A Practical Guide To Designing Phase II Trials In Oncology (Statistics Practice) Sarah R. Brown, Walter M. Gregory, Christopher J. Twelves, Julia B

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A Practical Guide
to Designing Phase II
Trials in Oncology

Sarah R. Brown
Walter M. Gregory
Chris Twelves
Julia Brown

Statistics in Practice

A Practical Guide to Designing
Phase II Trials in Oncology

STATISTICS IN PRACTICE
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Nottingham Trent University, UK
Statistics in Practice is an important international series of texts which provide
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A complete list of titles in this series appears at the end of the volume.

A Practical Guide to Designing
Phase II Trials in Oncology
Sarah R. Brown
University of Leeds, UK

Walter M. Gregory
University of Leeds, UK

Chris Twelves
St James’s University Hospital, Leeds, UK

Julia Brown
University of Leeds, UK

This edition first published 2014
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Library of Congress Cataloging-in-Publication Data
A practical guide to designing phase II trials in oncology / [edited by] Sarah R. Brown,
Walter M. Gregory, Christopher Twelves, Julia Brown.
p. ; cm.
Includes bibliographical references and index.
ISBN 978-1-118-57090-6 (hardback)
I. Brown, Sarah R., editor of compilation. II. Gregory, Walter M., editor of compilation.
III. Twelves, Chris, editor of compilation. IV. Brown, Julia (Julia M.), editor of compilation.
[DNLM: 1. Clinical Trials, Phase II as Topic. 2. Antineoplastic Agents–therapeutic use.
3. Drug Evaluation–methods. 4. Neoplasms–drug therapy. QV 771.4]
RC271.C5
616.99′ 4061–dc23
2013041156

A catalogue record for this book is available from the British Library.
ISBN: 978-1-118-57090-6
Set in 10/12pt Times by Aptara Inc., New Delhi, India
1 2014

To Austin, from Sarah, for your continued support and
encouragement.
And to the many patients and their carers who take
part in clinical trials, often at the most difficult of
times, helping in the development of new and better
treatments for people with cancer now and
in the future.

Contents
Contributors
Foreword I

xv
xvii

Elizabeth A. Eisenhauer

Foreword II

xix

Roger A’Hern

Preface
1 Introduction

xxi
1

Sarah Brown, Julia Brown, Walter Gregory and Chris Twelves

1.1
1.2
1.3
1.4
1.5
1.6

The role of phase II trials in cancer
The importance of appropriate phase II trial design
Current use of phase II designs
Identifying appropriate phase II trial designs
Potential trial designs
Using the guidance to design your trial

2 Key points for consideration

3
5
6
7
9
10
12

Sarah Brown, Julia Brown, Marc Buyse, Walter Gregory, Mahesh Parmar and
Chris Twelves

2.1

2.2

2.3
2.4

Stage 1 – Trial questions
2.1.1 Therapeutic considerations
2.1.2 Primary intention of trial
2.1.3 Number of experimental treatment arms
2.1.4 Primary outcome of interest
Stage 2 – Design components
2.2.1 Outcome measure and distribution
2.2.2 Randomisation
2.2.3 Design category
Stage 3 – Practicalities
2.3.1 Practical considerations
Summary

14
14
16
17
18
18
18
21
26
33
33
35

viii

CONTENTS

3 Designs for single experimental therapies with a single arm

Sarah Brown

3.1

3.2

3.3

3.4

3.5

3.6

3.7

One-stage designs
3.1.1 Binary outcome measure
3.1.2 Continuous outcome measure
3.1.3 Multinomial outcome measure
3.1.4 Time-to-event outcome measure
3.1.5 Ratio of times to progression
Two-stage designs
3.2.1 Binary outcome measure
3.2.2 Continuous outcome measure
3.2.3 Multinomial outcome measure
3.2.4 Time-to-event outcome measure
3.2.5 Ratio of times to progression
Multi-stage designs
3.3.1 Binary outcome measure
3.3.2 Continuous outcome measure
3.3.3 Multinomial outcome measure
3.3.4 Time-to-event outcome measure
3.3.5 Ratio of times to progression
Continuous monitoring designs
3.4.1 Binary outcome measure
3.4.2 Continuous outcome measure
3.4.3 Multinomial outcome measure
3.4.4 Time-to-event outcome measure
3.4.5 Ratio of times to progression
Decision-theoretic designs
3.5.1 Binary outcome measure
3.5.2 Continuous outcome measure
3.5.3 Multinomial outcome measure
3.5.4 Time-to-event outcome measure
3.5.5 Ratio of times to progression
Three-outcome designs
3.6.1 Binary outcome measure
3.6.2 Continuous outcome measure
3.6.3 Multinomial outcome measure
3.6.4 Time-to-event outcome measure
3.6.5 Ratio of times to progression
Phase II/III designs

4 Designs for single experimental therapies including randomisation

36
36
38
39
40
40
41
41
50
50
53
54
55
55
59
59
60
60
60
60
63
63
63
64
64
64
65
65
65
65
65
65
66
66
66
67
67
68

Sarah Brown

4.1

One-stage designs
4.1.1 Binary outcome measure
4.1.2 Continuous outcome measure

68
68
70

CONTENTS

4.2

4.3

4.4

4.5

4.6

4.7

4.1.3 Multinomial outcome measure
4.1.4 Time-to-event outcome measure
4.1.5 Ratio of times to progression
Two-stage designs
4.2.1 Binary outcome measure
4.2.2 Continuous outcome measure
4.2.3 Multinomial outcome measure
4.2.4 Time-to-event outcome measure
4.2.5 Ratio of times to progression
Multi-stage designs
4.3.1 Binary outcome measure
4.3.2 Continuous outcome measure
4.3.3 Multinomial outcome measure
4.3.4 Time-to-event outcome measure
4.3.5 Ratio of times to progression
Continuous monitoring designs
4.4.1 Binary outcome measure
4.4.2 Continuous outcome measure
4.4.3 Multinomial outcome measure
4.4.4 Time-to-event outcome measure
4.4.5 Ratio of times to progression
Three-outcome designs
4.5.1 Binary outcome measure
4.5.2 Continuous outcome measure
4.5.3 Multinomial outcome measure
4.5.4 Time-to-event outcome measure
4.5.5 Ratio of times to progression
Phase II/III designs
4.6.1 Binary outcome measure
4.6.2 Continuous outcome measure
4.6.3 Multinomial outcome measure
4.6.4 Time-to-event outcome measure
4.6.5 Ratio of times to progression
Randomised discontinuation designs
4.7.1 Binary outcome measure
4.7.2 Continuous outcome measure
4.7.3 Multinomial outcome measure
4.7.4 Time-to-event outcome measure
4.7.5 Ratio of times to progression

5 Treatment selection designs

70
70
72
72
72
73
74
75
75
75
75
75
75
76
76
76
76
76
76
76
76
77
77
77
77
77
77
77
77
79
80
81
81
82
82
82
82
82
82
83

Sarah Brown

5.1

Including a control arm
5.1.1 One-stage designs
5.1.2 Two-stage designs

84
84
84

CONTENTS

5.1.3
5.1.4
5.1.5
5.1.6
5.1.7

5.2

Multi-stage designs
Continuous monitoring designs
Decision-theoretic designs
Three-outcome designs
Phase II/III designs – same primary outcome measure at
phase II and phase III
5.1.8 Phase II/III designs – different primary outcome measures
at phase II and phase III
5.1.9 Randomised discontinuation designs
Not including a control arm
5.2.1 One-stage designs
5.2.2 Two-stage designs
5.2.3 Multi-stage designs
5.2.4 Continuous monitoring designs
5.2.5 Decision-theoretic designs
5.2.6 Three-outcome designs
5.2.7 Phase II/III designs – same primary outcome measure at
phase II and phase III
5.2.8 Randomised discontinuation designs

6 Designs incorporating toxicity as a primary outcome

88
89
89
89
89
99
102
103
103
106
108
109
110
110
110
111
112

Sarah Brown

6.1

6.2

6.3

6.4

Including a control arm
6.1.1 One-stage designs
6.1.2 Two-stage designs
6.1.3 Multi-stage designs
Not including a control arm
6.2.1 One-stage designs
6.2.2 Two-stage designs
6.2.3 Multi-stage designs
6.2.4 Continuous monitoring designs
Toxicity alone
6.3.1 One stage
6.3.2 Continuous monitoring
Treatment selection based on activity and toxicity
6.4.1 Two-stage designs
6.4.2 Multi-stage designs
6.4.3 Continuous monitoring designs

7 Designs evaluating targeted subgroups

112
112
114
115
117
117
118
122
125
126
126
127
128
128
129
129
131

Sarah Brown

7.1

One-stage designs
7.1.1 Binary outcome measure

131
131

CONTENTS

7.2

Two-stage designs
7.2.1 Binary outcome measure
Multi-stage designs
7.3.1 Binary outcome measure
7.3.2 Time-to-event outcome measure
Continuous monitoring designs
7.4.1 Binary outcome measure
7.4.2 Time-to-event outcome measure

132
132
135
135
137
138
138
139

8 ‘Chemo-radio-sensitisation’ in head and neck cancer

141

7.3

7.4

John Chester and Sarah Brown

Stage 1 – Trial questions
Therapeutic considerations
Primary intention of trial
Number of experimental treatment arms
Primary outcome of interest
Stage 2 – Design components
Outcome measure and distribution
Randomisation
Design category
Possible designs
Stage 3 – Practicalities
Practical considerations for selecting between designs
Proposed trial design
Summary
9 Combination chemotherapy in second-line treatment of non-small
cell lung cancer

141
141
142
142
142
142
142
143
143
144
146
146
148
150

151

Ornella Belvedere and Sarah Brown

152
152
152
152
152
153
153
153
153
154
155
155
158
162

xii

CONTENTS

10 Selection by biomarker in prostate cancer

163

Rick Kaplan and Sarah Brown

164
164
164
164
164
165
165
165
166
167
168
168
170
171
174

Sarah Brown and Steve Schey

Stage 1 – Trial questions
Therapeutic considerations
Primary intention of trial
Number of experimental arms
Primary outcome of interest
Stage 2 – Design components
Outcome measure and distribution
Randomisation
Design category
Possible designs
Stage 3 – Practicalities
Practical considerations for selecting between designs
Proposed trial design
Summary
12 Targeted therapy for advanced colorectal cancer

174
174
175
175
175
176
176
176
177
177
178
178
181
182
185

Matthew Seymour and Sarah Brown

185
185
186
186
186
187
187
187

CONTENTS

xiii

Design category
Possible designs
Stage 3 – Practicalities
Practical considerations for selecting between designs
Proposed trial design
Summary

188
189
190
190
191
194

Phase II oncology trials: Perspective from industry

195

Anthony Rossini, Steven Green and William Mietlowski

13.1
13.2
13.3

13.4

Introduction
Commercial challenges, drivers and considerations
Selecting designs by strategy
13.3.1 Basic strategies addressed by phase II studies
13.3.2 Potential registration
13.3.3 Exploratory activity
13.3.4 Regimen selection
13.3.5 Phase II to support predicting success in phase III
13.3.6 Phase II safety trials
13.3.7 Prospective identification of target populations
Discussion

195
196
197
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198
203
204
206
208
209
210

References

213

Index

227

Contributors
Sarah Brown Clinical Trials Research Unit, Leeds Institute of Clinical Trials
Research, University of Leeds, UK.
This book was collectively written by Sarah Brown with contributions from:
Ornella Belvedere Department of Oncology, York Hospital, York, UK.
Julia Brown Clinical Trials Research Unit, Leeds Institute of Clinical Trials
Research, University of Leeds, UK.
Marc Buyse International Drug Development Institute, Louvain-la-Neuve, Belgium.
John Chester Institute of Cancer and Genetics, School of Medicine, Cardiff University, and Honorary Consultant, Velindre Cancer Centre, Cardiff, UK.
Steven Green Novartis Pharma AG, Basel, Switzerland.
Walter Gregory Clinical Trials Research Unit, Leeds Institute of Clinical Trials
Research, University of Leeds, UK.
Rick Kaplan Medical Research Council Clinical Trials Unit at University College
London, University College London Hospital, and NIHR Cancer Research Network
Coordinating Centre, UK.
William Mietlowski Novartis Pharma AG, Basel, Switzerland.
Mahesh Parmar Medical Research Council Clinical Trials Unit at University
College London, and NIHR Cancer Research Network Coordinating Centre, UK.
Anthony Rossini Novartis Pharma AG, Basel, Switzerland.
Steve Schey Kings College, London, and Lead Myeloma Clinician, Kings College
Hospital, London, UK.
Matthew Seymour Leeds Institute of Cancer and Pathology, University of Leeds,
and NIHR Cancer Research Network, Leeds and National Cancer Research Institute,
London, UK.
Chris Twelves Leeds Institute of Cancer and Pathology, University of Leeds, and St
James’s University Hospital, Leeds, UK.

