerated dose in the standard phase I cancer clinical trial design. Drug Information Journal 2001;35(4):1189–1200. 5. Kang SH, Ahn C. An investigation of the traditional algorithmbased designs for phase I cancer clinical trials. Drug Information Journal. 2002;36:865–873. 6. Lin Y, Shih WJ. Statistical properties of the traditional algorithmbased designs for phase I cancer clinical trials. Biostatistics. 2001;2:203–215. 7. Reiner E, Paoletti X, O’Quigley J. Operating characteristics of the standard phase I clinical trial design. Computational Statistics and Data Analysis. 1999;30:303–315. 8. Ivanova A. Escalation, up-and-down and A+B designs for dosefinding trials. Statistics in Medicine. 2006;25:3668–3678. 9. Bekele BN, Thall FT. Dose-finding based on multiple toxicities in a soft tissue sarcoma trial. Journal of American Statistical Association. 2004;99:26–35. 10. Ivanova A, Flournoy N, Chung Y. Cumulative cohort design for dose-finding. Journal of Statistical Planning and Inference. 2007;137:2316–2317. 11. O’Quigley J, Pepe M, Fisher L. Continual reassessment method: a practical design for phase I clinical trials in cancer. Biometrics. 1990;46:33–48. 12. Thall P, Millikan R, Mueller P, Lee, S-J. Dose finding with two agents in phase I oncology trials. Biometrics. 2003;59: 487–496. 13. Ivanova A, Wang KA Nonparametric approach to the design and analysis of two-dimensional dose-finding trials. Statistics in Medicine. 2004;23:1861–1870. 14. O’Quigley J, Paoletti, X. Continual reassessment method for ordered groups. Biometrics. 2003;59:430–440. 15. Ivanova A, Wang K. Bivariate isotonic design for dose-finding with ordered groups. Statistics in Medicine. 2006;25:2018–2026.

Design of Phase II Trials

9 Hongkun Wang Mark R. Conaway Gina R. Petroni

The most common primary goal of a phase II trial is to assess the therapeutic efficacy of a new agent or treatment regimen, and decide if the activity of the new agent or regimen shows enough promise to warrant further investigation. Most phase II trials use onesample designs, in which all the patients accrued are treated with the new agent or treatment regimen. Methods of single-stage, multistage, and sequential designs and analyses have been proposed and are used in practice. In this chapter, we will describe some of the most common designs and provide examples of the use of each approach in practice. We will discuss designs with multiple arms and multiple endpoints and give some concluding remarks toward the end of the chapter. In order to illustrate the different design choices, we will apply all the methods we discuss to a common example based upon a phase II study by Rietschel et al. (1) of extended-dose temozolomide (TMZ) in patients with melanoma. Patients with stage IV or unresectable stage III melanoma were enrolled into the study and two cohorts of patients, M1c disease or not, were studied. Detailed information regarding patient entry criteria, dose and administration of TMZ, study design, and study results can be found in the original paper. The same study design and target rates were used within each cohort, and will serve as the basis to illustrate many of the designs discussed. In some

examples cohort specific data will be identified to display sequential design strategies.

SINGLE-STAGE DESIGNS Hypothesis Testing Framework In a single-stage phase II trial, n patients are accrued and treated. Based on the anticipated number of responses, a statistical test is formulated to decide whether the new therapy should be tested further for efficacy. It is common to define the response variable as a dichotomous outcome where patients are classified as having responded or not responded depending upon prespecified criteria. The population proportion of patients who respond to the new therapy is denoted by p. The population proportion of patients who respond to the standard therapy is denoted by p0, which is assumed known. With this notation, the hypothesis test can be written as H0: p ≤ p0 versus Ha: p > p0. The null hypothesis, H0, will be rejected if the number of observed responses is greater than a specified threshold; otherwise we fail to reject the null hypothesis. If X is the random variable that counts the number of responses in a sample of n patients, then the distribution follows a binomial (p) distribution with probability density function P(X = k) = kn pk (1 − p)n −k where n = n ! . If we let r k!( n − k)!

()

() k

65

66


denote the number of observed responses, and assume pa is the response rate in the alternative hypothesis that is “important not to miss” then the sample size n and critical value c should satisfy the following equations:

α = P(reject H0 | p = p0 ) = P(X ≥ c | p0 ) n

=∑ k=c

( )p (1 − p ) n k

k 0

n −k

(Eqn. 9-1),

0

and

Confidence Interval or Precision Framework 1 − β = P(reject H0 | pa ) = P(X ≥ c | pa ) n

=∑ k=c

( )p (1 − p ) n k

k a

n −k

(Eqn. 9-2),

a

where a and b are the maximum tolerable levels for the probability of type I (false positive) and type II (false negative) errors. The type I error a represents the probability that the study will incorrectly identify a new therapy as “sufficiently promising” when the new therapy is no more effective than the standard. The type II error β represents the probability that the study will incorrectly identify a truly promising therapy as “not sufficiently promising.” In the TMZ example, it was assumed that a null response rate of 10% would be considered “not sufficiently promising” while an alternative response rate similar to that of extended-dose TMZ with antiangiogenic agents of 30% would be considered “sufficiently promising.” Type I and type II error rates were set at 0.10. Using the above formulae (9-1) and (9-2) with p0 = 0.1 and pa = 0.3, a sample of size 25 will yield a = 0.098 and b = 0.090 (power = 0.910) with a critical value c = 5 responses. Thus, at the end of the study we would reject the null hypothesis in favor of the alternative if 5 or more responses are observed among the 25 patients. For large n and a moderate p, the test can be based on, pˆ = r/n, which is asymptotically normally distributed. A test statistic for testing H0 is given by z=

with z1−a and z1−a the (1 − a) and (1 − b) percentiles of the standard normal distribution. The sample size from the large-sample approximation can be quite different from the sample size calculated from binomial formulae (9-1 and 9-2). Using the TMZ design parameters with a type I error rate of 0.1 and power of 0.9, the required sample size would be 30 using equation (9-3).

pˆ − p0 p0 (1 − p0 ) n

=

r − np0 np0 (1 − p0 )

,

(Eqn. 9-3),

which follows asymptotically a normal distribution. H0 will be rejected if z > z1−α, where z1−α is the (1-α) percentile of the standard normal distribution. The p-value is given by P(Z ≥ z | p0 ) = 1 − Φ(z) , where Φ is the standard normal cumulative distribution function. The sample size n required to have a significance level a and power 1 − b can be calculated approximately from n = { z1−α [ p0 (1 − p0 )]1/ 2 + z1− β [ pa (1 − pa )]1/ 2 }2 / (p0 − pa )2

In a single-stage phase II trial, sample size can be chosen to satisfy a specified level of precision where a useful measure of precision is the confidence interval around the estimated parameter. Here the goal is estimation and not hypothesis testing. Consider the 95% confidence interval for p, the proportion of interest. At the end of the trial p is estimated by pˆ ± 1.96 pˆ (1 − pˆ ) / n where pˆ = (# responses / n) . For sample size estimation one must decide upon how narrow or precise a 95% confidence interval is desired at the final analysis (for example ±10%). Narrowness is defined by the half-width of the 95% confidence interval which is equal to 1.96 p (1 − p) /n . With an initial guess for p, the equation can be solved for n, or one can set p = 0.5 the maximal amount for p(1 − p). This method uses the normal approximation to the binomial distribution. For extreme values of p (say, p < 0.2 or p > 0.8) estimation should be based upon exact binomial confidence limits. In the TMZ example, we could assume that the response rate will be similar to that of extended-dose TMZ with antiangiogenic agents of 30%. Setting p = 0.30 then we would need n = 36 for a half-width of 15% or n = 81 for a half-width of 10%. MULTISTAGE DESIGNS In a multistage setting, patients are accrued into the study in several stages. Testing is performed at each stage after a predefined target accrual has been completed. At each stage a decision of whether to terminate the trial early or to continue to the next stage is made. In the most commonly used multistage designs, accrual was to stop early only when the preliminary data supported inactivity of the new agent. A variety of early stopping rules have been proposed. Gehan’s Two-Stage Designs The two-stage design for phase II setting was first proposed by Gehan (2) in 1961. The goal was to identify the minimum number of patients to observe with a

67

9 DESIGN OF PHASE II TRIALS

sequence of no responses before concluding that the new drug was not worthy of further study. It is important to note that Gehan proposed this design when the response rate for the new agent under investigation was expected to be low, for instance, no more than 20%. In the first stage, n1 patients are enrolled and X1 responses are observed. If X1 = 0, the trial is closed to accrual. If one or more patients respond (X1 > 0), then accrual to the second stage begins. In the second stage, n2 additional patients are accrued and X2 responses are observed. The number of additional patients is chosen to estimate the response rate within a specified level of precision. With this design the true response rate, p, can be estimated by X1 + X2 , the total number of responders n1 + n2 in both stages, divided by the number of patients accrued at each stage. In Gehan’s design, the first stage sample size n1 is chosen to give a small probability of early stopping (say, 5%) at a fixed target response rate pa, considered to be the minimum response rate of interest, in a sequence of no responses. The first stage sample size n1 is found by n solving 0.05 = P(Stop early | pa ) = P(X1 = 0) = (1 − pa ) 1 . The second stage sample size n2 is chosen to give sufficient precision for estimating the response rate p after all patients are observed. The precision is based on choosing a desired value for the standard p(1 − p) error, SE = . For example, if one wants the n1 + n2 precision of effectiveness to be no greater than s, then n2 can be chosen to solve s=

pˆ 1 (1 − pˆ 1) , where pˆ 1 = X1 n1 . n1 + n2

(Eqn. 9-4).

X1 + X2 , n1 + n2 with an approximate standard error given by At the end of the trial, p is estimated by pˆ =

pˆ (1 − pˆ ) . To be conservative, Gehan suggested n1 + n2 using the upper 75% confidence limit for the true percentage of treatment success in the first sample in equation (9-4). In Gehan’s design, the number of patients accrued in the second stage depends on the number of responses in the first stage and the desired standard error. In practice, Gehan’s design is often used with 14 patients in the first stage and 11 patients in the second stage. This provides for estimation with approximately a 10% standard error. Higher precision provides better estimates but requires much larger sample sizes. Gehan’s design is sufficient for the very specific context in which it was derived, for instance, low small expected SE(pˆ ) =

response rate, but has practical and statistical disadvantages in other situations, and is not often used today. In the TMZ design, the response rate of interest is defined as at least 0.3 (pa ≥ 0.3). Following Gehan’s approach, in the first stage the P(Stop early | pa ) ≤ 0.1 gives n1 = 7, the probability of observing all 7 consecutive failures is (1−0.3)7 = 0.082. The chance of at least one success would be 1 – 0.082 = 0.918 or 91.8%. Thus if 0/7 responses are observed, we would reject the new treatment and would be approximately 92% confident that the response rate with the new treatment is less than 30%. If at least one response is observed, then the trial would continue to accrue to the second stage. Assuming a precision of 10% or 5% with one observed success in the first stage, the sample size for the 2nd stage is approximately 16 or 83 patients, respectively (equation [9-4]). Fleming’s K-Stage Designs The design proposed by Gehan (2) was designed to allow for early termination only if preliminary data supported that the new therapy was likely to be ineffective. Schultz et al. (3) defined a general multiple testing procedure as alternatives to the single-stage design. Fleming (4) continued the work of Schultz et al. and proposed the K-stage design to determine appropriate acceptance and rejection regions at each stage. In addition to allowing for early stopping if a treatment appears ineffective, Fleming’s design allows for early stopping if the treatment appears overwhelmingly effective, while preserving (approximately) size and power characteristics of a single-stage design. The study is done in K stages, with the kth stage sample size equal to nk, k = 1, . . . ,K. The total sample size over all stages, n = n1 + n2 + . . . + nk, is guided by the fixed sample design using the exact binomial calculations (9-1 and 9-2) and the large sample approximation. Fleming derived upper and lower boundaries that would allow investigators to make decisions based on the accumulated number of responses observed by the end of each stage. If the number of responses at the end of the kth stage exceeds the upper boundary for the kth stage, the study can be terminated with the conclusion that the treatment shows promise. If the accumulated number of responses is less than the lower boundary, the study can be terminated with the conclusion that the treatment is not effective. If neither boundary is crossed, the study continues by enrolling the next set of patients. The stage boundaries are chosen to preserve the type I and type II error rates of the fixed sample size design. Even though Fleming derived the boundaries based on normal approximations, he

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evaluated the properties via simulations for small sample cases and concluded that the approximations give close answers. In Fleming’s design, decisions in favor of or against the new agent occur only when initial results are extreme. This permits the final analysis to be unaffected by interim monitoring if early termination does not occur. In practice, investigators rarely choose to terminate a phase II trial early if the data supports that the treatment is effective. Instead, they want to continue to get supportive data and to plan the possible followup phase III trial which will take time to develop. Referring to the TMZ design parameters, a Fleming two-stage design with 25 total patients and 15 in the first stage, would yield an exact α value of 0.093 and a β value of 0.102. In the first stage the trial would stop for futility if one or fewer responses is observed; or the trial would stop in favor of the new agent if at least five responses are observed; otherwise the trial would continue to a second stage. At final analysis (i.e., the end of the second stage) if only five responses are observed among all the patients, we would fail to reject the null hypothesis and conclude that the new agent does not warrant further study. If six or more responses are observed we would reject the null hypothesis and conclude that the data supports that the new agent is worthy of further study. Note in this example that the final critical value to reject the null hypothesis is increased by one compared to the single-stage decision rule. Simon’s Optimal Two-Stage Designs Simon (5) proposed an optimal two-stage design, where optimality is defined in terms of minimizing the expected sample size when the true response probability is p0. The trial is terminated early only for ineffective therapies. Simon argued that when the new agent has substantial activity, it is important for planning the larger comparative trial to estimate the proportion, extent, and durability of response for as many patients as possible in the phase II trial. The hypothesis to be tested is the same as in other phase II trials, H0: p ≤ p0 versus Ha: p > p0. The Simon design consists of choosing stage sample sizes n1 and n2 along with decision rules c1 and c2, where c1 and c2 are critical values to guide decisions at each stage. At the first stage, patients are accrued and X1 responses are observed. If too few responses are observed in the first stage X1 ≤ c1, the trial is stopped and the treatment is declared “not sufficiently promising” to warrant further study in a comparative trial (fail to reject H0). If the number of patients who respond exceeds the prespecified boundary X1 > c1, an additional n2 patients will be accrued into the second stage of the study. Among the n2 patients accrued in the

second stage, X2 responses are observed. If the total number of responders in both stages exceeds the prespecified boundary X1 + X2 > c2, the null hypothesis is rejected and the treatment is deemed sufficiently promising. If there are too few observed responders X1 + X2 ≤ c2, then the null hypothesis is not rejected. The boundaries c1and c2 are chosen to meet the following type I and type II error specifications: (size) P[ X1 > c1 , X1 + X2 > c2 | po ] ≤ α , and (power) P[ X1 > c1 , X1 + X2 > c2 | pa ] ≥ 1 − β . There are many choices of (c1, c2) that meet the type I and type II error specifications. Among all sets of (c1, c2) that meet the requirements, Simon proposed to choose the boundaries that minimize the expected sample size under H0. Intuitively, this is a sensible criterion in that, among all designs that meet the type I and type II error specifications, the optimal design is the one that on average treats the fewest number of patients with a therapy that is no better than the current standard therapy. Simon tabulated the optimal designs for various choices of design parameters N = n1+ n2, p0, pa, a and b. In addition, Simon tabulated designs for an alternate optimality criterion, which he called the “minimax design.” This design has the smallest maximum sample size among all designs that meets the type I and type II error requirements. The stage sample size and the boundaries for the two optimality criteria can be very different. Simon pointed out that in cases when the difference in expected sample sizes is small and the patient accrual rate is low, the minimax design may be more attractive than that with the minimum expected sample size under H0. The TMZ example was designed using the Simon minimax design. The study called for accrual of 16 patients in the first stage and 9 additional patients in the second stage for a maximum accrual of 25 patients. At the first stage, the trial would stop for futility if ≤1 response was observed, otherwise the trial would go on to the second stage. At the final analysis, if ≥5 responses were observed among all 25 patients, then they would reject the null hypothesis in favor of the alternative. In the TMZ study, the Simon’s minimax design resulted in the same total sample size and final decision rule as the one determined from the single-stage design; that will not always be the case. If Simon’s optimal design had been chosen, then accrual to the first stage would have been set at 12 patients, and 23 additional patients would have been accrued to the second stage if the first stage stopping criterion had not been met. With the optimal design the

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trial would stop at the first stage if ≤1 response is observed, otherwise it would continue to the second stage. At the final analysis, if ≥6 responses were observed among all 35 patients, then they would reject the null hypothesis in favor of the alternative. In this setting the stage and total sample sizes and critical values differed considerably among the two designs.

FULLY SEQUENTIAL DESIGNS The multistage designs can be considered as groupsequential designs where patients are entered in cohorts. A decision of whether to terminate the trial early or to continue to the next stage is made after each cohort is accrued and the test statistic is calculated. In a fully sequential design, an analysis is performed after the outcome of each new patient is observed using a test statistic based on the accumulated data to that point. The test statistic is then compared with an upper and lower boundary. If the test statistic falls in the region between the boundaries, an additional patient is sampled and his/her response to the new treatment is observed. If, however, the test statistic falls above the upper (below the bottom) boundary, then accrual is stopped and the null (alternative) hypothesis is rejected. A fully sequential design requires continuous monitoring of the study results, patient by patient, and thus it is often difficult to implement. Herson (6) proposed a fully sequential design for phase II trials. In this setting the null and alternative hypotheses were defined as H0: p ≥ pa versus Ha: p < pa, where pa is a “minimum acceptable response rate” chosen by the investigators. The technical details of Herson’s method, which use Bayesian predictive distributions, are beyond the scope of this chapter, but the idea is intuitive. A fixed sample size trial would reject Herson’s H0 if at the end of the trial there were too few responders. At any point in the trial, given information on the number of patients treated so far and the number of observed responders, it is possible to predict the probability that the null hypothesis will be rejected after n patients have been observed. If this predicted probability is too low or too high, it is reasonable to stop the trial. Thall et al. (7) also proposed a fully sequential design using Bayesian methods. The design requires specification of the response rate for the standard therapy p0, the experimental therapy p, the prior for p0, the prior for p, a targeted improvement for new therapy d0, and bounds Nmin and Nmax on the allowable sample size. The priors for p0 and p are chosen to be independent Beta distributions. Thall et al. give recommendations as to choosing the parameters of the prior distributions.

After the outcome from each patient is observed, Thall et al. calculate the posterior probability that the new therapy will be shown to be effective. The trial continues until the maximum sample size is reached, or the experimental therapy is shown with high probability to be effective. Thall et al. also calculate the posterior probability that the new therapy will meet the targeted improvement in response rate, and will terminate the trial early if this probability is too low. One of the advantages of Thall et al.’s approach is that it allows for the uncertainty in response rate with the standard therapy to be incorporated into the design. A disadvantage is that it requires monitoring the data continuously and needs numerous analyses. It can often arrive at “not convincing either way” decisions. For the TMZ example responses were observed in the 12th, 15th, and 23rd patients in the first cohort and in the 2nd, 15th, and 21st patients in the second cohort. Using a targeted improvement of 0.20, and the priors recommended in Thall and Simon, the trial would be stopped in the first cohort at the maximum of 4 or the preselected minimum sample size Nmin. In the second cohort, the trial would be stopped at the maximum of 9 or the preselected minimum sample size. In each case, the trial would be stopped because of a low posterior probability that the therapy would meet the targeted improvement in response rate. Lee et al. (8) proposed a predictive probability design for phase II cancer clinical trials based on Bayesian predictive probability framework. The predictive probability is defined as the probability of observing a positive result by the end of the trial based on the cumulative information in the current stage. A higher (lower) predictive probability means that the new treatment is (is not) likely to be efficacious by the end of the study, given the current data. Given p0, p, the prior distribution of response rate, and the cohort size for interim monitoring, they search for the maximum sample size Nmax, threshold values θ L , θT , θU (usually choose 1.0) for the predictive probability, to yield a design satisfying the type I and type II error rates constraints simultaneously. The smallest Nmax that controls both the type I and type II error rates at the nominal level is the one to choose. Similar to the Thall et al. approach, the predictive probability design is computationally intensive. OTHER PHASE II DESIGNS Bivariate Designs In some circumstances it is necessary to consider the use of multiple endpoints for determining sample size and stopping guidelines instead of a single endpoint.

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For example, in studies of high dose chemotherapy it may be hypothesized that a more intensive therapy will induce more responders; however, more intensive therapy may also cause more unacceptable adverse events. An increase in the adverse event rate may be acceptable as long as the toxicities are not too severe or are reversible as long as the higher dose results in an increased response rate. Similar in structure to Simon’s two-stage designs, Bryant et al. (9) proposed methods that integrate toxicity monitoring into phase II designs. The trials are terminated at the initial stage if either the number of observed responses is inadequate or the number of observed toxicities is excessive. If there are both a sufficient number of responses and an acceptable toxicity rate in the second stage, then the new agent is considered to be worthy of further study. The design parameters are determined by minimizing the expected accrual for treatments with unacceptable rates of response or toxicity. Conaway et al. (10) proposed similar designs. A new therapy may be acceptable if it can achieve a substantially greater response rate but with acceptable toxicity, or it has a slightly lower response rate but with substantially less toxicity. Conaway et al. (11) proposed two-stage designs to allow for early termination of the study if the new therapy is not sufficiently promising, and to allow for trade-offs between improvements in activity and increases in toxicity. Thall et al. (12, 13) took the Bayesian approach that allows for monitoring each endpoint on a patient by patient basis in the trial. They define for each endpoint in the trial a monitoring boundary based on prespecified targets for an improvement in efficacy and an unacceptable increase in the rate of adverse events. Thall et al. (14, 15) proposed another approach for multi-endpoint designs by quantifying a two-dimensional treatment effect parameter for efficacy and safety. Most bivariate designs require both endpoints to be binary, which may not always be the situation (i.e., when it is important to distinguish between grades of toxicities). Also, the specified trade-off between the response and toxicity may be viewed as too subjective. Phase II Design Using Time-to-Event Endpoints All the designs discussed so far focused on a binary(s) endpoint, tumor response, as a measure of efficacy. However, in situations when tumor response is difficult or not possible to evaluate, or when the agents studied are not expected to reduce tumor response (i.e., cytostatic agents), response rate may not be an appropriate endpoint to evaluate the efficacy of the new

agent. Endpoints that incorporate information of a time-to-event outcome such as disease free survival (DFS), progression free survival (PFS), or overall survival (OS) may be reasonable choices in this situation. The use of PFS estimates at a fixed time point, instead of the response rate as the primary endpoint, was proposed by Van Glabbeke et al (16). Mick et al. (17) proposed a methodology for evaluating time-toprogression as the primary endpoint in a single-stage design with each patient’s previous response time serving as their own control. If it is reasonable to assume that the time-to-event outcome, say survival, follows a known distribution (such as the exponential) then under specified assumptions for accrual and minimum follow-up time, sample size can be estimated from a one-sample test for median survival rates (Lawless [18]). Owzar et al. (19) recommended dichotomizing the time-to-event outcome at a clinically relevant landmark over the parametric and nonparametric methods for the design of phase II cancer studies. Randomized Designs The effects from single-arm designs are greatly influenced by entry criteria, the definition of response, patient selection bias, and so on. Randomized designs are considered when the aim of a phase II trial is to evaluate two or more regimens concurrently, adequate historical control data are not available, or to select which of the several new agents should be studied further. The standard single-arm paradigm may be inefficient in these settings. The randomized selection design (Simon et al. [20, 21]; Liu et al. [22]; Scher et al. [23]) allows multiple single-arm trials to be conducted at the same time with the same entry criteria. Typically patients are randomized to two or more experimental arms without a control arm. A test for activity using standard criteria for single-arm studies is conducted for each arm, and there is a selection rule for selecting the best arm(s) for further investigation. The advantages of this type of design include decreasing the patient selection bias, and the ability to ensure uniform evaluation criteria in each arm. The weakness is that the probability of selecting the better arm decreases if the difference between the arms decreases and if the number of arms increases (Gray et al. [24]). In a randomized control design, patients are randomly assigned to an experimental or control arm and the results obtained from the two arms are compared. Comparison to a control arm is useful when there is little prior information of the expected response rate in a population, or when endpoints such as time to progression (TTP) and PFS, which are influenced by


patient selection, are used. This design format is typical in the phase III setting, but has been proposed in phase II setting as well (Herson et al. [25]; Thall et al. [26]; Korn et al. [27]). Compared with a standard single-arm phase II study, a potential weakness of this type of design often includes the need for a second larger study before moving on to a phase III study. The randomized discontinuation design (Stadler et al. [28]; Rosner et al. [29]; Ratain et al. [30]) was proposed to select a more homogeneous group of patients thus to provide smaller bias. All patients are initially treated with the experimental drug. Patients free of progression at some defined time point are randomized between continuing the experimental drug and receiving a placebo. The effectiveness of the design depends on the accuracy of identifying true treatment responders who are clearly benefiting on the basis of disease stabilization versus rapid progression. It may overestimate the treatment benefit and may require a larger sample size compared with other phase II designs. As pointed out by Freidlin et al. (31), with careful planning, it can be useful in some settings in the early development of targeted agents where a reliable assay to select patients expressing the target is not available.

DISCUSSION There are many design methods available for phase II clinical trials. It is important to note that the study objectives should define the choice of design to use and not the reverse. If the main objective is to assess clinical response rates, then one can choose from the classic design methods. Whereas, for a more complicated study, it is recommended that a novel design method be used. This requires more interaction between the investigators and statisticians, and results in higher quality research. The methods discussed here are only some of the methods available in the literature, but we hope it will serve as a good starting point when considering the design of phase II trials. Appropriate trial design remains an expanding field of research.

References 1. Rietschel P, Wolchok JD, Krown S, et al. Phase II study of extended-dose Temozolomide in patients with melanoma. J Clin Oncol. 2008;26:2299–2304. 2. Gehan EA. The determination of number of patients in a follow-up trial of a new chemotherapeutic agent. J Chronic Dis. 1961;13:346–353. 3. Schultz JR, Nichol FR, Elfring GL, Weed SD. Multiple stage procedures for drug screening. Biometrics. 1973;29:293–300. 4. Fleming TR. One-sample multiple testing procedures for phase II clinical trials. Biometrics. 1982;38:143–151.

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5. Simon R. Optimal two-stage designs for phase II clinical trials. Control Clin Trials. 1989;10:1–10. 6. Herson J. Predictive probability early termination plans for phase II clinical trials. Biometrics. 1979;35:775–783. 7. Thall PF, Simon R. Practical Bayesian guidelines for phase IIB clinical trials. Biometrics. 1994;50:337–349. 8. Lee JJ, Liu DD. A predictive probability design for phase II cancer clinical trials. Clin Trials. 2008;5:93–106. 9. Bryant J, Day R. Incorporating toxicity considerations into the design of two-stage phase II clinical trials. Biometrics. 1995;51:1372–1383. 10. Conaway MR, Petroni GR. Bivariate sequential designs for phase II trials. Biometrics. 1995;51:656–664. 11. Conaway MR, Petroni GR. Designs for phase II trials allowing for trade-off between response and toxicity. Biometrics. 1996;52:1375–1386. 12. Thall PF, Simon RM, Estey EH. Bayesian sequential monitoring designs for single-arm clinical trials with multiple outcomes. Stat Med. 1995;14:357–379. 13. Thall PF, Simon RM, Estey EH. New statistical strategy for monitoring safety and efficacy in single-arm clinical trials. J Clin Oncol. 1996;14:296–303. 14. Thall PF, Cheng SC. Treatment comparisons based on twodimensional safety and efficacy alternatives in oncology trials. Biometrics. 1999;55:746–753. 15. Thall PF, Cheng SC. Optimal two-stage designs for clinical trials based on safety and efficacy. Stat Med. 2001;20: 1023–1032. 16. Van Glabbeke M, Verweij J, Judson I, et al. Progression-free rate as the principal endpoint for phase II trials in soft-tissue sarcomas. Eur J Cancer. 2002;38:543–549. 17. Mick R, Crowley JJ, Carroll RJ. Phase II clinical trial design for noncytotoxic anticancer agents for which time to disease progression is the primary endpoint. Control Clin Trials. 2000;21:343–359. 18. Lawless J. Statistical Models and Methods for Lifetime Data. Chap. 3. Wiley & Sons, 1982. 19. Owzar K, Jung S. Designing phase II studies in cancer with timeto-event endpoints. Clin Trials. 2008;5: 209–221. 20. Simon R, Wittes RE, Ellenberg SS. Randomized phase II clinical trials. Cancer Treat Rep. 1985;69:1375–1381. 21. Simon RM, Stienberg SM, Hamilton M, et al. Clinical trial designs for the early clinical development of therapeutic cancer vaccines. J Clin Oncol. 2001;19:1848–1854. 22. Liu PY, Dahlberg S, Crowley J. Selection designs for pilot studies based on survival endpoints. Biometrics. 1993;49: 391–398. 23. Scher HI, Heller G. Picking the winners in a sea of plenty. Clin Cancer Res. 2002;8:400–404. 24. Gray R, Manola J, Saxman S, et al. Phase II clinical trials: methods in translational research from the genitourinary committee at the eastern cooperative oncology group. Clin Cancer Res. 2006;12:1966–1969. 25. Herson J, Carter SK. Calibrated phase II clinical trials in oncology. Stat Med. 1986;5:441–447. 26. Thall PF, Simon R. Incorporating historical control data in planning phase II clinical trials. Stat Med. 1990;9:215–228. 27. Korn EL, Arbuck SG, Pluda JM, et al. Clinical trial designs for cytostatic agents: are new approaches needed? J Clin Oncol. 2001;19:265–272. 28. Stadler WM, Ratain MJ. Development of target-based antineoplastic agents. Investigational New Drug. 2000;18: 7–16. 29. Rosner GL, Stadler W, Ratain MJ. Randomized discontinuation design: application to cytostatic antineoplastic agents. J Clin Oncol. 2002;20:4478–4484. 30. Ratain MJ, Eisen T, Stadler WM, et al. Phase II placebocontrolled randomized discontinuation trial of Sorafenib in patients with metastatic renal cell carcinoma. J Clin Oncol. 2006;24: 2505–2511. 31. Freidlin B, Simon R. Evaluation of randomized discontinuation design. J Clin Oncol. 2005;23:5094–5098.