Foreword I
The past two decades have seen an unprecedented expansion in the knowledge about
the biological, immunological and molecular phenomena that drive malignancy. This
knowledge has subsequently been translated into a large number of potential anticancer therapeutics and potential predictive or prognostic molecular markers that are
under evaluation in clinical trials.
A key component of the oncology clinical trials development process is the
bridge that must be crossed between the end of phase I evaluation of a drug, at
which time information on its recommended dose, schedule, pharmacokinetic and
pharmacodynamics effects in a small group of individuals is available, and the definitive randomised efficacy trial of that drug in the appropriately defined population of
cancer patients.
This ‘bridge’ is provided by the phase II trial. Historically, phase II oncology studies sought evidence of sufficient drug efficacy (based on objective tumour response
in a specific cancer type) that large confirmatory phase III trials would be justified.
Those not meeting the efficacy bar would not be pursued in further studies in that
tumour type. In today’s highly competitive environment, the phase II study has come
under scrutiny – some have expressed the concern that too many ‘promising’ drugs
emerging from phase II studies yield negative phase III results, that clinical trial endpoints traditionally deployed in phase II may not be specific or sensitive enough for
today’s molecular-based agents to appropriately direct subsequent drug development
decisions, that efficiency is lost if discrete phase II and phase III trials are designed
and that much more should be learned about predictive or selection biomarkers before
and during phase II to optimally guide phase III design.
Numerous papers and opinion pieces on these and other phase II–related topics
have been published in the past decade. Thus this new book by Brown and colleagues:
A Practical Guide to Designing Phase II Trials in Oncology is a welcome addition
to the literature. This comprehensive and well-written guide takes a logical and stepby-step approach by reviewing and making recommendations on the key variables
that must be considered in phase II oncology trials. Some of these include tailoring
design components to the specific trial question, the approach to studies of singleand combination-agent trials, when and how randomised and adaptive designs might
be deployed, patient selection and phase II trial endpoints. In addition, the book drills
into issues that may be unique to designs in several specific malignancies such as

xviii

FOREWORD I

non-small cell lung cancer, prostate cancer and myeloma. Throughout, examples are
utilised as a means of providing context and guiding the reader.
What is clear is that the phase II oncology trial is not a singular or simple
construct. There is no formula for its design that meets all potential needs. These
trials the ‘shape-shifters’ of the cancer trial spectrum – how they are designed, the
endpoints that are utilised, and the population enrolled depends on the agent and its
associated biology, the type of cancer, the question the trial is intended to address
and how those results are intended to guide future decisions. This comprehensive text
provides much-needed practical information in this important area of clinical cancer
research.
Elizabeth A. Eisenhauer, MD, FRCPC
Head, Department of Oncology
Queen’s University
Kingston, ON, Canada

Foreword II
Twenty years ago, in the early 1990s, the term ‘phase II trial design’ was practically
synonymous with the Simon optimal and MINIMAX two-stage trials (1989) – designs
which have stood the test of time with their pragmatic trade-off between the need to
stop a trial early for inefficacy if response rates were low and the likely overshoot of
interim analysis points in small trials. The Gehan design was also widely used but
many statisticians were wary of designs which focussed on estimation but did not
have distinct success/failure rules which allowed error rates to be tightly specified.
The field of phase II trial design has expanded rapidly since these early days,
particularly in oncology. Phase I trial design has also been extended over the years to
go beyond mere dose finding and frequently includes an expansion phase at the chosen
dose level which provides initial information on efficacy and pharmacodynamic
predictors of response. Ideally this should enhance the relevance of the subsequent
phase II trials.
This book presents a much-needed guide to contemporary phase II clinical trial
design. Over the years trial endpoints have diversified to include the greater use
of endpoints such as progression free survival that cater for treatments that may
not cause tumour shrinkage and are thought to act by halting cancer cell growth
rather than killing the cell (cytostatic rather than cytotoxic). Recognition of the
inaccuracies inherent in designing trials on the basis of the expected response gleaned
from historical data has also seen more focus on the use of randomisation and the
incorporation of a control group. The increasing emphasis on stratified medicine,
recognising the need to tailor treatments more closely to the biological characteristics
of the individual patient’s disease, has also led to phase II trials designed to address
this need.
The recognition of the division between phase IIa trials designed to investigate
efficacy and phase IIb trials, which focus on determining whether a phase III trial
is worth undertaking, has also been welcome. The latter have increased in size and
complexity in an effort to forestall the possibility of a negative phase III trial. It
has been suggested that as many as two out of every three phase III oncology trials
are negative – a situation which is of real concern, given that drug development is
increasing in expense and comparatively few gain regulatory approval. It is reassuring
to note the number of phase II/III designs that have been developed to closely link
the development of phase II and phase III, but in some situations this is not possible.

FOREWORD II

The Simon Optimal Design (Simon 1989) is perhaps the seminal phase II single
arm design, and it is salutary to see how frequently this design is used and has acted
as a springboard for the development of other designs. It is frequently possible to add
judiciously placed interim analyses to trials without increasing the number of patients
or having an adverse effect on the error rates – a manoeuvre which is worth bearing
in mind. For example, the two-stage Simon MINIMAX design, which minimises
the number of patients needed to assess a binary endpoint, is frequently the same
size as the one-stage exact design – on occasion, the MINIMAX design is even
marginally smaller than the single-stage design! The MINIMAX design illustrates
the point that an optional futility interim analysis can be built into a planned onestage trial of a binary endpoint without increasing the number of patients or adversely
affecting the error rates. Alternatively, note that a one-stage design can frequently
be converted into a two-stage design by including a futility interim analysis at N/2
(here N is the fixed sample single-stage trial size or could be the number of events
for a time-to-event endpoint). The trial would be stopped on the grounds of futility if
the primary endpoint parameter did not exceed the value under the null hypothesis.
This approach is seen in the design mentioned by Whitehead (2009, Section 4.2.1).
A general boundary rule that I have also used is the p ≤ 0.001 rule (Peto–Haybittle)
and related to this are common-sense considerations that should not be overlooked.
For example, if five or more responses in a 41-patient trial are needed to demonstrate
efficacy, as soon as five responses have been observed the efficacy threshold for the
trial has been passed, and it is clear a phase III trial will be recommended. If the
toxicity profile is acceptable, the fact the efficacy criteria has been met should be
disseminated so that planning for the follow-on phase III trial can commence.
This book will act as a valuable reference source in addition to giving sound
practical guidance. The authors identify a number of areas that have not been explored;
for example, no references were identified for randomised trials with a multinomial
outcome measure (Section 4.1.3). Statisticians who read this book could perhaps ask
themselves which neglected areas they think deserve the highest priority. As regards
phase IIb designs, I would like to see a three-outcome version of the randomised
Simon (2001) design (Section 4.1.4) based on progression-free survival.
Roger A’Hern
Senior Statistician
Clinical Trials and Statistics Unit
Institute of Cancer Research
Sutton, United Kingdom

Preface
Phase II trials are a key element of the drug development process in cancer, representing a transition from initial evaluation in relatively small phase I studies, not
only focused on safety but also increasingly incorporating translational studies, to
definitive assessment of efficacy often in large randomised phase III trials. Efficient
design of these early phase trials is crucial to informed decision-making regarding
the future of a drug’s development. There are a number of textbooks available that
discuss statistical issues in early phase clinical trials. These cover pharmacokinetics
and pharmacodynamics studies, through to late phase II trials, and discuss issues
around sample size calculation and methods of analysis. There are few, however,
which focus specifically on phase II trials in cancer, and the many elements involved
in their design. Given the large number and variety of phase II trial designs, often
conceptually innovative, and involving multiple components, the purpose of this book
is to provide practical guidance to researchers on appropriate phase II trial design in
cancer.
This book provides an overview to clinical trial researchers of the steps involved
in designing a phase II trial, from the initial discussions regarding the trial idea itself,
through to identification of an appropriate phase II design. It is written as an aid
to facilitate ongoing interaction between clinicians and statisticians throughout the
design process, enabling informed decision-making and providing insight as to how
information provided by clinicians feeds into the statistical design of a trial. The book
acts both as a comprehensive summary resource of traditional and novel phase II trial
designs and as a step-by-step approach to identifying suitable designs.
We wanted to provide a practical and structured approach to identifying appropriate statistical designs for trial-specific design criteria, considering both academic
and industry perspectives. A comprehensive library of available phase II trial designs
is included, and practical examples of how to use the book as a resource to design
phase II trials in cancer are given. We have purposely omitted methodological detail
associated with statistical designs for phase II trials, as well as discussion of analysis,
that can be found elsewhere, including in the references for each of the designs listed
in the library of designs.
The book begins with an introduction to phase II trials in cancer and their role
within the drug development process. A structured thought process addressing the
key elements associated with identifying appropriate phase II trial designs is introduced in Chapter 2, including therapeutic considerations, outcome measures and

xxii

PREFACE

randomisation. Each of these elements is discussed in detail, describing the different
stages of the thought process around which the guidance is centred. The purpose of
this detailed information is to allow readers to narrow down the number of designs that
are relevant to their trial-specific design criteria. A comprehensive library of phase II
designs is presented in Chapters 3–7, categorised according to design criteria, and a
brief summary of each trial design available is included.
Chapters 8–12 outline a series of practical examples of designing phase II trials in
cancer, providing practical illustration from trial concept to using the library to select
an appropriate trial design. The examples give a flavour of how one might apply the
process described within the book, highlighting that there is no ‘one size fits all’
approach to trial design and that there are often many design solutions available to
any one scenario. We hope the book will help researchers to shortlist their options
in order to select an appropriate design to their specific setting, acknowledging other
options that may be considered.
This book has been written predominantly by academic clinical trialists, involving
both clinicians and statisticians. Many of the issues and considerations described
from an academic point of view are, however, also relevant to trials sponsored by
the pharmaceutical industry. The final chapter of this book describes the design of
phase II trials in cancer from the industry perspective. The commercial perspective
is described in detail, outlining the design processes for phase II trials according to
specific strategic goals. This highlights both the similarities and differences in the
approach to phase II trial design between academia and industry. In the academic
setting there may be more focus on the phase II trial itself and less on the overall
development programme of the drug, compared to industry where the trial is designed
as part of a programme-oriented clinical development plan.
The book is written for both clinicians and statisticians involved in the design
of phase II trials in cancer. Although some elements are written primarily with
statisticians in mind, the discussion around key concepts of phase II trial design,
as well as the practical examples, is accessible to scientists and clinicians involved
in clinical trial design. For those new to early phase trial design, the book provides
an introduction to the concepts behind informed decision-making in phase II trials,
offering a unique and practical learning tool. For those familiar with phase II trial
design, we hope the reader will benefit from exposure to new, less familiar trial
designs, providing alternative options to those which they may have previously used.
The book may also be used by postgraduate students enrolled on statistics courses
including a clinical trial or medical module, providing a useful learning tool with
core information on phase II trial design.
We hope that readers will benefit from the step-by-step approach described, as
well as from the library of designs presented, enabling informed decision-making
throughout the design process and focused guidance on designs that fit researchers’
pre-specified criteria.
Finally, we would like to thank all our colleagues who have contributed to this
book, for their advice and support.

Introduction
Sarah Brown, Julia Brown, Walter Gregory
and Chris Twelves

Traditionally, cancer drug development can be defined by four clinical testing phases
(Figure 1.1):

∙

Phase I is the first clinical test of a new drug after pre-clinical laboratory
studies and is designed to assess the safety, toxicity and pharmacology of
differing doses of a new drug. Typically such studies involve a limited number
of patients and ask the question ‘Is this drug safe?’

∙

Phase II studies are designed to answer the question ‘Is this drug active, and is
it worthy of further large-scale study?’ They predominantly address the shortterm activity of a new drug, as well as assessing further safety and toxicity.
Typically sample sizes for phase II studies range from tens to low hundreds of
patients.

∙

Phase III trials are often large-scale trials of hundreds, even thousands, of
patients and are usually designed to formally evaluate whether a new drug is
more effective in terms of efficacy or toxicity than current treatments. Here the
focus generally is on long-term efficacy, with the aim of identifying practicechanging new drugs.

∙

Finally, phase IV studies are carried out once a drug is licensed or approved
for a specific indication. Within the pharmaceutical industry setting, phase
IV studies may be designed to collect long-term safety information; in the
academic setting, phase IV trials may investigate the efficacy of a drug outside
of its licensed indication.

A Practical Guide to Designing Phase II Trials in Oncology, First Edition.
Sarah R. Brown, Walter M. Gregory, Chris Twelves and Julia Brown.
© 2014 John Wiley & Sons, Ltd. Published 2014 by John Wiley & Sons, Ltd.

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

Phase I

Phase II

Phase III

Phase IV

• Determine dose and
preliminary toxicity
• Sample size–low tens

• Establish intermediate
activity
• Gain further toxicity
information
• Sample size–high
tens to hundreds

• Validate efficacy and
obtain further
toxicity information
• Sample size–
hundreds to
thousands

• Post-marketing
surveillance

Figure 1.1 Four clinical phases of drug development.