Randomization

10 Susan Groshen

In the perfect and ideal clinical trial that is designed to compare the effects of two or more interventions, all study participants would be alike and would be the same as all other patients in the target population to which the conclusions will be applied. In this perfect and ideal trial, each intervention or treatment would be delivered to the assigned patients in exactly the same way, the effect would be the same on each patient, and this effect would be measured correctly and exactly. Thus, the only difference from patient to patient would be the real effect of the intervention. In contrast in a typical oncology trial, patients are heterogeneous, treatment cannot be delivered in a completely reproducible fashion, and the effect of the treatment is not the same from patient to patient. Furthermore, not all factors affecting the outcome can be adequately controlled and the measurement of effect is often difficult. To deal with the realities of clinical research, as in all scientific research, the design of an experiment involves control, randomization, and replication (1). The objective is to have patients in the treatment groups to be similar on average in all important aspects, except for the treatment assigned; and in this way, observed differences can be attributed to treatment. The first step in designing a clinical trial is to identify sources of patient heterogeneity, treatment variability, and outcome assessment measurement error. To the extent possible, all known sources of heterogeneity and variability should be controlled or limited. For

those sources of heterogeneity that are either not known or that cannot be directly controlled, randomization is used to reduce and limit the impact of nonrandom differences between patients in the treatment arms. Replication is the mechanism by which the impact of random error or noise is controlled; sample sizes are calculated to ensure that there is a high probability of detecting a specified signal-to-noise ratio. Issues of control and replication are discussed in other chapters of this book; the purpose of this chapter is to discuss the application of randomization and to describe some common and effective randomization procedures. In this chapter, the terms treatment and intervention will be used interchangeably, as will patient and study participant. In addition, we will use the phrases “assign each patient to a treatment arm” and “assign a treatment to each study participant” to mean the same thing. Bias Bias is the term used to describe systematic error, in contrast to random error. In the context of clinical trials, serious bias arises when systematic (nonrandom) differences in patient characteristics are confused with treatment effect. An illustration of bias (i.e., systematic error) can be found in a registry of patients with muscle invasive transitional cell bladder cancer who

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have undergone radical cystectomy (2). In this series, many patients with involved lymph nodes were treated off protocol with adjuvant chemotherapy. When the survival of patients who received chemotherapy was compared to the survival of patients who did not receive chemotherapy (all with involved lymph nodes), the patients who received adjuvant chemotherapy had inferior survival. This was not because chemotherapy had a detrimental effect on survival, but rather because patients with other unfavorable features (not all easily specified) were more likely to receive adjuvant chemotherapy. Because patients were not randomly assigned to receive chemotherapy, the assignment to chemotherapy depended on factors that are not all readily apparent. The resulting comparison of survival between the chemotherapy and nonchemotherapy groups was biased because the differences observed were not due to the chemotherapy, but rather to patient or disease characteristics. There are other potential sources of bias, such as those that occur during the assessment of response to treatment, that cannot be reduced or eliminated by randomization. Many trials are single-blind (when the patient does not know which treatment he/she is receiving) or double-blind (when the patient and the individual evaluating the response, often the physician, do not know the treatment assignment) in order to reduce potential bias in outcome measurement. Thus even with randomization, there is still a need to exercise as much control as possible in the design of the trial in order to reduce bias. This systematic error, this bias, cannot be overcome or corrected by increasing the sample size. If the cause of the bias can be identified, then possibly the error can be corrected with careful analysis. But this is often not possible, and often the study investigators may not be aware of the bias. And this, finally, is the problem with bias—it is usually undetected. One can never say that there is no bias in a trial; one can only say that every precaution was taken to reduce the possibility of bias.

done by ensuring that each patient is as likely to be assigned a particular treatment as any other patient. That is, patient with feature X is just as likely as patient with feature Y, to be assigned to a specific treatment. With randomization correctly executed, there is no systematic preference to assigning one treatment over the other, based either on patient characteristics or physician preference or (often) subconscious opinion. Randomization does not guarantee that at every stage, the treatment arms will be exactly equally balanced in terms of known and unknown patient characteristics that could impact the patient response to treatment; the randomization process will decrease the chances that this deleterious imbalance occurs with small numbers of patients, and has a high chance of achieving balance with large numbers of patients. Thus randomization has the feature that in the long run, the patients in one treatment group will be similar (on average) to patients in another treatment group. It is this long run balance that will permit the conclusion that observed differences between treatment groups are due to treatment. Finally, randomization can confer robustness to the statistical analysis. That is, the set of all possible randomization outcomes provides a context by which to evaluate the observed treatment differences; often this will suggest that standard (parametric) tests can be used to calculate p-values to summarize the strength of the evidence refuting the null hypothesis. From a practical perspective, the randomization scheme should be easy to use, it should be unpredictable, and it should be truly random; wherever possible it should assign individual patients and not groups of patients. For example, a scheme that assigns patients registered on Mondays to one treatment and those registered on Wednesdays to another treatment will invite bias. Patients making appointments for Monday may differ from those making appointments for Wednesday (e.g., traveling from out of town and/or attempting to

Goals of Randomization For all the considerations discussed above, trials using randomization to assign treatment to study participants are regarded as the most credible type of investigation for generating experimental data to compare the benefit and safety of therapies for the treatment of cancer. Randomization, properly implemented achieves two goals. The first goal is to assign a treatment to each study participant. The second, equally important goal of randomization is to reduce the chance of bias (as summarized in Table 10.1). This is

TABLE 10.1

Goals of Randomization. 1. 2.

3.

4.

Assign treatment to study participants. Ensure that each study participant is as likely to receive each of the trial treatments as any other participant. Ensure that in the long run, on average, the treatment groups are similar in terms of the participants’ characteristics. Justify statistical analysis of results.

10 RANDOMIZATION

minimize work days missed); this is sometimes called experimental bias. In addition, this form of assignment allows physician preference to intervene; this is sometimes called selection bias. Other forms of systematic assignment of patients to one treatment or another are also vulnerable to (often subconscious) selection bias of patients. Hence, a treatment assignment scheme that assigns patients with a medical record number ending in an even digit to one treatment and assigns all other patients to a second treatment invites patient selection bias if the scheme becomes known. In 1930, the Department of Health for Scotland undertook a nutritional experiment in the schools of Lanarkshire (3). Ten thousand children received free milk for 4 months and 10,000 children were observed as controls. Assignment was done by ballot or alphabetically, although adjustment by the head teacher at each school was allowed if it appeared that “an undue proportion of well fed or ill nourished children” was assigned to one group. At the end of the experiment, it was observed that the control group weighed more than the milk group. Analysis of baseline heights and weights demonstrated that children assigned to the milk group had (on average) weighed less both at the start of the experiment and at the end, although they had gained more weight during the 4 months of the study. This example demonstrates the bias in personal selection of subjects for treatment or control; randomization is needed to ensure that assignment is free of bias and to maximize the likelihood that the comparison groups are similar on average.

Deciding Whether to Randomize Two issues must be considered in deciding whether a planned trial should include randomization. One consideration is scientific: can the potential problem of bias be managed without randomization? The other consideration is ethical: will it be ethical to randomly assign one of several treatments to a study participant, rather than use medical opinion? There are disadvantages and logistic difficulties to using randomization to assign treatment. These are not usually insurmountable, but they can complicate the conduct of the trial. Explaining the choice of treatments and the randomization process to patients is difficult to do well; many patients, as well as their physicians, would rather that the treating physician select the treatment option thought or believed to be best for the patient. As a result, some patients will not enroll in a trial that involves randomization, resulting in slower accrual and longer-lasting studies. To mitigate the reluctance of patients to enroll in a trial with a not-

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yet-determined treatment, Zelen introduced the randomized consent design (4). In this design, the treatment assignment is obtained (by randomization) prior to the consent process, and the patient is presented with the study knowing the treatment assignment. The goal of this design was to increase participation; however, if a sizable portion of patients decline participation after randomization, then interpretation of the results will be more complicated and possibly compromised (see the discussion on intention-to-treat later in the chapter). As a result, this approach has not been used often. Acceptance of randomization remains an obstacle for many patients and physicians. Randomized trials are recognized as the most scientifically sound mechanism for establishing which of two or more treatments is superior. This is especially true in oncology clinical research, where phase III trials aim to establish standard of care options, and therefore require a control group or comparator in order to compare the new therapeutic regimen to a standard of care option (i.e., the control). In this setting, historical controls or concurrent nonrandomized controls are almost always unacceptable due to vulnerability to substantial bias. Because for most cancers, therapies now exist that offer palliation if not cure, differences needed to establish superiority or equivalence will be incremental and not large; treatment effect differences may not be substantially larger than differences resulting from changes in referral patterns or changes in ancillary care procedures. In addition, supportive care and diagnostic procedures have evolved substantially over the last decades and continue to do so. Hence, the use of historical series is (at best) problematic and often invalid; concurrent, nonrandomized controls are usually subject to even more bias than historical controls. The onus will be on the study investigators to convincingly demonstrate to the skeptical reviewer that differences observed between the new treatment and the historical control group (or nonrandomized concurrent control group) are not due to bias. This will be (at best) difficult. Thus, definitive trials that aim to change standard or care, or convincingly compare two or more standard treatment options, should incorporate concurrent controls and randomization. While the scientific justification for randomly assigning treatment to patients is rarely disputed, the ethical justification is not straightforward. The term clinical equipoise provides the ethical justification for clinical trials with randomization. Clinical equipoise is satisfied when there is “genuine uncertainty in the expert medical community . . . about the preferred treatment” (5). This occurs when there are no clear and definitive data supporting or refuting the hypothesis of benefit or superiority and individual clinicians and

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clinical investigators are either unsure or have conflicting opinions regarding the new treatment. It is not the purpose of this chapter to review all the ethical arguments for and against using randomization. However, these issues must be carefully discussed before initiating a randomized trial, by evaluating the potential harm to study participants and weighing the risks and benefits of undertaking the study to study participants and to society. Much has been written on this subject (6–8).

PRACTICAL CONSIDERATIONS There are many practical and logistic issues that must be resolved in order to correctly and effectively incorporate randomization into a clinical trial. To begin with, randomization should not be done by involved investigators; a separate office (possibly with telephone randomization) should be used. A document should be created and saved for each randomization, indicating the time and date of the randomization, the individual initiating the randomization, the pertinent patient information, and the randomization outcome. Timing of Randomization Randomization should not take place until after the patient is confirmed to be eligible and has signed the informed consent. In addition, randomization should be delayed until the latest practical moment before the intervention is to begin (see Durrleman and Simon for a discussion of this issue (9)). In general it is reasonable for the intervention to begin within 1 or 2 weeks of randomization. This narrow window reduces the likelihood of intervening events to cause the patient to discontinue trial participation or fail to adhere to the treatment schedule as required. Noncompliance and dropouts can introduce bias and may complicate the final interpretation of the results. In 1991, the Children’s Cancer Group began a trial for the treatment of children with high-risk neuroblastoma (10). All patients were treated with the same initial regimen of chemotherapy. Those without disease progression at the completion of the initial therapy were then randomly assigned to receive either three cycles of intensive chemotherapy, or to receive myeloablative therapy with autologous bone marrow rescue. Patients who completed the second phase of cytotoxic therapy without disease progression were then randomized to no further treatment or 6 months of 13-cis-retinoic acid. In this study, both randomizations were delayed until patients were ready to begin the next phase of treatment. Had randomization taken place prior to the start of the initial chemotherapy with

all 539 eligible patients randomized, then only 379 of the 539 patients would have begun the three cycles of intensive chemotherapy or myeloablative therapy, with 160 patients not receiving the randomly assigned treatment. Only 258 of the initial 539, who were still free of progression after all cytotoxic therapy, would have been able to comply with the second randomization. By delaying the randomization until patients were ready to begin the treatment, the investigators clearly defined the appropriate comparison groups and eliminated (upfront) those patients who would not contribute meaningful data to the planned comparisons. Intention-to-Treat Analysis In a randomized trial, an intention-to-treat (ITT) analysis is one in which all eligible patients who are randomized are included in the analysis of the results and are classified according to the treatment assigned, regardless of whether this was the treatment actually received. The ITT analysis should be the primary analysis in a randomized trial designed to show the superiority of one regimen. The Children’s Cancer Group, by delaying the randomization, was able to focus the ITT analysis on those patients who were still able to benefit from the second phase or third phase of therapy. When some of the randomized patients fail to receive the assigned treatment, there is no correct way to include or exclude these patients in the analysis. Nor is there a way to correctly adjust the statistical analysis. This is because the outcome of these patients, had they received the assigned treatment, is unknown; furthermore, it is often the case that these patients are different from those who received the assigned treatment, but it is not usually known how they differ. In the presence of noncompliance, any analysis will lead to a biased estimate of the true treatment difference. The ITT analysis is advocated in the case of trials designed to establish a difference (that one treatment arm is superior) because the bias, to the degree that it exists, will lead to an underestimate of the magnitude of the treatment difference. With other approaches, such as the as treated analysis or inclusion of only the compliant patients, the impact of the bias is not known: the resulting observed treatment difference could be either too large or too small. The ITT analysis is known to be a conservative strategy, and if the ITT results indicate a clear difference (i.e., statistically significant at the planned level), then the results can be considered conclusive. If the ITT analysis does not result in a clear (statistically significant) difference, but the as treated or another analysis does, then interpretation of the results will be inconclusive.

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Balanced versus Unbalanced Randomization

randomization in a clinical trial (13). In this section, several methods will be described; simple randomization and the permuted block design are by far the more commonly used methods, but the others can be very useful in selected situations and are presented briefly to indicate the range of randomization options. For illustration purposes, it will be assumed that there will be two treatments (A and B), and that a balanced allocation will be used (i.e., 50% of patients will be assigned treatment A and 50% will be assigned treatment B). However, each of the methods presented can easily be adapted to three or more treatment arms and to unequal allocation. Computer programs exist and are easy to create in order to generate the random treatment assignments. For many of the randomization designs, a list can be prepared in advance, although this is not feasible for adaptive or minimization randomization schemes.

Generally, it is most efficient to assign the same number of patients to each of the treatment groups under comparison in the clinical trial. That is, for the same total number of patients, the power will be greatest when the treatment arms have equal numbers. On some occasions, however, it may be appropriate to assign more patients to one treatment arm. In some trials, more patients will be required for secondary objectives; additional studies may be performed on patients assigned to one of the treatments. In randomized pilot studies, there may be a need to obtain more data on the new or experimental arm, while sufficient experience exists for the arm that represents standard of care. On occasion, one treatment may be substantially more expensive than the other. Sometimes, there might be more variability associated with one arm compared to the other, and in this case it would be more efficient to randomize more patients to the treatment with greater variability. In a related situation, Sposto and Krailo discuss unequal allocation when the primary outcome is time to an event and fewer events are expected in one arm (11). It is not appropriate, however, to design a study with fixed unequal allocation that will assign fewer patients to an arm that is thought to be inferior; this would suggest that clinical equipoise is not satisfied.

Simple Randomization (Completely Randomized Design) Simple randomization is equivalent to flipping a coin or rolling a die every time a patient is randomized. If the coin is fair (i.e., the probability of getting a head is equal to getting a tail), Pr{head} = Pr{tail} = 1/2, then the randomization is balanced. With this form of randomization, the outcome (heads or tails) does not depend on the number of previously randomized patients or their characteristics. That is, if the last five flips all resulted in heads, the probability that the next flip is a head is still 1/2. Although computers can quickly create a list of treatment assignments using simple randomization, Table 10.2 of random digits is used here to illustrate the process.

METHODS OF RANDOMIZATION There are many ways to randomly assign treatments to patients (12). Kalish and Begg provide a comprehensive review of different schemes that are available for

TABLE 10.2

Three Hundred Random Digits.

A B C D E F G H I J K L M N O

1

2

3

4

5

6

7

8

9

10

11

12

13

14

15

16

17

18

5 0 1 6 7 4 5 9 0 3 6 2 6 7 7

6 8 3 1 9 8 6 1 9 9 8 8 6 6 8

1 7 3 2 5 8 0 3 8 5 3 6 5 3 7

0 4 8 8 0 3 7 0 9 8 5 8 8 5 0

6 5 1 7 1 5 4 2 0 4 7 6 8 2 1

2 6 9 8 8 0 4 7 9 2 6 6 5 0 2

1 2 2 1 2 2 5 1 2 3 7 1 1 7 3

8 5 5 6 4 2 2 7 5 2 6 9 6 5 9

7 3 8 8 7 3 3 3 0 2 2 6 0 7 4

9 9 4 4 5 4 1 9 0 1 1 9 2 8 0

4 2 9 5 4 9 8 4 5 7 5 2 6 3 7

2 4 5 8 7 8 3 9 7 4 9 6 1 4 4

4 6 1 0 7 8 5 3 7 4 9 5 0 1 8

5 5 3 6 2 8 0 8 6 9 4 7 4 7 6

2 8 6 9 9 0 9 4 1 9 5 5 8 5 9

8 7 7 3 8 4 5 7 7 0 0 9 1 1 4

2 5 1 5 2 1 2 7 6 4 7 8 0 6 1

1 7 7 4 1 7 2 0 9 3 7 1 1 0 3

19 20 0 3 4 1 9 9 9 3 4 4 9 9 6 3 7

4 4 1 6 0 9 4 7 1 8 0 7 3 9 3

78


Biased Coin Randomization (14)

Table 10-2 contains 300 random digits; that is, each of the 10 digits (0 to 9) appears in about 10% of the entries in the table, in no order. If even digits (0, 2, 4, 6, 8) are used to correspond to treatment A and odd digits (1, 3, 5, 7, 9) correspond to treatment B, then Table 10-2 can be used to assign treatment to 15 patients. First it is necessary to identify a starting point in Table 10-2, and then read a sequence of 15 digits originating at the starting point. Selection of the starting point should also be done randomly. If the starting point is column 8, row A, and 15 digits down column 8 are read, then the assignment of treatment to 15 patients is given in Figure 10.1. In this case, treatment A was assigned to 8 patients and treatment B was assigned to 7 patients. The features of simple randomization can be summarized as:

This randomization scheme begins with simple randomization: for each new patient, the probability of being assigned treatment A is 1/2. If the difference in the number of patients assigned to A minus the number of patients assigned to B differs by some prespecified number, D (or -D) then the probability of assignment to A is changed. If D more patients have been assigned to A, then the probability of assigning A to the next patient is changed to “p” where p < 1/2. If D more patients have been assigned to treatment B, then the probability of assigning A to the next patient is changed to “1-p” where 1-p > 1/2. In general, p = 1/3 is reasonable; smaller values will result in assignments that are too predictable. The choice of D should depend on the total number of patients planned and the timing of interim analyses. The features of the biased coin randomization can be summarized as:

· · · ·

completely unpredictable (eliminates selection bias) eliminates experimental bias in the short run, can lead to serious imbalance rarely exactly balanced, but balance is good in the long run · procedure is flexible and easy · resulting statistical analysis is easy

· · · ·

largely unpredictable (eliminates selection bias) eliminates experimental bias better balance in the short run rarely exactly balanced, but close to exactly balanced; balance is good in the long run · flexible but a little more complicated to set up · resulting statistical analysis can be somewhat more complicated

Replacement Randomization It is possible that the randomization scheme described above will produce substantial imbalance in the early part of the trial. A simple fix to avoid this problem is to specify a requirement in advance. For example, a possible requirement might be: in the first 40 patients, the difference in the number of patients assigned to receive A versus assigned to receive B should not exceed 8. The randomization list is prepared in advance; if the list does not fulfill the requirement, the entire list is rejected and another randomization list is prepared. As long as the entire randomization list is replaced and as long as this is done before the first patient is enrolled, this is one reasonable way to overcome the potential short-run imbalance of the simple randomization scheme.

Permuted Block Design The permuted block design is one of the most commonly used methods for randomly assigning treatment to patients. The advantage of this method is that it forces exact balance at very regular intervals during the accrual phase of the trial, and not just at the end. To construct a randomization list using the permuted block design, the first step is to select the block size which will be a multiple of K (2K, 3K, 4K, etc.), where K is the number of treatments in the trial. To illustrate this scheme for K = 2, block sizes of 6 = 3 × 2 will be used. In a block of 6 units (or patients), there

Pt. Seq.

1

2

3

4

5

6

7

8

9

10

11

12

13

14

15

Random Digit

8

5

5

6

4

2

2

7

5

2

6

9

6

5

9

Treatment

A

B

B

A

A

A

A

B

B

A

A

B

A

B

B

FIGURE 10.1 Assignment of treatment to 15 patients using simple randomization.

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10 RANDOMIZATION

are 20 different orders that the 2 treatments can be assigned with each treatment assigned to 3 patients (e.g., AAABBB or ABBAAB or ABABBA, etc.). There are two ways to construct the randomization list. The first way is to randomly select blocks from a list of all 20 possible blocks; this is probably the fastest method. The second way is to randomly assign treatment to patients in groups of 6. This second method is demonstrated below in Figure 10.2 for 30 patients, which will require 5 blocks with 6 patients per block. Taking random digits from Table 10.2, using row F for Block #1, row G for Block #2, through row J for Block #5, six digits will be read across each row, beginning in column 11. As before, even digits will correspond to treatment A and odd digits to treatment B. At the end of each block, both treatment arms have exactly the same number of patients assigned. This short run balance, and ease of implementation, are very favorable characteristics of this method of randomization. However, this randomization scheme is not as unpredictable as simple randomization, replacement randomization, or the biased coin method since, if the block size is known, one could anticipate the assignment of the last patient in the block. For this reason, a variation on this randomization scheme is frequently adopted in which the block sizes are also varied. For example, with K = 2 treatments, the block size of 4, 6, or 8 could be randomly chosen. The features of the permuted block design randomization can be summarized as:

· closely balanced at end (exactly balanced if total number of patients is a multiple of the block size) · flexible but a little more complicated to set up · resulting statistical analysis is easy Adaptive Randomization for Treatment Assignment In this class of treatment assignment schemes, the probability that the next patient is assigned to treatment A or B will depend on the outcomes of the previously randomized and treated patients. It is for this reason that the methods are called adaptive, since the probability of assigning treatment A will be adapted to the data observed to date. Zelen first described the adaptive “play the winner” strategy in 1969 (15) for clinical trials; the statistical properties of these designs are reviewed by Simon (16). These randomization schemes are somewhat controversial with proponents citing that in the long run, patients are more likely to be assigned to the regimen with the better outcome. Concerns regarding these designs involve practical and ethical issues. From a practical perspective, these designs can lead to early imbalance in treatment assignment which may compromise the ability to perform an adequate comparison; that is, they are not efficient in terms of estimating the difference between treatments. In addition, for many of these designs, the treatment assignments can become nearly completely predictable quickly, exposing the trial to selection bias. Those that cite ethical concerns state that if clinical equipoise is not maintained, then it is not appropriate to assign even a few patients to the inferior

· largely unpredictable, except at end of each block (can vary block size to decrease predictability) · eliminates experimental bias · very good balance in the short run

Pt. Seq

1

2

3

4

Random #

9

8

8

8

Treatment

B

A A

A

5

B

6

B

7

8

9

10

8

3

5

0

9

A

B

B

A

B

Block 4 Pt. Seq

5

7

7

Treatment

B

B

B

A

11 12

A

Block 5

19 20 21 22 23 24

Random #

Block 3

Block 2

Block 1

A

A

25 26 27 28

29 30

7

4

4

9

9

B

A

A

B

B

A

FIGURE 10.2 Assignment of treatment to 30 patients using the permuted block design.

13

14

15 16

17

4

9

3

8

4

A

B

B

A

A

18

B

Note: The numbers in the shaded cells with the strikethrough lines indicate that those treatment assignments were required to ensure that 3 patients were assigned to A and to B.

80


treatment; that is, one should be prepared to use balanced randomization or not randomize at all. Trials of neonatal extracorporeal membrane oxygenation (ECMO) used adaptive randomization and provide a fascinating discussion of the issues involved with randomization (in general) and adaptive randomization (in particular) (6). On a practical note, adaptive designs may not be feasible in many oncology trials which involve time-to-event outcomes such as survival or time-to-recurrence that is not expected for several years. In general, these designs are not used in oncology clinical trials (16).

STRATIFICATION AND RANDOMIZATION In most clinical trials, there are patient and tumor characteristics which are known to influence the response to treatment. Randomization can be expected (in the long run) to yield treatment arms that are balanced in terms of these characteristics. Furthermore, statistical methods exist to adjust for these factors at the time of the final analysis. However, this may not be sufficient: interim analyses are planned, studies are terminated early, and sometimes “in the long run” implies a very large trial. Hence, it is often desirable to control the randomization process to increase balance across the treatment arms in terms of these patient characteristics. This is done by stratification. While often successfully used, stratification can lead to loss of power and efficiency if not done properly. The patient and tumor characteristics used for stratification should be available at the time of randomization and based on objective data, free of interpretation. Care should be taken not to over stratify and create too many subsets of patients with very small numbers. The statistical analyses should incorporate the stratification that was used at the time of randomization. Byron Brown (17) summarized the rationale for stratification with “. . . there is much to be gained in persuasiveness or credibility by presentation of data that show the numbers of patients assigned to the several treatments to be closely balanced with regard to the variables commonly felt to be related to the course of the disease and the response to treatment. No amount of poststratification and covariance analysis, particularly if the techniques used are complex in nature, will be as convincing as the demonstration that the groups were balanced in the beginning. . . .” Simple Stratification Simple stratification works well when there are one or two patient or disease characteristics and these can each be grouped into two to four categories. The

stratification variables will be cross-classified to create strata. For example, if there are two stratification variables, one with two classes (e.g., good performance status vs. poor performance status) and one with three classes (e.g., no prior chemotherapy, prior chemotherapy but no taxanes, prior treatment with a taxane), then there will be a total of 6 = 2 × 3 strata. Within each stratum, a separate randomization list (on paper or in the computer) will be created to assign treatment to the patients in that stratum. Operationally, each patient is first classified into one stratum and then randomized within that stratum. In the neuroblastoma example, at the first randomization, patients were stratified according to whether they had metastatic disease or not; at the second randomization, patients were stratified according to the treatment they had been assigned at the first randomization (10). A permuted block design was used for random treatment assignment within each stratum. The replacement, biased coin, and permuted block randomization schemes can all be easily adapted to this type of stratification. Balance (or near balance) should be achieved within each stratum. While there are no set rules for the maximum number of strata permitted, practical considerations would suggest that there should be on average at least 10 patients per stratum, but at least 20 is better. Adaptive Randomization to Minimize Imbalance: Minimization Randomization Stratified randomization (as described above) is attractive for its simplicity and general effectiveness within each stratum. However, this approach can lead to troublesome imbalance across strata during the early stages of a trial. Consider the hypothetical example in Figure 10-3 where there are 3 strata, 2 treatments, and within each stratum, a permuted block design with block size 4 used. In Figure 10.3, after the first 10 patients, with 6, 3, and 1 patients in stratum 1, 2, and 3, respectively, 3 patients have been assigned A and 7 have been assigned B. Within each stratum, there is only slight imbalance, but the cumulative effect is more pronounced. This example highlights the potential problem with simple stratification when there are many strata, especially early in the trial. In 1974, Taves published a method to minimize imbalance over the entire study, and within each of the subgroups, dictated by the individual patient characteristics (i.e., each stratification variable) separately, but not within the strata formed by cross-classifying all the stratification variables (18). His method was deterministic and did not incorporate randomization. Pocock and Simon independently and subsequently published an extension of the Taves method which

81

10 RANDOMIZATION

Stratum 1 B A B A B B A* A

Stratum 2 A B B A* A B A B

Gender

Stratum 3 B B* A A B A B A

A: B:

Example of cumulative imbalance across strata with simple stratification

included randomization (19). Their method is illustrated with the following simplified example. Suppose that 50 patients have already been enrolled and randomized in a trial with 2 treatments and 3 stratification variables giving rise to 12 strata, as displayed in Figure 10.4(A). The minimization method considers the stratification variables separately, as displayed in Figure 10.4(B). Figure 10.4(C) shows the impact on the treatment assignment balance when the next patient, a male with low performance status and no prior therapy, is assigned to either A or B. In Figure 10.4(C), the imbalance for each level of each stratification variable is calculated (bottom line). A summary of the imbalance is then calculated either by squaring the differences and adding them or by taking the absolute values and adding them. Squaring the differences will put greater weight on large differences; taking the absolute value tends to weight all the differences more equally. Using the squared differences, if the next patient is assigned to A, the summary of imbalance becomes (−3)2 + (−1)2 + (0)2 = 10; if this next patient is instead assigned to B, the summary of imbalance becomes (−5)2 + (−3)2 + (−2)2 = 38. Assigning this patient to receive treatment A will minimize the imbalance at this point. The Taves

Mid. 9 9

Low 11 12

procedure would assign the treatment A; the PocockSimon approach would randomly assign treatment with probability p* > 1/2 for treatment A. Variations exist: stratification variables can be weighted and a term can be added that accounts for the overall balance across all strata. With available computer programs, both the simple stratification and the minimization randomization are easy to implement. Simple stratification achieves balance within each of the strata, while minimization is more likely to achieve balance across the stratification variables and overall.

SUMMARY Randomized clinical trials remain the most robust and credible method for generating data to formally compare treatments for patients with cancer. In planning the technical aspects of the randomization during the design of the clinical trial, the stratification variables and the randomization scheme must be selected. Choice of the number of stratification variables represents a trade-off between controlling as much as possible and striving for simplicity to the extent that it is possible. Criteria for using a stratification variable in the design should include the strength of the association between the variable and the outcome measures, its known ability to affect the response to treatment, and the reliability with which it can be measured prior to start of treatment. If there are only 1 or 2 stratification variables and the final study size will be Gender: Male

Females No

Performance Status High 5 4

Yes 6 4

Balance of treatment assignments within each of the stratification variables—number of patients assigned to A or B.

FIGURE 10.3

H M L 2 4 5 1 2 7

Prior Therapy No 19 21

Female 15 11

FIGURE 10.4(B)

*Treatment assignments for future patients. Only 6, 3, and 1 patients randomized in strata 1, 2, 3, respectively.