Presented in this way drug development may appear to be a straight line pathway, but
this is often not the case in practice, with much more time and money invested in large
phase III trials than in other stages of development. Likewise, the boundaries between
the different stages of drug development are increasingly blurred. For example, many
phase I trials treat an expanded cohort of patients at the recommended phase II dose
often at least in part to demonstrate proof of principle or seek evidence of activity.
In recent years a wide range of new ‘targeted’ cancer therapies have emerged with
well-defined mechanisms of action directed at specific molecular pathways relevant
to tumour growth and often anticipated to be used in combination with other standard
treatments. This contrasts with cytotoxic chemotherapy from which the traditional
four phases of cancer drug development emerged. Nevertheless, phase II cancer trials
retain their pivotal position between initial clinical testing and costly, time-consuming
definitive efficacy studies.
The process from pre-clinical development to new drug approval typically takes
up to 10 years and is estimated to cost hundreds of millions of dollars, although
there is some uncertainty over the true costs (Collier 2009). Cytotoxic therapies,
which lack a specific target and mechanism of action, often have a low therapeutic
index, and historically have high rates of failure during drug development due to
lack of efficacy and/or toxicity (Walker and Newell 2009). Although attrition rates
for targeted cancer therapies appear lower than those of cytotoxic drugs, more drugs
progress to expensive late stages of development before being abandoned in cancer
than other therapeutic areas (DiMasi and Grabowski 2007). These worrying statistics
have led to increased attention on clinical trial design, aiming to reduce the attrition
rate and improve the efficiency of cancer drug development.
This book focuses on the high-risk transition between phase II and III clinical
trials and provides a practical guide for researchers designing phase II clinical trials
in cancer. There is a clear need for phase II trials that more accurately identify
potentially effective therapies that should move rapidly to phase III trials; perhaps
even more pressing is the need for earlier rejection of ineffective therapies before they
enter phase III testing. On this basis we aim to provide researchers with a detailed
background of the key elements associated with designing phase II trials in patients
with cancer, a thought process for identifying appropriate statistical designs and a
library of available phase II trial designs. The book is not intended to be proscriptive
or didactic, but instead aims to facilitate and encourage an interactive approach by

INTRODUCTION

the clinical researcher and the statistician, leading to a more informed approach to
designing phase II oncology trials.

1.1

The role of phase II trials in cancer

Phase II trials in cancer are primarily designed to assess the short-term activity of
new treatments and the potential to move these treatments forward for evaluation of
longer-term efficacy in large phase III studies. In this respect, the term ‘activity’ is
used to describe the ability of an investigational treatment to produce an impact on
a short-term or intermediate clinical outcome measure. We distinguish this from the
term ‘efficacy’ which we use to describe the ability of an investigational treatment
to produce a significant impact on a longer-term clinical outcome measure such as
overall survival in a definitive phase III trial. Cancer phase II trials are therefore
invariably conducted in the metastatic or neo-adjuvant settings, where measurable
short-term assessments of activity are more easily obtained than in the adjuvant
setting. We focus on phase II trials in cancer, where assessments of ‘activity’ are
usually not immediate and cure not achievable. Nevertheless, many of the statistical
designs available for phase II cancer trials, and concepts discussed, may be applied
to other disease areas.
Phase II trials act as a screening tool to assess the potential efficacy of a new
treatment. That broad description incorporates many different types of phase II trials
including assessing not only traditional evidence of tumour response but also proof
of concept of biological activity, selection between potential doses for further development, choosing between potential treatments for subsequent phase III testing and
demonstration that the addition of a new agent to an established treatment appears to
increase the activity of that treatment.
In 1982 Fleming stated that ‘Commonly the central objective of phase II clinical
trials is the assessment of the antitumor “therapeutic efficacy” of a specific treatment
regimen’ (Fleming 1982). More recently the objective of a phase II trial in an idealised
pathway has been described to ‘establish clinical activity and to roughly estimate
clinical response rate in patients’ (Machin and Campbell 2005). Others have taken
this a step further to claim ‘The objective of a phase II trial should not just be to
demonstrate that a new therapy is active, but that it is sufficiently active to believe that
it is likely to be successful in pivotal trials’ (Stone et al. 2007a). A common feature
of phase II trials is that their aim is not primarily to provide definitive evidence of
treatment efficacy, as in a phase III study; rather, phase II trials aim to show that a
treatment has sufficient activity to warrant further investigation.
The International Conference on Harmonisation (ICH) Guideline E8: General
Considerations for Clinical Trials prefers to consider classification of study objectives rather than specific trial phases, since multiple phases of trials may incorporate
similar objectives (ICH Expert Working Group 1997). The objectives associated with
phase II trials in the ICH guidance are predominantly to explore the use of the treatment for its targeted indication; estimate or confirm dosage for subsequent studies;
and provide a basis for confirmatory study design, endpoints and methodologies.

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

Additionally, however, ICH notes that phase II studies, on some occasions, may
incorporate human pharmacology (assessing tolerance; defining or describing
pharmacokinetics/pharmacodynamics; exploring drug metabolism and interactions;
assessing activity) or therapeutic confirmation (demonstrating/confirming efficacy;
establishing a safety profile; providing an adequate basis for assessing benefit/risk
relationship for licensing; establishing a dose/response relationship).
These definitions have in common that oncology phase II trials act as an intermediate step between phase I testing on a limited number of patients to establish the
safety of a new treatment and definitive phase III trials aiming to confirm the efficacy
of a new treatment in a large number of patients. The specific aims of a phase II trial
may, however, differ depending on the mechanism of action of the drug in question,
the amount of information currently available on the drug and the setting in which it
is being investigated (e.g. pharmaceutical industry vs. academia). Phase II trials can
be broadly grouped into phase IIa and phase IIb trials. A phase IIa trial may be seen
as seeking proof of concept in the sense of assessing activity of an investigational
drug that has completed phase I development or may investigate multiple doses of a
drug to determine the dose–response relationship. Phase IIa trials may be considered
learning trials and be followed by a decision-making ‘go/no-go’ phase IIb trial to
determine whether or not to proceed to phase III; phase IIb trials may include selection of a single treatment or dose from many and may include randomisation to a
control arm.
Dose–response can be evaluated throughout the early stages of drug development,
including phase II, but this book does not specifically address studies where this is
the primary aim. Many designs are available to assess the dose–response relationship,
perhaps the simplest and most common being the randomised parallel dose–response
design incorporating a control arm and at least two differing dose levels. Cytotoxics
are usually given at the highest feasible dose, but investigating dose–response relationships may be important with targeted agents that are not necessarily best given
at the maximum possible dose. Such trials serve a number of objectives including
the confirmation of efficacy; the estimation of an appropriate dose; the identification
of optimal strategies for individual dose adjustments; the investigation of the shape
and location of the dose–response curve; and the determination of a maximal dose
beyond which additional benefit would be unlikely to occur.
Considerations around choice of starting dose, study design and regulatory issues
in obtaining dose–response information are provided in the ICH Guideline E4: Dose
Response Information to Support Drug Registration (ICH Expert Working Group
1994). Such considerations are, however, outwith the remit of this book, which
focuses on phase II trials designed to assess activity of single-agent or combination
therapies or those designed to select the most active of multiple therapies. We do,
however, discuss phase II selection designs to identify the most active dose from a
number of pre-specified doses rather than specific issues around evaluating dose–
response relationships.
There are often significant differences between trials conducted within the pharmaceutical industry and those conducted within academia. Such differences are
predominantly associated with the approach to designing phase II trials, within

INTRODUCTION

a portfolio of research, and decision-making around the future development of a
compound or drug. Consequently, the way in which clinical trials are designed,
particularly in the early phase setting, will likely differ between the two environments. For example, in the academic setting, regardless of the specific aim of the
phase II trial (e.g. proof of concept, go/no-go), decision criteria are pre-specified
to correspond with the primary aim of the trial and form the criteria on which
decision-making and conclusions of the trial are based. Within the pharmaceutical
industry the same pre-defined study aims and objectives apply; however, decisionmaking may be complicated by additional factors external to the phase II trial itself,
such as the presence of competitor compounds, patent life or company strategy.
There is inherent pressure within the pharmaceutical industry to achieve timely
regulatory approval and a license indication for a new drug. This does not apply
in the same way within the academic setting where, by the time a drug reaches
phase II testing, it may have been through considerable testing within the pharmaceutical setting and perhaps be already licensed in alternative disease areas or
in differing combinations or schedules. There are, however, initiatives to facilitate
increased academic/pharmaceutical collaboration in the early stages of drug development. Thus, more academic phase II trials may be conducted using novel agents
with only limited clinical data available, so thorough discussion of the aims and
design of these trials becomes even more pertinent. A detailed insight into the industry approach to the design of phase II trials within a developing drug portfolio is
provided in Chapter 13. By contrast, the remainder of this book, including terminology and practical examples of designing phase II trials, draws its focus from the
academic setting.

1.2

The importance of appropriate phase II
trial design

Design of phase II trials is a key aspect of the drug development process. Poor
design may lead to increased probabilities of a false-positive phase II trial resulting
in unnecessary investment in an unsuccessful phase III trial; or a false-negative phase
II resulting in the rejection of a potentially effective treatment. There is a pressing
need for phase II trials to more accurately identify those cancer therapies that will
ultimately be successful in phase III studies and to allow earlier rejection of ineffective
therapies before undertaking costly and time-consuming phase III trials.
As the development of new cancer drugs moves further away from conventional
cytotoxics and more into targeted therapies, the challenges and opportunities in
phase II trial design are ever greater. The choice of phase II design includes not only
statistical considerations, but also decisions regarding the aims of the trial, whether
or not to include randomisation, the choice of endpoints and the size of treatment
effects to be targeted. Each of these elements is critical to ensure the phase II trial
is designed and conducted efficiently and that the results of the trial may be used to
make robust, informed decisions regarding future research.

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

Some researchers have suggested moving directly from phase I to phase III in the
drug development process, on the basis that survival benefit in phase III trials may
be observed in the absence of improved response rates therefore rendering phase II
irrelevant (Booth et al. 2008). The potential perils of this approach are demonstrated
by the INTACT1 and INTACT2 trials of gefitinib in chemotherapy-naı̈ve advanced
non-small cell lung cancer (NSCLC) patients (Giaccone et al. 2004; Herbst et al.
2004). Phase I trials of gefitinib in combination with chemotherapy had shown
acceptable tolerability and gefitinib as monotherapy was active in phase II NSCLC
trials; however, phase II trials of gefitinib in combination with chemotherapy were
not performed. Subsequently, these two phase III NSCLC trials in over 2000 patients
failed to show improved efficacy with the addition of gefitinib to cisplatin-based
chemotherapy (Giaccone et al. 2004; Herbst et al. 2004). A conventional, single-arm
NSCLC trial of gefitinib in combination with chemotherapy may have avoided the
subsequent negative phase III trials. This experience highlights the importance of
designing and conducting appropriately designed and potentially novel phase II trials
prior to embarking on large-scale phase III trials.

1.3 Current use of phase II designs
Several systematic reviews have considered current use of designs in published phase
II trials in cancer (Lee and Feng 2005; Mariani and Marubini 2000; Perrone et al.
2003). Common approaches to trial design included single-arm studies with objective
response as the primary efficacy endpoint, utilising Simon’s two-staged hypothesis
testing methods (Simon 1989), and randomised trials based on single-arm designs
embedded in a randomised setting (Lee and Feng 2005). All highlighted a distinct
lack of detail regarding an identifiable statistical design, and design characteristics,
as a marked weakness of many published phase II studies, raising the possibility
that low quality may bias study findings. Also striking is the consistent use of a
limited number of the same phase II study designs, emphasising the need for better
understanding of alternative statistical designs. A key recommendation from these
reviews is better communication between statisticians and clinical trialists to increase
the use of newer statistical designs. Likewise, the need for ‘the development of
practical designs with good statistical properties and easily accessible computing
tools with friendly user interface’ (Lee and Feng 2005) is recognised as essential so
statisticians can implement these new designs.
In 2009 the Journal of Clinical Oncology (JCO) published an editorial making
recommendations for the types of phase II trials that they would consider for publication (Cannistra 2009). The differing aims of phase II trials according to the nature
of the treatment under investigation were identified, with discussion as to the likely
priority given to each trial design. The specific categories and outcomes of phase II
trials were

∙

single-arm phase II studies that represent the first evidence of activity of a new
drug class;

INTRODUCTION

∙

phase II studies of novel agents that not only confirm a class effect, but also
provide evidence of extraordinary and unanticipated activity compared to prior
agents in the same class;

∙

phase II studies of an agent or regimen with prior promise (based on previous
reports of clinical activity), but that are convincingly negative when studied
more rigorously;

∙

phase II studies of a single-agent or combination that convincingly demonstrate
a new, serious and unanticipated toxicity signal, despite being a rational and
potentially active regimen;

∙

phase II studies with biomarker correlates that validate mechanism of action,
provide convincing insight into novel predictive markers or permit enrichment
of patients most likely to benefit from a novel agent;

∙

randomised phase II studies such as randomised selection, randomised comparison and randomised discontinuation designs.