Gender: Males No Yes Pror Therapy: H M L Performance Status* H M L 1 1 0 Assigned to A: 2 2 4 1 2 0 Assigned to B: 2 4 5

Male 10 14

Yes H M L 0 2 2 0 1 0

*H = High (KPS = 100), M = Middle (KPS = 90–80), L = Low (KPS = 70–60)

FIGURE 10.4(A) Status of trial with 3 stratification variables after 50 patients—number of patients assigned to treatments A and B within each of the 12 strata

New Patient Assigned to: New # in A: New # in B: Difference: A –B

Prior Therapy: No

Performance Status: Low

A

B

A

B

A

B

11 14

10 15

20 21

19 22

12 12

11 13

–3

–5

–1

–3

–0

–2

FIGURE 10.4(C) Impact of assigning the next patient (male, no prior therapy, and low performance status) to A or B.

82


large, then simple stratification will be sufficient. In this case, randomization using the permuted block design is both easy and effective. If there are many stratification variables or if there will be early interim analysis or the study is relatively small, then minimization randomization will be more effective for achieving shortterm balance across the stratification variables. All three elements of trial design are essential: control, randomization, and replication. Properly designing and executing the randomization is critical for the success of the trial.

References 1. Fisher RA. The Design of Experiments. Edinburgh: Oliver and Boyd. 1935. 2. Stein JP, Stein JP, Lieskovsky G, et al. Radical cystectomy in the treatment of invasive bladder cancer: long-term results in 1,054 patients. J Clin Oncol. 2001;19:666–675. 3. Student. The Lanarkshire milk experiment. Biometrika. 1931;23:398–406. 4. Zelen M. Randomized consent designs for clinical trials: an update. Stat Med. 1990;9:645–656. 5. Freedman B. Equipoise and the ethics of clinical research. N Engl J Med. 1987;317:141–145. 6. Royall RM. Ethics and statistics in randomized clinical trials. Statist Sci. 1991;6:52–88.

7. Temple R, Ellenberg SS. Placebo-controlled trials and activecontrolled trials in the evaluation of new treatments. Part 1: ethical and scientific issues. Ann Intern Med. 2000;133:456–464. 8. Ellenberg SS, Temple R. Placebo-controlled trials and activecontrolled trials in the evaluation of new treatments. Part 2: practical issues and specific cases. Ann Intern Med. 2000;133:464–470. 9. Durrleman S, Simon R. When to randomize? J Clin Oncol. 1991;9:116–122. 10. Matthay KK, Villablanca JG, Seeger RC, et al. Treatment of high-risk neuroblastoma with intensive chemotherapy, radiotherapy, autologous bone marrow transplantation, and 13-cisretinoic acid. N Engl J Med. 1999;341:1165–1173. 11. Sposto R, Krailo MD. Use of unequal allocation in survival trials. Stat Med. 1987;6:119–125. 12. Pocock SJ. Allocation of patients to treatment in clinical trials. Biometrics. 1979;35:183–197. 13. Kalish LA, Begg CB. Treatment allocation methods in clinical trials: a review. Stat Med. 1985;4:129–144. 14. Efron B. Forcing a sequential experiment to be balanced. Biometrika. 1971;58:403–417. 15. Zelen M. Play the winner rule and the controlled clinical trial. J Amer Stat Assoc. 1969;64:131–146. 16. Simon R. Adaptive treatment assignment methods and clinical trials. Biometrics. 1977;33:743–749. 17. Brown BW Jr. Statistical controversies in the design of clinical trials—some personal views. Cont Clin Trials. 1980;1:13–27. 18. Taves DR. Minimization: a new method of assigning patients to treatment and control groups. Clin Pharmacol Ther. 1974;15:443–453. 19. Pocock SJ, Simon R. Sequential treatment assignment with balancing for prognostic factors in the controlled clinical trial. Biometrics. 1975;31:103–115.

11

Design of Phase III Clinical Trials

Stephen L. George

A phase III clinical trial is a randomized prospective controlled study designed to compare the efficacy of two or more regimens for the treatment of a specified disease or medical condition. These trials employ accepted scientific principles of good experimental design including, among other things, specification of eligibility criteria (types of patients appropriate for study), explicit statements of primary and secondary objectives, details of the treatment regimens to be compared, and statistical considerations (hypotheses tested, sample size and expected duration of the trial, statistical procedures, interim analysis plans, and related topics). A properly designed and executed phase III clinical trial provides the best available scientific evidence on the relative efficacy of the treatments being studied and the most reliable information for evidence-based medicine. The adoption and wide-spread use of phase III clinical trials in the latter half of the twentieth century and the early twenty-first century represents one of the more important contributions to the practice of scientific medicine during the last 60 years. The statistical aspects of the design, conduct, and analysis of clinical trials have been extensively studied during this time and there are now many textbooks (including this one) covering this material at various levels of statistical sophistication. Other chapters in the current text cover important topics in the design and analysis of phase III clinical trials, including selecting endpoints, randomization and stratification, interim analysis, adaptive

design, and Bayesian designs. The focus in the present chapter will be on determining the required sample size (number of patients or number of events) and duration of a phase III clinical trial in many commonly encountered practical situations (1, 2). In an attempt to provide maximum clarity for the underlying concepts, free of unnecessary complexity, the situations considered are elementary ones. References to papers covering more complex scenarios are provided where appropriate.

CANONICAL SAMPLE SIZE FORMULAE Testing Hypotheses The sample size considerations in this chapter are derived from a statistical hypothesis testing perspective, usually involving a test of a null hypothesis, H0, against an alternative hypothesis, H1. In the simplest case, suppose the outcome variable (endpoint) of a clinical trial comparing two treatments is some continuous random variable, X, and we wish to compare the mean value of X for the two treatments. The usual null and alternative hypotheses in this case may be expressed as H0 : m1 = m2 vs. H1 : m1 ≠ m2

(Eqn. 11-1),

where mi is the mean for treatment i (= 1, 2). 83

84


The statistical inference in this case is a decision rule, based on the observed values of X in the two treatment groups, for deciding between the two competing hypotheses. In the standard statistical approach, the trial is designed to control the rates for the two possible types of error: · Type I—rejecting H0 (in favor of H1) when H0 is true · Type II—not rejecting H0 when H1 is true The error rates for these two types of errors are conventionally denoted by a and b, respectively, with the power of the test defined as 1—b, the complement of the type II error rate. That is, the power of the test is the probability of correctly rejecting H0 when H1 is true. The usual approach to determining the required sample size is to set the type I error rate a at some acceptable level, often 0.05 or 0.01, and then to find the minimum required sample size to achieve a power of at least some specified value 1—b, often 0.80 or 0.90, at some specified alternative value (i.e., some particular value in the alternative hypothesis space when H1 is a composite space). Suppose (for simplicity) that the endpoint Xi in the ith treatment group (i = 1, 2) has a normal statistical distribution with mean mi and known variance s 2, denoted, Xi ∼ N (mi, s 2), and we plan to enter an equal number of patients, n, on each treatment. In this case, the usual test statistic, Z, used in testing H0 versus H1 may be written as: Z=

n X1 – X2 2 σ

(Eqn. 11-2),

– where Xi is the sample mean of X in the ith treatment group. The hypothesis H0 : m1 = m2 is rejected in favor of H1 : m1 ≠ m2 if Z ≥ za /2, where zx is the upper 100 (1 – x) percentile of the standard normal distribution. To determine the required common sample size, we need to solve the following equation for n:

(

)

P Z ≥ zα /2 δ ≥ 1− β

(Eqn. 11-3),

where P(X⎪Y) denotes the probability of X given Y and d = m1– m2 ≠ 0 is some prespecified value in the alternative hypothesis space. That is, we want the power to be at least 1—b when the true difference between the means is d. Some straight-forward algebraic manipulation of (11-3) yields the following sample size formula for the approximate number of patients, n, required on each treatment group:

(

⎡ 2σ 2 z + z α /2 β n=⎢ ⎢ δ2 ⎢⎣

)

2

⎤ ⎥ ⎥ ⎥⎦

(Eqn. 11-4),

where [x] denotes the smallest integer ≥ x. Equation (11-4) is the canonical sample size formula for the hypothesis-testing scenario considered here. If the variances in the two groups are not equal, the formula becomes

)(

(

⎡ σ 2+ σ 2 z + z 1 α /2 β 2 n=⎢ ⎢ δ2 ⎢⎣

)

2

⎤ ⎥ (Eqn. 11-5), ⎥ ⎥⎦

These formulae can also be used to determine the power for a given sample size by solving for zb when n is given. Although the above formulae are strictly applicable only for the assumptions underlying their derivation, they are approximately correct in many other settings. Often the test statistic or some simple transformation of the test statistic is approximately normally distributed for reasonably large sample sizes. Also, the formulae nicely illustrate several general points about the required sample size in phase III clinical trials: ·The required sample size n increases as the variance s 2 increases. The size of s 2 is a feature of the population under study. ·The required sample size n increases as the error rates decrease. For example, an increase in power (decrease in b) requires an increase in sample size. ·The required sample size n increases as the detectable effect size d decreases. The required sample size calculated from (11-4) for some common values of a and b as a function of the standardized effect size, d /s, is given in Table 11.1. If the variances are not equal, the standardized effect size _ 2 2 may be defined as d /s where σ = σ 1 + σ 2 2 .

(

)

For example, if a = 0.05, 1—b = 0.90, and d /s = 0.50, the number of patients required on each treatment is n = 85 and the total required sample size is 2n = 170. Unknown Variances If we relax the assumption that sigma is known, the appropriate test statistic is not (11-2) but the t-statistic T=

n X1 – X2 2 s

(Eqn. 11-6),

where s is the pooled estimate of the common, but unknown, standard deviation s. In this case, a good approximation (3) to the required sample size n* is: ⎡ z2 ⎤ n* = n + ⎢ α / 2 ⎥ ⎣ 4 ⎦

(Eqn. 11-7),

85

11 DESIGN OF PHASE III CLINICAL TRIALS

TABLE 11.1

Required Sample Size on Each Treatment Arm to Test H0 : μ1 = μ2 vs. H0 : μ1 ≠ μ2. d/s a

1—b

0.10

0.25

0.50

0.75

1.00

0.01

0.80 0.90

2336 2976

374 477

94 120

42 53

24 30

0.05

0.80 0.90

1570 2102

252 337

63 85

28 38

16 22

where, as before, [x] is the smallest integer ≥ x and n is defined in (11.4). Although n* is always greater than n, the difference is not large. For example, n*− n = 1 when a = 0.05 and n*− n = 2 when a = 0.01. Thus, in most practical situations, the required number of patients when the variance is unknown is only one or two more patients per treatment group than the number required when the variance is known. Unequal Sample Sizes

More Than Two Treatment Groups

To allow for different sample sizes ni on the two arms, (11-4) may be written as: ⎛ 1 1⎞ ⎜⎝ n + n ⎟⎠ 1 2

−1

(

⎡σ 2 z + z α /2 β =⎢ ⎢ δ2 ⎢⎣

)

2

⎤ ⎥ ⎥ ⎥⎦

(Eqn. 11-8),

Any pair of values (n1, n2) that satisfy (11-8) will work. However, the required total sample size, n1 + n2, is minimized when n1 = n2. If we randomize patients to the two treatments in the ratio r:1, for some r > 1, rather than in the usual balanced 1:1 ratio (i.e., n1 = rn2), the required sample sizes are ⎡r +1 ⎤ n1 = ⎢ n⎥ ⎣ 2 ⎦ ⎡r +1 ⎤ n2 = ⎢ n⎥ ⎣ 2r ⎦

(Eqn. 11-9),

and the required total sample size is approximately n1 + n2 = 2n ( r + 1) 4r

entered on treatment 1 than on treatment 2), we would require (2n)(9/8) patients, a 12.5% increase over the 2n required in the balanced case. However, there may be other reasons for an unbalanced randomization (such as wanting more patients on one of the treatments to increase the precision of the estimated outcomes for that treatment). If so, an unbalanced allocation might be preferable to a balanced one even with the resultant sample size inflation factor.

2

(Eqn. 11-10), where n is determined by (11-4). The inflation factor of (r +1)2/4r in the required total number of patients is the primary reason that balanced randomization is generally preferred to unbalanced randomization. For example, if r = 2 (i.e., twice as many patients are

In many phase III clinical trials there are k > 2 treatments (4). Unfortunately, in order to control the error rates in this setting, the above sample size formulae cannot be extended simply by entering n patients on each of the k treatments (a total of kn patients). More than kn patients are required. Three important types of phase III clinical trials with more than two arms are considered below. Testing Equality Among k Treatment Arms. In the simplest type of k arm clinical trial, there is a randomization to one of the k arms and the primary objective is to test a global null hypothesis. With an obvious extension of the notation in (11-1), the hypotheses being tested are H0 : m1 = m2 = . . . = mk vs. H1 : mi ≠ mj for some i ≠ j (Eqn. 11-11), If s 2 is known then the test statistic, analogous to (11-2) in the two-sample case, is k

X2 =

2

n ∑ ( xi − x ) i =1

σ2

(Eqn. 11-12),

where x–i is the sample mean in the ith treatment arm and x– is the overall sample mean. The hypothesis

86


H0 is rejected in favor of H1 if X2 > χ2a,k–1, the upper 100(1–α) percentile of a chi-square distribution with k – 1 degrees of freedom. To determine the required sample size we need to solve an equation similar in form to (11-3):

(

)

P X 2 ≥ χ α2,k−1 Δ ≥ 1− β k

2

where Δ = ∑ ( μi − μ )

σ 2 and μ =

i =1

(Eqn. 11-13), 1 k ∑ μ. When Δ ≠ 0, k i =1 i

X2 has a noncentral chi-square distribution with noncentrality parameter nΔ and no closed-form solution for n exists analogous to (11-4). However, solutions are easily available either from computer programs or from tables of the noncentral chi-square distribution. As noted previously, the required sample size per treatment arm for k > 2 will be larger than that required when k = 2, increasing as a function of k. Table 11.2 gives the multiplication factor required for k = 3, 4, 5, and 6 when all means other than the largest and smallest are midway between the largest and smallest. For example, the number of patients required for k = 3 is 1.23n per arm (i.e., 23% more patients on each arm) when a = 0.05, 1—b = 0.80. For k = 4, 5, and 6, the requirements are 1.39n, 1.52n, and 1.63n, respectively. Although Table 11.2 represents the worst-case scenario, the one with the least favorable configuration of mean values between the two extreme means, there is generally a high price to be paid for increasing the number of treatment arms on a clinical trial. Two or More Experimental Arms and a Control Arm. Another common k-arm design results when we wish to compare k—1 new or experimental arms with a standard or control with randomization of each patient to one of the k arms. In this case, there are k—1 comparisons of interest. If we let arm 1 be

TABLE 11.2

Multiplication Factors for the Number of Patients Required for k > 2 Treatment Arms. k = NUMBER

OF

ARMS

a

1—b

3

4

5

6

0.01

0.80 0.90

1.19 1.17

1.32 1.29

1.43 1.39

1.53 1.48

0.05

0.80 0.90

1.23 1.20

1.39 1.35

1.52 1.47

1.63 1.57

* the control arm and define δ = min { μi − μ1 } , then a i = 2,...,k

simple, albeit conservative, approach in this setting is to apply equation (11-4), substituting α/2(k—1) for α/2 and δ* for δ. This approach ensures that a sufficient number of patients are entered to achieve the requisite power for all comparisons, allowing for the multiple comparisons. A better approach, requiring fewer patients, is to adjust for the inherent multiplicity using a less conservative multiple comparison procedure (5–7). Jung et al. (8) use a Dunnett-type procedure for this purpose in the setting of survival distributions (see the “Comparing Survival Distributions” section later in the chapter for more details on survival endpoints). Factorial Designs. In a factorial design there are several factors (or treatment types in a clinical trial) to be tested in combination (9). In the simplest type of factorial design, referred to as a 2 × 2 design, there are two treatments, each given at one of two levels. For example, the treatments might refer to particular therapeutic agents (say, A and B) and the two levels might refer to the presence or absence of a specified regimen for the agent. The four possible combined treatment regimens are: A and B absent; A absent and B present; A present and B absent; A and B both present. In general, with two factors we could define a R × C factorial design, with R levels of one factor and C levels of the other factor, although in clinical applications it would be rare for R or C to exceed three. A 2 × 2 design is by far the most common factorial design. In a factorial design it is possible to compare the effects of each of the treatments separately as well as to estimate the interaction effects among treatments. An interaction implies that the effect of a treatment depends on the presence or absence of another treatment. To make this point clear, consider a 2 × 2 design with two treatments either present or absent. The mean values in each of the four possible treatment combinations are given in Table 11.3. The treatment effects in Table 11.3 are the differences in mean values when the treatment is given compared to when it is not given. The quantity ε measures the interaction between treatments. If e = 0, the effect of treatment A is δ0 regardless of whether treatment B is given or not, and the effect of treatment B is δ1 regardless of whether treatment A is given or not. If e > 0 (a positive interaction), there is synergy between the treatments; the effect of each treatment is increased in the presence of the other. If e < 0 (a negative interaction), there is antagonism between the treatments; the effect of each treatment is decreased by the presence of the other.

87


TABLE 11.3

Treatment Effects in a 2 × 2 Factorial Clinical Trial. TREATMENT B ABSENT Treatment A

absent present Treatment A effect

m m + d0 d0

If one can assume that ε ≅ 0, then a factorial design is highly efficient. One can design the trial to test the effect of treatment A or B without consideration of the other treatment and get “two trials for the price of one.” If nA and nB are the required sample sizes for the two individual trials, then a single factorial trial of size n = max {nA,nB} will achieve at least the same power for each individual treatment comparison as two trials with total sample size of nA + nB. In fact, the power will be greater than required for the comparison with the smaller required ni. However, if e < 0, the power of the individual comparisons may be considerably less than that when there is no interaction. To allow for this possibility, one option is to assume a slight negative interaction in the design of the trial and increase the size of the trial accordingly. Unfortunately, if one wishes to test formally for interactions, the required size of the trial will be quite large, counteracting one of the primary advantages of a factorial design (9). It would also be possible to consider the trial as if it were a trial with k = RC treatments and use the approach outlined above for k treatment arms. However, this approach also can result in a very large trial, and in any case does not take advantage of the unique structure of the factorial design. Factorial clinical trials can play an important role in evaluating therapies, especially in a setting where treatments are likely to be used in combination in practice. Indeed, such trials are essential to learn about the joint effects of treatments. However, if the treatment combinations are not likely to be used in practice, factorial designs are not appropriate because of the potential for negative interactions and the resultant loss of power.

COMPARING SUCCESS RATES If the assumptions underlying the above derivations are approximately correct, the resultant sample size formulae can in principle be used directly. However, it is often necessary to consider modifications of the approach

PRESENT

TREATMENT B EFFECT

m + d1 m + d0 + d1 + e d0 + e

d1 d1 + e

when designing actual clinical trials. One such situation requiring special consideration concerns trials in which the outcome measure is a binary variable. Such trials are considered in this section. Another important special case, trials in which the outcome measure is time to some event, is considered in the subsequent section. In some phase III clinical trials the outcome on each patient is assessed as a success or a failure and the objective of the trial is to compare the success rates of the treatments under study. For example, a success might be defined as achieving a particular clinical status, perhaps achieving an objective response or remaining disease free for some specified time period. In these cases, the observed success rate on treatment i will have a binomial distribution with a mean pi, the unknown probability of success, and variance pi (1 – pi)/n. The hypotheses equivalent to those in (11-1) are H0 : p1 = p2 vs. H1 : p1 = p2

(Eqn. 11-14),

Even though the binomial distribution is not a normal distribution, for large samples a normal approximation is reasonable and one may use equation (11-5) directly with δ = p1 – p2 and si2 = pi(1 – pi). That is,

)(

(

⎡ p (1 − p ) + p (1 − p ) z + z 1 1 2 2 α /2 β n= ⎢ 2 ⎢ ( p1 − p2 ) ⎢⎣

)

2

⎤ ⎥. ⎥ ⎥⎦

(Eqn. 11-15), A second approach is to apply the variance-stabilizing transformation arcsin x/ n to the observed proportion of success x/n. This approach yields 2 ⎡ zα / 2 + zβ ⎢ n= ⎢ ⎢⎣ 2 arcsin p1 − arcsin p2

(

(

)

⎤ ⎥ . 2 ⎥ ⎥⎦

)

(Eqn. 11-16),

88


TABLE 11.4

Number of Patients on Each of Two Treatments to Compare Success Rates (a = 0.05, 1–b = 0.80). d = p2—p1 P1

0.10 0.20 0.30 0.40 0.50

0.05

0.10

0.15

0.20

0.25

0.30

0.35

0.40

725 1134 1416 1573 1605

219 313 376 408 408

113 151 176 186 183

72 91 103 107 103

51 62 68 70 66

38 45 49 49 45

30 35 37 36 33

25 28 29 28 25

A third approach, also based on the approximate normality of the sample proportions (10), yields

(

) ⎤⎥⎥.

⎡ ⎢ zα /2 2 p (1 − p ) + zβ p1 (1 − p1 ) + p2 (1 − p2 ) n= ⎢ 2 ( p1 − p2 ) ⎢ ⎣

2

⎥ ⎦

(Eqn. 11-17), Haseman (11) showed that all of the above formulae result in values that are too small when the actual test being used is an exact test. Casagrande et al. (12) provided an improved formula in this setting and Fleiss et al (13) showed that a better approximation results from a simple modification to (11-17):

(

⎡ ⎢ zα /2 2 p (1 − p ) + zβ n= ⎢ ⎢ ⎢⎣

(

) )

(

p 1− p + p 1− p 1 1 2 2 2 p −p 1 2

(

))

2

⎤ +2 p −p ⎥ 1 2 ⎥. ⎥ ⎥⎦

(Eqn. 11-18), Table 11.4 gives the required sample sizes based on (11-18) for some selected cases. COMPARING SURVIVAL DISTRIBUTIONS When the hypotheses being tested involve time-toevent, or survival data, several complications arise. The most important one is that the observations may be incomplete (or censored) at the time of the analysis, either because of dropouts or loss to follow-up or because the event in question (recurrence, progression, death, etc.) has not yet occurred for some patients. Censoring affects both the number of patients that need to be enrolled on trial as well as the required duration of trial. For reasons that will be made clearer below, the number of events, rather than the number of patients on trial, is the key quantity to be determined

and the duration of the trial must be planned to achieve the desired number of events. There has been a vast literature on the design of clinical trials with survival as the major endpoint (8, 14–32), mostly at a more advanced statistical level than the level of this chapter. Required Number of Events For a random variable T representing the time to some event, the key probability functions are the survival distribution or probability of surviving beyond time t, S(t) = P(T > t), and the hazard function l(t) = f(t)/S(t), where f(t) is the probability density function. The hazard function may be thought of as the instantaneous failure rate at time t for a patient who has survived up to time t. Each function may be derived from the other if the other is fully specified. The simplest type of survival distribution is the exponential distribution, for which the hazard function is constant over time. George and Desu (15) provided a framework for determining both the required number of events and the required duration of study when the survival distributions under study follow an exponential distribution. In this case, the survival function, the probability of surviving beyond time t, is Si(t) = exp(–lit) in the ith treatment group, where li is the hazard rate in the ith treatment group. The hypotheses being tested, analogous to those in equation (11-1), are H0 : l1 = l2 vs. H1 : l1 ≠ l2

(Eqn. 11-19),

Or equivalently, in terms of the hazard ratio, Δ = l1/l2, H0 : Δ = 1 vs. H1 : Δ ≠ 1

(Eqn. 11-20),

89


ards are not. The log-rank statistic is available as the score statistic from the maximum likelihood fitting of the proportional hazards model (33). Schoenfeld (34) showed that the method of George and Desu approximates the power of the log-rank test as long as the assumption of proportional hazards holds. Rubinstein et al. (19) show via simulations that trial lengths calculated using the statistic of George and Desu and assuming exponential failure times give valid powers for the log-rank test when the underlying survival distributions are exponential and Weibull. Under a proportional hazards model, the distribution of the log of ˆ can be approximated by the estimated hazard ratio, Δ, the same approximate normal distribution as in the exponential case. Thus, although the exponential distribution represents a simple special case of proportional hazards, the required number of events defined by (11-21) applies directly to the more general proportional hazards case. A more precise formulation is given in two papers by Lakatos (24, 26). If the proportional hazards assumption is not correct, the sample size formulae based on the assumption can produce erroneous results (27).

The ratio of the estimated hazard rates has an F distribution, so the required sample size can in principle be derived by solving an equation analogous to (11-3) for the F distribution. But these equations do not yield a closed form expression for the sample size. A much simpler and quite accurate approximation for a reasonably large number of events is based on the approximate normality of the natural logarithm of the estimated hazard rate in each treatment group: 1 ⎞ ⎛ ln λˆ i ~ N ⎜ ln λi , ⎟ , ⎝ di⎠ where di is the number of observed events. Thus, the distribution of the log of the estimated hazard ratio can be approximated as: ⎛ λˆ ⎞ ⎛ ⎛ 1 1 ⎞⎞ ln Δˆ = ln ⎜ 1 ⎟ ~ N ⎜ ln Δ, ⎜ + ⎟ ⎟ . ˆ ⎝ d1 d2 ⎠ ⎠ ⎝ ⎝ λ2 ⎠ The required number of events on the ith treatment group, di, can be obtained from the following equation, directly analogous to equation (11-8):

(

−1 ⎡ z +z ⎛ 1 1⎞ β ⎢ α /2 + = 2 ⎜⎝ d d ⎟⎠ ⎢ 1 2 ⎢⎣ ( ln Δ 0 )

)

2

⎤ ⎥ . (Eqn. 11-21), ⎥ ⎦⎥

Required Duration of Study The sample size approximation formula (11-21) and the tabulated values in Table 11.5 are for the required number of events at the time of the final analysis. In order to observe the requisite number of events, it is necessary to follow patients over time until the events are observed. At one extreme, we could enter exactly 2d patients on trial and follow all until failure; at the other extreme, we could enter patients continuously until 2d patients have failed. The former approach will require the maximum duration of study; the latter will yield the shortest duration of study but at the cost of entering the maximum number of patients. Either approach will yield the requisite power. However, some intermediate approach would be more appropriate in most cases.

where Δ0 ≠ 1 is the specified hazard ratio for which we desire the power of the test to be1 – b . Table 11.5 gives values of d1 + d2, for some common design situations. Here we assume d1 ≅ d2, yielding the minimum required total number of events. If the di are expected to differ substantially, an inflation factor similar to equation (11-10) should be applied. The exponential assumption is not as restrictive as it might first appear since the calculations are approximately correct for the general proportional hazards case, in which the ratio of the hazard functions is independent of time, even though the individual haz-

TABLE 11.5

Total Number of Events Required to Compare Two Survival Distributions. ∇ a

1—a

0.90

0.85

0.01

0.80 0.90

4209 5362

1769 2254

0.05

0.80 0.90

2829 3787

1189 1592

0.80

= HAZARD RATIO

0.75

0.70

0.65

0.60

0.55

0.50

939 1196

565 720

368 468

252 321

180 229

131 167

98 124

631 845

380 508

247 331

170 227

121 162

98 118

66 88

90


We assume that we will enter a sufficient number of patients (at least 2d) on study during some accrual period, each randomized to one of the two treatment arms. After this accrual period, there will be an additional follow-up period (T, T + τ) for all patients who have not failed before T in order to obtain the necessary 2d events. It is shown in George and Desu (15) that the expected number of events at time t, denoted D(t), can be written as E ⎡⎣ D ( t ) ⎤⎦ =

γt* p1 ( t ) + p2 ( t ) 2

(

)

(Eqn. 11-22),

where g is the average accrual rate, t* = min(T, t), and −1 pi ( t ) = 1 − ( λi t *) exp ( – λi t ) ⎡⎣exp ( λi t *) − 1⎤⎦ . To find

an appropriate accrual period T and follow-up time τ, we may require that the expected number of events at time T + τ be at least 2d: E ⎡⎣ D (T + τ ) ⎤⎦ ≥ 2d

(Eqn. 11-23),

As noted earlier, the minimum T + τ occurs when τ = 0 (i.e., enter patients continuously until the end of the study with no follow-up), although this also results in the maximum number of patients entered on study. Table 11.6 gives the minimum length of study for the case τ = 0 for some selected cases. In this table, the median time in the control group is assumed to be one year. For other median times, the times in Table 11.6 must be adjusted accordingly by multiplying by the correct control median. If the control median is in fact t years, the required length of study is t times the values given in Table 11.6. In addition, it should be noted that the time at which the required number of deaths occurs is a random variable. The above formulation in terms of the expected number of deaths yields a result that can provide a rough

approximation to the required length of study. Even if the assumptions are exactly correct, the actual time at which the required number of events will occur on any given clinical trial might be considerably different from the expected time. If we enter only the minimum number of patients (2d), we will require the maximum length of study T + τ. Indeed, the expected time until the last patient fails (this is required if we enter only the minimal number of patients) will be approximately 2d/g + (1.44M1 ln (2d))/Δ, where M1 is the median in the control group. For example, if we consider a = 0.05, 1—b = 0.80, and Δ = 0.70 then from Table 11.5, 2d = 248. If the entry rate (g ) is 200 per year, then from Table 11.6, the required minimum duration of study is 2.3 years when M1 = 1. However, if we enter only 248 patients and follow all of them to failure, the expected length of study would be approximately 12.6 years (T ≅ 1.2 years, t ≅ 11.4 years). Obviously, some kind of compromise approach is needed between the two extremes discussed above. Although we desire a reasonably short time until the study is completed, it is also desirable to keep the excess number of patients entered over the required number of events to be relatively small. One practical approach is to define a maximum proportionate increase, p, in patients entered over the required number of events, set T = 2d(1 + p)/g, and solve (Eqn. 11-23) for t. The duration of study calculations in this section, in contrast to the required number of events calculations in the previous section, depend heavily on the exponential assumption. For example, if the hazard rates decrease sharply over time, additional follow-up will not yield sufficient numbers of events as quickly as in the constant hazard rate model. In designing actual clinical trials, it is important to make realistic assumptions about the anticipated hazard rates. The

TABLE 11.6

Required Minimum Duration of Study (In Years) to Compare Two Survival Distributions (a = 0.05, b = 0.80). g = ANNUAL ACCRUAL RATE

∇ 0.90 0.80 0.70 0.60 0.50

2d

50

100

150

200

250

2830 632 248 122 68

58 14 6.2 3.6 2.3

30 7.6 3.7 2.2 1.5

20 5.5 2.8 1.7 1.2

16 4.4 2.3 1.4 1.0

13 3.8 2.0 1.3 0.9


general approaches outlined here still apply, but the details will differ.

CONCLUDING COMMENTS The situations considered in this chapter are simple ones, in order to emphasize the basic design principles without introducing unnecessary complexity. In practice, the complexity cannot be ignored. Some of the topics that will need consideration include interim analyses, missing data, dropouts, crossovers, timedependent losses, nonproportional hazards, unequal and informative censoring, composite endpoints, stratification and covariates, equivalence testing, nonuniform accrual, and others. Several chapters in this book are devoted in part to one or more of these topics. Also, many of these topics are covered in the papers by Ahnn et al. (29) and Barthel et al. (32) on complex clinical trials. In addition, there have been several books devoted exclusively to sample size determination for clinical trials, including those by Shuster (35), Desu (36), Machin (37), and Chow, et al (38). These books and the other references cited in the “References” section can be consulted for more extensive coverage of the design of complex clinical trials.

References 1. Donner A. Approaches to sample size estimation in the design of clinical trials—a review. Stat Med. 1984;3(3):199–214. 2. George SL. The required size and length of a clinical trial. In: Buyse ME, Staquet MJ, Sylvester RJ, ed. Cancer Clinical Trials. Oxford: Oxford University Press; 1984:287–310. 3. Guenther WC. Sample size formulas for normal theory t tests. Am Stat. 1981;35(4):243–244. 4. George SL. Multiple treatment trials. In: Crowley J, ed. Handbook of Statistics in Clinical Oncology. New York: Marcel Dekker; 2001:149–160. 5. Bang H, Jung SH, George SL. Sample size calculation for simulation-based multiple-testing procedures. J Biopharm Stat. 2005;15(6):957–967. 6. Cook RJ, Farewell VT. Multiplicity considerations in the design and analysis of clinical trials. J Roy Stat Soc(A). 1996;159(1): 93–110. 7. Bauer P. Multiple testing in clinical trials. Stat Med. 1991;10(6): 871–889. 8. Jung SH, Kim C, Chow SC. Sample size calculation for the logrank tests for multi-arm trials with a control. J Kor Stat Soc. 2008;37(1):11–22. 9. Peterson B, George SL. Sample size requirements and length of study for testing interaction in a 2 × k factorial design when time-to-failure is the outcome. Contr Clin Trials. 1993;14(6): 511–522. 10. Fleiss JL. Statistical Methods for Rates and Proportions. 2nd ed. New York: Wiley & Sons; 1981. 11. Haseman JK. Exact sample sizes for use with the Fisher-Irwin test for 2 × 2 tables. Biometrics. 1978;34(1):106–109. 12. Casagrande JT, Pike MC, Smith PG. An improved approximate formula for calculating sample sizes for comparing two binomial distributions. Biometrics. 1978;34(3):483–486.

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13. Fleiss JL, Tytun A, Ury HK. A simple approximation for calculating sample sizes for comparing independent proportions. Biometrics. 1980;36:343–346. 14. Pasternack BS, Gilbert HS. Planning the duration of long-term survival time studies designed for accrual by cohorts. J Chronic Dis. 1971;24(11):681–700. 15. George SL, Desu MM. Planning the size and duration of a clinical trial studying the time to some critical event. J Chron Dis. 1974;27(1):15–24. 16. Peto R, Pike MC, Armitage P, et al. Design and analysis of randomized clinical trials requiring prolonged observation of each patient. I. introduction and design. Br J Cancer. 1976;34(6): 585–612. 17. Peto R, Pike MC, Armitage P, et al. Design and analysis of randomized clinical trials requiring prolonged observation of each patient. II. analysis and examples. Br J Cancer. 1977;35(1):1–39. 18. Bernstein D, Lagakos SW. Sample size and power determination for stratified clinical trials. J Statist Comput Simul. 1978;8: 65–73. 19. Rubinstein LV, Gail MH, Santner TJ. Planning the duration of a comparative clinical trial with loss to follow-up and a period of continued observation. J Chron Dis. 1981;34:469–479. 20. Freedman LS. Tables of the number of patients required in clinical trials using the log-rank test. Stat Med. 1982;1(2):121–129. 21. Makuch RW, Simon RM. Sample size requirements for comparing time-to-failure among k treatment groups. J Chron Dis. 1982;35(11):861–867. 22. Schoenfeld DA. Sample-size formula for the proportionalhazards regression model. Biometrics. 1983;39(2):499–503. 23. Palta M, Amini SB. Consideration of covariates and stratification in sample size determination for survival time studies. J Chron Dis. 1985;38(9):801–809. 24. Lakatos E. Sample size determination in clinical trials with timedependent rates of losses and noncompliance. Cont Clin Trials. 1986;7(3):189–199. 25. Lachin JM, Foulkes MA. Evaluation of sample size and power for analyses of survival with allowance for nonuniform patient entry, losses to follow-up, noncompliance, and stratification. Biometrics. 1986;42(3):507–519. 26. Lakatos E. Sample sizes based on the log-rank statistic in complex clinical trials. Biometrics. 1988;44:229–241. 27. Lakatos E, Lan KK. A comparison of sample size methods for the log-rank statistic. Stat Med. 1992;11(2):179–191. 28. Ahnn S, Anderson SJ. Sample size determination for comparing more than two survival distributions. Stat Med. 1995;14(20): 2273–2282. 29. Ahnn S, Anderson SJ. Sample size determination in complex clinical trials comparing more than two groups for survival endpoints. Stat Med. 1998;17(21):2525–2534. 30. Jung SH, Hui S. Sample size calculation for rank tests comparing k survival distributions. Lifetime Data Anal. 2002;8(4): 361–373. 31. Halabi S, Singh B. Sample size determination for comparing several survival curves with unequal allocations. Stat Med. 2004;23(11):1793–1815. 32. Barthel FMS, Babiker A, Royston P, Parmar MKB. Evaluation of sample size and power for multi-arm survival trials allowing for non-uniform accrual, non-proportional hazards, loss to follow-up and cross-over. Stat Med. 2006;25(15):2521–2542. 33. Cox DR. Regression models and life tables (with discussion). J Roy Stat Soc(B). 1972;34:187–220. 34. Schoenfeld D. The asymptotic properties of nonparametric tests for comparing survival distributions. Biometrika. 1981;68: 316–319. 35. Shuster J. Practical Handbook of Sample Size Guidelines for Clinical Trials. Boca Raton: Chemical Rubber Company; 1993. 36. Desu MM, Raghavarao D. Sample Size Methodology. San Diego: Academic Press; 1990. 37. Machin D, Campbell MJ. Statistical Tables for the Design of Clinical Trials. 2nd ed. Oxford: Blackwell Scientific; 1996. 38. Chow SC, Shao J, Wang H. Sample Size Calculations in Clinical Research. 2nd ed. New York: Chapman and Hall; 2008.


Multiple Arm Trials

12 Susan Halabi

Many phase III trials evaluate more than one experimental regimen against a standard therapy or a control. Loosely defined, multiple arm trials are trials that have more than two treatment arms. Historically, a common approach has been to estimate the sample size based on a two-arm trial and then increase the sample size by multiplying the number of patients per arm by k, where k is the number of arms. The main problem with using this heuristic approach is that the investigator does not take into account the multiple comparisons that are made. In addition, the power may be insufficient. In this chapter we review the basic principles involved in the design, conduct, and analysis of phase III trials with multiple treatment arms. We begin with a brief review of types of multiple treatment trials, and subsequently describe the factorial design. Next, we present a general discussion of design considerations including the control of type I error rate and sample size estimation. Finally, we provide an overview of the inherent challenges in analyzing data from multiple arms trials.

TYPES OF MULTIPLE ARM TRIALS Perhaps the oldest multiple arm trial was conducted in 1747 on board on the sailing ship Salisbury where sailors were randomized to one of six possible treat-

ments for scurvy: cider, vinegar, elixir vitriol, sea water, nutmeg, or oranges and lemon. Although the sample size was very small (two patients per treatment arm), patients who received oranges and lemon had visible benefit and were able to resume their duties on board. There are several different types of multiple treatment trials, we will discuss the more common types in this chapter. We focus on three arms for simplicity; however, the same principles apply to the situation when the design includes more than three arms. Monotonic Increasing or Decreasing Relationship with a Certain Therapy The primary hypothesis is that there is a monotonic increasing or decreasing relationship between the dose level and endpoint. As an example, a trial in metastatic prostate cancer is conducted where men are randomized to receive hydrocortisone (40 mg per day) plus three different doses of suramin: low (3.192 g/m2), intermediate (5.320 g/m2), or high (7.661 g/m2) (1). The primary hypothesis is that there is a monotonic relationship between the dose level and objective response rate in men with prostate cancer. In other words, men who receive an intermediate dose will have a higher response proportion than men with a low dose, but men in the high dose will have an even higher response proportion than both groups of men.

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BCG followed by maintenance (control) R A N D O M I Z E

BCG +α interferon followed by maintenance (control + drug A)

BCG + Gemcitabine followed by maintenance (control + drug B)

R A N D O M I Z A T I O N

Arm A: Cetuximab + FOLFOX or FOLFIRI (control) Arm B: Bevacizumab + FOLFOX or FOLFIRI (control + drug A) Arm C: Cetuximab + Bevacizumab + FOLFOX or FOLFIRI (control + drug A + drug B)

FIGURE 12.1 First type of multiple arm trials.

FIGURE 12.2 Second type of multiple arm trials.

Control Versus Several Experimental Drugs In these types of trials, specific combinations of experimental therapies are of interest. The first type of these trials compares the control with control plus experimental regimen A and the control with control plus experimental regimen B (Fig. 12.1). In other words, this type of design tests two hypotheses: is experimental drug A efficacious, and is experimental drug B efficacious? Note that the investigator is not interested in comparing control plus experimental drug A versus control plus experimental drug B. To illustrate this point, consider an example where an investigator is interested in testing two hypotheses in patients with bladder cancer where the primary endpoint is complete response rate at 6 months. The first hypothesis is: the proportion of complete response is higher in patients randomized to BCG followed by maintenance (control) versus BCC plus interferon alpha followed by maintenance (experimental regimen). Whereas, the second hypothesis to be compared is: the proportion of complete response is higher among patients randomized to BCG followed by maintenance (control) versus BCC plus gemcitabine followed by maintenance (experimental regimen). The second type of trials are those that test the two hypotheses: is drug A efficacious, and is drug B efficacious over and above A? In an ongoing CALGB/ SWOG trial in patients with untreated advanced or metastatic colorectal cancer with K-ras wild type mutations, an investigator is interested in testing the two primary hypotheses concerning the overall survival endpoint (Fig. 12.2). The primary objectives were: to determine if the addition of bevacizumab and treatment with chemotherapy (FOLFOX or FOLFIRI) prolongs survival of patients treated with chemotherapy plus cetuximab. Furthermore, the investigator is interested in testing whether the addition of bevacizumab and treatment with chemotherapy prolongs survival of patients treated with bevacizumab plus chemotherapy plus cetuximab.

The third type of multiple arm study is a trial which tests hypotheses based on all pair-wise comparisons. For example, in a randomized cancer intervention trial, women were randomized to usual care (control), tailored print (TP), and TP plus telephone counseling (TC) (TP + TC). The major endpoint is proportion with adhered mammography and the investigator was interested in testing the three pair-wise comparisons (2). Factorial Trials The fourth type of multiple arm trials is the factorial design where two factors each at two or more levels are compared. The 2 × 2 factorial experiment is the simplest and one of the most common types of designs where two different treatment regimens are tested simultaneously in the same study without increasing the sample size. This type of design allows certain comparisons to be made that cannot be tested in regular k-arm trials. In some situations, if there is no interaction between the two treatments, two factors can be tested using the same number of subjects. In addition, factorial trials are the only design in which an investigator can test for treatment interaction between two drugs. The literature is rich in examples of factorial designs (3–4). We will consider a 2 × 2 factorial design. Table 12.1 presents the 2 × 2 design with four possible groups: λ11, λ21, λ12, λ22. The elements are ordered such that the last subscript (associated with factor B) changes first and the first subscript (associated with factor A) changes last. λ11 is the hazard rate in patients randomized to receive neither factor A nor factor B, whereas λ22 is the hazard rate in patients randomized to receive both factors A and B. λ2. is the average hazard where treatment A is present pooled over treatment B categories. For instance, in testing for drug A difference, we are interested in comparing the margins

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12 MULTIPLE ARM TRIALS

TABLE 12.1

Example Factorial Design Cells with Two Factors A and B. FACTOR B FACTOR A

NO

YES

POOLED

No Yes Pooled

λ11 λ21 λ.1

λ12 λ22 λ.2

λ1. λ2. λ. .

λ1.− λ2.. On the other hand, in testing drug B difference, we are focused on comparing the margins λ.1− λ.2. Factorial designs are widely used not only in estimating and testing the effect due to the difference in treatment arms, but also in the interaction effects of the treatment arms or interaction of gene by treatment arm. One way to test interaction is to use the proportional hazards model with: λ (t| x1, x2) = λ0(t) exp(b1x1 + b2x2 + b3 x1x2), where λ0(t) is the baseline hazard function, xi = 0 or 1 represents the absence or presence of the factor A or B, respectively. The null hypothesis β3 = 0 indicates that there is no interaction between factors A and B. Testing for interaction is not sufficient as generally the power to detect interaction between two factors is poor. In fact, the main drawback to factorial trials is that interaction between the two treatment groups is common and investigators do not take this into account, and as a result such trials are usually underpowered. We will need to consider the quantity (λ11− λ12)— (λ21– λ22) for a test of interaction between factors A and B. Peterson et al. developed the sample size required in a 2 × 2 factorial design in the presence of interaction when the endpoint is time-to-event (5). Simon et al. proposed inflating the sample size by 30% to account for the possibility that an interaction may be present between the two factors (6).

SELECTION AND SCREENING DESIGN Selection Design Selection or screening designs, whereby patients are randomized to several treatment regimens, are commonly used in clinical trials in oncology (7–9). One of the main objectives in randomized phase II trials is to screen for multiple experimental regimens and choose

the most promising agent to take forward in a phase III setting (7). Investigators often use multiple variations of a new regimen to select the best regimen. Selection trials do not follow the traditional hypothesis testing framework, but are designed to achieve a high probability of selecting the true best treatment correctly. Furthermore, selection trials are usually underpowered, being designed with smaller sample size than a phase III trial. In addition, the type I error rate is not controlled at the design stage, as they do not allow for formal comparisons. Refer to Chapter 9 for more details on these designs. Chen et al. developed a procedure for comparing the experimental arms that differ from the control for the preferred treatment among several experimental arms (10–12). By using the multiple selection procedure, the type I error rate is protected for the preferred treatment.

DESIGN CONSIDERATIONS Type I Error Rate The type I error rate, or the false-positive rate which is often referred to as α, is the probability of rejecting the null hypothesis when the null is true. It is well recognized by investigators that the type I error rate increases with each hypothesis that is tested. The probability of finding one significant result by chance when in fact there are no differences is 1− (1− α)m if we conduct m independent tests of significance, each test with type I error rate of α. Table 12.2 presents the true type I error rate if multiple hypotheses are performed assuming α = 0.05 for each test and independence. For instance, if three hypotheses are tested to evaluate whether new treatments prolong survival compared to a standard therapy, the type I error rate is 14%. As a result, the probability of committing a type I error rate has increased from 5%, which is the original design, to 14%.

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TABLE 12.2

Effect of Multiple Testing on the True Type I Error Rate Assuming α = 0.05. NUMBER 1 2 3 4 5 10

OF

TESTS

TYPE I ERROR RATE 0.0500 0.0975 0.1426 0.1855 0.2262 0.4013

Clinical trials are expensive and take a long time to conduct and the investigator needs to protect himself/herself from making erroneous claims when in fact there are no real effects. Therefore, it is critical for an investigator to control for the type I error rate prospectively and to specify the methods to adjust for multiplicity at the design stage. This is particularly important with multiple arm trials whereby several hypotheses will be compared and multiplicity will occur in the data analysis phase. Many multiple arm trials start with a global test of equality in hazard rates (or survival times). If the global null hypothesis of the equality of hazard rates is rejected, then one is generally interested in identifying treatments where hazard rates differ significantly. There are two common approaches to hypothesis testing after a global null hypothesis is rejected: either follow by pair-wise comparisons or use sequentially rejective methods. The Bonferroni procedure is one of the older procedures for controlling for the type I error rate (13). By using this approach, an investigator is assured that the type I error rate does not exceed α. The procedure is simple to calculate and is implemented by dividing the overall type I error rate α by the number of independent tests (m) to be conducted. Therefore, each hypothesis will be tested with αj = α/m. This procedure is considered a single-step approach, as only one step is needed to find the critical value and to perform the test. The main drawback of the Bonferroni procedure is that it is very conservative, especially when the tests are correlated and the number of independent tests (m) is large, and therefore will require large sample sizes. Various modifications of the Bonferroni procedure have been proposed for controlling for the type I error rate (14–18). These procedures are sequentially rejective methods (or stepwise) since the result of a given test depends upon the results of the other tests. These methods can be described as either step-down or

step-up procedures. Let us assume that we have m independent hypotheses to be tested. In the step-down procedure we start by ordering the p-values from the most significant test and then step down to the least significant test (15). For the step-up procedure (on the other hand) we start by controlling the p-value for the least significant test and then step up to the most significant test (16–17). Hochberg’s approach is one of the most commonly used step-up procedures (17). For example, in an international lung trial, patients with stage III B to IV non-small-cell lung cancer were randomly assigned with equal probability to receive docetaxel (75 mg/m2) and cisplatin or docetaxel and carboplatin every 3 weeks or vinorelbine and cisplatin every 4 weeks (19). The investigators used the Hochberg method to control the type I error rate for the two hypotheses being tested (treatment comparisons). The trial will be statistically significant if both tests achieved p-value ≤0.05 or if only one of them achieved p-value ≤0.028. Sample Size Determination There are different approaches to designing trials with several treatment groups (20–24). In this section, we discuss sample size computations based on a time-to event endpoint, the most common endpoint that is used in phase III trials in oncology. Comparison of Three Survival Curves For simplicity, we assume that the equal number of patients are randomly allocated to all treatment groups. Table 12.3 presents the accrual times (T) for k = 3 treatment groups, given the follow-up time τ, yearly entry rate n, a common hazard rate Φ for the censored observations, two hazard ratios Δ1 = λ1/λ2 and Δ2 = λ1/λ3, and two-sided type I error rate of 0.05. λ1, which is the hazard in the control arm and may be unknown at the design stage, but the median survival time (M1) in the control group is known. Therefore, using the wellknown relationship λ1 = (log 2) /M1 for the exponential distribution, λ1 can be determined. The hazard ratio (denoted as Δ = λ1/λ2) is the ratio of the hazard rate in subjects assigned to the control and experimental arms, respectively. Alternatively, we can define the hazard ratio as the ratio of the median survival time in the experimental arm to the control arm (Δ = M2/M1) if the survival time follows an exponential distribution. For each τ, Δ1, Δ2, there are two rows: the first row gives values of T for the power of 0.80 and the second row gives values of T for the power of 0.90. The values of T are obtained by solving nonlinear equations using the Newton-Raphson procedure.

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TABLE 12.3

Accrual Period in Years (T) Assuming Equal Allocation Across the Groups and Type I Error Rate = 0.05. ENTRY RATE (PER

YEAR)

s

D1

D2

60

80

100

120

180

240

1

1.20

1.25

1.30

1.35

1.40

1.45

1.50

1.55

2.00

2.05

20.48 25.85 12.36 15.30 8.88 10.87 7.00 8.50 3.65 4.40

16.16 20.22 9.94 12.22 7.22 8.79 5.71 6.92 3.00 3.62

13.53 16.82 8.44 10.32 6.16 7.48 4.89 5.92 2.56 3.10

11.75 14.53 7.39 9.01 5.42 6.57 4.31 5.21 2.25 2.73

8.67 10.62 5.54 6.72 4.09 4.94 3.23 3.93 1.68 2.05

7.03 8.57 4.53 5.48 3.34 4.04 2.65 3.21 1.36 1.67

1.20

1.25

1.30

1.35

1.40

1.45

1.50

1.55

2.00

2.05

19.78 25.14 11.66 14.60 8.20 10.17 6.33 7.82 3.06 3.78

15.46 19.52 9.26 11.52 6.55 8.10 5.07 6.26 2.44 3.03

12.83 16.12 7.76 9.63 5.02 6.81 4.27 5.27 2.04 2.54

11.06 13.83 6.73 8.33 4.78 5.91 3.70 4.57 1.76 2.20

7.99 9.93 4.91 6.06 3.49 4.31 2.69 3.34 1.26 1.58

6.37 7.90 3.92 4.85 2.79 3.45 2.13 2.66 0.98 1.24

1.20

1.25

1.30

1.35

1.40

1.45

1.50

1.55

2.00

2.05

18.42 23.78 10.34 13.23 6.94 8.85 5.14 6.55 2.16 2.77

14.12 18.17 7.98 10.20 5.36 6.84 3.97 5.07 1.66 2.13

11.52 14.78 6.53 8.34 4.39 5.61 3.24 4.15 1.34 1.73

9.76 12.51 5.55 7.08 3.72 4.76 2.75 3.52 1.13 1.46

6.77 8.66 3.85 4.92 2.57 3.30 1.89 2.43 0.77 1.00

5.23 6.68 2.96 3.80 1.97 2.54 1.44 1.86 0.58 0.76

2

5

Suppose we are interested in testing the null hypothesis H0: λ1 = λ2 = λ3 against the alternative hypothesis H1: λ1 = 0.25, λ2 = 0.17, λ3 = 0.161 assuming a follow-up period of 2 years, power of 80%, and a two-sided type I error rate of 0.05. In our example, Δ1 = 1.50 and Δ2 = 1.55. From previous studies, we know that the yearly entry rate is 80 patients. Given the above values (from Table 12.3), the accrual length is 5.07 years and, therefore, the total duration of the trial is 7.07 years. In the colorectal cancer example, the investigators are interested in testing two primary hypotheses and the study is designed with a type I error rate = 0.025 (global type I error rate = 0.05) to be used to test each hypothesis. The study was designed with 90%

power to detect hazard ratio = 1.25 (median survival 27 months/22 months in the control arm). The accrual rate was assumed to be 75 patients/month with an accrual period ~30.5 and the follow-up = 24 months and the total trial duration is 64.5 months. The target sample size is 2,289 patients with 1,478 deaths expected at the end of the trial. Factorial Design Without Interaction An investigator was interested in testing the effect of two regimens (epothilone or taxotere and docetaxel) in men with castrate resistant prostate cancer. There are two factors each with two levels. Let Mij represent the

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median survival time in months for the ith treatment of Factor A and the jth treatment of factor B. Overall survival was the primary endpoint and the median survival times were assumed to be M11 = 18, M12 = 23, M21 = 23, and M22 = 29 months. Based on historic data, an accrual rate of 240 patients per year was assumed (or nij = 60 patients per cell). We control on the type I error rate as we are testing two hypotheses. The following calculations assume a total of 1,200 patients accrued over a 4-year period, and followed for 4 years after study closure and a two-sided alpha level of 0.025. The power to detect a hazard ratio = 1.25 (equivalent to an increase in median overall survival [OS] from 20 months to 25 months) is 92%. With Interaction In an ongoing CALGB phase III trial patients with transitional cell carcinoma, patients are randomized to one of two treatments: (a) gemcitabine, cisplatin, and placebo, or (b) gemcitabine, cisplatin, and bevacizumab. It is assumed that the prevalence of a positive VEGF marker is 30%. The primary endpoint is OS. The investigator is interested in testing treatment by VEGF level interaction in predicting overall survival using a two-sided α = 0.05 level to attain a power of 0.80. In this example, the two factors A and B correspond to treatment with two levels (gemcitabine, cisplatin, and placebo and gemcitabine, cisplatin, and bevacizumab) and VEGF with two levels (negative and positive). The median survival times in months were assumed to be 13.80 (i.e. M11 = M12 = 13.80) for patients treated with gemcitabine, cisplatin, and placebo regardless of VEGF levels whereas M21 = 15.18 and M22 = 28.15 for patients treated with gemcitabine, cisplatin, and bevacizumab with negative and positive VEGF levels, respectively. The total yearly accrual rate of 167 patients will be randomized equally between the two treatments. With a 30% positive VEGF marker prevalence, 25 patients per year were expected to have a positive VEGF marker in each treatment arm, and 58.5 patients per year in each treatment arm were expected to have a negative VEGF marker. Also, we assumed a follow-up period of 12 months to detect the median survival differences noted above. Using the methodology developed by Peterson et al. (5), the accrual period is 3.52 years with a required sample size of 588 patients and an expected number of deaths of 428.

CHALLENGES IN MULTIPLE ARM TRIALS Because of space limitations, we cannot go in depth discussing some of the common challenges that

investigators may face in conducting and analyzing multiple arm trials; however, we provide an overview below. In multiple arm trials, plans to stop accrual in one experimental arm(s) need to be prespecified at the design stage to prepare for the situation when the results reach statistical significance depending on the study objective. If one experimental arm is closed, then the trial may continue accrual and patients will be randomized to the other arms. In the situation described in Figure 12.1, if the control arm is shown to be inferior to either experimental arm then it is necessary to terminate the entire study. Another important question is whether to control on the type I error rate and what approach to use. Recently, Freidlin et al. argued that there is no need to control the type I error rate when several experimental arms are compared to a control or standard arm (25). Their rationale is that such trials are designed to answer the efficacy question for each experimental drug separately, and as such the results of one comparison should not influence the results of the others. We have focused on the type I error rate, but power is also jeopardized by testing several hypotheses. Although the individual power to test each hypothesis may be sufficient, the global power may be less than optimal. Trials with either induction (obtain response from patients) or maintenance randomization may end up with different timing of randomization, and as such the interpretation of results may be difficult. Design of factorial or multiple arm trials becomes more complex when testing for superiority and for noninferiority. For instance, investigators designed the TAX 326 to answer both superiority and noninferiority questions, and thus the sample size is much larger compared to two-arm trials (19). Finally, we concentrate on the situation where k = 3 arms. The design of trials with more than 3 arms can become extremely complicated. In some instances, investigators may be able to frame their alternative hypothesis based on a partial order. The statistical methodology under order restriction is very mathematical and complex and the reader is referred to Singh et al. (24).

SUMMARY In summary, multiple arm trials pose many challenges in their design, conduct, and analysis. In such studies, investigators should explicitly state the hypotheses to be tested a priori, and specify the type I error rate and the method of controlling the type I error rate at the design stage. If designed and analyzed appropriately,


multiple arm trials can answer important questions concerning a relevant patient population and provide the basis to make valid inferences about the experimental therapies being tested.

References 1. Small EJ, Halabi S, Ratain M, et al. Randomized study of three different doses of suramin administered with a fixed dosing schedule in patients with advanced prostate cancer: results of Intergroup 0159, Cancer and Leukemia Group B 9480. J Clin Oncol. 2002;20:3369–3375. 2. Rimer BR, Halabi S, Skinner CS, et al. Effects of a mammography decision-making intervention at 12 and 24 months. Am J Prev Med. 2002;22:247–257. 3. Henderson, IC, Berry DA, Demetri GD, et al. Improved outcomes from adding sequential paclitaxel but not from escalating doxorubicin dose in an adjuvant chemotherapy regimen for patients with node-positive primary breast cancer. J Clin Oncol. 2003;21: 976–983. 4. Stampfer MJ, Buring JE, Willett W, et al. The 2 × 2 factorial design: its application to a randomized trial of aspirin and carotene in U.S. physicians, Stat Med. 1985;4:111–116. 5. Peterson B, George SL. Sample size requirements and length of study for testing interaction in a 2 × k factorial design when time-to-failure is the outcome. Cont Clin Trials. 1993;14: 511–522. 6. Simon R, Freedman LS. Bayesian design and analysis of 2 × 2 factorial clinical trials. Biometrics. 1997;53:456–464. 7. Green S, Benedetti J, Crowley J. Clinical Trials in Oncology. New York: Chapman and Hall; 1997. 8. Simon R, Wittes RE, Ellenberg SS. Randomized phase II clinical trials. Canc Treat Rep. 1985;69:1375–1381. 9. Gibbons JD, Olkin I, Sobel M. Selecting and Ordering Populations: A New Statistical Methodology. New York: Wiley & Sons; 1977. 10. Chen TT, Simon R. A multiple step procedure with sequential protection of preferred treatments. Biometrics. 1993;49: 753–761.

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11. Chen TT, Simon R. Extension of two-sided test to multiple treatment trials. Commu Statist Theory Methods. 1996;25: 947–965. 12. Chen TT, Simon RM: Extension of one-sided test to multiple treatment trials. Cont Clin Trials. 1994;15:124–134. 13. Bland JM, Altman DG. Multiple significance method. Br Med J. 1995;310:170. 14. Simes RJ. An improved Bonferroni procedure for multiple tests of significance. Biometrika. 1986;73:751–754. 15. Holm S: A simple sequentially rejective multiple test procedure. Scand J Stat. 1979;6:65–70. 16. Hochberg Y, Benjamini Y. More powerful procedures for multiple significance testing. Stat Med. 1990;9:811–818. 17. Hochberg Y. A sharper Bonferroni procedure for multiple tests of significance. Biometrika. 1988;75:800–802. 18. Dunnett CW. A multiple comparison procedure for comparing several treatments with a control. J Am Stat Assoc. 1955;50:1096–1121. 19. Fossella F, Pereira JR, Pawl J, et al: Randomized multinational phase III study of docetaxel plus platinum combinations versus vinorelbine plus cisplatin for advanced non-small cell lung cancer: The TAX 326 study group. J Clin Oncol, 2003; 21:3016–3024. 20. Makuck RW, Simon RM. Sample size requirements for comparing time-to-failure among k treatment groups. J Chron Dis. 1982;35:861–867. 21. Liu PY, Dahlberg S. Design and analysis of multiarm clinical trials with survival endpoints. Cont Clin Trials. 1994;16: 119–130. 22. Ahnn S, Anderson SJ. Sample size determination for comparing more than two survival distributions. Stat Med. 1995;14:2273–2282. 23. Halabi S, Singh B. Sample size determination for comparing several survival curves with unequal allocations. Stat Med. 2004;23:1793–1815. 24. Singh B, Halabi S, Schell M. Sample size selection in clinical trials when population means are subject to a partial order. J Appl Stat. 2008;35:583–600. 25. Freidlin B, Korn E, Gray B, et al. Multi-arm clinical trials of new agents: some design considerations. Clin Cancer Res. 2008;14:4368–4371.