The consistent use of single-arm, two-stage, response-driven designs as depicted
in the systematic reviews described previously would not optimally cover the majority
of these trial scenarios. The categories listed above were intended to provide authors
with guidance as to the types of phase II trials most relevant to informing the design of
subsequent phase III trials. Such recommendations highlight the need for awareness of
the many components contributing to the design of phase II trials and the importance
of making informed decisions to achieve the objectives of a trial and ensure the results
are robust and interpretable.

1.4

Identifying appropriate phase II trial designs

This book aims to provide guidance to both the clinical researcher and statistician
on each of the key elements of phase II trial design, enabling an understanding of
how they inform the overall design process. Recommendations published by the
Clinical Trial Design Task Force of the National Cancer Institute Investigational
Drug Steering Committee (Seymour et al. 2010) and by the Methodology for the
Development of Innovative Cancer Therapies (MDICT) Task Force (Booth et al.
2008) provide guidance on current best practice for individual aspects of early clinical
trial design. General discussion of choice of endpoints and use of randomisation
is given for the differing settings of monotherapy and combination therapy trials
(Seymour et al. 2010), as well as in the specific context of targeted therapies (Booth
et al. 2008), and discussion on reporting of phase II trials is also provided. Neither set
of recommendations, however, provides detailed guidance on the statistical design
categories available for phase II trials. Here we aim to guide researchers in a stepby-step manner through the thought process associated with each element of phase
II design, from initial trial concept to the identification of an appropriate statistical
design. With detailed discussion on each of the elements we aim to provide researchers

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

with a thorough understanding of the overall process and each of the stages involved,
therefore providing a more informed approach.
Central to this approach is an overall thought process, presented in detail in Chapter 2 and outlined briefly below. The approach consists of three stages, highlighting
eight key elements associated with identifying an appropriate phase II trial design:

∙

Stage 1 – Trial questions:
◦ Therapeutic considerations
◦ Primary intention of trial
◦ Number of experimental treatment arms
◦ Primary outcome of interest

∙

Stage 2 – Design components:
◦ Outcome measure and distribution
◦ Randomisation
◦ Design category

∙

Stage 3 – Practicalities:
◦ Practical considerations

Each of these elements is discussed in detail in Chapter 2, and practical examples
of using this approach to design phase II cancer trials are provided in Chapters 8–12.
These elements were identified as being essential to the design of phase II trials in
cancer through a comprehensive literature review of available statistical methodology
for phase II trials (Brown et al. 2011). The thought process itself is iterative, such that
information obtained during discussion of each element may feed into and inform
later elements of the design. The starting point of any trial design should, however, be a
discussion between the clinical researcher and the statistician that primarily concerns
clinical factors relating to the specific treatment(s) under investigation (Stage 1).
Continued interaction between the clinician and the statistician is essential throughout
the design process.
Using the detail provided in Chapter 2, each of the elements is addressed in
turn and iteratively. Decisions made throughout the process enable the statistician to
narrow down the specific statistical designs appropriate to the pre-specified criteria.
These statistical designs are provided in Chapters 3–7, a library resource of statistical
designs, as introduced here. Each design is categorised to enable efficient navigation
and identification of appropriate designs. Designs are laid out taking into account

∙

The use of randomisation including
◦ Single-arm designs, arranged by design category and outcome measure –
Chapter 3

INTRODUCTION

◦ Randomised designs, arranged by design category and outcome measure –
Chapter 4
◦ Treatment selection designs, arranged by inclusion of a control arm, design
category and outcome measure – Chapter 5

∙

The focus on both activity and toxicity, or toxicity alone, as the primary outcome
of interest – Chapter 6

∙

The evaluation of treatment activity in targeted subgroups – Chapter 7

Within each of Chapters 3–5, where there is no identified literature for specific design category and outcome measure combinations, this is highlighted within
the relevant subsection. For example, there were no references identified discussing
single-arm trial designs specifically focused on continuous outcome measures, therefore this subsection is included to highlight this to the reader. For Chapters 6 and 7,
only those specific design category and outcome measure combinations for which
references have been identified are listed, since generally there are fewer designs
focused on activity and toxicity and targeted subgroups.
In the majority of cases there will be more than one statistical design that suits the
pre-specified trial parameters determined via the thought process. In such cases, the
final stage in the thought process, that of practical considerations, may allow a choice
to be made between the alternatives. On the other hand, that choice may be based
on previous experience or assessment of various trial scenarios by mathematical
modelling or simulation. Further detail on choosing between multiple designs is
provided in Chapter 2.

1.5

Potential trial designs

The statistical designs summarised in Chapters 3–7 were identified from a comprehensive literature review of phase II statistical design methodology conducted in
January 2008 and updated in January 2010 (Brown et al. 2011). Individual designs
were specifically assessed to determine their ease of implementation. Designs were
defined as not easy to implement if

∙
∙

the data required to enable implementation were not likely to be available;

∙

criteria were not specified for the study being positive or negative as this makes
the trial of little if any use in taking a new treatment forward;

∙

each patient needed to be assessed prior to the next patient being recruited, as
this will usually be prohibitively restrictive in a phase II cancer trial; and

∙

the necessary statistical softwares were not detailed as being available and/or
insufficient detail was provided to enable implementation.

there was no sample size justification rendering the design difficult or impossible to interpret;

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

While this assessment of ease of implementation is inherently subjective, these
criteria reflect the practicalities of design implementation.
Applying the above criteria, those designs classed as being easy to implement
are included in Chapters 3–7. This amounts to over 100 statistical designs, ranging
from Gehan’s original two-stage design published in 1961 (Gehan 1961) to complex multi-arm, multi-stage designs of more recent years. Mariani and Marubini
highlighted researchers’ preferences for single-arm, two-stage designs (Mariani and
Marubini 2000); there are, however, a wealth of alternative designs available, ranging
from adaptations of Simon’s original two-stage design to incorporate adjustments for
over-/under-recruitment, to randomised trials with formal hypothesis testing between
experimental and control arms. The intention of this book is to present researchers
with the designs available to them for their specific trial, rather than to recommend
one design over another. In doing so we incorporate the well-established designs of
Gehan (1961), Fleming (1982) and Simon (1989), as well as bringing lesser known
designs to the attention of researchers, allowing the user to make informed choices
regarding trial design. A brief overview of each design identified is presented; however, the technical detail of each design is omitted and may be further evaluated by
considering the complete references, as appropriate.
With the continued development of targeted therapies in cancer, and a drive
towards personalised medicine, the role of biomarkers within phase II trials is an
important area for discussion. Where known biomarkers are available to identify
selected patient populations most likely to benefit from an intervention, phase II trials
may be designed as enrichment trials, whereby only biomarker-positive patients are
included. In these cases, any of the statistical designs listed within Chapters 3–6
may be appropriate, focusing solely on the target population. Alternatively, when
selected populations are perhaps less well validated, biomarker-stratified designs
may be considered. Here both biomarker-positive and biomarker-negative subgroups
are explored within a trial, ensuring adequate numbers of patients within each cohort
to potentially detect differing treatment effect sizes. Such designs are listed within
Chapter 7. A more detailed discussion of the incorporation of biomarkers within phase
II trials in cancer is provided in Chapter 2. There have, however, been a number of
recently published articles in this area that may not be included in the library of
available statistical designs since they post-date the updated systematic review on
which the library is based. Where the incorporation of biomarkers is of particular
relevance to a trial design, the researcher may use the thought process described
within this book and should consider not only any appropriate designs identified in
Chapters 3–7, but also additional, more recent, designs specifically intended for trials
incorporating biomarkers.

1.6 Using the guidance to design your trial
We present a thought process for the design of phase II trials in cancer, introduced
briefly in Section 1.4, addressing the key elements associated with identifying an
appropriate trial design; each of these elements is discussed in detail in Chapter 2.

INTRODUCTION

The information in Chapter 2 will allow researchers to narrow down the number of
appropriate designs for their trial and then navigate to the relevant designs in Chapters
3–7, where a brief summary of each trial design is provided. The statistical theory
underpinning the designs detailed is published elsewhere (Mariani and Marubini
1996; Machin et al. 2008; Machin and Campbell 2005), as well as in the individual
papers referenced.
This process is illustrated in Chapters 8–12 by a series of practical, real-life examples of designing phase II trials in cancer following the thought process and library
of statistical designs. The examples are intended merely as pragmatic illustrations of
how one might apply the process described within the book; they should not be taken
as sole solutions to trial design under the particular settings presented. It is acknowledged that there may be a number of appropriate designs available, and exploration
of various possibilities is encouraged. Examples are presented in the setting of head
and neck cancer, lung cancer, prostate cancer, myeloma and colorectal cancer. Each
example gives differing trial design scenarios highlighting various common issues
encountered when designing phase II trials in cancer. These examples demonstrate
the types of discussions expected between statisticians and clinicians in order to
extract the necessary information to design a phase II trial. They also provide practical advice regarding how choice of design may be made when several designs fit the
trial-specific requirements.

Key points for consideration
Sarah Brown, Julia Brown, Marc Buyse, Walter
Gregory, Mahesh Parmar and Chris Twelves

Designing a phase II trial requires ongoing discussion between the clinician, statistician and other members of the trial team, so the design can evolve on the basis of
information specific to each trial. Central to the approach of identifying an optimal
phase II trial design is the thought process introduced in Chapter 1, and presented
diagrammatically in Figure 2.1. The process provides an overview of the key stages
and elements for consideration during the phase II trial design process. Each of these
elements should be worked through in turn in an iterative manner as information
derived at earlier stages feeds in to design choices and decisions in the latter stages
and consideration of alternative designs.
The thought process is made up of three stages:

∙

Stage 1 – Trial questions. This stage elicits information predominantly relating
to the trial itself in relation to the treatment under investigation, the primary
intention of the trial, number of arms and primary outcome of interest.

∙

Stage 2 – Design components. The information from the first stage feeds
into the discussions relating to design components considering the outcome
measure, randomisation (or not) and category of design, enabling attention to
be focused on the specific statistical designs relevant to the trial.

∙

Stage 3 – Practicalities. Finally, practical considerations may inform which,
from a number of candidate trial designs, is the one best suited to a particular
situation.

Proof of
concept

Go/no-go
decision for
phase III

Mechanism
of action

Aim of
treatment

Biomarker
dependent
(enrichment
or endpoint)

Single or
combination
therapy

Primary
intention of
trial

Therapeutic
considerations

Activity and
toxicity or
Toxicity

Activity

Primary
outcome of
interest

Ratio of
times to
progression

Time-toevent

Multinomial
(e.g. CR vs.
PR vs.
SD/PD)

Continuous
(e.g.
biomarker)

Binary (e.g.
response/no
response)

Outcome measure
and distribution

Randomisation
to experimental
arms (selection)

Randomisation
incl. control,
with formal
comparison

Randomisation
incl. control,
with no formal
comparison
(reference arm
only)

Single arm (no
randomisation)

Targeted
subgroups

Randomised
discontinuation

Phase II/III

Three-outcome

Decision-theoretic

Continuous
monitoring

Multi-stage

Two-stage

One-stage

Operating
characteristics

Early
termination
for evidence
of activity

Early
termination
for lack of
activity

Availability /
robustness of
prior data

Programming
requirements

Practical
considerations

Randomisation
Design category

Stage 3 –
practicalities

Stage 2 – design
components

Figure 2.1 Thought process for identifying phase II trial designs.

More than
one

One

Number of
experimental
treatment arms

Stage 1 – trial
questions

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

This chapter works through each of the stages and components of Figure 2.1.

2.1 Stage 1 – Trial questions
2.1.1

Therapeutic considerations

The choice of trial design depends not only on statistical considerations, but more
importantly on the clinical factors relating to the treatment(s) and/or disease under
investigation. Discussion of these therapeutic considerations is essential to inform
decisions to be made later in the thought process. At the first meeting between the
clinician and statistician, discussion of the following points will provide an overview
of the setting of the trial and the specific therapeutic issues to be incorporated into
the trial design.
2.1.1.1

Mechanism of action

An important question to ask when beginning the trial design process is ‘how does
this treatment work?’ The term ‘cytotoxic’ may be used to describe chemotherapeutic agents, where tumour shrinkage or response is widely accepted as reflecting
anti-cancer activity. Many new cancer therapies are, however, targeted at specific
molecular pathways relevant to tumour growth, apoptosis (programmed cell death)
or angiogenesis (new blood vessel formation). Such ‘targeted therapies’, including
tyrosine kinase inhibitors, monoclonal antibody therapies and immunotherapeutic
agents, may be ‘cytostatic’. Here, a change in tumour volume may not be the expected
outcome: in such cases, tumour stabilisation or delay in tumour progression may be
a more anticipated outcome.
The mechanism of action of the agent under investigation will inform many
subsequent decisions, including the choice of outcome measure and whether or not
the trial should be randomised.
2.1.1.2

Aim of treatment

The aim of the treatment under investigation should be considered both in the context
of its mechanism of action and the specific population of patients in which the
treatment is being considered.
It is important to consider the ultimate aim of treatment, which would inform the
outcome measures in future phase III studies, and how this relates to shorter term
aims that can be incorporated into phase II trials. For example, in a population of
patients with a relatively long median progression-free survival (PFS) and overall
survival (OS), the aim of a phase III trial may be to prolong further PFS and/or
OS. These would, however, be unrealistic short-term outcomes for a phase II trial;
tumour response, which may reflect PFS or OS, can be an appropriate shrinkage aim
in a phase II trial. By contrast, where the prognosis is less good PFS may provide a
realistic short-term outcome in phase II.

KEY POINTS FOR CONSIDERATION

It is essential to consider how the longer term and shorter term aims of treatment
are related, to ensure an appropriate intermediate outcome measure is chosen in phase
II that provides a robust assessment of potential efficacy in subsequent phase III trials.
2.1.1.3

Single or combination therapy

It is important to ascertain whether the treatment under investigation will be given
as a single agent or in combination with another novel or established intervention.
This distinction can inform the decision as to whether or not randomisation should
be incorporated. Where an investigational agent, be it a conventional cytotoxic or a
targeted agent, is used in combination with another active treatment it can be very
difficult to distinguish the effect of the investigational agent from that of the standard
partner therapy; this distinction can be made easier by incorporating randomisation
(see Section 2.2.2 for further discussion).
Similarly, the assessment of toxicity for combination treatments should also be
addressed. Where the addition of an investigational therapy is expected to increase
both activity and toxicity to a potentially significant degree, dual primary endpoints
may be considered to assess the ‘trade-off’ between greater activity and increased
toxicity (see Section 2.1.4 for further discussion).
2.1.1.4

Biomarker dependent

Biomarkers are an increasingly important part of clinical trials. They can be defined
as ‘a characteristic that is objectively measured and evaluated as an indicator of
normal biological processes, pathogenic processes, or pharmacologic responses to a
therapeutic intervention’ (Atkinson et al. 2001).
Biomarkers may be considered in the design of phase II trials in two ways.
First, a biomarker may serve as an outcome measure. The biomarker may be an
intermediate (primary) endpoint in a phase II trial provided it reflects the activity of a
treatment and is associated with efficacy; this may form the basis for a stop/go decision
regarding a subsequent phase III trial. Decisions regarding the use of biomarkers as
primary outcome measures will feed into the decision regarding use of randomisation,
considering whether any historical data exist for the biomarker with the standard
treatment and the reliability of such data. Where a change in a biomarker reflects
the biological activity of an agent, but is not predictive of the natural history of the
disease, this alone may be an appropriate endpoint for a proof of concept phase II trial;
in such cases a second, go/no-go phase IIb trial may be required to assess the impact
of the treatment on the cancer prior to a decision on proceeding to a phase III trial.
The use of biomarkers as outcome measures is discussed further in Section 2.2.1.
Second, in the era of targeted therapies a molecular characteristic of the tumour
that is relevant to the mechanism of action of the treatment under investigation may
serve as a biomarker to define a specific subgroup of patients in whom an intervention
is anticipated to be effective. This has been done especially successfully in studies
of small molecules and monoclonal antibodies targeting HER-2 and related cell
surface receptors (Piccart-Gebhart et al. 2005; Slamon et al. 2001). The potential

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

for a biomarker to identify a subpopulation of patients may, however, only become
apparent after phase III investigation, as in the case of the monoclonal antibody
cetuximab in colon cancer where efficacy is limited to patients with no mutation in
the KRAS oncogene (Bokemeyer et al. 2009; Tol et al. 2009; Van Cutsem et al. 2009).
Where available, using a biomarker to enrich the population in a phase II trial in
this way can increase the likelihood of anti-tumour activity being identified, and thus
speed up drug development. By definition, when using a biomarker for population
enrichment, the resulting phase II population is not representative of the general
population. Interpreting outcomes in the enriched population may, therefore, be more
challenging as historical control data may be unreliable; randomisation incorporating
a control arm should be considered in such situations.
There are, however, potential risks with an over-reliance on biomarkers in phase
II trials. If the mode of action of a novel therapy has been incorrectly characterised,
the biomarker chosen for enrichment may be inappropriate and could lead to a
false-negative phase II trial because the wrong patient population has been treated.
Likewise, if a biomarker used to demonstrate proof of principle of biological activity
does not accurately reflect the clinically relevant mode of action, the outcome of a
phase II trial may be misleading. When a biomarker is the primary endpoint for a trial
or used to enrich the patient population of patients it is vital that the biomarker be
adequately validated. Where there is insufficient evidence that a biomarker reliably
reflects biological activity or identifies an optimal patient group, measurement of
the biomarker in an unselected phase II trial population may be appropriate as a
hypothesis-generating exercise for future studies.
Approaches to trial design that incorporates biomarker stratification are discussed
further in Section 2.2.3.

2.1.2

Primary intention of trial

In this context, we define the ‘intention’ of a trial not as the specific research question
but in the wider sense of classifying trials into two categories:

∙
∙

proof of concept, be that biological or therapeutic, or phase IIa;
go/no-go decision for further evaluation in a phase III trial, or phase IIb.

A proof of concept, or phase IIa, trial may be undertaken after completing a phase
I trial to screen the investigational treatment for initial evidence of activity. This may
then be followed by a go/no-go phase IIb trial to determine whether a phase III trial
is justified. Running two sequential phase II trials may, in some cases, be inefficient.
The Clinical Trial Design Task Force of the National Cancer Institute Investigational
Drug Steering Committee proposed that, where appropriate, proof of concept may be
embedded in a single go/no-go trial (Seymour et al. 2010).
A model that is increasingly relevant to the development of targeted anticancer agents is to incorporate proof of concept translational imaging and/or
molecular/biomarker studies within the expanded cohort of patients treated at the
recommended phase II dose in a phase I trial. Where clear proof of concept can

KEY POINTS FOR CONSIDERATION

be demonstrated in this way, there is a blurring of the conventional divide between
phase I and IIa studies but the need remains for a subsequent phase IIb trial with the
intention of making a formal decision regarding further evaluation in a phase III trial.
While this specific point for consideration is not used to group the trial designs
given in Chapters 3–7, it is important in considering issues such as primary outcome
measures and the use of randomisation. Where a trial is designed as a proof of
concept study alone, it may be appropriate to conduct a single-arm trial to obtain
an estimate of the potential activity of a treatment to within an acceptable degree
of accuracy. Short-term clinical or biomarker outcomes may be appropriate to give
a preliminary assessment of activity prior to embarking on a larger scale phase IIb
study. Where the aim of the phase II trial is to determine whether or not to continue
evaluation of a treatment within a large-scale phase III trial, the ability to make formal
comparisons between experimental and standard treatments may be more appropriate,
to be more confident of that decision to proceed or not. Similarly, in phase IIb
trials outcome measures known to be strongly associated with the primary phase III
outcome measure are desirable for robust decision-making. Further discussion on the
choice of outcome measures and the use of randomisation is given in Sections 2.2.1
and 2.2.2, respectively.

2.1.3

Number of experimental treatment arms

Whereas historically phase II cancer trials invariably had a single-arm, an increasing
number now comprise multiple arms, one of which is often a ‘control’ standard
treatment arm. The most common randomised phase II cancer trial designs have a
single experimental arm with a control arm so the activity seen in the experimental
arm can be compared formally or informally with that seen in the control arm.
Randomisation may be appropriate where historical data on the outcome measure are
unreliable or when a novel agent is being added to an effective standard therapy (see
Section 2.2.2 for discussion).
Where multiple experimental treatments are available, or a single treatment that
may be effective using different doses or schedules, a phase II trial may be designed to
select which, if any, of these options should be taken forward for phase III evaluation.
Randomisation can also be used to evaluate multiple treatment strategies such as
the sequence of first- and second-line treatments. In these settings assessment of
activity of each individual novel treatment, based on pre-specified minimal levels of
activity, can be assessed using treatment selection designs which are described in
Chapter 5.
Where multiple treatments are being investigated in a single phase II trial,
with each single treatment in a different subgroup of patients (e.g. treatment A
in biomarker-X-positive patients, and treatment B in biomarker-X-negative patients),
this should not be considered as a treatment selection trial since only one experimental treatment is being investigated within each subgroup. For the purposes of
trial design, such trials fall under the ‘single experimental arm’ category. Further
discussion regarding trials of subgroups of patients is provided in Section 2.2.3.

2.1.4

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

Primary outcome of interest

The primary outcome of interest will depend on the existing evidence base and/or
stage of development of the treatment under investigation, its mechanism of action
and potential toxicity. Thus, information obtained from discussion of the therapeutic
considerations of the treatment is important in deciding the primary focus of the trial,
as well as incorporating data from previous studies of the same, or similar, treatments.
At this stage, for the purpose of categorising trial designs, the primary outcome of
interest is categorised as being either activity alone, or both activity and toxicity.
Designs are also available that address a third option, of considering toxicity alone as
the primary outcome measure in a phase II trial. These designs are incorporated with
those assessing both activity and toxicity and are described in Chapter 6. Discussion
regarding the specific primary clinical outcome measure is given in Section 2.2.1.
2.1.4.1

Activity

Where the toxicity of the investigational treatment is believed to be modest in the
context of phase II decision-making or the toxicity of agents in the same class is
well known, the primary phase II trial outcome measure will usually be anti-tumour
activity, with toxicity included amongst the secondary outcome measures.
2.1.4.2

Activity and toxicity (or toxicity alone)

If the toxicity profile of the investigational treatment, be it a single-agent or combination therapy, is of particular concern, the activity and toxicity of the treatment
may be considered as joint primary outcome measures, such that the investigational
treatment must show both promising activity and an acceptable level of toxicity to
warrant further evaluation. Such designs allow incorporation of trade-offs between
pre-specified levels of increased activity and increased toxicity, to determine the
acceptability of a new treatment with respect to further evaluation in a phase III trial.

2.2 Stage 2 – Design components
2.2.1

Outcome measure and distribution

Emerging cancer treatments have many differing modes of action, which should be
reflected in the choice of outcome measures used to assess their activity. While tumour
response according to Response Evaluation Criteria in Solid Tumours (RECIST)
(Eisenhauer et al. 2009) has historically been the most widely used primary outcome
measure, non-binary definitions or volumetric measures of response, measures of time
to an event such as disease progression or continuous markers such as biomarkers
may be more relevant when evaluating the activity of targeted or cytostatic agents
(Adjei et al. 2009; Booth et al. 2008; Dhani et al. 2009; Karrison et al. 2007; McShane
et al. 2009).
When choosing between the many possible primary outcome measures for a
phase II trial the key points to consider include the expected mechanism of action of

KEY POINTS FOR CONSIDERATION

the intervention under evaluation, the aim of treatment in the current population of
patients, whether there are any biomarker outcome measures available, the stage of
assessment in the drug development pathway (i.e. phase IIa or IIb) and the strength
of the association between the proposed phase II outcome measure and the primary
outcome measure that would be used in future phase III trials. The chosen outcome
measure should also be robust with respect to external factors such as investigator
bias and patient and/or data availability.
The primary outcome measure of a phase II trial should be chosen on the basis
that if a treatment effect is observed, this provides sufficient evidence that a treatment
effect on the phase III primary outcome is likely to be seen. The use of surrogate endpoints has been investigated in a number of disease areas, including breast
(Burzykowski et al. 2008), colorectal (Piedbois and Buyse 2008) and head and neck
cancer (Michiels et al. 2009). While the outcome measures used in phase II trials do
not need to fulfil formal surrogacy criteria (Buyse et al. 2000) evidence of correlation
between the phase II and III outcome measures is important to ensure reliability in
decision-making at the end of a phase II trial.
The choice of primary outcome measures for a phase II trial reflects the outcome
distribution. This section outlines the various options used to categorise phase II trial
designs within Chapters 3–7, according to the distribution of the chosen primary
outcome measure (as described in Chapter 1).
2.2.1.1