13

Noninferiority Trials in Oncology

Suzanne E. Dahlberg Robert J. Gray

The randomized phase III clinical trial is the gold standard for establishing the clinical efficacy of a new therapy. The majority of trials are designed to demonstrate the superiority of a novel agent or of a novel combination of therapies over a placebo or the current standard of care. In oncology, the remainder of these trials tends to fall into a class of trials known as noninferiority trials, which aim to determine whether or not a new treatment is no worse than the standard treatment by a prespecified margin. These designs are especially appropriate if the new treatment is thought to be less toxic, less expensive, or less invasive than the standard of care without placing a patient at an unacceptable amount of additional risk relative to the standard therapy, or more generally, when the new agent is thought to provide practical benefits without compromising efficacy. This chapter discusses issues pertaining to the design, monitoring, analysis, and interpretation of noninferiority trials. Many of these issues are also relevant for equivalence studies, but these are rare in oncology. Equivalence trials test whether or not a new treatment is no worse and no better than a standard therapy by a particular margin. Because curing cancer is the ultimate goal of cancer researchers, it generally is not of interest to conduct trials to show that a new agent does not provide more benefit than currently available therapies. Although the words noninferior and equivalent may be used interchangeably in certain

settings, it is important to emphasize the different statistical interpretations of these words when used in the context of clinical research. The examples discussed throughout this chapter illustrate designs of phase III noninferiority trials in oncology. Phase II noninferiority trials are an oxymoron; phase II trials generally aim to demonstrate a level of efficacy that deems an agent worthy of further study, and this level should be large enough to justify the use of resources to conduct a phase III trial. On the other hand, noninferiority studies also require very large sample sizes, which are not a feasible characteristic of phase II studies. Therefore, establishing noninferiority in the phase II setting is generally not of interest.

STATISTICAL DESIGN In noninferiority trials, patients are randomized between the new treatment (or combination) and an active control arm (usually representing the current standard of care). The most important aspect of any noninferiority design is the selection of the noninferiority margin (Δ). The value of Δ is a measure of the difference in the efficacy outcome between the treatment arms, and the magnitude of Δ is chosen so that the new treatment would be preferred if it is worse (less efficacious) than the standard by an amount < Δ. No formal rules for the

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selection of this margin exist. The International Conference on Harmonization (ICH) recommends choosing a margin that is both statistically and clinically justified in a study population similar to those previously studied in the disease of interest (1). The magnitude of the noninferiority margin must be smaller than the magnitude of efficacy of the control arm, since otherwise a conclusion of noninferiority might be possible for a treatment that was not superior to best supportive care (Fig. 13.1). The small increase in risk characterized by the noninferiority margin must be compared to and considered an acceptable trade-off for the possible benefits in side effects, quality of life, and cost. The most common endpoints for noninferiority trials in oncology are time-to-event endpoints such as overall survival (OS) or progression free survival (PFS). Binary endpoints are feasible, but they provide less information and precision than the time-to-event endpoints, which report both the binary event status and the time of the event; therefore, binary endpoints provide less power than time-to-event outcomes given a fixed sample size. If registration with the Food and Drug Administration (FDA) is the ultimate goal of the trial, one should proceed with caution on the use of binary endpoints, since the FDA has stated that noninferiority trials “with endpoints other than survival are problematic” (2). Therefore, the examples that follow highlight noninferiority trials that implement time-to-event endpoints.

Types of Designs Traditional (Fixed Margin) Method The traditional noninferiority design, called the fixed margin method, uses a fixed prespecified noninferiority margin. For time-to-event endpoints, treatment differences are often expressed in terms of the hazard rate ratio. The hazard rate at follow-up time t is the instantaneous rate at which events occur among patients who have not had an event by t, and the hazard ratio Θ is the ratio of the hazard rate in the new treatment arm over that in the control arm. In general, the hazard ratio would vary with t, but under the common proportional hazards assumption, the ratio is assumed to be constant over time. That is, the event rate is assumed to be increased or decreased by the same proportionate amount across follow-up time. When the hypotheses are expressed in terms of hazard ratios under the proportional hazards assumption, the noninferiority margin Δ is >1, and 100(Δ − 1) is the minimum percent increase in the hazard rate where the new treatment would be considered unacceptably worse than the standard.

1

BSC

Standard 2 New Drug FIGURE 13.1

The magnitude of the noninferiority margin, Δ2, must be less than the magnitude of superiority, Δ1, of the control arm over best supportive care (BSC).

The null hypothesis in the traditional noninferiority design is usually taken to be inferiority: H0: Θ ≥ Δ. (The new treatment is at least 100 (Δ − 1)% worse than the standard of care.) HA: Θ < Δ. (The experimental arm has at most 100 (Δ − 1)% higher risk than the control.) The sample size is chosen to ensure adequate power to reject inferiority in favor of equivalence (Θ = 1). Since the amount a new treatment could be worse than the standard and still be considered acceptable is usually quite small, the difference between the null and alternative hazard ratios (Δ and 1) is usually smaller than in superiority studies, so noninferiority trials tend to require much larger sample sizes. The null hypothesis in this formulation cannot be tested using a standard log-rank test, but Cox proportional hazards models can be used instead. The hypothesis in a noninferiority trial can also be formulated with equivalence (Θ = 1) as the null and inferiority (Θ > 1) as the alternative. In this setting, the sample size is chosen to ensure adequate power to detect a ratio of Θ = Δ, so in either case the study is designed to discriminate between hazard ratios of Δ and 1. One advantage of using the null of equivalence is that the traditional log-rank test can be used. In the second version, the interpretation of the type I and type II error rates are reversed from their usual definitions in the superiority test setting. The type I error is the probability of falsely rejecting the null hypothesis. Rejecting the null hypothesis of equality results in the continued use of the standard therapy, so a type I error corresponds to rejecting a new treatment with equivalent efficacy. The type II error rate is defined as the

13 NONINFERIORITY TRIALS IN ONCOLOGY

probability of falsely declaring equality of the two regimens, which in this setting results in adopting a new regimen that is truly inferior to the standard of care. With the null hypothesis of equivalence, controlling the type II error rate is very important, so values of 0.025 to 0.05 are common; whereas larger type I error rates (0.05 to 0.10, one-sided) may be appropriate. When the null hypothesis of inferiority is used, rejecting the null hypothesis is the same as concluding noninferiority, and the usual definitions of the type I and type II error rates apply. Therefore, controlling the one-sided type I error rates is as important for the null of inferiority as it is in a superiority trial. With either null hypothesis, it is strongly recommended that confidence intervals for the primary endpoint always be presented in addition to any p-value from the hypothesis test so that the precision of the estimates may be considered in the context of previously conducted studies of the standard agent (3 − 5). These confidence intervals are compared to the noninferiority margin to declare noninferiority, as discussed later in this chapter.

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appropriate. In hybrid designs, a noninferiority margin Δ > 1 is specified as in the traditional fixed margin design, and the null hypothesis of inferiority (Θ = Δ) is used, but the sample size is chosen to have adequate power to detect an alternative ratio of Θ = ΘA < 1. Since the difference between Δ and ΘA is larger than between Δ and 1, hybrid designs require smaller sample sizes than true noninferiority designs. However, they are also underpowered for concluding noninferiority when the new treatment is only equivalent to (rather than superior to) the current standard. These designs allow for a formal test of superiority in addition to the noninferiority test. First, the null hypothesis of inferiority is tested. If inferiority is rejected, then the null hypothesis of equivalence can be tested against the alternative of superiority. There is not an inflation of the overall type I error rate, because the second test is only performed if the first is significant. This superiority test may be underpowered for realistic alternatives, though, unless this hypothesis has been considered in determining the sample size. Examples of Study Designs

Percent Retention Method The fixed margin method assumes that prior data or other considerations support an absolute standard for the noninferiority margin. However, there is always some uncertainty in the estimated benefit of the standard treatment, both in terms of statistical variability in the estimates of benefit from prior studies and from other differences between the current study and the prior studies that established the benefit of the standard, such as differences in patient population or supportive care. A more appropriate approach may be the percent-retention method proposed by Rothmann et al. (6), which takes into account the uncertainty in the benefit of the standard treatment to ensure that a conclusion of noninferiority establishes that the new treatment is superior to best supportive care by at least a specified percent of the benefit of the current standard over best supportive care. This method compares the two-sided 95% confidence interval for comparing the new treatment to the active control in the noninferiority study to the confidence interval for the hazard ratio from a meta-analysis of the control compared to placebo, with the confidence level adjusted to preserve the overall type I error rate of the study. Hybrid Design If a new therapy has a milder toxicity profile and an expected modest benefit in efficacy compared to the standard treatment, a hybrid design (7) may be

One study utilizing a traditional noninferiority design is the Eastern Cooperative Oncology Group-led intergroup phase III trial, TAILORx, which compares hormonal therapy alone to chemotherapy plus hormonal therapy in node-negative, hormone receptor positive patients with an Oncotype DX Recurrence Score (RS) of 11-25 (8, 9). Patients with low RS levels have been shown to have low absolute recurrence rates (10), and retrospective data suggest that the benefit of adjuvant chemotherapy is primarily in patients with high RS levels (11), so the purpose of the study is to examine the effect of chemotherapy in the population with intermediate RS values. Since the study population consists of patients meeting standard guidelines for treatment with chemotherapy, the study uses a noninferiority design to determine if hormonal therapy alone is as efficacious as hormonal therapy plus chemotherapy in this selected subset. In addition, patients with low risk disease (RS < 11) are directly assigned to hormonal therapy alone, to prospectively validate whether the recurrence rate in this group is as low as expected. This study uses the null hypothesis of equivalence (the second form discussed above) with inferiority as the alternative. Thus, under the null hypothesis, the addition of chemotherapy to hormonal therapy is assumed to have the same effect on disease free survival (DFS) as hormonal therapy alone. Since hormonal therapy is known to be beneficial in this population, the considerations discussed above for choosing the noninferiority margin small enough to ensure that it corre-

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sponds to benefit for the new therapy compared to best supportive care do not apply to this study. Rather, the noninferiority margin was chosen based on the minimum benefit that chemotherapy would have to have to be considered worth the side effects and cost. In extensive discussions with oncologists and patient advocates, it was agreed that a 3% absolute increase in the 5-year DFS event rate with hormonal therapy alone would be unacceptable. Since the 5-year DFS rate was expected to be 90% with chemotherapy, the noninferiority margin on the hazard ratio was set at a 32.2% increase in the DFS hazard rate (Δ = 1.322), since this increase in hazard corresponds to a decrease in the 5-year DFS rate of 90% to 87%, assuming proportional hazards. The design uses a one-sided type I error rate of 10% and a type II error rate of 5%, which reflects the reversal of the roles of the type I and type II errors when the null hypothesis of equivalence is used in a noninferiority design. The design calls for randomization of 4,390 patients, and full information will be reached when 534 DFS events have occurred (in this case, the large sample size is a result of the low event rate, rather than because of a small noninferiority margin). The primary comparison is also planned to use an intention-to-treat analysis, where patients are included with their assigned treatment group regardless of treatment received. If some patients assigned to chemotherapy do not receive it, and some assigned to hormonal therapy alone receive chemotherapy, there will be dilution of the treatment difference between the randomized arms, and consequently a loss of power and inflation of the type II error. The planned sample size includes an inflation of 10.8%, based on the LachinFoulkes adjustment (12), to compensate for an assumed treatment nonadherence rate of 2.5% (average on each arm). This is a critical issue in a noninferiority study, since this dilution of the treatment effect could result in an inferior treatment appearing noninferior, due to reduced power. Since controlling the type II error is critical in a noninferiority design using the null hypothesis of equivalence, it is important to closely monitor the treatment adherence rates and to adjust the design, if necessary, to ensure adequate power. In the case of TAILORx, preliminary data suggest that the nonadherence rate is higher than allowed in the design, and that a substantial increase in the planned sample size will be needed to ensure adequate power. A second example of a trial utilizing a traditional noninferiority design was published by Scagliotti et al, who reported results from a phase III trial comparing cisplatin/gemcitabine to cisplatin/pemetrexed as firstline therapy for patients with metastatic non-small-cell lung cancer (13). Because pemetrexed has a better safety profile and is easier to administer, this study was

designed using a noninferiority design. The noninferiority margin for the overall survival endpoint was set at 1.176 comparing cisplatin/pemetrexed to cisplatin/ gemcitabine. This study used the null hypothesis of inferiority, defining inferiority to be a 17.6% increase in the mortality hazard rate with cisplatin/pemetrexed (the 17.6% increase corresponds to the cisplatin/ gemcitabine hazard rate being 15% lower than the cisplatin/pemetrexed rate). Therefore, cisplatin/ pemetrexed would be considered noninferior to cisplatin/gemcitabine if the upper bound of the two-sided 95% confidence interval for the overall survival hazard ratio was less than 1.176. This study design required 1,725 patients and full information of 1,190 deaths to provide adequate power to discriminate between hazard ratios of 1.176 and 1.0. The reported hazard ratio was 0.94 (95% CI: 0.84, 1.05) and the authors concluded that these two treatment regimens have similar efficacy in this patient population. Since the new treatment is being used in combination with the same drug used in the current standard of care (cisplatin), comparison to best supportive care is not relevant in this study. The current standard of care for first line chemotherapy treatment of NSCLC consists of cisplatin or carboplatin doublets (usually in combination with a taxane, vinorelbine, or gemcitabine). These doublets have been shown to improve survival over the older control arm of cisplatin plus etoposide, and are thought to be roughly equivalent to each other. Instead of indirect comparison to best supportive care, the relevant question here is whether the noninferiority margin was sufficient to establish that adding pemetrexed to cisplatin improves survival over the older control arm of cisplatin plus etoposide, since the current standard treatments are known to do so. A meta-analysis of survival outcomes of 4,556 patients randomized to gemcitabine plus platinum chemotherapy or other platinum therapy in 13 other trials resulted in an OS hazard ratio of 0.90 (95% CI: 0.84–0.96) in favor of gemcitabine (14); specifically, one of the studies included in this metaanalysis was a study of cisplatin/gemcitabine versus cisplatin/etoposide (15). The reported overall survival hazard ratio from this study of 135 patients with advanced NSCLC was 0.77 (95% CI: 0.55–1.10), but it should be noted that the primary endpoint of this trial was response rate. Neither of these results is consistent with a hazard ratio of 0.85 favoring gemcitabine/ cisplatin, since the upper limits of both confidence intervals exceed this margin. In fact, none of the upper confidence bounds from the 13 trials in the meta-analysis is lower than 0.85, and therefore the choice of the noninferiority margin for the pemetrexed study seems suspect. Since the upper confidence limit of the overall survival hazard ratio in the Scagliotti trial (1.05) is

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less than the upper bound reported in the meta-analysis (1.10), one could argue that the observed results of the pemetrexed trial may be sufficient to establish noninferiority. An example of a clinical trial utilizing a hybrid design is the phase III ECOG trial E1A06 comparing melphalan, prednisone, and thalidomide (MPT) to melphalan, prednisone, and lenalidomide (MPL) in newly diagnosed myeloma patients who are not candidates for high dose therapy. Although MPT is considered the standard of care for this patient population because of its dramatic improvement in efficacy, thalidomide is a very toxic agent. Lenalidomide, an agent with similar activity to thalidomide, is less toxic than thalidomide, hence justifying the use of a noninferiority trial in this setting. Although it is anticipated that MPL will prove the superior regimen with improved PFS and lower toxicity, neither feature can be confidently predicted since long-term follow-up for the MPL regimen is lacking and myelosuppression may prove limiting and may compromise drug dosing and efficacy. Therefore, this trial aims to test the following hypotheses: H0: Θ ≥ 1.220. (MPL is inferior to MPT.) HA: Θ < 1.220, but the study is powered to detect ΘA < 0.935. (MPL is noninferior to MPT, but superiority is expected.) Here Θ represents the PFS hazard ratio for MPL versus MPT, and the noninferiority margin corresponds to the PFS hazard rate being 22% larger on MPL than on MPT. Instead of powering the comparison to detect a difference between ratios of 1.22 and 1.0, the hybrid design is only powered to conclude noninferiority if it turns out that the new treatment is slightly better than the standard. Additionally, the PFS hazard ratio for MPT versus MP is 0.51, and the 95% CI is (0.39–0.66) (16), which is consistent with an event rate that is 1/0.66 = 1.52 times the event rate on MPT. Since the noninferiority margin of 22% is much less than the known magnitude of benefit of MPT over the previous standard of care, rejecting the null hypothesis of inferiority would be more than sufficient to establish that MPL was superior to melphalan and prednisone (MP) alone. The noninferiority margin is substantially smaller than the difference between MPT and MP because, in the judgment of the investigators, an increase of 22% in the PFS hazard rate over MPT would make the use of MPL inappropriate. Assuming PFS follows exponential distributions, the hazard ratios can be translated into differences in median PFS. The trade-off in toxicity associated with MPL would be considered acceptable as long as the median PFS for the MPL arm was not more than

5 months less than the median PFS of 28 months assumed for the MPT arm, even though MPL is expected to demonstrate a 2-month improvement in median PFS. With 560 patients to be randomized and full information of 366 events, this hybrid design has 80% power at a one-sided 0.05 significance level to test these hypotheses. Implementing a traditional noninferiority design for this trial with the same type I and type II errors as the hybrid design would require randomizing 1,003 patients and full information of 655 events.

MONITORING Randomized clinical trials require formal monitoring by a data monitoring committee (also known as a data safety monitoring committee) at planned intervals throughout their duration, but noninferiority trials may be subject to monitoring rules that vary from those established for superiority trials. Generally, noninferiority studies should include early stopping rules based on clear evidence of inferiority at interim analyses. On the other hand, there may not be a clear ethical imperative to stop early for evidence of noninferiority, and early stopping in favor of noninferiority should only be considered when there is strong evidence that the new treatment is not inferior to the standard. For these reasons, rules for early stopping in favor of noninferiority may be more conservative (if used at all) than typical of early stopping rules in superiority studies. Given the importance of confidence intervals for interpreting the results of noninferiority studies, repeated confidence intervals (17) provide a natural approach for interim analyses in noninferiority studies. This approach uses a confidence interval on the treatment effect as the basis of the stopping rules, and adjusts the width of the intervals so that their intersection has the desired coverage probability. The monitoring rules for the TAILORx study illustrate these points. The rule for stopping in favor of inferiority uses a conventional O’Brien-Fleming boundary to control the type I error rate (for the null hypothesis of equivalence) at an overall one-sided 10% rate. The stopping rule in favor of inferiority uses a two-sided 95% repeated confidence interval on the hazard ratio, and stops only when the ratio corresponding to the noninferiority margin lies above the upper confidence limit. When this occurs, the hypothesis of inferiority is rejected at the conventional one-sided 2.5% level (taking into account the multiple interim analyses). This is stronger evidence than required at the final analysis, since the study is designed to have 95% power rather than 97.5%. Because noninferiority studies typically enroll large numbers of patients with very lengthy follow-up

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periods, noninferiority studies may take a much longer time to complete. For a patient facing a treatment decision, early release of results from a noninferiority study may help guide the choice of therapy. Korn et al. (18) outlined a set of guidelines by which noninferiority studies may undergo early stopping by a data monitoring committee without harm to the conduct or error structure of the study. The proposed method is not data driven and has some useful practical implications that should be considered before implementation of any noninferiority design. The guidelines require that accrual be terminated, that all patients be off treatment, and that a considerably lengthy follow-up period remain before any data can be released. It is also important that both of the therapies being studied in the trial be publicly available at the time of early data release; if an experimental agent is being compared to standard of care, most patients are probably receiving the standard of care anyway, and early release of data will not have an impact on their course of treatment since the other agent is unavailable. If data are to be released early, it must seem unlikely that patients will modify treatment once the trial results are made available, and all results should be clearly communicated as preliminary results, accompanied by confidence intervals and descriptive statistics about follow-up times. The main problem with early release of results from a noninferiority study is not unique to this type of trial; because data cleaning and analysis take place each time results are released, early release of data can potentially increase and burden the workflow of data managers. Another argument against the use of these guidelines is that it violates the formal monitoring guidelines for the trial and they challenge the degree of reliability of the early results in the absence of established stopping rules.

ity trial, but a review of equivalence studies by Ebbutt et al. demonstrated that the conservatism of the results demonstrated by wider confidence intervals around point estimates is due entirely to smaller sample sizes rather than lack of bias from noncompliance (20). Therefore, it is often required to demonstrate noninferiority in both the ITT and PP analysis populations to declare success in such a study. TAILORx again illustrates these points. With nonadherence rates possibly as large as 10% to 15%, there will be substantial reduction in power in the ITT analysis. However, the prognosis of patients choosing to receive chemotherapy when assigned to hormones alone may be different than those who choose not to receive chemotherapy when assigned to receive it, so performing a PP analysis, which excludes both of these groups, could also bias the comparison of the treatment arms. INTERPRETATION When the results of a phase III trial demonstrate strong statistical evidence for rejecting the null hypothesis, interpretation of the results is relatively easy. For example, when the null hypothesis is inferiority, such an instance allows one to conclude that the experimental agent is noninferior or even superior to the standard of care. Noninferiority can be declared if the confidence interval for the estimate of the primary endpoint excludes the noninferiority margin in favor of improved outcomes, and if this interval also excludes the null value in favor of even better outcomes, then superiority can be declared (Fig. 13.2). When the data are not convincing enough to declare superiority or noninferiority, the most important thing to remember is that failure to reject the null

Superiority

ANALYSIS Choosing the appropriate analysis population in noninferiority studies can be quite a challenge because inherent flaws in the study conduct may bias results toward the conclusion of noninferiority (19). The intent-to-treat (ITT) principle induces conservatism into the analysis of superiority trials, since the analysis includes all randomized patients. The inclusion of nonadherent patients biases results toward the null hypothesis of no treatment difference; nonadherence in a noninferiority study, therefore, biases results toward treatment similarity. The per-protocol (PP) population, which consists of all patients who complete treatment without major protocol violations, is sometimes viewed as the more appropriate analysis set for a noninferior-

Noninferiority Inconclusive Inconclusive Inferiority Hazard ratio 1 New treatment better

New treatment worse

FIGURE 13.2 Conclusions to be made based on where the 95% confidence intervals for the hazard ratio fall in relation to the noninferiority margin (Δ).


hypothesis is not the same as accepting the null hypothesis, and the clinical interpretation of a trial in these circumstances can be challenging. If the confidence interval around the estimate of the primary endpoint excludes the noninferiority margin in the direction of worse outcomes, then inferiority should be concluded. Confidence intervals containing the noninferiority margin are inconclusive and should be described as such in a conservative manner.

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Concluding Noninferiority from a Superiority Trial Concluding noninferiority from a superiority trial that failed to meet its primary endpoint is a controversial convention that happens too often in the reporting of clinical trials. Superiority trials are typically underpowered for a formal test of noninferiority, so failure to demonstrate that a new therapy provides a statistically significant benefit compared to a standard treatment should not be interpreted as clinical equivalence. That is not to say this does not happen; in a study by Greene et al., 78% of clinical trials concluding equivalence between the years of 1992 and 1996 did not fit their established statistical criteria of a genuine noninferiority study: defining the noninferiority margin, implementing the appropriate sample size, and conducting a formal test for noninferiority (21). Herein lies the debate over the need for concordance between the clinical and statistical interpretation of the data. Concluding noninferiority from a superiority trial if a noninferiority boundary was prespecified in the protocol can still be problematic (22), but it does not impact the sample size or primary hypothesis test of the study. Rather, the confidence interval approach should be used to consider the precision of the estimates with regard to the prespecified noninferiority margin, which should always be clinically relevant and justified. In the absence of a prespecified noninferiority margin, it remains a challenge for the oncology community to avoid the assumption of equivalence when a superiority study fails to meet its endpoint, but it is also unreasonable to expect that each failed superiority trial should be followed by a formal noninferiority study of the same agents. Resources and patients are too limited to do this, and some argue that even the best-conducted noninferiority trial does little to drastically improve outcomes for cancer patients.

6. 7. 8. 9. 10. 11.

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17. 18. 19. 20.

References

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Harmonization Guideline: Guidance on Choice of Control Group and Related Design and Conduct Issues in Clinical Trials. ICH E10. July 2000. U.S. Department of Health and Human Services, Food and Drug Administration. Guidance for Industry: Clinical Trial Endpoints for the Approval of Cancer Drugs and Biologics. May 2007. Makuch R, Simon R. Sample size requirements for evaluating a conservative therapy. Cancer Treat Rep. 1978;62:1037–1040. Piaggio G, Elbourne DR, Altman DG, et al. Reporting of noninferiority and equivalence randomized trials: an extension of the CONSORT statement. JAMA. 2006;295: 1152–1160. Zee BC. Planned equivalence or noninferiority trials versus unplanned noninferiority claims: are they equal? J Clin Oncol. 2006;24:1026–1028. Rothmann M, Li N, Chen G, et al. Design and analysis of noninferiority mortality trials in oncology. Stat Med. 2003;22:239–264. Freidlin B, Korn EL, George SL, Gray R. Randomized clinical trial design for assessing noninferiority when superiority is expected. J Clin Oncol. 2007;25:5019–5023. Sparano JA. TAILORx: Trial assigning individualized options for treatment (Rx). Clin Breast Cancer. 2006;7:347–350. Sparano JA, Paik S. Development of the 21-gene assay and its application in clinical practice and clinical trials. J Clin Oncol. 2008:26;721–728. Paik S, Shak S, Tang G, et al. A multigene assay to predict recurrence of tamoxifen-treated, node-negative breast cancer. N Engl J Med. 2004;351:2817–2826. Paik S, Tang G, Shak S, et al. Gene expression and benefit of chemotherapy in women with node-negative, estrogen receptor-positive breast cancer. J Clin Oncol. 2006;24: 3726–3734. Lachin JM, Foulkes MA. Evaluation of sample size and power for analyses of survival with allowance for nonuniform patient entry, losses to follow-up, noncompliance, and stratification. Biometrics. 1986;42:507–519. Scagliotti GV, Parikh P, von Pawel J, et al. Phase III study comparing cisplatin plus gemcitabine with cisplatin plus pemetrexed in chemotherapy-naive patients with advanced-stage non-smallcell lung cancer. J Clin Oncol. 2008;26:3543–3551. Le Chevalier T, Scagliotti G, Natale R, et al. Efficacy of gemcitabine plus platinum chemotherapy compared with other platinum containing regimens in advanced non-small-cell lung cancer: a meta-analysis of survival outcomes. Lung Cancer. 2005;47:69–80. Cardenal F, Lopez-Cabrerizo MP, Anton A, et al. Randomized phase III study of gemcitabine-cisplatin versus etoposidecisplatin in the treatment of locally advanced or metastatic nonsmall-cell lung cancer. J Clin Oncol. 1999;17:12–18. Facon T, Mary JY, Hulin C, et al. Melphalan and prednisone plus thalidomide versus melphalan and prednisone alone or reduced-intensity autologous stem cell transplantation in elderly patients with multiple myeloma (IFM 99-06): a randomised trial. Lancet. 2007;370:1209–1218. Jennison C, Turnbull B. Group Sequential Tests with Applications to Clinical Trials. Chapman and Hall/CRC. 2000. Korn EL, Hunsberger S, Freidlin B, et al. Preliminary data release for randomized clinical trials of noninferiority: a new proposal. J Clin Oncol. 2005:23;5831–5836. Sanchez MM, Chen C. Choosing the analysis population in noninferiority studies: per protocol or intent-to-treat. Stat Med. 2006;25:1169–1181. Ebbutt AF, Firth L. Practical issues in equivalence trials. Stat Med. 1998;17:1691–1701. Greene WL, Concato J, Feinstein AR. Claims of equivalence in medical research: are they supported by the evidence? Ann Intern Med. 2000;132:715–722. Le Henanaff A, Giraudeau B, Baron G, Ravaud P. Quality of reporting of noninferiority and equivalence randomized trials. JAMA. 2006;295:1147–1151.


14

Bayesian Designs in Clinical Trials

Gary L. Rosner B. Nebiyou Bekele

In this chapter, we discuss issues that arise when developing, writing up, and implementing clinical study designs that incorporate Bayesian models and calculations. We have had the opportunity to work with many such designs at The University of Texas M. D. Anderson Cancer Center. We feel that study designs that incorporate Bayesian models offer many advantages over traditional frequentist designs, and we will discuss these advantages in this chapter. At the same time, Bayesian models require a lot of thought and close work with the clinical investigators. Also, there may be some reluctance on the part of some clinical investigators to accept a study design that is built on Bayesian considerations. We will provide some arguments and real examples that may help statisticians overcome such reluctance. Although our examples tend to come from the field of oncology, the lessons and underlying ideas have broad application. (See Carlin and Louis [1] for a general introduction to Bayesian methods.)

WHY BAYESIAN DESIGNS What Are Bayesian Designs? Types of Bayesian Designs First we need to define what we mean by a Bayesian design. In the first paragraph, we specifically avoided writing the term “Bayesian design,” choosing instead

the phrase “clinical study designs that incorporate Bayesian models and calculations.” The latter phrase allows us to include many designs that are not fully Bayesian, meaning that they do not choose the design to minimize some risk. Instead, many of these “calibrated Bayes” (2) designs incorporate a Bayesian model, possibly considering prior information, in the stopping rules of the study. An example of this calibration is the following. The statistician and clinical investigators decide on the general form of the criteria for decisions at interim analyses, such as basing decisions on the posterior probability that the treatment’s success probability exceeds a threshold value. Next, the statistician will typically carry out a large number of simulations under various scenarios. The statistician reviews the simulation results with the clinical investigators, allowing them to decide on the criteria that yield the best (to their minds) operating characteristics. This process may include changing the benchmark value against which one compares the posterior treatment-related success probability or the degree of certainty (e.g., 80% or 90%) that one will require before one will consider stopping the study. There also exist more formal Bayesian designs for clinical trials. Berry argues for the application of decision theory in clinical trial design (3, 4). Even if one takes a fully Bayesian view, one will still find that reviewing these a priori simulations serves to make the

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transition from frequentist designs to Bayesian ones easier for clinical investigators. Simulations under various scenarios also help reveal sensitivity of the study’s decisions and inferences to prior assumptions. We discuss these ideas later in this chapter through our examples. Advantages of Bayesian Designs Why is one interested in Bayesian designs for clinical trials? One can view a clinical trial as an experiment that will lead to a decision (use the new treatment or do not use the new treatment) or prediction (the new treatment regimen will provide a benefit of so much over the standard treatment). Bayesian methods are ideal for decision making (i.e., minimizing risk or maximizing utility) and for prediction. Additionally, Bayesian methods are ideal for combining disparate sources of information. Thus, one can construct a coherent probability model to combine the information from the current study with historical data and with any information available from ongoing studies using Bayesian considerations. Perhaps a further impetus to the current interest in Bayesian designs is the fact that the Bayesian inference obeys the likelihood principle. Many of the clinical studies we see include interim analyses, and when there is no provision for interim analyses, we often suggest them in our reviews. The likelihood principle is important as it relates to interim analyses of an ongoing study. One develops frequentist stopping rules, such as group sequential designs (5), in a way that preserves the overall type I error under the null hypothesis. Thus, a treatment effect that might have been statistically significant without any prior interim analyses may not be significant after accounting for the number of prior analyses. The likelihood principle, however, requires that data that lead to the same likelihood for the parameter of interest should lead to the same inference (6). A consequence of the likelihood principle is that the number of interim analyses does not affect Bayesian inference, since the likelihood is the same whether the current analysis had been the first or the most recent of several earlier analyses. All that matters to the Bayesian are the data at hand and not what happened before, unless earlier analyses somehow alter the likelihood. Another reason more and more clinical trials are incorporating Bayesian ideas is the desire in many situations to include adaptive randomization. Such clinical trials change the randomization probabilities in light of the accruing data. The study may start randomizing patients to the different treatments with equal probability. Then, perhaps after enrolling some minimum number of patients, the randomization probabilities adapt to favor the better performing treatments.

Bayesian methodology may enter the study by way of using posterior probability calculations to influence the randomization probabilities (7). The ethical idea is to reduce the number of patients who receive inferior treatment while still accruing convincing evidence within the clinical trial. (There have been interesting discussions of the ethics of randomization and adaptive randomization (8–12), but we do not discuss this aspect of clinical trial design here.) We discuss an example of Bayesian adaptive randomization later in this chapter.

REQUIREMENTS FOR A SUCCESSFUL BAYESIAN DESIGN As with all clinical studies, considerable work has to go into the preparation of the study design. The statistician and the clinical investigators need to discuss the study’s aims and objectives. Care must go into selecting end points for the primary and secondary aims of the study. Much of these considerations are discussed elsewhere in this volume, so we will focus more on the aspects that relate to the Bayesian part of the design. In particular, we will talk about the prior distribution and stopping rules. Additionally, if one takes a decision-theoretic approach, one will have to consider the utility function that accounts for the study’s aims. If one wishes to calibrate the design, then one will have to review with the other investigators the implication of various decision-rule parameters on the operating characteristics. Software for Real-Time Updating Real-time updating is an important aspect of modern Bayesian trial designs. These designs incorporate early stopping rules, allowing the investigator to stop early for lack of efficacy, superiority, or excessive toxicity. For example, in a single-arm phase II study that will compare the progression free survival (PFS) associated with a new treatment to historical information for one or several standard treatments, an investigator may desire to stop the study early if there is evidence that the new treatment results in worse outcomes than the historical standard. A Bayesian approach to this problem might assume that PFS follows an exponential distribution (with rate parameter q ) and, with a conjugate gamma prior, that q follows, a posteriori, a gamma distribution. A common stopping rule under this setup is to stop the trial if at any point Pr(q > q *| Data) > C (where q * usually represents some historical event rate and C is some pre-specified threshold value). One computes this probability each time a new patient (or group

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14 BAYESIAN DESIGNS IN CLINICAL TRIALS

of patients) enters the study or when a patient already enrolled experiences disease progression. Typically, calculation of the above probability requires numerical integration, and one must develop statistical software to carry out the calculations necessary to monitor the accruing data and determine whether the interim stopping boundaries have been crossed. By software, we include R scripts or SAS macros written solely for use by the collaborating statistician, stand-alone desktop computer programs written for use by other statisticians, or even Web-based applications for use by nonstatistical research staff. The kind of application one develops is a function of who the end user will be and how often future studies may use the same sort of design. For example, it may be sufficient for the collaborating statistician to have a function that runs within a general purpose statistical or mathematical package when carrying out a singleinstitution study that will evaluate outcomes for a rare disease with slow accrual in which posterior updating will be necessary only every 4 to 6 weeks. In contrast, a rapidly accruing multicenter, multiarm study may require real-time updating via a Web-based application or a telephone voice-response system. Part of the work involved in implementing Bayesian methods is to determine the exact software needs of the particular study’s design. Below we describe a set of commonly used trials that require real-time updating.

Types of Studies Phase I Oncology Dose-finding Study Many drugs used in oncology are associated with severe toxicities and have a narrow therapeutic window, meaning that there is only a small range of doses that may be efficacious without being overly toxic. Therefore, the initial step in assessing these compounds in humans usually focuses on finding a dose that has an acceptable level of toxicity. Because one of the most important constraints on the conduct of these initial trials is the desire to limit the number of patients who experience severe toxicity, these studies are conducted with dose escalation proceeding in a sequential manner. That is, the study enrolls small cohorts of patients (e.g., three to six) and does not assign a higher dose until each patient in a given cohort has been through at least one cycle of treatment and their outcomes assessed. The toxicity outcomes observed from these (and earlier) patients may enter into an algorithm that the investigators use to select the dose for the next cohort. The purpose of this sequential approach is to decrease the chance that large numbers of patients receive doses that are too toxic.

The assumption underlying this approach in oncology, at least, is that toxicity and response are correlated through dose. That is, higher doses lead to an increase in the toxicity risk and an increase in the probability that a patient will respond to treatment. This assumption was historically reasonable in oncology, where one defined activity in terms of killing cancer cells. Thus, phase I oncology studies have traditionally attempted to determine the highest dose that has an acceptable toxicity level, since by assumption this dose will also lead to greater efficacy than lower doses. Bayesian phase I designs treat a patient’s risk of toxicity at a given dose as a quantity about which the investigator has some degree of uncertainty. One quantifies this uncertainty via a probability distribution. Decisions to escalate the dose, continue with the current dose, or de-escalate from the current dose incorporate the most current data. Given what one has learned to date, one will treat the next patient with the dose with an expected risk of toxicity that is closest to a predefined target toxicity risk. In such a setting, Bayesian methods offer clear advantages. The Bayesian framework provides a means by which one can learn about toxicity risks at the different doses and naturally make decisions based on the data observed in a sequential manner. The increase in knowledge is reflected by a decrease in uncertainty as one moves from prior to posterior. Phase II Adaptive Randomization Trials Bayesian adaptive randomization designs successively (as patients are evaluated for outcome) modify the randomization probabilities based on either posterior or predictive probabilities favoring one treatment over another. In essence, data from patients previously enrolled and evaluated in a study are used so that patients currently enrolling onto the trial will have a higher probability of being randomized to the most efficacious treatments. In these types of designs, subjects are initially randomized fairly (i.e., with equal probability) to the various (at least two) treatment arms. Since many adaptive randomization trials usually have a period in which patients are equally randomized prior to the implementation of adaptive randomization, it is important that the statistician monitor the actual randomization versus expected randomization. Other Trials Other interesting and useful examples of successful Bayesian applications in the design of clinical trials include single-treatment phase II studies that consider efficacy and toxicity, with stopping rules based on both

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end points (13–16). Another interesting innovation is the so-called seamless phase II/III design (17, 18). With this design, randomization begins within the context of a small phase II study that collects survival information but has an intermediate end point as the primary outcome. Based on early results with respect to the intermediate end point, however, the study may expand to a large randomized phase III study with survival as the primary outcome. Berry et al. discuss a design that simultaneously sought the best dose of a drug in an adaptive way and maintained a randomized comparison with placebo (19). Other examples exist in the literature (20). As mentioned earlier, the Bayesian inferential machinery fits well with decision theory. Once one has determined an appropriate utility function, one can set up the design to optimize the utility. Furthermore, one can carry out sequential decision making, either fully via backward induction (21) or by looking ahead one or a few steps. In all cases, one maximizes the utility, taking into account posterior uncertainty. There also exist more formal Bayesian designs for clinical trials. Berry argues for the application of decision theory in clinical trial design (3, 4). Kadane (22) presents an interesting example of a clinical trial, describing the background and development of the study. The literature includes other examples of formal Bayesian designs (23–26). Rossell et al. (27) and Ding et al. (28) present decision-theoretic designs for phase II studies that screen out active therapies from among a sequence of new treatments.

Realistic Priors Historical Priors Often, there have been earlier studies with one or more of the agents under investigation in the current study. These data usually inform the study’s design, either informally (as in determining the null and alternative hypotheses in frequentist designs) or formally via a prior distribution. One may find, however, that if one assumes that the current study’s patients will be exchangeable with the historical information, the historical information will be extremely informative with respect to inference during the current study. In fact, in some cases, it may well be that there is little reason to embark on the current study, given the evidence in the historical information. (In many situations, it may well be appropriate to consider whether there really is a need for the current study, given the strength of historical evidence. That is a topic for another discussion, however.) Since the current study will go forward, one has to find a way to discount the historical information

or choose not to assume that the patients in the current study are exchangeable with the earlier studies. If we consider a binary outcome, such as treatment success or failure (however defined), then we might characterize the historical data by means of a beta distribution. For example, if an early study enrolled 50 patients, and 30 patients experienced a treatment success, we might characterize the uncertainty about the treatment’s underlying success probability by a beta distribution with parameters equal to 30 and 20. One might think of this prior as the posterior distribution arising from an experiment that gave rise to these data and a fully noninformative beta[0,0] prior. (Alternatively, one could consider an initial uniform[0,1] prior or a Jeffreys beta[0.5, 0.5] prior and determine a posterior beta distribution with slightly different parameters[1].) Now, one might feel that the beta[30,20] prior is too informative for this study. For example, this distribution has 95% of the central mass between 0.46 and 0.73. If one wants to entertain the possibility of smaller success probabilities than 0.4, then one may want to discount this prior data in some way. A natural way to keep the prior mean 0.6 but increase the uncertainty is to decrease the prior sample size. For example, one might choose to reduce prior information to the equivalent of a prior sample size of 5 by way of a beta[3, 2] distribution. Now the central 95% of the mass lies between 0.19 and 0.93. A related approach for discounting the historical information is with a power prior (29, 30). The power prior extends the notion of discounting to a general class and allows for inference with respect to the degree of discounting. Briefly, one considers a parameter in the probability model that will characterize the level of discounting for the historical information. The basic idea of the power prior is that the more similar the prior and current data are, the less discounting that takes place and vice versa. Let L (q | D) represent the likelihood function that will characterize the data at the end of the current study (i.e., after collecting the data represented by D). Using the same likelihood function with the historical data DH, the power prior is p(q | DH, δ) ∝ L(q | DH )δ p(q | f), where the parameter f is a hyperparameter for an optional initial prior. The parameter d will serve to discount or down-weight the information content of the historical data when one will apply this prior to carry out posterior inference in the analysis of the current study. Another way people have discounted prior information is less direct: they have modified parameters in the stopping rules to make it more difficult to stop early. In other words, one uses the historical information to generate an informative prior but makes the


cutoff for early stopping more stringent than perhaps one would normally consider reasonable. For example, if one is basing the stopping rule on a criterion based on the posterior probability that some parameter or function of model parameters exceeds a threshold, one may require a very high probability (e.g., 99%) of this event before considering early stopping. Making the stopping rule more stringent basically provides a way to keep the prior from dominating early decision making and allows the current study to continue accumulating data. The process of determining the boundary criteria often proceeds iteratively. One determines the criteria for early stopping by carrying out simulations under various scenarios and then deciding which stopping rules lead to satisfactory operating characteristics. Although such devices tend to make the designs acceptable to frequentists, because of the calibrated operating characteristics, they also may tend to undermine the benefit of the underlying Bayesian model. The historical information may become almost neglected or, at most, these data enter into the design as a formality without giving full consideration of their importance to the inferential question under investigation. Elicitation of Experts Elicitation of priors from experts would seem a reasonable approach, especially in the absence of historical data. Carlin et al. (31) describe their experience eliciting prior information for a clinical trial. Problems may occur in a clinical trial for which the experts may have provided a prior that subsequently appears to be at odds with the data. An informative example is discussed by Carlin et al. in the context of a randomized clinical trial evaluating the benefit of prophylaxis against possible infection with toxoplasmic encephalitis (TE) (32). In this study, the five experts whose opinions went into the prior distribution turned out to have been overly optimistic. Each expert anticipated a treatment benefit. Although there was widespread disagreement among these five individuals, none considered the possibility that the treatment would be no better than placebo, let alone worse. The key points resulting from these investigators’ experience with this study are instructive. In particular, the experts may provide point estimates, but there is underlying uncertainty in each expert’s opinion. Perhaps a mixture of these separate prior distributions will be more robust to the analysis than combining the experts’ point estimates into a single prior. Another point brought out in this study was that different experts might find it easier to specify priors for the effect of the treatment on different end points. For

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example, one expert was not able to provide a prior estimate of the effect of the treatment on the risk of death or TE, whereas the other four could and did. In our experience, it is also important that those whose opinions one seeks see the consequences of their a priori estimates. Graphical displays of uncertainty distributions or of observable quantities, given prior specification, allow the experts to gain insight into the implications of their stated beliefs (16, 33). Quite often, this feedback reveals inconsistencies and leads to revisions. Thus, one has to be careful about incorporating expert opinion into a prior distribution for a clinical trial’s design. Operating Characteristics One of the biggest challenges to utilizing Bayesian methods when designing studies is having software available to assess the operating characteristics of a design. For any Bayesian design used in practice, the collaborating statistician must provide operating characteristics that summarize the behavior of the proposed method under a wide variety of situations (called scenarios). Because these designs typically involve complex models and decision rules, one has to carry out simulations to evaluate the operating characteristics of the proposed design. Some of the characteristics that one typically summarizes are the number of patients assigned to each treatment, the probability of selecting each dose as most efficacious, the probability of stopping a trial if all treatments are too toxic, etc. The statistician typically considers a wide variety of possible scenarios ranging from very pessimistic, such as the case when no treatment provides any benefit, to optimistic cases in which several of the treatments are effective. Purpose of Checking Operating Characteristics (Calibration) Controversy Surrounding Evaluation of Frequentist Properties If one has chosen to demonstrate the frequentist characteristics of the Bayesian design, then one will have to simulate the design under different scenarios. It may seem odd to want to evaluate the frequentist characteristics of a proposed Bayesian design, but some reasons are as follows. First, one may want to convince the non-Bayesian audience that the proposed design offers benefits over standard frequentist designs without incurring a loss in terms of the frequentist characteristics. For example, some sequential designs base their stopping rules on posterior probability calculations, such as Prob(treatment difference > delta | Data) > cutoff. One

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can certainly view these posterior probabilities as test statistics, being functions of the data, even though they differ from more common test statistics. Thus, one can evaluate the operating characteristics. Another reason one might want to estimate the operating characteristics of the proposed design is to evaluate how robust the design is under different scenarios. If one feels that the prior distribution is based on rather limited historical information, for example, then one might want to ensure that the prior does not overly dominate inference in certain situations. Potential Pitfalls Potential pitfalls include not stopping when one should, stopping a study and later regretting it, and the often perceived possibility that the study’s Bayesian analysis will not receive widespread acceptance. The surest way to avoid these problems is to carry out simulations under many, many different scenarios. EXAMPLES OF BAYESIAN DESIGNS What Worked and Why We have seen dozens of successful Bayesian clinical trials at the M. D. Anderson Cancer Center. One characteristic that has contributed to successful implementation is a schedule of regular meetings between the statisticians and the clinical research staff during the trial’s design stage. The meetings serve to educate both groups to the other’s needs and perspectives. After initiation of patient enrollment, meetings between the research staff and the statistician continue for the purpose of interim review of the trial’s progress. Also, the statistician should provide some data management oversight to ensure that the database accurately reflects the trial data. Clear communication between the clinical investigators and statisticians with respect to what a design can and cannot do is essential. It is also vitally important for the statistician to test the computer code and interface to ensure everything is working properly. Is the program computing the posterior probabilities correctly? Do the results and recommendations in different hypothetical situations make sense mathematically and clinically? Is the user interface (for example, a stand-alone graphical user interface or a Web-based application) intuitive and easily navigated by the individuals who will be using it? Does the interface perform appropriately? These are important questions to address while preparing the protocol and well before the study enrolls the first patient if one wants to realize the full potential of the Bayesian design. When clinical studies with Bayesian designs work well, the

benefits of these designs are very much appreciated by the collaborating investigators. Below we give three examples of clinical studies from our institution (from a potential list of dozens). Correlated Ordinal Toxicity Monitoring in Phase I In this example, investigators used a Bayesian design within a new statistical framework for dose-finding based on a set of qualitatively different, ordinal-valued toxicities (34). The objective of this trial was to assess the toxicity profile associated with the anticancer drug gemcitabine when combined with external beam radiation to treat patients with soft-tissue sarcoma. The study’s design allowed for possible evaluation of a total of 10 gemcitabine doses, combined with a fixed dose of radiation. Traditionally, phase I studies in oncology consider a binary end point as the primary outcome. This binary end point is an indicator of whether or not each patient experienced a dose-limiting toxicity, as defined in the protocol. This single end point reduces all toxicity information across grade or severity of the toxicity and across organ systems into a single yes-orno outcome. (Berry et al. discuss the use of a hierarchical model to borrow strength across types of toxicities within organ systems in the context of drug safety monitoring [35]). In most phase I oncology settings, however, the patient is at risk of several qualitatively different toxicities, each occurring at several possible levels of severity. Moreover, the different toxicities often are not of equal clinical importance. The design of this soft-tissue sarcoma phase I study represented a radical departure from conventional phase I study design in oncology. It was based on an underlying probability model that characterized the relationship between dose and the severity of each type of toxicity. The model included a set of correlated normally distributed latent variables to induce associations among the risks associated with the different toxicities. Additionally, there were weights or numerical scores to characterize the importance of each level of each type of toxicity. The statistician met with the physicians prior to initiation of the trial to elicit from them these scores. An algorithm combined the scores associated with each type and level of toxicity with the probability of observing each particular type and level of toxicity. This algorithm produced a weighted average toxicity score. This weighted average toxicity score informed decisions about doses for successive cohorts of patients in this phase I study. Concerns expressed by the oncologists motivated the development of this design. The clinicians wanted a dose-finding method that would account for the fact


that, clinically, the toxicities that they had identified are not equally important. Additionally, the different toxicities do not occur independently. The investigators also requested that the dose-finding method utilize the information contained in the grade or severity of an observed toxicity. That is, if patients experience a low-grade toxicity at a given dose, while not dose limiting, this event suggests that higher doses may be more likely to lead to a higher grade of that toxicity. The Bayesian framework of this study’s design was capable of addressing all of the investigators’ concerns regarding characterization of toxicity while also incorporating key design aspects required for institutional approval of the protocol, such as early trial termination for excessive toxicity at the lowest dose. At the end of the study, the model recommended a dose to take forward into phase II, and the investigators were in complete agreement with this choice as the appropriate dose. Joint Modeling Toxicity and Biomarker Expression in a PhaseI/II Dose-Finding Trial In this example, the investigators used a Bayesian framework to model jointly a binary toxicity outcome and a continuous biomarker expression outcome in a phase I/II dose-finding study of an intravesical gene therapy for treating superficial bladder cancer (36). Since the toxicity and efficacy profiles of the gene therapy were unknown, the investigators proposed a phase I/II dose-finding study with four possible doses. This trial’s motivation was partially attributable to the increasing use of biomarkers as indicators of risk or as surrogate outcomes for activity and efficacy. In many contexts, the biomarker is observable immediately after treatment, allowing the investigators to learn about the therapeutic potential of the compound without having to wait months or even years as survival data mature. Unlike conventional phase I studies, this study’s objective was to determine the best dose based on both biomarker expression and toxicity. This dual outcome required a joint model for the two end points. For ethical reasons, the study escalated doses between patients sequentially. An algorithm based on the joint model chose the dose for each successive patient using both toxicity and activity data from patients previously treated in the trial. The modeling framework incorporated a correlation between the binary toxicity end point and the continuous activity outcome via a latent Gaussian random variable. The dose-escalation/de-escalation decision rules were based on the posterior distributions of model parameters relating to toxicity and to activity. The study’s

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stopping rule called for it to stop if the estimated risk of toxicity appeared excessive or if there was clear evidence that the treatment was not modulating the biologic marker. The Bayesian framework used in this study allowed for flexible modeling of some rather complicated outcomes. In addition, this framework provided a coherent mechanism for incorporating prior information into the modeling process. The study ended, in fact, when it became evident that the drug was not modulating the biologic marker. Adaptive Randomization Investigators wished to evaluate the effectiveness of combinations of three drugs (an immunosuppressive agent, a purine analog anti-metabolite, and an antifolate) to prevent graft-versus-host disease (GVHD) after transplantation (37). The study used adaptive randomization and was to enroll a maximum of 150 patients. A success was defined in this study as “alive with successful engraftment, without relapse, and without a GVHD 100 days after the transplant.” The design called for comparing each treatment to the control arm (i.e., the combination treatment with the immunosuppressive agent and anti-folate) in terms of the probability of success in the following manner. Let p0 be the success probability in the control arm. Similarly, let p1, p2, p3, and p4 be the success rates in the 4 other treatment arms (three-arm combination treatments with varying doses of the purine analog antimetabolite). As information accrued about the treatments, the investigators altered the randomization probabilities from equal randomization to biased randomization based on the posterior probability that each treatment-specific success probability exceeded that of the control arm. That is, the randomization would adapt to favor treatments associated with success probabilities that were greater than that of the control via P(pk > p0 | data) (for k = 1, 2, 3, 4) after appropriate scaling. In addition, the study’s design allowed for early stopping based on predictive probabilities. Specifically, the investigators dropped a treatment arm if the predictive probability that its success probability will be greater than p0 was less than 0.05, given the data at hand and the data yet to accrue. The design was successful in that it limited the number of patients who received the inferior treatments to 18.2% of all of the 110 patients randomized to one of the four experimental arms. By contrast, a design that randomized patients equally to the treatments and did not allow for early stopping would have exposed 50% of patients to these ineffective therapies.

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What Did Not Work and Why When designing clinical studies, the collaborating statistician should be aware of potential pitfalls associated with the design or designs of choice. This is true of Bayesian designs, which may have some unique issues to consider. The most common difficulties include problems with the computer code, such as bugs that lead to incorrect posterior probability calculations; human error in data entry and management; and reconciling differences in how statisticians (or statistical models) define adequate evidence of treatment effects and how physicians define these effects. Below we give examples of three of these potential problems and discuss steps one can take to avoid them. Over time, Bayesian designs have found more application and become more complicated. While most of the designs developed in the early 1990s focused on binary end points, current implementations include models for time-to-event end points that include parameter effects for treatment, patient-specific covariates (e.g., patient’s risk of death) and covariate-bytreatment interactions (e.g., Xian et al. [38]). For very simple designs based on a binary end point, the data management requirements for posterior updating were relatively straightforward. These types of models only require keeping track of the number of patients in the trial and the total number of patients who have experienced the event of interest. In contrast, as the models have become increasingly complex, more data (and more data management) are required for calculation of posterior probabilities. As a consequence, an increase in data management can lead to data entry errors. For example, Maki et al. (39) describe a two-arm open-label phase II clinical study in sarcoma with tumor response as the primary end point. The study employed a Bayesian adaptive randomization procedure that accounted for treatment-by-sarcoma-subgroup interactions. Specifically, the adaptive randomization scheme incorporated information on the type of sarcoma. After randomizing the first 30 patients equally to the two treatment regimens, the design called for adapting the randomization probabilities for subsequent patients to favor the better performing treatment, according to the accrued data. The investigators subsequently found that the initial recorded sarcoma subtypes for some patients were incorrect. The consequence of this incorrect labeling was that, for one sarcoma subtype, the probability of randomization to the top performing arm was less than it should have been, relative to the other treatment arms. While in this example all patients continued to have higher probability of randomization to the better performing treatment arm, it is conceivable that if such an error were

not discovered early, patients could have been randomized to inferior treatments. Therefore, it is extremely important that the statistician be involved with data-management oversight to ensure that such errors do not occur. One of the key considerations in designing Bayesian clinical trials involves navigating the relationship between the proposed Bayesian model and the realities of medical research. A model may indicate that one treatment confers benefit over another (calculated via posterior probabilities), but if one is claiming this benefit on a very small number of patients, one is going to have a hard time convincing a medical audience that the results are robust (robust in an English and not statistical sense). For example, Giles et al. (40) reported a phase II trial that randomized patients to receive one of three treatment regimens: idarubicin and ara-C (IA); troxacitabine and ara-C (TA); and troxacitabine and idarubicin (TI). The study’s Bayesian design adaptively randomized patients to the treatments. Initially, there was an equal chance for randomization to IA, TA, or TI, but treatment arms with higher success proportions progressively received a larger fraction of patients. The adaptive randomization led to a total of 18 patients randomized to the IA arm; 11 patients randomized to the TA arm; and just 5 patients randomized to the TI arm. The small sample size associated with the TI arm left this trial open to concerns that the results were not conclusive. This story is reminiscent of the controversy surrounding the early randomized trials of extracorporeal membrane oxygenation (ECMO) for neonates in respiratory failure. Two early ECMO trials (41, 42) included adaptive randomization algorithms that led to very few babies receiving the non-ECMO treatment. In the end, a vocal part of the medical community seemed to think that these trials included too few patients treated conventionally (i.e., without ECMO) to justify making ECMO the standard treatment for neonates in respiratory distress. (See Ware and related discussion for more information about the ECMO trials [43].) Eventually, a randomized clinical trial without adaptive randomization in the United Kingdom demonstrated the benefit of ECMO (44). The lesson to learn is that one should ensure that the trial will include some minimum number of patients in all treatments (subject to safety assurances) before it begins to adapt the randomization in light of the accruing evidence. A common criticism voiced by some investigators with whom we have collaborated relates to recommendations based on Bayesian models that do not match the investigators’ expectations based on experiences with other designs. This tension is


exemplified in the context of dose escalation decisions in phase I studies in oncology. Although we described and illustrated Bayesian phase I oncology studies earlier in this chapter, most of these phase I studies use non-Bayesian algorithms for dose-finding, such as the 3 + 3 design (45). Their popularity is driven by the fact that clinicians can easily understand these trial designs, and the decision rules employed make intuitive sense. Yet, much is left unspecified in the implementation of these methods. For example, algorithmic designs implicitly target toxicity risks smaller than 33% (1 in 3) as being acceptable. In contrast, while Bayesian phase I designs may seem (to some clinicians) to be black boxes, these models make explicit the outcomes being targeted. In particular, all Bayesian designs explicitly specify a target probability of toxicity (usually between 25% and 33%). We believe that one of the main reasons this criticism occurs is a lack of communication between the statistician and the clinical investigator. This lack of communication may result, in part, from difficulty explaining these methods to non-statisticians (46). One way to overcome these difficulties is by making the underlying assumptions of the Bayesian model clear to the investigator. One can illustrate these assumptions by providing the investigator with sample trajectories of virtual trials simulated under different scenarios, in addition to providing the operating characteristics of the trial’s average behavior (as discussed earlier in this chapter). While potentially time consuming, this type of upfront examination and assessment before the study begins will help the clinician understand both the merits and limitations of the design and underlying model contained in the protocol.

SUMMARY OF RECOMMENDATIONS In this chapter, we have illustrated the use of Bayesian methods in the design of clinical studies. Although we work with investigators interested in treating cancer, the examples illustrate ideas that are applicable in all disease areas. The main advantages of Bayesian ideas in the design of clinical trials are the inherent flexibility of Bayesian inference; the ease with which one can incorporate information from outside of the study, including measured outcomes of mixed types (e.g., continuous and discrete); the natural notion of evolving knowledge evinced by the transformation from prior uncertainty to posterior uncertainty based on observations; and the way the Bayesian methodology allows one to make decisions and maximize utility, taking into account all uncertainty captured in the

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basic probability model. Although our examples concerned novel designs and new methodology, Bayesian ideas are applicable when designing any clinical study.

References 1. Carlin BP, Louis TA. Bayesian Methods for Data Analysis, 3rd ed. Boca Raton: Chapman & Hall/CRC; 2008. 2. Little RJ. Calibrated Bayes: A Bayes/Frequentist roadmap. Am Stat. 2006;60(3):213–223. 3. Berry DA. A case for Bayesianism in clinical trials. Stat Med. 1993;12(15–16):1377–1393; discussion 95–404. 4. Berry DA. Decision analysis and Bayesian methods in clinical trials. In: Thall PF, ed. Recent Advances in Clinical Trial Design and Analysis. Boston: Kluwer Academic Publishers; 1995:125–154. 5. Jennison C, Turnbull BW. Group sequential methods with applications to clinical trials. Boca Raton, FL: Chapman & Hall/CRC; 1999. 6. Berger JO, Wolpert RL. The Likelihood Principle. Hayward, California: Institute of Mathematical Statistics; 1984. 7. Thall PF, Wathen JK. Practical Bayesian adaptive randomisation in clinical trials. Eur J Cancer. 2007;43(5):859–866. 8. Anscombe FJ. Sequential medical trials (Com: p384–387). J Am Stat Assoc. 1963;58:365–383. 9. Armitage P. Sequential medical trials: some comments on F. J. Anscombe’s paper. J Am Stat Assoc. 1963;58(302):384–387. 10. Armitage P. The search for optimality in clinical trials. Int Stat Rev. 1985;53(1):15–24. 11. Bather JA. On the allocation of treatments in sequential medical trials. Int Stat Rev. 1985;53(1):1–13. 12. Royall RM. Ethics and statistics in randomized clinical trials. Stat Sci. 1991;6(1):52–62. 13. Thall PF, Sung HG. Some extensions and applications of a Bayesian strategy for monitoring multiple outcomes in clinical trials. Stat Med. 1998;17(14):1563–1580. 14. Thall PF, Simon RM, Estey EH. New statistical strategy for monitoring safety and efficacy in single-arm clinical trials. J Clin Oncol .1996;14(1):296–303. 15. Thall PF, Simon RM, Estey EH. Bayesian sequential monitoring designs for single-arm clinical trials with multiple outcomes. Stat Med. 1995;14(4):357–379. 16. Thall PF, Cook JD. Dose-finding based on efficacy-toxicity trade-offs. Biometrics. 2004;60(3):684–693. 17. Inoue LYT, Thall PF, Berry DA. Seamlessly expanding a randomized phase II trial to phase III. Biometrics. 2002;58(4):823–831. 18. Thall PF. A review of phase II/III clinical trial designs. Lifetime Data Anal. 2008;14(1):37–53. 19. Berry DA, Müller P, Grieve AP, et al. Adaptive Bayesian designs for dose-ranging drug trials. In Gatsonis C, Carlin B, Carriquiry A, eds. Case Studies in Bayesian Statistics V. New York: Springer-Verlag; 2001:99–181. 20. Spiegelhalter DJ, Abrams KR, Myles JP. Bayesian Approaches to Clinical Trials and Health-Care Evaluation. Chichester, UK: Wiley & Sons; 2004. 21. DeGroot MH. Optimal Statistical Decisions. New York: McGraw-Hill; 1970. 22. Kadane JB, ed. Bayesian Methods and Ethics in a Clinical Trial Design. New York: Wiley & Sons; 1996. 23. Berry DA, Wolff MC, Sack D. Decision making during a phase III randomized controlled trial. Cont Clin Trials. 1994;15(5):360–378. 24. Carlin BP, Kadane JB, Gelfand AE. Approaches for optimal sequential decision analysis in clinical trials. Biometrics. 1998;54(3):964–975. 25. Stallard N, Thall PF. Decision-theoretic designs for pre-phase II screening trials in oncology. Biometrics. 2001;57(4):1089–1095.