Binary

Response is usually evaluated via a continuous outcome measure, that is, the percentage change in tumour size. This is, however, typically dichotomised as ‘response’
versus ‘no response’ following RECIST criteria (Eisenhauer et al. 2009). Such binary
outcomes, categorised as ‘yes’ or ‘no’, may be used for any measure that can be
reduced to a dichotomous outcome including toxicity or change in a biomarker. Other
outcome measures that may be expressed as continuous, such as time to disease progression, are frequently dichotomised to reflect an event rate, such as progression at
a fixed time point.
In phase II studies of cytotoxic chemotherapy the biological rationale for response
as an indicator of anti-cancer activity is based in part on the natural history of
untreated cancers which grow, spread and ultimately cause death. Administration
of each cycle or dose of treatment kills a substantial proportion of tumour cells
(Norton and Simon 1977) and as such is linked to delaying death (Norton 2001).
These principles may be applicable to chemotherapeutic agents which target tumour
cell kill, and therefore the endpoint of response may be a relevant indicator of antitumour activity.
There are inherent issues in the assessment of tumour response, associated with
investigator bias, inter-observer reliability and variation in observed response rates
over multiple trials (Therasse 2002). These may, to some degree, be alleviated by the
incorporation of independent central review of response assessments or the incorporation of a randomised control arm when historical response data are unreliable.
The use of classical response criteria for trials of drugs that may not cause tumour

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

shrinkage is likely to be inappropriate and raises questions over the design of phase
II trials and the endpoints being used (Twombly 2006). Measures of time to an event
such as disease progression or novel endpoints such as biomarkers may be more relevant when evaluating the activity of newer targeted therapies. Nevertheless, because
most targeted or biological therapies are selected for clinical development on the
basis of pre-clinical data demonstrating at least some degree of tumour regression,
tumour response may remain an appropriate outcome measure for novel agents, as
acknowledged by two Task Force publications (Booth et al. 2008; Seymour et al.
2010).
2.2.1.2

Continuous

Continuous outcome measures such as tumour volume or biomarker response may
be appropriate and relevant outcome measures for consideration in studies of novel
agents (Adjei et al. 2009; Karrison et al. 2007; McShane et al. 2009). The use of
biomarkers in clinical trials is becoming increasingly common in the development
of targeted treatments with novel mechanisms of action. Only when a biomarker has
been validated as an outcome measure of activity, that is, when a clear relationship
has been established with a more conventional clinically relevant outcome measure,
should a biomarker be used as the primary outcome measure of a phase II trial.
The difficulties in identifying validated biomarkers have been highlighted (McShane
et al. 2009), in addition to the need for technical validation and quality assurance
of the relevant assays. As discussed above, biomarkers may be dichotomised to
produce a binary outcome; statistical designs can, however, incorporate biomarkers
as a continuous outcome, which may often lead to more efficient trial design.
2.2.1.3

Multinomial

Multinomial outcome measures may offer an alternative to binary outcomes when
multiple levels of a clinical outcome may be of importance. For targeted or cytostatic
therapies, an alternative to binary tumour response (i.e. response vs. no response) that
remains objective may be the ordered categories of tumour response such as complete
response plus partial response versus stable disease versus progressive disease (Booth
et al. 2008; Dhani et al. 2009). Alternatively activity of an experimental therapy may
be evidenced by either a sufficiently high response rate or a sufficiently low early
progressive disease rate (Sun et al. 2009).
2.2.1.4

Time to event

Time to progression (TTP), time-to-treatment failure (TTF) or PFS may be considered
as appropriate outcome measures to assess the activity of treatments in phase II clinical
trials (Pazdur 2008).

∙

TTP may be defined as the time from registration or randomisation into a
clinical trial to time of progressive disease;

KEY POINTS FOR CONSIDERATION

∙

TTF may be defined as time from registration/randomisation to treatment discontinuation for any reason, including disease progression, treatment toxicity,
patient preference or death;

∙

PFS may be defined as time from registration/randomisation to objective
tumour progression or death.

The use of these endpoints has increased in recent years as a means of assessing
the activity of targeted or cytostatic treatments, including cancer vaccines. While
TTP and PFS may better capture the activity of such agents, they do present their
own challenges. Trials incorporating TTP or PFS as the primary outcome measure
may be constrained by a lack of accurate historical time-to-event population data
with which to make comparisons. This limitation may be overcome by randomised,
comparative designs, but they inherently require larger sample sizes. TTP or PFS may
be influenced by assessment bias in terms of frequency of assessment irrespective of
randomisation, highlighting the need to carefully consider the schedule of follow-up
assessments; increasingly, assessments are recommended at fixed time points rather
than in relation to the number of cycles of treatment received to avoid such biases.
Additional time-to-event outcome measures may also be considered including, for
example, time to developing an SAE in trials primarily concerned with safety assessment or time to a clinical event such as bone fracture in trials of drugs specifically
acting against bone metastases.
2.2.1.5

Ratio of times to progression

One way to overcome the limitations of TTP and PFS as outcome measures with
regard to the challenges of unreliable historical data, and to avoid the need for
additional patient numbers in a randomised study, may be to use each patient as their
own control. The ratio of times to progression or ‘growth modulation index’ has been
proposed for trials in patients who have had at least one previous line of treatment
(Mick et al. 2000; Von Hoff 1998).
The growth modulation index (GMI) represents the ratio of the TTP on the current
investigational treatment relative to that on the previous line of ‘standard’ treatment,
that is, sequentially measured paired failure times for each patient. Although originally proposed in the 1990s, this outcome measure may be considered exploratory, as
it has not been widely used in phase II trials to date and relies on TTP data from the
previous line of treatment, the accuracy of which may be uncertain as it will usually
have been administered outside a clinical trial when assessments are less structured.
A GMI of 1.33 has been proposed as clinically relevant, but this threshold has not
been validated (Von Hoff 1998). Time-to-event ratios may, however, be worthy of
consideration as a phase II outcome measure where randomisation is not appropriate.

2.2.2

Randomisation

The use of randomisation in phase II trials is widely debated (Buyse 2000; Redman
and Crowley 2007; Yothers et al. 2006). Randomisation protects against selection bias,

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

balances treatment groups for prognostic factors and contributes towards ensuring a
valid comparison of the treatments under investigation, such that any treatment effect
observed can reasonably be attributed to the treatment under investigation and not
external confounding factors.
Although randomised phase III clinical trials provide the mainstay of evidencebased clinical research, the use of randomisation within phase II is not so straightforward. Those opposed to randomisation in phase II trials argue that it can be
unacceptably restrictive from a resource perspective, as it inevitably requires at least
twice the number of patients (assuming 1:1 randomisation), increasing both the cost
and duration of the trial (Yothers et al. 2006). A further criticism is that where the
main purpose of randomisation is to balance for potential prognostic factors (of
which there may be many), this is unlikely to be achieved in randomised phase II
trials that are generally only modest in size (Redman and Crowley 2007). On the
other hand, those making the case for randomised phase II trials stress the inherent
problems of selection bias in uncontrolled trials (Buyse 2000). Therapeutic benefits
are generally smaller than potential differences in outcome due to baseline patient
and disease characteristics; patient selection bias can, therefore, seriously confound
the interpretation of non-randomised phase II trials, and thus the decision to take a
treatment forward to phase III. This may not be a problem in a phase IIa trial of a
new cytotoxic that is simply screening to establish whether it has a pre-specified, and
often low, level of activity; bias is more of a challenge in a phase IIb trial where the
key question is whether a new treatment has a sufficiently high level of activity to
warrant a large phase III trial.
For an increasing number of phase II studies, especially those of cytostatic or
targeted agents, where ‘traditional’ endpoints such as response rate are not likely
to be the most appropriate outcome measures, historical controls are problematic as
data for alternative endpoints such as PFS may not be available. Where such data do
exist, the population of patients on which the data are available must be considered
since patients entering phase II clinical trials will not be representative of the broader
patient population treated in routine practice from which historical outcome data
may be derived. It is, therefore, important that the patients from whom the historical
outcome data are derived are matched as closely as possible to the phase II population
in terms of baseline characteristics and disease biomarkers if used for enrichment.
If this is not possible, there is a strong argument to include randomisation against a
control arm within the phase II trial.
In the context of randomisation, another important point is whether the experimental therapy under investigation is to be delivered as a single agent or in combination.
Where an experimental therapy is given in combination with the current standard
treatment, it is very difficult to identify any additional activity of the experimental agent over and above that of the standard partner therapy unless a comparative
control arm is incorporated into the trial. Even if historical activity data do exist
for the standard therapy, patient selection and evolving patterns of patient care may
often render the interpretation of such data difficult. This should be considered in
detail when making the decision as to whether or not to incorporate a randomised
control arm.

KEY POINTS FOR CONSIDERATION

Although randomisation is increasingly being incorporated into phase II trial
design, it can take various forms. Simply because randomisation between experimental and control treatments is incorporated into a phase II trial does not automatically
imply that the two arms are formally statistically compared with sufficient power; the
reasons for randomisation should, therefore, be critically evaluated.
The statistical implications of conducting a single-arm or a randomised phase II
study have been evaluated in simulation studies. One study compared the results of
multi-centre single-arm and randomised phase II trials of the same sample size, where
the decision as to whether or not the experimental treatment was deemed successful
was based solely on it showing a higher response rate than in the historical control
population, or randomised control population, that is, no formally powered statistical
comparison was employed (Taylor et al. 2006). Where there was expected to be little
variability in response rates between centres, and both the variability and uncertainty
in the response rate for the control population were small, single-arm studies were
found to be adequate in terms of correct decision-making. However, with increased
variability and uncertainty in response rates for either the experimental or control
population, randomised studies were more likely to make the correct recommendation regarding proceeding to phase III, and should be considered as a possible
option. A further study compared error rates between single-arm and randomised
comparative phase II trials, which reflected more realistically the characteristics of
a phase II trial (Tang et al. 2010). Although sample sizes for the randomised trials were at least double those of the single-arm trials, the false-positive error rates
(type I error) in single-arm trials were two to four times those projected when the
characteristics of the study patients differed from those of the historical controls;
by contrast, randomised trials remained close to the planned type I error. Statistical
power (type II error) remained stable for both designs despite differences in the patient
populations.
The impact of misspecification of the control data for either approach should be
considered in detail, for example, the impact of specifying a control response rate of,
say, 60% when in fact it may be as low as, say, 50%, or as high as 70%. In the singlearm setting, the impact of such misspecification, potentially leading to increased
false-negative or false-positive results, is much higher than in the randomised setting
since there is no concurrent control arm against which to verify the initial control
assumptions made. Thus where there is uncertainty in the control data, the inclusion
of a control arm may be considered appropriate.
There is no one-size-fits-all approach to phase II trial design, and the theoretical
and practical implications of randomisation must be considered on a trial-by-trial
basis. Below we discuss the various randomisation options for phase II trial design
and provide examples of when each setting may be appropriate. Randomisation is
categorised within the thought process as
i. no randomisation (single-arm phase II trial);
ii. randomisation incorporating a control arm, no formally powered statistical
comparison intended;

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

iii. randomisation incorporating a control arm, formal comparison intended; and
iv. randomisation to multiple experimental treatments.
The use of randomised discontinuation designs is addressed separately in Section
2.2.3.
2.2.2.1

No randomisation

Chapter 3 outlines those designs that incorporate only a single experimental arm. The
results of most single-arm phase II trials are interpreted in the context of historical
control data. The reliability, or otherwise, of these historical data is one of the main
issues driving discussion about randomisation in phase II studies (Rubinstein et al.
2009; Vickers et al. 2007). Single-arm phase II designs have been reported that utilise
historical data but incorporate an estimate of potential variability arising from the
number of patients or trials from which those historical data have been derived, and
are presented in Chapter 3.
A single-arm study may be considered appropriate where

∙

comparison with a control group is not relevant. For example, a phase IIa trial
designed to show proof of concept, where the intention is to obtain an initial
estimate of treatment activity to inform the design of a randomised phase IIb
trial;

∙

the historical data are sufficiently robust for the primary outcome measure as
to allow a reliable comparison, for example, a study of a single-agent cytotoxic
treatment with response rate as the primary outcome measure, conducted in
a broad population of patients with a common cancer refractory to standard
therapy.