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26. Stallard N, Thall PF, Whitehead J. Decision theoretic designs for phase II clinical trials with multiple outcomes. Biometrics. 1999;55(3):971–977. 27. Rossell D, Müller P, Rosner GL. Screening designs for drug development. Biostatistics. 2007;8(3):595–608. 28. Ding M, Rosner GL, Müller P. Bayesian optimal design for phase II screening trials. Biometrics. 2008;64(3):886–894. 29. Chen M-H, Ibrahim JG. The relationship between the power prior and hierarchical models. Bayesian Anal. 2006;1(3): 551–574. 30. Ibrahim JG, Chen MH. Power prior distributions for regression models. Stat Sci. 2000;15(1):46–60. 31. Carlin BP, Chaloner K, Church T, Louis TA, Matts JP. Bayesian approaches for monitoring clinical trials with an application to toxoplasmic encephalitis prophylaxis. Statistician. 1993;42(4):355–367. 32. Carlin BP, Chaloner KM, Louis TA, Rhame FS. Elicitation, monitoring, and analysis for an AIDS clinical trial (with discussion). In Gatsonis C, Hodges JS, Kass RE, Singpurwalla ND, eds. Case Studies in Bayesian Statistics, Vol. II. New York: Springer-Verlag; 1995:48–89. 33. Chaloner K, Church T, Louis TA, Matts JP. Graphical elicitation of a prior distribution for a clinical trial. Statistician. 1993;42(4):341–353. 34. Bekele BN, Thall PF. Dose-finding based on multiple toxicities in a soft tissue sarcoma trial. J Am Stat Assoc. 2004;99(465): 26–35. 35. Berry SM, Berry DA. Accounting for multiplicities in assessing drug safety: a three-level hierarchical mixture model. Biometrics. 2004;60(2):418–426. 36. Bekele BN, Shen Y. A Bayesian approach to jointly modeling toxicity and biomarker expression in a phase I/II dose-finding trial. Biometrics. 2005;61(2):343–354. 37. de Lima M, Couriel D, Munsell M, et al. Pentostatin, tacrolimus, and “mini”-methotrexate for graft-versus-host

38. 39.

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disease (GVHD) prophylaxis: A phase I/II controlled, randomized study. Blood (ASH Annual Meeting Abstracts) 2004;104:727. Xian Z, Suyu L, Kim ES, Herbst RS, Lee JJ. Bayesian adaptive design for targeted therapy development in lung cancer—a step toward personalized medicine. Clin Trials. 2008;5(3):181–193. Maki RG, Wathen JK, Patel SR, et al. Randomized phase II study of gemcitabine and docetaxel compared with gemcitabine alone in patients with metastatic soft tissue sarcomas: results of sarcoma alliance for research through collaboration study 002 [corrected]. J Clin Oncol. 2007;25(19):2755–2763. Giles FJ, Kantarjian HM, Cortes JE, et al. Adaptive randomized study of idarubicin and cytarabine versus troxacitabine and cytarabine versus troxacitabine and idarubicin in untreated patients 50 years or older with adverse karyotype acute myeloid leukemia. J Clin Oncol. 2003;21(9):1722–1727. Bartlett RH, Roloff DW, Cornell RG, Andrews AF, Dillon PW, Zwischenberger JB. Extracorporeal circulation in neonatal respiratory failure: a prospective randomized study. Pediatrics. 1985;76(4):479–487. O’Rourke PP, Crone RK, Vacanti JP, et al. Extracorporeal membrane oxygenation and conventional medical therapy in neonates with persistent pulmonary hypertension of the newborn: a prospective randomized study. Pediatrics. 1989;84(6): 957–963. Ware JH. Investigating therapies of potentially great benefit: ECMO (with discussion). Stat Sci. 1989;4(4):298–340. UK Collaborative ECMO Trial Group. UK collaborative randomised trial of neonatal extracorporeal membrane oxygenation. Lancet. 1996;348(9020):75–82. Korn EL, Midthune D, Chen TT, Rubinstein LV, Christian MC, Simon R. A comparison of two phase I trial designs. Stat Med. 1994;13:1799–1806. Rosenberger WF, Haines LM. Competing designs for phase I clinical trials: a review. Stat Med. 2002;21(18):2757–2770.

15

The Trials and Tribulations of Writing an Investigator Initiated Clinical Study Nicole P. Grant Melody J. Sacatos Wm. Kevin Kelly

Most clinical trials sponsored by industry or specialized groups such as the National Institutes of Health cooperative groups come to the investigator through a well-defined route with accompanying documentation structuring the conduct of the trial. Not so with the investigator-initiated clinical trial. Hence, trial and tribulation may be inevitable when you initiate your own clinical trial if you don’t know what you need to do and plan for the trial. A clinical trial in health care may be defined as “a research study involving human subjects, designed to evaluate the safety and effectiveness of new therapeutic and diagnostics treatments” (www.hss.energy .gov/healthsafety/ohre/roadmap/achre/glossary.html). Others have defined a clinical trial as “a systematic investigation of the specific treatments according to a formal research plan in patients with a particular disease or class of diseases” (www.jhu.edu/wctb/coms/ booklet/book5.htm). The Food and Drug Administration (FDA) defines a clinical trial as “any experiment in which a drug (or biologic) is administered or dispensed to, or used involving, one or more human subjects” (www.accessdata.fda.gov- CFR—Code of Federal Regulations Title 21). Whether we are conducting an early phase I or a phase III study, all trials typically have in common: a hypothesis supported by scientific data, a method to conduct safe research, and a plan to evaluate the outcomes. A well-written clinical study should be a

free-standing document that can support the study rationale and be a complete roadmap to conduct the research. Writing a good clinical trial is both a science and an art which has evolved over the years. Due to the increased regulatory concerns along with more sophisticated and complicated therapies, clinical trials are increasingly becoming more complex. To aid in writing clinical trials there have been multiple templates developed for phase I, phase II, or phase III studies and the details of the trial vary pending on whether the study is an institutional investigator–initiated trial, a cooperative group trial, or an industry-based trial. The basic principles and sections of a study remain constant although the order and depth of involvement may vary between the type, phase, and sponsor of the study. For individuals who want to write a trial, the National Cancer Institute’s (NCI) Cancer Therapy Evaluation Program (CTEP) has made significant investments in the development of standardized protocol templates that cover a wide range of types of studies to facilitate the development of novel therapies by individual investigators. These templates can be accessed at http:// ctep.cancer.gov/protocolDevelopment/templates _applications.htm and all investigators interested in writing protocols should review this site (1). While the development of a protocol is driven by the principal investigator, this is a team effort made of coinvestigators, statisticians, clinical research nurses, data managers, regulatory experts, and editors.

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Coordinating all the required inputs to ensure a scientifically sound protocol that is feasible and compliant with all required external and internal regulations, policies, and best practices can be a time-consuming and sometimes tedious task. A designated protocol coordinator can be indispensable in collecting all of the essential perspectives and incorporating them into the protocol for the investigator to review so that the study may move forward in a timely and well-integrated manner. The protocol coordinator may be the research nurse or a protocol developer/regulatory expert or editor with basic understanding and literacy of the science involved. Some academic medical centers offer specific expertise and assistance through their clinical trials office that may help. More recently, computerized collaborative clinical trial writing systems have been developed which have facilitated the protocol writing process (2). Regardless, it is essential that there be a capable individual designated as the coordinator of the development effort and that all of the critical elements of a protocol are considered. This chapter will provide some basic principles on writing a therapeutic investigator-initiated study; and it will highlight some of the pitfalls and the obscurities that may be encountered in writing a protocol. These principles can be applied to most clinical therapeutic trials regardless of the type, phase, or sponsor of the study. Table 15.1 is a list of the basic sections

TABLE 15.1

Protocol Requirements. · · · · · ·

· · · · · · · · · · · · ·

Title page Protocol schema or synopsis Table of contents Study objectives Background Patient selection (eligibility criteria) · Inclusion criteria · Exclusion criteria Registration procedures Treatment plan Dosing delays and dose modifications Adverse event reporting, safety monitoring, and quality assurance Pharmaceutical information Correlative and special studies Study calendar Measurement of effect or outcome measures Data reporting Statistical considerations References Informed consent Appendices

that are required in most protocols, and we will review these sections in more detail below.

PREPARING TO WRITE A CLINICAL STUDY Prior to actually writing the protocol, it is useful to prepare a brief protocol concept sheet or a letter of intent that can be presented to the research team to review. The concept sheet should give a brief rationale of the study, primary objectives, study population, outcome parameters, sample size, and whether correlative studies are to be included. Most importantly the concept sheet should provide why this study or concept is important and whether the risk/benefit ratio to the subject population involved is favorable. How is this research going to change the current treatment practices? How do you build on the result of the trial? What is the next clinical trial if results are positive? Is this study ethically sound? Does the study’s potential benefit(s) outweigh the potential risk(s) to subjects? It is always important to ask what the next step is and whether this study brings benefit to individual subjects or a population of subjects; or increases meaningfully scientific knowledge. If it does not answer these questions, then you need to really consider why you are doing this study. The research group should evaluate the concept critically and pose the following questions: 1. Are the objectives well defined and obtainable? 2. Is the study population well defined to answer the objectives? 3. Is the study population available to study this question? Include estimated anticipated drop-out rate of those screened versus those enrolled and those expected to complete the study. 4. Do we have the appropriate statistical design and power to give confidence in the results? Do the objectives correlate with the outcome measures? Are the outcome measures well defined and measurable? 5. Are the correlative studies appropriate and doable? 6. What is the funding source of the trial and is the funding sufficient to complete the study? It is also important at this stage to consider whether the study will be investigational new drug (IND)-exempt or require an application to the FDA to obtain approval to conduct the trial. When in doubt, a regulatory expert should be consulted as investigatorsponsors have all the responsibilities of an industry sponsor, and this means that resources and systems for regulatory compliance must be available.

15 THE TRIALS AND TRIBULATIONS OF WRITING AN INVESTIGATOR INITIATED CLINICAL STUDY

Once you have addressed your questions internally, it is helpful to get opinions on the concept outside of your research group since outsiders may have different perspectives on the research and often will improve the study.

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be the sole individual that has control over protocol version and the version number. This will eliminate many difficulties as your team provides comments for the study or the study is amended in the future. Abbreviations and Definitions

CRITICAL COMPONENTS OF AN INVESTIGATIONAL STUDY Title Page The title page is typically the last page written; however, it is one of the more crucial components of the document. The title page lists the title of the study, local or group protocol number, and the coordinating center. Typically, the title includes the clinical trial phase; the overall design (such as randomized, doubleblind); whether the study is a single-site or multicenter study; the name of the investigational product; the class of subject population; and the disease, condition, or disorder under study. Usually the long title is followed by a short protocol title that is used as the every-day identifier. The critical personnel for the study should be listed on the title page. For each study, there can be only one principal investigator, and in therapeutic studies this is typically a physician. The principal investigator has ultimate responsibility for the safe conduct of the study and the integrity of the data, and has oversight over all other research personnel in the study. Other individuals that need to be identified on the title page include coinvestigators, statistician, responsible research nurse, and responsible data manager. It is often helpful to list the institutional contractual and financial point-of-contact. All contact information (address, telephone, fax, and e-mail) need to be listed for each individual on the study. A 24-hour emergency number(s) and points-of-contact who can be reached any day of the week (including weekends), if such coverage is required by the nature of the study, should also be included. It is also recommended, but sometimes not required, to identify who may consent patients on the clinical trial. This is more critical in a single institution, investigator-initiated trial. It is most important to have a very organized system to keep track of the versions of the protocol as you write and conduct the trial. It is very typical that you may have 5 to 10 versions of the study before the final document is produced, and during the trial you may have a half dozen or more amendments. In the footnote or the header of the protocol title page, version number and version date should be listed and updated as protocols are changed or amended. The principal investigator or designated protocol coordinator should

It is helpful to have a listing of some abbreviations and definitions following the title page. Common and basic terms do not have to be included, but esoteric terms relating to specific diseases or procedures should be. This will help expedite the review of the protocol through internal and external review and approval authorities; and help the members of your research team better understand the protocol. Protocol Schema or Synopsis Following the protocol title page, a study schema or synopsis is used to provide a quick overview of the study. Sometimes just a study schema is provided which outlines the treatment regimen or treatment arms of the study. More commonly, a synopsis is provided which presents a quick reference to the study. This should not be a total duplication of the protocol, but an abbreviated version highlighting the salient points of the study. It should be kept to a minimum, and most studies should be summarized in one or two pages. It is important to remember that the synopsis and the protocol body need to be congruent and not contradictory. Table 15.2 lists an example of a template for a protocol synopsis. TABLE 15.2

Example of a Protocol Synopsis Template. TITLE

OF

STUDY

Protocol Number Sponsor/Investigator Project Phase Indication Number of Study Center(s) Study Design Objectives

Methodology Subject Selection Criteria Duration of Treatment Number of Patients Safety Efficacy

Primary: Secondary: Correlative Studies:

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Table of Contents The table of contents should be a quick reference to locate the place in the protocol for specific and critical information, such as eligibility criteria or treatment plan. The table of contents should include at least the major categories in the study, but also may include subsections for more specific details. Unless you have programs that link pages to the table of contents, often page shifts occur when you add or delete sections of the study, requiring changes in the page numbering in the table of contents. This is a time-consuming process and some investigators advocate to keep the number of categories in the table of contents to a minimum. References and appendices should also be included in the table of contents. Study Objectives The study objectives in a protocol are similar to the specific aims in a research grant and should be very specific and concise. These should be “clearly defined and stated in a manner that will allow the objectives to be investigated by a quantitative assessment of appropriate outcomes” (3). They typically are divided into the primary objective for which the study is designed to answer. Secondary and tertiary objectives may also be included, but these are considered to be more exploratory in nature. The following is an example of a primary objective that is vaguely written: “To determine if the administration of Zolendronic acid to patients with newly diagnosed prostate cancer will improve the patient’s outcome.” This primary objective needs to be more specific about the primary outcome parameter that will be assessed in this study. A more concise objective would be: “To determine whether treatment with Zolendronic acid at the time of initiation of androgen deprivation therapy for metastatic prostate cancer will delay the time to first skeletal related event.” Some studies will have correlative science objective also imbedded within the study and these should also be concisely defined. Background This is equivalent to the introduction in a research paper and puts the proposal in context. It should answer the question of why and what: “Why does the research need to be done?” and “What will be its relevance?” A brief description of the most relevant studies published on the subject should be provided to support the rationale for the study. This section should include background information on the study drug and the disease being studied.

Depending on the type of study (e.g., a phase I study administering an IND), detailed prior laboratory and animal testing may need to be included as well as justification for the proposed dosage. If the study involves the administration of an FDA approved drug, whether the proposed use is within the approved labeling or is a new intended use, it should be described and justified. There should also be background information on the correlative studies, if applicable. Key components of this section would include: 1. Description of disease being studied and problem being addressed 2. Description of current therapy (treatment regimen or medical management currently in wide use or prescribed by professional practice standards and/or approved by the FDA) and any shortcomings 3. Description of drug and its activity 4. Description of any comparator drugs and justification for its use as the control 5. Justification for use of a placebo, if applicable 6. Summaries of studies conducted to date 7. Summary statement The background section should be written in a concise manner; it is useful to summaries with large amounts of data in tables. The background section should give a summary of the supportive literature; it does not have to include all the literature. This section should be limited to 3 to 5 pages. Be sure to identify any nonstandard assays, procedures, or materials proposed to be used and indicate basis for safety and reliability of such.

PATIENT SELECTION Patient selection is one of the most critical components of the research plan, and each specific eligibility and exclusion criteria needs to be scrutinized. The conditions under which a patient is eligible to join the study need to be specifically stated. This would include references to pathologic diagnosis, prior therapies, age, performance status, and organ and marrow function. This section will also include criteria that make a patient ineligible for the study, such as treatment with other agents, allergies to the class of agent under study, pregnancy, brain metastasis, and HIV-positive patients. CTEP has developed guidelines that can be used during the protocol authoring process that outline the inclusion of various populations (1). Note that if the patient selection criteria are too stringent, it is often


difficult to find such ideal patients; however, if the criteria are not stringent enough, it increases the heterogeneity of your study population compromising your endpoints of your study. Many groups have established acceptable inclusion and exclusion criteria for certain malignancies. However, these inclusion and exclusion criteria may vary depending on study agents being used in the trial. For instance, studies that are using an antiangiogenesis agent such as Bevacizumab may exclude patients with prior thromboembolic events within 1 year. This is due to the known risk for recurrent and serious thromboembolic adverse events that can occur in these patients. If an investigational drug brochure is available, important data relating to inclusion and exclusion criteria may be included. This section should include under what circumstances subject participation in the study may be prematurely terminated; if a subject is prematurely terminated or withdraws voluntarily, describe the plan for: documenting the occurrence, individual subject follow up, and use of data or specimens obtained. If there are any safety considerations associated with premature termination or subject withdrawal before the completion of the study, state them under the Risks section of the protocol. Centralized Institutional Registration Procedures Procedures for patient registration vary between institutions and groups; you should contact your clinical trials office to understand the local process. Most will have a template of the procedure that can be used in your protocol. If more than one center is involved in the study, the registration becomes a little more complex, and this may have already been addressed by your local institution. The basic registration procedures should be specifically outlined, step by step from the beginning to the end and have the appropriate delegation of responsibilities identified in the process. One example of a registration procedure for an investigator-initiated multicenter study is outlined in Table 15.3.

TREATMENT PLAN The treatment plan should be complete, clearly written, and simple to follow. This section needs to include the eligibility screening procedures for study entry as well as the administration schedule for the study drug(s) outlining the specific dose, how it is administered, how long it is administered if an intravenous medication, sequence of administration, route of administration, and concomitant medications for safe administration of the drugs. Notations and nomencla-

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TABLE 15.3

Institutional Centralized Registration Procedure Example. To register a patient, the following documents should be completed by the research nurse or data manager and faxed (fax #) or e-mailed (e-mail address) to the study coordinator: · · · ·

Copy of required laboratory tests Signed patient consent form HIPAA authorization form Other appropriate forms (e.g., Eligibility Screening Worksheet, Registration Form)

The research nurse or data manager at the participating site will then call (phone #) or e-mail (e-mail address) the study coordinator to verify eligibility. To complete the registration process, the study coordinator will: · Assign a patient study number · Register the patient on the study · Fax or e-mail the patient study number and dose to the participating site · Call the research nurse or data manager at the participating site and verbally confirm registration

ture in the treatment plan should be consistent. Note that the NCI provides detailed instructions and a common standard in its Guidelines for Treatment Regimen Expression and Nomenclature (http://ctep.cancer.gov/ protocolDevelopment/policies_nomenclature.htm). This standard advises: · Drug names should not be abbreviated; use complete generic drug names. · All details of the treatment regimen should be provided, but do not duplicate these details throughout the protocol. · All units, such as kg/m2, q8h, or TID, should be used consistently throughout the protocol. If using units, spell it out; do not use abbreviations, such as U. · Do not trial a whole number with a decimal point followed by a zero (e.g., 5mg, not 5.0mg); similarly in expressing units that are less than the whole number 1, the dosage should be written with a decimal preceded by a zero (e.g., 0.125mg, not .125mg). Additionally, the following should be considered when writing the Treatment Plan: · The protocol should specify if the medications are dosed based on actual, ideal, or lean body weight. In addition, the study should indicate if the dose of

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the study medication(s) needs to be adjusted every treatment or cycle based on change in weight, if applicable. · The number of days of treatment, the day of treatment(s), and duration of treatment should be clearly identified. An example of this is illustrated in Table 15.4. · The route of administration should be clarified. If an oral medication, there need to be clear instructions if this is fasting or nonfasting conditions. With oral medications, it also is important to indicate if there are any other medications or foods that need to be avoided while taking the study medication. For instance, the consumption of grapefruit juice can interfere with the clearance of certain medications (e.g., Ketoconazole) that are metabolized through the CYP3A4 enzymes. A list of the medications that are to be avoided when on the study medication(s) should be listed; if it is a lengthy list, reference it in the protocol and provide the listing as an appendix. · If intravenous medication is involved, indicate if this can be administered through a peripheral vein or needs to be through a central catheter; whether the medication needs to shielded from light; if there are incompatible fluids or drugs that cannot be administered through the same intravenous line; or include

any other potential problems or conditions that optimize the drug administration. · More details on writing the treatment regimen can be found at the website. If part or all of the study takes place on an out-patient basis, indicate methods to check on subject compliance (e.g., pill counts, plasma concentration monitoring, questionnaires, etc.). When randomization is employed, indicate who will generate the code and how the code will be generated, who will have access to the identifiers in the code, and conditions and methods for breaking the code in case of an emergency. Subjects participating in a blinded study are often provided with wallet cards describing how their status may be disclosed if an emergency occurs. Phase I studies will also include a section on the dose escalation rules. The maximal tolerated dose (MTD) and dose limiting toxicity (DLT) should be well defined for the study. This should define the types and grades of adverse events that will be considered intolerable or DLT. Below are examples on how the MTD and DLT can be defined: · The Maximum Tolerated Dose (MTD) is defined as the highest dose level with an observed incidence of DLT in no more than 1 out of 6 patients.

TABLE 15.4

Typical Drug Administration Schedule. DAY

>1

2

Dexamethasone Docetaxel Bevacizumab or Placebo Prednisone 10 mg

X

X X X X

3

X

4

X

5

6–21

X

Rest Rest Rest Daily

Continue treatment until disease progression or unacceptable toxicity. 1 Cycle = 21 days. Days 1-3 of each cycle Premedicate patients with dexamethasone 8 mg orally twice per day starting the day prior to docetaxel administration and continuing until the day after the docetaxel dose (i.e., 6 doses over 3 days). Day 2 of each cycle (every 21 days) Docetaxel: at 70 mg/m2 intravenously over 1 hour. Placebo: (Arm A) IV every 21 days administered after docetaxel. Initial dose given over 90 minutes, second dose over 60 minutes, and all subsequent doses over 30 minutes if prior infusions are tolerated without infusion-associated adverse events. Bevacizumab: (Arm B) 15 mg/kg IV every 21 days administered after docetaxel. Initial dose given over 90 minutes, second dose over 60 minutes, and all subsequent doses over 30 minutes if prior infusions are tolerated without infusion-associated adverse events. Day 1 until completion of the study Prednisone 10 mg po daily.


· Dose Limiting Toxicity (DLT) in a patient is defined as Grade 3 or greater toxicity using the NCI Common Toxicity Criteria (Appendix B) during the initial cycle of treatment. There continues to be a debate of the most appropriate dosing schedules for phase I trials but historically a “3 × 3” dose escalation design has been used in phase I studies (Table 15.5) (5). More recently, other dose escalation schemas such the continual reassessment method has gained popularity (6). It is beyond the scope of this chapter to go into details on these trial designs, but there have been multiple published reviews on the subject. The primary endpoint of a phase I study is not always to push the drug(s) to intolerable toxicity, but rather may be to define a biologic endpoint. If this is the primary objective, these endpoints need to be specifically identified in the protocol. For more details the reader is referred to Chapter 8 on design of the phase I studies.

DOSING DELAYS AND DOSING MODIFICATION The investigational study should be very explicit on when and how a study medication should be held or modified. While all complications for the study medications cannot be covered, the major complications

should have a detailed schema outlined for the study staff. “For instances, in patients with neutropenia NCI grade 3 or 4, the dose of study medication will be held until the neutropenia is grade 1 or less. Then the dose is reduced by 25% on the subsequent cycle.” Investigators should provide explicit definitions of the type(s), grade(s), and duration(s) of adverse events that will be considered dose-limiting toxicity(ies), or provide definitions of other endpoints that will be used to determine dose modifications in this section. The NCI protocol templates have well written samples, and more complex examples may be found at the following Web site: http://linus.nci.nih.gov/~brb/ Methodologic.ht.

DATA AND SAFETY MONITORING PLAN The plan should reflect the unique nature of the study and should be commensurate with its risk, size, and complexity. It should describe how the principal investigator will ensure that the study is monitored in terms of safety, generation, and analyses of quality data, and how he/she intends to provide ongoing supervision of the study, including assessing whether appropriate progress is being made. Assuring the safety of every individual in the study is the primary responsibility of the principal investigator, who is also responsible to keep the appropriate

TABLE 15.5

Dose Escalation Schema for Phase I Studies. NUMBER OF PATIENTS WITH DLT AT A GIVEN DOSE LEVEL

ESCALATION DECISION RULE

0 out of 3 ≥ 2

Enter 3 patients at the next dose level. Dose escalation will be stopped. This dose level will be declared the maximally administered dose (highest dose administered). Three (3) additional patients will be entered at the next lowest dose level if only 3 patients were treated previously at that dose.

1 out of 3

Enter at least 3 more patients at this dose level. · If 0 of these 3 patients experience DLT, proceed to the next dose level. · If 1 or more of this group suffer DLT, then dose escalation is stopped, and this dose is declared the maximally administered dose. Three (3) additional patients will be entered at the next lowest dose level if only 3 patients were treated previously at that dose.

≤1 out of 6 at highest dose

This is generally the recommended phase II dose. At least 6 patients must be entered at the recommended phase II dose.

level below the maximally administered dose

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regulatory review boards cognizant of any increased risk to the patient. The principal investigator is also responsible to ensure the integrity of the data. Data and Safety Monitoring Plans typically address adverse events, safety monitoring, and quality assurance. Detailed guidance is available from the NCI’s Web site (http://www .cancer.gov/clinicaltrials/conducting/dsm-guidelines). The Adverse Events section would include recording and reporting requirements for your local institutional review board (IRB), along with any required reporting to regulatory agencies or any other organization involved, such as a pharmaceutical company supplying the drug. What is most important is a plan demonstrating that applicable government regulatory and local institutional requirements will be fulfilled, and that the plan will also assure the best possible protection for human subjects is reasonable and feasible, and likely to preserve public trust in the conduct of clinical trials. The adverse events section should address how to identify and then collect, record, and report adverse events as well as describe the expected follow-up. Additionally, the Adverse Event section should address: · The expected adverse events for each drug and reference to supporting documentation, such as the FDA labeling or the investigational drug brochure. · The quality control (within the research team) and quality assurance (external to the functioning of the research team) program and procedures for the conduct of the study, including demonstrated incorporation of good clinical practice (GCP) (7), monitoring by external monitors, use of a Data Safety and Monitoring Board (if applicable), and procedures for ensuring the timeliness and quality of the data (8). · Define what constitutes a nonserious adverse event versus a serious adverse event. · Describe the procedures for tracking all adverse events, regardless of severity, attribution, and reporting requirements, will be identified, monitored, and addressed.

PHARMACEUTICAL INFORMATION The pharmaceutical sections should include information about all investigational drugs and ancillary medications used in the study. A section for each agent to be used in the trial should be included with the following information: 1. Product description: Include the available dosage forms, ingredients, packaging, and labeling, as appropriate. Also state the agent’s supplier.