2.2.2.2

Randomisation including a control arm

Randomisation including a control arm can be considered in two ways: randomisation
with no formal comparison between experimental and control arms and randomisation
with a formal comparison between experimental and control arms. Further discussion
of each of these is given below. Phase II trial designs incorporating randomisation between a single experimental therapy (or combination therapy) and a control
arm are presented in Chapter 4.
With no formal comparison
Those designs that incorporate a control arm with no formal comparison intended
as the primary decision-making assessment are highlighted in Chapter 4, as the
study is not designed to have sufficient power to detect statistically significant differences between treatment arms. This does not infer that a comparison may not be
made of outcomes between the arms; rather, that these comparisons be made with
the acknowledgement of reduced statistical power therefore providing additional
exploratory comparisons only. This approach may be appropriate if it is sufficient to

KEY POINTS FOR CONSIDERATION

simply show that the experimental treatment has activity within a certain range. Randomisation provides a level of reassurance that the study population is representative
and guards against patient selection bias; this approach is more acceptable when at
least some historical data exist to further aid interpretation of the activity of the investigational agent.
In the absence of formal comparison between treatment arms, the sample size may
simply be doubled compared to a single-arm study and decision-making at the end of
the trial based primarily on the results of the experimental arm, albeit in the context
of outcomes in the control arm. Data from the patients randomised to the control
arm can be more formally incorporated. For example, response rates in the control
arm may be compared to the historical control rates to determine whether they are
reflective of the assumptions made when designing the trial (Buyse 2000; Herson and
Carter 1986).
It has been suggested that the use of a control arm as a reference arm only
should be avoided, particularly in trials of targeted or cytostatic agents, since it may
be difficult to interpret the results when unexpected outcomes are observed in the
control arm and when the sample size is not sufficient enough to permit direct formally
powered comparisons (Rubinstein et al. 2009). For example, if positive results were
observed in the experimental arm on the basis of pre-defined criteria, but higher than
expected activity was also observed in the control arm, does this call into question
the positive trial outcome? On the other hand, if the outcome of the experimental
arm is negative and the control arm also has a lower level of activity than expected,
should the apparent low activity of the experimental treatment be questioned? These
uncertainties may be mitigated by looking at both study arms in relation to appropriate
historical data, where available.
With formal comparison
When a phase II trial aims to determine more than whether the investigational agent
has activity within a broad range, or there are serious doubts about the accuracy
of historical control data, formal comparison between the control and experimental
treatment arms is preferred. The trade-off for increased reliability is inevitably a
larger sample size.
The level of statistical significance within a comparative, randomised phase II
trial should be considered carefully as this will further impact on sample size. It is
acceptable to increase the type I error in a phase II trial compared to the typical 5%
level used within phase III trials, and error rates of up to 20% have been used. This
may enable more realistic sample sizes, and the error associated with incorrectly
declaring a non-active treatment worthy of further investigation in phase III (i.e. the
type I error) may be deemed more acceptable than that of incorrectly rejecting a
treatment that is active. It is, therefore, important to maintain the power associated
with the design of the trial.
Another consideration in the use of formally comparative phase II designs is
the feasibility of achieving the treatment difference that is being specified. While it
may be appropriate to target large treatment effects in some circumstances, this may

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

not be the case in others. The size of the clinically relevant treatment effect should,
therefore, be considered carefully to ensure the outcome assumptions are realistic
and not simply used as a method of reducing sample size.
It must also be stressed that with the use of formally comparative phase II designs,
a statistically significant result at phase II would not usually obviate the need for a
subsequent phase III trial. In contrast to the short-term endpoints usually selected
in phase II trials, longer term endpoints such as PFS and OS are typically selected
in large-scale phase III trials. Additionally, in a relatively small randomised phase
II study only a limited number of patients will have received study drug so not all
clinically relevant toxicities may be identified and should therefore be studied further.
Information gained from the phase II trial may also influence patient selection for
the definitive phase III study. Subsequent confirmatory phase III trials are, therefore,
usually required even after a statistically positive randomised phase II trial.
2.2.2.3

Randomisation to experimental arms (selection)

Where the aim of a phase II trial is to select which of several candidate investigational
treatments to take forward for further evaluation, randomisation may be incorporated
to randomise patients between several experimental treatments. Where historical
control data are either available or not relevant as discussed above, this will influence
the decision as to whether or not a control arm is also incorporated, also as discussed
above.

2.2.3

Design category

Phase II statistical designs can be broadly separated into nine statistical design categories:

∙
∙
∙
∙
∙
∙
∙
∙
∙

one-stage;
two-stage;
multi-stage (or group sequential);
continuous monitoring;
decision-theoretic;
three-outcome;
phase II/III;
randomised discontinuation; and
targeted subgroups.

These categories are not mutually exclusive. For example, a one-stage trial
may incorporate a three-outcome design, or analysis based on a decision-theoretic
approach. Where this is the case, designs have been listed according to their primary
design categorisation.

KEY POINTS FOR CONSIDERATION

A brief description of these nine categories is provided below, focusing on the
practical implementation of each design. Previous reviews have used alternative categories for phase II designs, focusing either on single-arm versus randomised studies
(Seymour et al. 2010) or specific designs such as randomised designs, enrichment
designs and adaptive Bayesian designs for trials of molecularly targeted agents only
(Booth et al. 2008). Mariani and Marubini also previously conducted a review of
the statistical methods available for phase II trials, categorising designs according to
one sample versus controlled, as well as according to the number of stages of assessments, and focusing on a framework for trial analysis, that is, frequentist, Bayesian or
decision theoretic (Mariani and Marubini 1996). The grouping of trial designs within
this book adopts a similar design categorisation to Mariani and Marubini (Mariani
and Marubini 1996), but the thought process incorporates points for discussion prior
to making the specific design decision. Additional categories of design that Mariani
and Marubini (Mariani and Marubini 1996) did not consider are also included.
2.2.3.1

One-stage

A one-stage design utilises a fixed sample of patients, recruited until the required
sample size is obtained. After the necessary follow-up of patients, analysis and
decision-making regarding proof of concept, whether to move to phase III or not, or
which treatment(s) to select to take forward to phase III, is made. One-stage designs
are relatively straightforward, avoiding complexities relating to recruitment strategies
if interim analyses are undertaken. They do not, however, allow for adaptations
such as early trial termination due to low levels of activity. Where the safety of a
treatment is well known, and data are already available to suggest activity, either for
a similar treatment or for the same treatment in an alternative population of patients,
a single-stage design may be appropriate since an interim ‘check’ may be deemed
unnecessary.
Where the experimental therapy is highly active, over and above the current
standard therapy, fewer patients may be required under a one-stage design than
other two- or multi-stage designs that incorporate early termination for lack of
activity only.
2.2.3.2

Two-stage

Under a two-stage design patients are recruited to the trial in two stages such that at
the end of the first stage an interim analysis is performed and the trial may be stopped
for a number of reasons, including lack of activity, early evidence of activity or
unacceptable toxicity; otherwise, the trial continues to a second stage. Alternatively,
the interim analysis may be used to select which of several experimental treatments
to take forward to the second stage. Additional adaptations may be incorporated at
the end of the first stage according to the specific trial design, for example, sample
size re-estimation.
Stopping rules are developed for each stage of the study to determine whether
to stop or continue, based on pre-specified operating characteristics relevant to the

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

specific trial and design. At the end of the study, data from both stages are typically
used in deciding how to proceed.
Two-stage designs are beneficial in that the analysis at the end of the first stage
may act as a ‘check’ on the treatment(s) under investigation, potentially exposing
fewer patients to an inactive treatment than would be exposed using a one-stage
design (i.e. under the null hypothesis of no treatment activity, two-stage designs may
be more efficient). There are, however, issues around patient recruitment while data
from the first stage of the trial are being analysed. This is a particular issue if the
outcome of interest requires a substantial period of follow-up or observation, for
example, PFS requiring a specific number of events to be observed. During this time,
patients either continue to be recruited, therefore contributing to the second-stage
sample size, without the results of the first stage being known, or recruitment is
suspended. Continuing recruitment avoids the trial losing momentum and may be
acceptable where recruitment is slow. If a trial is recruiting rapidly, however, the total
required number of patients may be entered to the second stage of the trial before the
first-stage analysis is complete, rendering the two-stage design futile.
Careful thought must be given to these points when a two-stage design is being
considered. A compromise may be considered, which does not require a break in
recruitment but takes into account data from patients recruited during the follow-up
and analysis period of the first-stage patients if required (Herndon 1998). If the firststage analysis suggests stopping due to lack of activity, recruitment may be suspended
at this stage and an additional assessment performed incorporating data on all patients
recruited during the follow-up and analysis period to determine whether to stop the
trial permanently or to resume recruitment (see Chapter 3). Additionally, other twostage designs can be adapted when the attained sample size is different to the planned
sample size, especially if this results in over-recruitment, where the decision-making
criteria may be updated in line with the actual number of patients recruited (Chen
and Ng 1998; Green and Dahlberg 1992).
Due to the nature of two-stage designs, the total sample size requirement is not
fixed, so a maximum sample size and an average sample number (ASN) are generally
specified, to account for possible early termination of the trial.
2.2.3.3

Multi-stage

Multi-stage designs, also known as group-sequential designs, are similar to the twostage designs described above, but with additional analyses throughout the course of
the trial. This allows more opportunities to terminate the trial, exposing fewer patients
to inactive and/or toxic treatments, or to accelerate the start of the phase III trial
through early termination of the phase II trial if sufficient evidence of activity is seen.
Additional adaptations may be incorporated at each stage, and again stopping rules are
developed for each stage of the study based on pre-specified operating characteristics
relevant to the specific trial. As with two-stage designs, multi-stage designs require
consideration of whether to continue recruitment whilst interim assessments are
underway. Again, due to the nature of multi-stage designs, a maximum sample size
and an ASN are generally specified.

KEY POINTS FOR CONSIDERATION

Two-stage or multi-stage designs are generally chosen because of their ability
to terminate a trial earlier than a fixed sample one-stage design and may be seen to
allow a more cautious approach. This is useful when the activity of a treatment is
not known and/or toxicity is likely to be considerable. In this case a two-stage or
multi-stage design may be appropriate irrespective of the implications of continuing
or suspending recruitment. Where such caution is not necessary, a two-stage or multistage design may not be appropriate, especially when either suspending or continuing
recruitment is problematic; in these cases, a one-stage design may be an alternative.
2.2.3.4

Continuous monitoring

With continuous monitoring designs the outcome of interest is assessed after each
individual patient’s primary outcome has been observed. The rationale behind this
design is generally to allow early termination of the trial in case of lack of activity. This
provides, therefore, a more cautious approach to trial design, allowing termination
as soon as possible rather than waiting for a pre-defined number of patients to
be recruited. Again, pre-defined stopping rules are required and determined via
the specific design operating characteristics. Recruitment may continue while the
outcomes are observed, but real-time reporting of outcomes is fundamental to this
design. This is not possible if the primary outcome requires a prolonged period of
observation as with PFS or even best response, both of which may not be available
for some months following the start of treatment. In such cases there is little to be
gained from continuous monitoring over a multi-stage design, since many additional
patients may be recruited before data from the ‘last’ patient can be analysed. This may
be less problematic where, for example, acute treatment toxicity is the key outcome
measure, as this can generally be assessed more quickly than activity.
2.2.3.5

Decision-theoretic

Decision-theoretic designs consider costs and gains associated with making incorrect
decisions at the end of the phase II trial and incorporate utility functions associated
with these costs and gains. Variables such as the total patient ‘horizon’, that is,
the likely number of patients who would be treated with an effective new drug as
standard therapy after completion of a successful phase III trial, before the next new,
more effective drug becomes available, are required (Sylvester 1988). If that patient
population is small, and especially if the likely cost of the new treatment high, there
may be a financial imperative that the magnitude of the treatment effect sought in
the phase II study be large. Decisions are generally made at the end of the trial after
a fixed number of patients have been recruited, as in a one-stage design, although
multi-stage designs may also be used. These designs allow decisions to be made based
on an all-round assessment of gain, as opposed to concentrating solely on clinical
activity (Sylvester and Staquet 1980).
Although the ability to incorporate information regarding costs and gains
associated with decisions made throughout a trial is clearly potentially useful,
decision-theoretic designs are rarely used in phase II oncology trials. This may reflect

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

the difficulty of identifying accurately the cost and patient horizon information that is
often required for their design and difficulty in formulating realistic and interpretable
models.
2.2.3.6

Three-outcome

The three-outcome design may be seen as a sub-design of the one-, two- or multi-stage
designs (Storer 1992). The main characteristic of this design is that instead of there
being two possible outcomes at the end of the phase II trial, that is, reject the null
hypothesis or reject the alternative hypothesis, a third outcome is incorporated where
the trial is inconclusive on the basis of primary endpoint data. This approach may
be used when there is a region of uncertainty between, for example, a response rate
above which further investigation in phase III is warranted and a response rate below
which it is not. If the primary outcome measure data of such a trial are inconclusive,
the decision to move to phase III or not may be based on alternative outcome measures
such as safety or cost.
Three-outcome designs may be single arm or randomised. Upper and lower
stopping boundaries are developed for each stage of the study to determine whether
to stop, continue or declare the trial inconclusive. To calculate these boundaries,
in addition to the conventional type I and type II errors (𝛼 and 𝛽, respectively),
two further errors must also be considered. The probability of correctly making
the decision to reject the null hypothesis when the alternative is true (𝜋) and the
probability of correctly making the decision to reject the alternative hypothesis when
the null is true (𝜂), are required. With these four errors specified one can then
determine the probability of incorrectly declaring an inconclusive result when in fact
the alternative hypothesis is true (𝛿) and the probability of incorrectly declaring an
inconclusive result when in fact the null hypothesis is true (𝜆). These differing error
rates are shown graphically in Figure 2.2, assuming a binary outcome measure of
success or failure. Here, nL and nU represent the lower and upper stopping boundaries,
respectively, for the number of successes observed; N is the sample size; and p0 and
p1 represent the success rates associated with the null and alternative hypotheses,
respectively. Alternatively, the probabilities of concluding in favour of either the null
or alternative hypotheses when in fact the true response rate lies within the region of
uncertainty may be specified (Storer 1992).
Three-outcome designs generally require fewer patients than a typical twooutcome design using the same design criteria. They may also be seen as better
reflecting clinical reality than the typical two-outcome design where the decision
λ

π
nL

Np0

Np1

Figure 2.2 Probabilities associated with the three-outcome design.