2. Solution preparation (how the dose is to be prepared): Include reconstitution directions and directions for further dilution, if appropriate. 3. Storage requirements: Include the requirements for the original dosage form, reconstituted solution, and final diluted product, as applicable. 4. Investigational agents: Address stability, purity, and pyrogenicity and adherence to FDA quality assurance manufacturing requirements. 5. FDA approved agents: Include the stability of the original dosage form, reconstituted solution, and final diluted product, if applicable. 6. Route of administration: Include a description of the method to be used and the rate of administration, if applicable. Describe any precautions required for safe administration. Information on availability, ordering, and accountability should be included; include procedures for receipt, use, and eventual disposition. Correlative and Special Research Studies Not all studies will have a Correlative Studies section. This section can be a description of any research activity as simple as evaluating a biomarker such as obtaining a tube of blood to evaluate baseline vascular endothelial growth factor or drug level to correlate with clinical outcome. In other instances it can be a very complicated set of tests, such as serial positron emission tomography (PET) scans or pharmacokinetic studies. Regardless of the study being obtained, this section needs to provide specific aims and rationale for the studies and detail the specifics regarding the handling, preserving, and storage of the tissue or blood to be used; procedure and addresses for shipping bio-specimens; or methods, timing, and procedures for other tests involving the patient. It is particulary critical to understand the biology of the bio-specimen that you are obtaining. For instance, certain proteins in the blood may break down if left at room temperature; and in order to preserve this protein, the plasma needs to be separated immediately and then frozen at −80ºC within 30 minutes. This will require onsite processing which needs to be planned and budgeted for in the protocol; if not, alternative procedures need to be developed. Information on endpoint validation, including additional background (as needed), description of the assay(s) used, materials and methods, and assay validation, should be provided in an appendix. If the sample is going to be shipped out to have the test performed at another location, the protocol needs to include packing instructions (i.e., shipped with dry ice), shipping address, and time when the sample can be shipped. There have been many bio-specimens that have been shipped


overnight on dry ice on a Friday afternoon, to find that the recipient does not receive weekend deliveries; thus degrading the integrity of the specimen. STUDY CALENDAR This is one of the most useful and referenced sections of the research protocol, and it will be prudent to ensure it is complete and reflects your study accurately. The study calendar is a quick reference that includes all patient activities, tests (including correlative studies), and outcome measures that will occur before, during, and after the study. Table 15.6 is an example of a study calendar. It is most useful early in the protocol writing process to complete the study calendar first, since it will help organize your thoughts and allow you to refer back to the study calendar as you write the other sections to ensure there is consistency throughout the protocol. The study calendar will also help to generate the study budget and highlight data collection requirements. If this is completed and verified early in the protocol process, this can help expedite the budget, contract, composing of the data collection instruments and case report forms, and ultimately opening of the study. MEASUREMENT OF EFFECT OR OUTCOME MEASURES All your trial endpoints should be defined in this section and correlate with the specific aims of the study. For example, in the phase II studies, changes in tumor volume or delay in progression of the cancer could be typical endpoints. For studies that are evaluating changes in tumor masses seen on radiographs, the Response Evaluation Criteria in Solid Tumors (RECIST) Criteria is typical response criteria utilized in solid tumors (9). The RECIST criterion has been the standard for patients with objective disease; complete definition of the response criteria can be found at http://ctep.cancer .gov/protocolDevelopment/docs/ quickrcst.doc. However, other criteria may be used, such as Cheson Criteria for lymphomas (10) or the International Uniform Criteria for Multiple Myeloma (11). Other studies may use other outcome measures that include progression free survival (PFS) or overall survival; however, the definitions of each of these need to be detailed. DATA MANAGEMENT The protocol should provide information on how the data will be managed, including data handling and coding for computer analysis, monitoring and verification.

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Multicenter guidelines would also be included in this section, if applicable. Case histories must be prepared and maintained in such a manner that there is a systematic and accurate record of all observations and other data pertinent to the study for each individual subject. For the investigator initiating a study this poses a challenge, as he/she must anticipate the data that should be collected and maintained in data collection forms and case report forms. An “include it all approach” unnecessarily burdens resources and may obscure critical data, although an “overly minimalist approach” may preclude collection and analyses of essential data. A good reference and collection of templates for case report forms may be found in the Manual for the Completion of the NCI/DCTD/CTEP Clinical Trials Monitoring Service, Case Report Forms, prepared by Theradex® (http://www.theradex.com/CTMS/CTMS _CRF_Manual_313.pdf). This section should describe the procedures for data collection and the data collection forms that will be used for collecting, storing, and processing study data, including outlining specific case report forms. The protocol should clearly identify the timing of when the data will be recorded, revised, and stored; which category of staff member(s) will be entering the data; proposed validation and quality control methods (e.g., cross validation) that are going to be used in the study; and the source documentation required. All case report forms, data collection forms, and checklists (such as eligibility checklists and checklists for specific visits) should be attached as appendices. Whenever possible, the documents should be formatted in a standard manner and must include identifying headers, dates, and initials or signatures of those individuals recording or revising data on them. Remember that federal legislation and the publication policies of many professional journals require online registration of the study in clinicaltrials.gov. Requirements to post results of clinical trials are also required by federal legislation. Investigators must be familiar with these requirements and plan for the collection and maintenance of appropriate data for reporting purposes.

CONDUCTING AN INVESTIGATORINITIATED MULTISITE STUDY When serving as lead principal investigator for a multisite study, a plan documenting how management and coordination responsibilities will be carried out should be provided. For relatively simple and minimal risk studies, this plan may be presented within the

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TABLE 15.6

Study Calendar Example. Schedules shown in the study calendar below are provided as an example and should be modified as appropriate. Baseline evaluations are to be conducted within 1 week prior to start of protocol therapy. Scans and X-rays must be done ≤4 weeks prior to the start of therapy. In the event that the participant’s condition is deteriorating, laboratory evaluations should be repeated within 48 hours prior to initiation of the next cycle of therapy. PRE- WK STUDY 1 Study Agent Other Agent(s) Informed consent Demographics Medical history Concurrent meds

A B X X X X

Physical exam Vital signs Height Weight Performance status CBC w/diff, plts Serum chemistrya EKG (as indicated) Adverse event evaluation

X X X X X X X X

Tumor measurements

X

Radiologic evaluation B-HCG Other tests, as appropriate Other correlative studies

X

WK 2

WK 3

B

WK 4

WK 5

A B

B

WK 6

WK 7

WK 8

A B

B

WK 9

WK 10

WK 11

A B

B

WK OFF 12 STUDYC

X—————————————————————————————————— ——————————————————————————————————— ——————X X X X X X X X X

X X

X X X X

X X X X

X X

X X

X X X X

X X

X X

X X X X

X X

X X

X X X X

X X

X X

X—————————————————————————————————— ——————————————————————————————————— ——————X Tumor measurements are repeated every [# weeks] weeks. Documentation (radiologic) must be provided for patients removed from study for progressive disease. Radiologic measurements should be performed every [# weeks] weeks.

X Xc

Xc

Xb

A: Study Agent: Dose as assigned; administration schedule B: Other Agent(s): Dose as assigned; administration schedule a: Albumin, alkaline phosphatase, total bilirubin, bicarbonate, BUN, calcium, chloride, creatinine, glucose, LDH, phosphorus, potassium, total protein, SGOT [AST], SGPT [ALT], sodium b: Serum pregnancy test (women of childbearing potential) c: Off-study evaluation

protocol. Complicated studies and/or moderate or high risk studies most likely should have a standalone manual of procedures (MOP) included as an appendix. The MOP should detail programmatic structure and procedural requirements across institutional lines of authority and responsibilities

to ensure optimal safety of subjects, regulatory compliance, and protocol-specific consistency. Minimal elements include: · Means by which to document approval for start-up of research activity at the participating site


· Confirmation of applicable regulatory requirements such as having current federal wide assurances and local IRB approvals (as applicable) · Provisions to ensure qualification and training of participating site personnel and documented agreements for collecting, maintaining, and distributing research data and time lines for such; including procedures for central registration at the principal investigator’s site; and, especially important, reporting of serious and adverse events · Monitoring procedures to verify compliance and consistency in all activities of the study · Documented acceptance of the protocol and all updates by the participating site

STATISTICAL CONSIDERATIONS Prior to writing the study, the investigators should meet with the statistician to discuss the study, the primary endpoints of the study, the appropriate statistical design, and methods used for evaluating the outcomes of the study. This section should clearly provide the rationale for the statistical design; justification for the sample size selected; power of the study and level of significance to be used; the procedures for accounting for any missing or false data; and specific methods to evaluate the outcome measures. A statistical section for any correlative studies should also be included. If correlative studies are only exploratory, then this should be stated. Other chapters in this book outline more details in the statistical design of the studies and should refer to these sections.

REFERENCES A protocol is a scientific document and the appropriate references should support the research plan and other factual statements in the protocol.

· · · ·

Note that the collection and use of human biomaterial (parts of a subject) deserves attention in the protocol. Aside from retrieval methods, whether specimens are associated with individually identifiable information and the potential risks associated with the data accompanying the specimen primarily drives the level of concern within a subject protection context. Genetic germ-line testing which may reveal a proclivity for disease or illness, for example, when associated with individual subject identifiers requires diligence in minimizing risk of health insurance discrimination, employability, or family/subject distress. Means to minimize such risks should be included. INFORMED CONSENT The informed consent is a critical component of any investigational protocol that describes the risk and benefits of the research study. This is covered in detail in chapter 35 and one should refer to this chapter for more details on writing an informed consent. APPENDICES The appendices should contain any additional information that will help conduct the study. For instance, the Eastern Cooperative Oncology Group (ECOG) performance status scale may be included to ensure that all investigators consistently report the performance status as well as other information, such as detailed process for collecting correlative blood sample or an oral medication log. Typical appendices may include:

SECTION ON PROTECTION OF HUMAN SUBJECTS

· · · ·

Means to minimize risk and enhance protections to participants in clinical trials should be included in the protocol. Minimal issues that should be addressed include:

·

· Recruitment methods · Continuation of benefit (if the investigational treatment proves beneficial) · Consent process (including parental permission for minors, surrogate permission for unable-to-consent

adult subjects, and adolescent and child assent, as appropriate) Subject payments (if any) Cost to subject for participation In case of injury procedures Subject confidentiality and privacy

· · · · · ·

Data collection sheets Case report forms Screening and enrollment log Checklists to ensure consistency and compliance drug accountability Log Manual of procedures for complex and/or multisite studies Signature and delegation of duty/authority log Performance status criteria Consent form template NCI CTC 3.0 Drug-drug interaction lists Quality of Life or other questionnaires

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· Study diaries or patient drug accountability logs · Eligibility checklists

CONCLUSION Writing a clinical study is a dynamic process and continues from the inception of the study to the final analysis of the data. One cannot expect to write a perfect study that addresses all the unforeseen obstacles and scenarios that present to the investigators; and the research team needs to meet on a regular basis to review and update the protocol to address the issues that arise. This does take considerable time and effort from the principal investigator to ensure this does occur on a timely basis so it does not hinder study accrual or patient safety. It is always important that patient’s safety comes first in any study and it is the study team’s responsibility that this occurs.

References 1. Protocol templates and guidelines. Cancer Therapy Evaluation Program. 2008 [cited]. (Accessed May 2009 from http://ctep .cancer.gov/protocolDevelopment/templates_applications.htm#p oliciesAndGuidelines.)

2. Weng C, Gennari JH, McDonald DW. A collaborative clinical trial protocol writing system. Stud Health Technol Inform. 2004;107(Pt 2):1481–1486. 3. Gebski V, Marschner I, Keech AC. Specifying objectives and outcomes for clinical trials. Med J Aust. 2002;176(10): 491–492. 4. Guidelines for Treatment Regimen Expression and Nomenclature. (Accessed May 2009 from http://ctep.cancer.gov/protocol Development/policies_nomenclature.htm.) 5. Eisenhauer EA, O’Dwyer PJ, Christian M, Humphrey, JS. Phase I clinical trial design in cancer drug development. J Clin Oncol. 2000;18(3):684–692. 6. O’Quigley J, Pepe M, Fisher L. Continual reassessment method: a practical design for phase I clinical trials in cancer. Biometrics. 1990;46(1):33–48. 7. International conference on harmonization of technical requirements for registration of pharmaceuticals for human use. 1996. (Accessed May 2009 from http://www.ich.org/LOB/media/ MEDIA482.pdf.) 8. Guide for writing a research protocol for research involving human participation. World Health Organization. 2008. (Accessed on October 11, 2008, http://www.who.int/rpc/ research_ethics/guide_rp/en/index.html.) 9. Therasse P, Arbuck SG, Eisenhauer EA, et al. New guidelines to evaluate the response to treatment in solid tumors. European Organization for Research and Treatment of Cancer, National Cancer Institute of the United States, National Cancer Institute of Canada. J Natl Cancer Inst. 2000;92(3):205–216. 10. Cheson BD, Pfistner B, Juweid ME, et al.; International Harmonization Project on Lymphoma. Revised response criteria for malignant lymphoma. J Clin Oncol. 2007;25(5):579–586. 11. Durie BG, Harousseau JL, Miguel JS, et. al.; International Myeloma Working Group. International uniform response criteria for multiple myeloma. Leukemia. 2006;20(9):1467–1473.

Data Collection

16 Eleanor H. Leung

The data collection process in clinical trials has been extensively described from the perspectives of statisticians and data managers (1–9). As a result, a common but erroneous assumption is that once a protocol is written, the statisticians and data managers assigned to a study will take care of the data collection. In reality, the data collection process is a complex team effort and the primary purpose of this chapter is to show that the principal investigator also plays a critical role—during the forms design stage in particular. The principal investigator will be asked to: · Verify that all the key data elements needed to meet study objectives will be captured in case report forms. · Specify how often adverse events, laboratory, imaging, and clinical assessments have to be performed to obtain valid outcome measures. · Identify the critical variables that will require verification with source documentation. The principal investigator will be performing these tasks early during the forms development process when the case report forms (CRFs) are being designed. Since these forms must reflect the entry, treatment, and follow-up requirements set by the protocol, it may be tempting to postpone forms review until a protocol is finalized and approved. However, because the forms development team involves so many parties working

behind the scenes, preliminary forms review is crucial. Fortunately, the initial set of CRFs the principal investigator is asked to review will already include many of the key data elements that need to be captured. These preliminary drafts will have been gleaned from actual forms used in previous studies investigating similar agents and treatment regimens as well as National Cancer Institute (NCI) form templates developed as part of the NCI cancer Biomedical Informatics Grid (caBIG) and Common Data Elements (CDE) initiatives seeking to make datasets across phase III cancer clinical trials comparable and thus facilitate multidisciplinary data sharing across institutions. This chapter is divided into two sections. The first section will focus on the role the principal investigator plays in determining the content of CRFs and will be the more extensive one. The second section will discuss quality control procedures used by data management and statistical teams to ensure the completeness and accuracy of collected data.

COLLECTING KEY DATA VARIABLES Because only the data captured in CRFs will be entered into the database and form the basis of the final report, the responsibility of ensuring that all the key data variables needed to meet study objectives are collected prospectively in the CRFs will rest with the principal

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investigator. Let’s examine how this responsibility is carried out with four categories of data in clinical trial studies: patient characteristics, treatment compliance, adverse events, and outcome variables. Screening and Baseline Patient Information Patient characteristics that could serve as prognostic and predictive variables of outcome are collected at study entry using two types of case report forms: the registration form and the on-study form. Patient demographics (i.e., height, body surface area, age, gender, race, ethnicity, zip code and country of residence, performance status, and medical payment method) are captured in a standard registration form used by all NCI cooperative groups. The registration form also collects the following information: · Patient identifiers—Initials, treating institution and physician, medical record number, social security number. The latter is optional but recommended to help track survival status via the Social Security Death Index or local tumor registries if patients don’t return for follow-up visits. Patient identifiers are always stored in a secure limited access database separate from the clinical research database. · Regulatory information, such as, institutional review board (IRB) approval and patient informed consent dates. · Enrollment information, such as date(s) of registration and randomization, projected treatment start date, stratification factors, and treatment assignment. · Assigned unique patient identification number, linking all data collected for a patient from baseline through final outcome. Although not a CRF in the strictest definition because it is not entered into the database, the study eligibility checklist deserves a brief discussion. Using an easy-to-follow format, it lists inclusion criteria (i.e., disease stage and histologic type, prior treatments allowed, performance status, age range, gender, and acceptable range of laboratory values) and exclusion criteria (i.e., banned prior therapies, treatments and medications to be discontinued, and preexisting medical conditions). Because the eligibility checklist is used as a screening tool, it should also provide thorough explanations of difficult to understand eligibility prerequisites to enrollment. For instance, now that electronic nomogram calculators are increasingly being used to stratify patients prior to randomization, the eligibility checklist should include instructions for accessing these nomogram calculators and

stipulate the values required for the nomogram calculation. The checklist should emphasize that unavailability of any of these values would preclude patient enrollment. Unlike the eligibility checklist which establishes minimum entry criteria, the on-study form captures information about a patient’s actual disease status and disease extent at baseline, prior treatments, preexisting comorbidities, and current medications. The on-study form deserves close scrutiny; it should capture baseline values of every variable that might affect whether a patient would benefit or not from the experimental treatment under investigation. The fact that the NCI has developed over 50 disease-specific on-study form templates for use in patients with early stage (previously untreated/ adjuvant/localized) vs. advanced (metastatic/recurrent/non-localized) disease is further evidence that the on-study form must be carefully customized to meet study requirements. To illustrate this point, let’s compare the on-study information collected in CALGB 90401 to that in the NCI on-study form template. CALGB 90401 is a randomized phase III closed trial comparing docetaxel and prednisone treatment with and without bevacizumab in men with hormone refractory prostate cancer. Both on-study forms collect Gleason grades and sum from initial diagnostic biopsy specimen, start and end dates of all prior therapies, metastatic/recurrent sites, presence/absence of measurable and non-measurable disease, and baseline prostate specific antigen (PSA) value at study entry. However, the CALGB 90401 study team requested that the following supplementary information be also captured at study entry: · Measures of bone disease extent in terms of the number of bone lesions present in the baseline bone scan (i.e., no bone disease, 20 bone lesions, or superscan (10) · Baseline laboratory values (absolute neutrophil count, platelet count, bilirubin, creatinine, aspartate transaminase, and urine to protein creatinine ratio) confirming patient could proceed safely to treatment, plus those (hemoglobin, alkaline phosphatase, and lactate dehydrogenase) that have previously been found to be of prognostic significance in evaluating treatment of castration-resistant prostate cancer (11) · Information about patient prior histories of myocardial infarction, coronary artery bypass graft, cardiac stent/angioplasty, coronary artery disease, hypertension, thrombosis, vascular disease, and cardiovascular medications, as these factors have previously been shown to increase the risk of arterial thromboembolic events (12)

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16 DATA COLLECTION

· Three additional pre-study PSAs to verify that patients enrolling on the basis of biochemical progression met the disease progression criteria set by the Prostate-Specific Antigen Working Groups I/II (13–14) Thus, the principal investigator is faced with difficult decisions early on. Achieving the proper balance between too much information and not enough will be the predicament the principal investigator will repeatedly face during the forms design process. Treatment Compliance To confirm that study treatment is administered per protocol, standard treatment forms have been created to collect dosages, dose delays and reductions, and dose modification reasons (due to toxicity, drug order delays, scheduling issues, etc.) of treatment agent(s) on a cycle-by-cycle basis, without considering whether all this information is actually necessary. To avoid this common pitfall, data collection should be governed by the information that will be reported in the final treatment summary table, namely: · Number of patients treated with each agent (or, combination of agents) · Median number of cycles administered (and range) · Percent of patients experiencing dose delays · Percent of patients experiencing dose reductions · Percent of major protocol deviations · Percent of patients who completed maximum treatment allowed vs. those who discontinued treatment early due to disease progression, adverse event, consent withdrawal, death, or other reason In addition, the principal investigator will also need to: · Be familiar with the definitions of major vs. minor deficiencies used by the Clinical Trials Monitoring Branch (CTMB) of the Cancer Therapy Evaluation Branch (CTEP) of the NCI during institutional audits (15). When asked to classify treatment deviations as major or minor, investigator responses should be consistent with NCI CTMB guidelines. NCI CTMB defines a major deficiency as “a variance from protocol-specified procedures that makes the resulting data questionable.” Examples of major treatment deficiencies are: · Giving a blinded drug assigned to another patient or a commercial agent instead of the blinded drug supplied by the NCI, or omitting one of the agents in a particular cycle

· Continuing to administer study treatment when protocol requires discontinuation, as when progression criteria have been met or unacceptable toxicity occurs · Making dose deviations or modifications, leading to dosing errors greater than +/− 10% · Modifying doses not prescribed in the protocol · Delaying treatment to provide drug holidays not allowed per protocol A minor or lesser deviation is “a deficiency that is judged to not have a significant impact on the outcome or interpretation of the study and is not described above as a major deficiency. An unacceptable frequency of lesser deficiencies should be treated as a major deficiency in determining the final assessment of a component” (15). Examples of minor deficiencies are treatment delays due to holidays, extended vacation, unexpected scheduling problems, or delayed delivery of an NCI-supplied drug. Since the number of major deviations will be reported in the final publication, steps should be taken to track deviations and classify them as major or minor on an ongoing basis during the course of treatment. · Decide how adherence to oral antineoplastic or preventive agents will be tracked. Self-reports of adherence, medication calendar diaries, pill counts, records of prescription refills, and use of microelectronic monitoring system (MEMS) have all been tested and used, but none has yet been adopted as the definite gold-standard method for measuring adherence to oral agents (16). · Identify the relevant concomitant medications that need to be tracked and whether their dosage and usage frequency will also be needed. · Determine whether an off-treatment form should be used in addition to treatment-by-cycle forms. Such a form would capture total number of cycles completed for each agent, dates of first and last cycles, and reason for ending (or never starting) protocol treatment. This off-treatment form would allow sites that have fallen behind in their submission of treatment-by-cycle forms to report treatment discontinuation as soon as it happens. Toxicity Assessment Adverse events (AEs) in cancer clinical trials are monitored using two types of reporting: routine and expedited. Routine reporting of adverse events uses study-specific AE forms submitted at regular intervals during study treatment, while expedited reporting of serious adverse events (SAEs) is required when an

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adverse drug experience is life-threatening “or results in death, inpatient hospitalization or prolongation of existing hospitalization, a persistent or significant disability/incapacity, or a congenital anomaly/birth defect.” Currently, SAEs are reported via the NCI Adverse Event Expedited Reporting System (AdEERS). Whether an SAE needs to be reported depends on the severity grade of the SAE, whether the primary SAE is expected or unexpected, the degree to which the SAE can be attributed to study treatment (i.e., unrelated, unlikely, possibly, probably, or definitely related) and time since last course of treatment. For more extensive discussion of AdEERS submission requirements or to access the AdEERS Web application, refer to the following CTEP Web sites: http://ctep.info.nih.gov/protocolDevelopment/ electronic_applications/docs/newadverse _2006.pdf https://webapps.ctep.nci.nih.gov/openapps/plsql/ gadeers_main$.startup This chapter will focus instead on three issues concerning routine reporting of adverse events. 1. Which toxicities should be monitored? Because one of the goals in a clinical trial is to determine the cost/benefit ratio of a new treatment agent or regimen, the principal investigator and study team must select the AEs that will be systematically monitored during treatment, and thus, specified in routine AE CRFs so that the events can be graded on a cycle-by-cycle basis. Which, if not all, of the following adverse events should be regularly monitored? · The most common ones (e.g., nausea, diarrhea, anorexia, pain, neuropathy, rash, fatigue) that might lead to early patient withdrawal from study treatment? · Low-grade, persistent AEs (hypertension, confusion, dizziness) that are not serious, but that might be early warning signs of life-threatening SAEs? · Platelet, neutrophil, and hemoglobin counts and kidney and liver function test results that monitor patient well-being and safety? · Exam-based assessments of AEs (e.g., neuropathy, muscle weakness, dyspnea, cardiac arrhythmia) that would otherwise go unreported? · Potentially serious AEs included in the CAEPR (Comprehensive Adverse Event and Potential Risks) list issued by the NCI for each investigational agent?

2. What is the best way of assessing toxicities? To promote consistency in adverse event reporting in oncology trials, the CTEP branch of the NCI first developed the NCI Common Toxicity Criteria (CTC) in 1982 to provide the terminology and severity grading system for 49 commonly occurring AEs encountered during oncology treatment. By 2003, the table (CTCAEv3) had expanded to over 1,000 terms, and the latest version (CTCAEv4.0) now covers about 790 terms (17,18). As a result, toxicities in oncology trials have traditionally been assessed using the AE terms in the CTCAE version in effect at the time an AE form is designed. Recent studies (19–22) have questioned the usefulness of this type of AE reporting in the case of patient symptoms. When asked to assess symptoms such as fatigue, pain, nausea, vomiting, constipation, cough, and hot flushes using patient-reported outcome (PRO) questionnaires, patients can grade these symptoms just as reliably (if not more reliably) than clinical research associates (CRAs) who often abstract toxicity information from medical reports onto AE forms without any direct patient contact. Similarly, since measures of hypertension, kidney and liver functions, and blood chemistries can be obtained objectively, it might be more efficient to ask CRAs to report actual levels of blood pressure, creatinine, bilirubin, neutrophil/platelet/ white blood cell counts, together with the lower and upper limits of their normal range, than to grade the events themselves. Upon receipt, statistical center programs would translate the lab values into severity grades, per CTCAE grading guidelines (http://safetyprofiler-ctep.nci.nih.gov/ CTC/CTC.aspx). In summary, principal investigators play a major role in determining how toxicities will be assessed. They select the AEs that will be most closely monitored during treatment. They decide whether AE reports will consist of CTCAE-based AE forms, PRO questionnaires, or study-specific CRFs that capture actual laboratory values. 3. The principal investigator will also need to decide how often toxicities will be assessed during treatment. Traditionally, toxicities have been assessed at the end of every treatment cycle to identify potentially serious AEs early during treatment. However, since toxicity summaries report number of patients experiencing an AE at each grade level, and neither the total count of AEs experienced by all patients, nor the number of cycles associated with each AE, principal investigators should

16 DATA COLLECTION

consider decreasing the frequency of toxicity assessments to alleviate the reporting burden of participating sites. Indeed, insisting that sites submit AE forms every 3-4 weeks when no toxicities are occurring is a waste of time, especially in prevention studies (e.g., selenium, statins, aspirin) where expected toxicities are few and rare, or in studies where treatment has been so successful that patients are being treated beyond 12 months! As this chapter is being written, a new Web-based software tool—caAERS–for the reporting of both CTCAE-based routine and serious adverse events in cancer clinical trials is being developed by the NCI-caBIG group. caAERS will be used by sites to report both CTCAE-based routine and expedited serious AEs in cancer clinical trials. Scheduled to be released in 2010, Web demonstration of this application can be accessed via the NCI caBIG Web site: https://cabig.nci.nih.gov/ tools/caAERS. Although implementation of caAERS will allow collection of AE data on a realtime basis and eliminate discrepancies in reporting of SAEs associated with current routine and expedited AE reporting systems, the principal investigator’s role in collecting adequate toxicity data in a clinical trial will remain unchanged. He/she will still have to identify the AEs requiring regular monitoring, decide whether CTCAEbased approach of collecting toxicity information needs to be supplemented with patient-reported outcomes and objective laboratory assessments, and determine the most appropriate schedule for toxicity assessments. Outcome Measures Overall survival is the most common primary end point reported in randomized cancer clinical trials (23) and the easiest outcome variable to collect. NCI cooperative groups automatically send monthly delinquency notices or expectation reports to participating institutions if a patient’s survival fails to be updated every 6 months during the first 2 years after enrollment and annually thereafter. If a patient is still on study, survival dates are obtained from regularly submitted laboratory reports, treatment, AE, follow-up, and tumor measurement CRFs. The real challenge starts when protocol treatment is discontinued and the patient has not yet progressed but refuses to return for follow-up exams. An even greater challenge is posed by patients who never start assigned treatment in phase III studies. Because phase III studies adhere to the intent-to-treat principle, even these patients need to be followed until study end

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points have been met. Since these two groups of patients could become lost to follow-up, CALGB does not officially declare patients as lost or remove them from data delinquency lists used to evaluate institutional performance until patients have been lost for two consecutive years. Sites that have proactively requested contact information for relatives, employers, and primary care physicians at enrollment and obtained permission to contact them, may reduce these losses. Although the Social Security Death Index and local tumor registries can be regularly checked to determine whether patients are still alive, these registries cannot be used if patients have withdrawn consent from survival follow-up or Social Security numbers are unavailable. Because of the numerous difficulties encountered with long-term follow-up and the increasing need to evaluate new promising treatments at a faster rate, surrogates of overall survival have been proposed (24–25). The validity of using progression-free survival (PFS), time-to-progression (TTP), failure-free survival (FFS), objective disease response/progression, biomarker response/progression, or other measures as surrogate end points will be addressed in other chapters. Instead, this chapter will focus on the problems associated with collecting accurate outcome measures from follow-up, tumor measurement, and biomarker forms. Standard information collected in follow-up forms consists of: Patient vital status (alive or dead), date of last contact (or, date of death), cause of death (if patient is dead), and if patient is alive, dates of last clinical assessment, first local-regional progression (and site), first distant progression (and site), first non-protocol therapy (and type), new primary (and site), and reports of any long-term toxicities (Grade >=3) prior to recurrence or new primary. These variables usually provide all the information needed to calculate time to progression or failure in most adjuvant and neoadjuvant solid tumor studies where the patient has been diagnosed as disease-free at the end of study treatment. However, if the patient has metastatic disease, is not eligible for surgery, and is allowed to continue study treatment until progression, determining when the patient has responded or progressed becomes more complex if he/she is being followed with both tumor and biomarker measurements. If these patients are prematurely diagnosed as having progressed, treatment will be discontinued early, depriving them of the full benefit of treatment to which they are entitled. Sometimes, sites may not even realize patients have progressed and erroneously deliver extra courses of treatment. Special efforts should be made to ensure that tumor measurements are reported accurately. For

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example, if target lesions are present at baseline, but omitted from baseline tumor measurement forms, they may be misrepresented as new at restaging, and consequently, misinterpreted as evidence of progression. Moreover, if treatment efficacy is being evaluated in terms of tumor response, radiologists should be trained and certified in the tumor measurement system— RECIST 1.0 (26) or RECIST 1.1 (27)— designated in the protocol so they can precisely identify, follow, and evaluate changes in target and nontarget lesions. They should be encouraged to complete study measurement forms themselves or submit the equivalent ones used at their local institution. Completion of measurement forms by untrained CRAs on the basis of measurements provided in scan reports should be discouraged, especially if different radiologists are performing the evaluations. Optimally, all previous scans (including baseline) should be available for comparison at each restaging so that all target and nontarget lesions are consistently followed at each timepoint. Timing of baseline and subsequent assessments is also important. Care should be taken to collect baseline values within the pre-treatment time frame set in the protocol. Take the case of a prostate cancer patient with rapidly rising PSAs. If PSA assessment is not repeated before Cycle 1, and an earlier, lower PSA acts as a reference value, PSA progression criteria may be met prematurely, cutting short a treatment that might have started to take effect and resulted in PSA declines had an extra course been administered. With respect to restaging scans, investigators should determine a priori whether they should be scheduled at fixed time intervals or tied to the number of cycles completed, and decide whether restagings should be delayed when a cycle is delayed. Indeed, timing of restaging scans impacts on estimates of time to progression and should be carefully considered prior to study activation and specified in the study protocol. In studies where patients continue study treatment until progression, two important issues also need to be discussed. First, study protocol progression criteria have to be clearly defined, and if different from established convention or practice, the differences should be underscored. For example, in CALGB 90401, bone progression has not occurred if two or fewer new bone lesions are detected at restaging. Measurable disease progression criteria have not been met either if the sum of the longest diameters of target lesions has increased

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