KEY POINTS FOR CONSIDERATION

between accepting and rejecting the null hypothesis may be determined by a single
success or failure (i.e. a single stopping boundary).
2.2.3.7

Phase II/III

Phase II/III designs are used when the transition from phase II to III is required to be
seamless. Such designs typically allow data generated from the phase II component of
the trial to be incorporated in the final phase III analysis. These trials are, therefore,
usually randomised, incorporating a control arm. Randomisation may be used to
select the ‘best’ of several treatments in the phase II component to be carried forward
into phase III or to decide whether or not to continue an individual experimental
treatment (single-agent or combination therapy) into the phase III component.
One of the main benefits of these designs is that they reduce the total time required
for the study to progress through phases II and III compared to running separate trials.
Since data from the phase II component may also be incorporated in the phase III
analysis, patient resources are also reduced; this is a major benefit in rarer cancers
or disease sub-types where the patient population is small. Where a limited number
of patients are available for trial recruitment, the optimal use of patient data is even
more crucial than usual.
Alternatively, where separate phase II and phase III trials are to be carried out, a
phase II trial allowing early termination for evidence of activity may be considered
appropriate, bringing forward the phase III trial and saving patient resource. Where
patient numbers are limited, various trial design scenarios should be investigated
to identify the design which is most efficient in terms of patient numbers whilst
providing sufficiently robust results.
As with multi-stage designs, the issue of whether to continue or suspend recruitment during the analysis of the phase II component arises. The trial risks losing
momentum if recruitment is suspended, but rapid recruitment during this period may
result in a substantial number of patients being entered into the phase III element,
rendering the phase II/III design futile in its attempts to reduce the number of patients
exposed prior to embarking on phase III. For these trials to be carried out successfully,
the funding body, be it academic or industry, must commit to the full phase II/III
package in the knowledge that the trial may terminate after the phase II component.
Often many more centres will participate in the phase III component than in the phase
II. Since the trial may terminate for lack of activity after the phase II component, the
early preparation of centre set-up to enable a smooth transition to phase III must be
weighed against this possibility of early termination.
Specific phase II/III designs are outlined in Chapters 3–7. An alternative approach
to designing a phase II/III trial is to use conventional stand-alone phase II designs to
make decisions as to whether to continue to phase III or not and incorporate these
into phase III seamlessly (Storer 1990). Typically in this case, the primary outcome
measure under investigation during phase II is different to the primary outcome
measure under investigation during the phase III component, to avoid the need to
adjust the type I error rate in the phase III component. Otherwise, when the same
outcome measure is used in both phases II and III, with a formal comparison between
control and experimental treatments at the end of phase II, this essentially becomes

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

a phase III trial with at least one interim analysis. This approach, using the same
endpoints, is not generally recommended since the phase III endpoint will usually
be a long-term outcome such as OS. A long follow-up period would, therefore, be
required for that endpoint to be assessed in the interim/phase II analysis. Multi-stage
approaches may, however, be based on the phase II outcome measure with subsequent
interim analyses within the phase III component based on the phase III endpoints.
Phase II/III designs are inevitably associated with patient and resource efficiencies, accelerating the transition between the two trial phases, and usually allowing
patients recruited to phase II to be incorporated in the phase III analysis. However, by
performing separate phase II and phase III trials the results of the phase II trial, and
lessons learned during its set-up and conduct, may be incorporated into the design of
the phase III trial. Changes to eligibility criteria or follow-up schedules, for example,
may be required for the phase III trial. Here separate phase II and III trials enable
these alterations to be made. Such an approach to the planning of current and future
trials may be beneficial where experience with an experimental treatment is minimal,
or data for the control population of the disease area in question are minimal, enabling
additional learning between stages of the development pathway.
2.2.3.8

Randomised discontinuation

Randomised discontinuation, or enrichment, trial designs (Kopec et al. 1993; Rosner
et al. 2002; Stadler 2007) involve all study patients initially being treated with the
experimental treatment for a pre-defined period of time, and then assessed for response
to treatment. Typically, those with progressive disease come off study whilst patients
who are responding continue to receive the experimental agent; those with stable
disease are randomised to either continue the experimental treatment or discontinue
it and either remain off treatment or receive standard treatment depending on the
question being asked in the trial.
Such an approach may be appropriate when the specific population of patients
in which the experimental treatment is expected to be effective is unknown. For
example, when evaluating a targeted agent where the level of expression of the relevant
target required for potential activity is not known, a randomised discontinuation
design may allow de facto enrichment of the patient population. Against this, only a
limited proportion of the population recruited to the trial actually contributes to the
randomised part of the study. An overview of the randomised discontinuation design
is presented by Stadler, providing an example of where the design has been used
successfully, as well as providing a summary of the advantages and disadvantages of
the design (Stadler 2007).
The role of the randomised discontinuation design has been reviewed in detail
(Booth et al. 2008; Capra 2004; Freidlin and Simon 2005; Kopec et al. 1993; Rosner et
al. 2002; Rubinstein et al. 2009). The Methodology for the Development of Innovative
Cancer Therapies (MDICT) Task Force (Booth et al. 2008) considered the design as
being exploratory in nature due to lack of clarity on its role in oncology. One study
comparing the randomised discontinuation design with a comparative randomised
design showed that the randomised discontinuation design may be underpowered
in comparison to the traditional design due to the number of patients who start the

KEY POINTS FOR CONSIDERATION

investigational treatment who are not then randomised (Capra 2004). An accurate
estimate of the proportion of patients likely to enter randomisation is, therefore,
essential in planning the study sample size. By contrast, a second study concluded
that, although the randomised discontinuation design may be less efficient than the
classical randomised design in many settings, it can be useful in the early development
of targeted agents where a reliable assay to select patients expressing the target is not
available (Freidlin and Simon 2005). The randomised discontinuation design may
be especially appropriate when treatment benefit is restricted to a select group of
patients who are not identifiable at the start of the trial.
2.2.3.9

Targeted subgroups

In the era of targeted therapies it may be appropriate to investigate the activity of a
treatment in a specific subgroup of patients in whom the intervention is anticipated to
be effective. Alternatively, where the specific subgroup of patients is not determined,
or there is uncertainty about whether a biomarker accurately identifies a ‘sensitive’
patient population, it may be appropriate to assess activity simultaneously in several
subgroups of patients according to biomarker characterisation. Population enrichment
for a specific biomarker in phase II trials was discussed in Section 2.1.1.4, highlighting
the risks associated with incorrect characterisation and the possibilities of falsenegative results, as well as issues surrounding the use of historical data.
Designs that incorporate subgroup stratification may be used to enable the
inclusion of separate cohorts of patients defined by the biomarker in question, or
populations defined by other disease sub-types or patient characteristics, ensuring that
adequate numbers are recruited into each cohort. Approaches incorporating stratification range from separate phase II trials within each stratification level, to hierarchical
Bayesian designs (Thall et al. 2003) and tandem two-stage methods where the experimental treatment is first tested in an unselected patient population, and if there is
insufficient activity in this overall group, the trial continues in a select population
(e.g. marker-positive patients) only (Pusztai et al. 2007). Trials may also be partially
enriched to include a larger proportion of, for example, biomarker-positive patients,
providing additional power to detect treatment effects in this targeted subgroup of
patients.
These designs are discussed in Chapter 7; however, as noted in Chapter 1, a
number of recent papers have been published on biomarker stratification (An et al.
2012; Buyse et al. 2011; Freidlin et al. 2012; Freidlin and Korn 2013; Jenkins et al.
2011; Lai et al. 2012; Mandrekar et al. 2013; Roberts and Ramakrishnan 2011;
Tournoux-Facon et al. 2011), therefore we encourage consideration of additional
literature outlining alternative designs available.

2.3

Stage 3 – Practicalities

2.3.1

Practical considerations

At this stage of the design process, when faced with a number of statistical designs
from which to choose, deciding which particular design is most appropriate to your

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

particular setting can be difficult. Although all the designs considered are deemed
easy to implement, this section focuses on key practical aspects.
2.3.1.1

Programming requirements

For each statistical design described in Chapters 3–7, the programming requirements have been considered. It is important that the statistical methodology can be
implemented easily and efficiently, allowing the statistician to consider various trial
scenarios during the design process. Only those designs that detail availability of
programs, or for which sufficient information is provided to allow the design to be
implemented, have been incorporated in this book. Nevertheless, some designs may
still be easier to implement than others depending on the resources available.
2.3.1.2

Availability/robustness of prior data

It is essential to consider the design parameters that must be defined in order to
implement each design and the variability associated with each of these parameters.
There may be, for example, a paucity of data on the primary outcome measure for
patients receiving the current standard treatment in the particular trial setting, so what
is the impact of those historical data being unreliable? For example, if the response
rate with standard therapy is estimated to be 20%, a phase II study may aim for a
response rate of 30% with the experimental arm. If a randomised phase II trial is
powered on such a basis but the patients in the control arm have better outcomes than
expected, the study may be underpowered. On the other hand, if a single-arm study is
undertaken and the historical response rate is overestimated an active treatment may
be inappropriately discarded. The implication of misspecification of study parameters
may be investigated by simulation or may already be addressed within the specific
design publication. If a trial design is not robust with regard to misspecification, it
may be more appropriate to consider a design that allows either an estimate of the
variance of the parameter to be incorporated into the design or to select a different
outcome measure that is robust in the face of misspecification. Additionally there may
be a specific design parameter for which no reliable data are available, for example, an
estimate of the correlation between a change in a biomarker and a clinically relevant
outcome measure. Here it may be possible either to consider a design that does not
require the parameter in question or to simulate the performance of the design under
differing parameter assumptions.
2.3.1.3

Early termination

Typically in phase II trials, early termination of a trial is incorporated to ensure
the safety and appropriate treatment of patients, usually in the context of lack of
activity or unacceptable toxicity. Early termination when evidence of activity has
been demonstrated may not be deemed necessary given the desire to obtain as much
information on the treatment as possible to provide a more robust estimate of the
treatment’s activity to inform the design of subsequent trials. On the other hand,

KEY POINTS FOR CONSIDERATION

this may delay opening of subsequent phase III trials and there are designs that do
incorporate early termination for activity.
2.3.1.4

Operating characteristics

In phase II trials, a larger type I error than typically used in phase III trials (e.g. 5%
two sided) is generally accepted due to the nature of phase II trials. Type I errors
of up to 20% have been used where the consequences of incorrectly rejecting an
active treatment are deemed less acceptable than those of inappropriately continuing
to develop a treatment that will ultimately not be active. In such circumstances,
subsequent larger phase III studies would be expected to identify the treatment as
inactive, whereas if a treatment is rejected the situation may well not be remedied as a
phase III trial is unlikely. The selection of an appropriate type I error rate is, therefore,
crucial to the reliability of the trial results and the efficient development of new
treatments. While larger type I error rates allow smaller sample sizes, investigators
need to consider carefully whether it is appropriate to conduct a small phase II study
with a high risk of a false-positive result, and ‘negative’ subsequent phase III trial;
the alternative is a larger phase II study with a lesser chance of development of an
ultimately ‘negative’ phase III trial.
Since the primary aim of many phase II trials is to determine whether a treatment
has a pre-specified level of activity, the power of phase II studies should generally
remain high; in practice, this means a power of at least 80%.

2.4

Summary

This chapter provides guidance on decision-making when identifying a trial design
for a phase II trial (Figure 2.1). Clinical researchers and statisticians should consider
carefully each of the three stages of the thought process; additional resources should
be consulted where necessary, and discussion maintained between the clinician and
statistician. The guidance we offer is not intended to be exhaustive or proscriptive.
Further reading and discussion around specific areas relevant to each specific phase
II design element should always be encouraged.
Examples of using the thought process in practice are presented in Chapters 8–12
for various trial design scenarios. These are intended as practical examples of how
the thought process may be implemented.

Designs for single experimental
therapies with a single arm
Sarah Brown

3.1 One-stage designs
3.1.1

Binary outcome measure

Fleming (1982)

∙
∙

One-stage, binary outcome
Standard software available

Fleming proposes a one-stage, two-stage and multi-stage design requiring specification of response rates under the null and alternative hypotheses and type I and
II error rates. Decision criteria are based around rejecting the null hypothesis that
the response rate of the experimental treatment is not less than some pre-specified
response rate, typically defined as the expected response rate of the current historical
control treatment. Sample size is based on normal approximation to the binomial
distribution. This is a widely used design and programs are readily available (e.g.
Machin et al. 2008).
Fazzari et al. (2000)

∙
∙

One-stage, binary outcome
Requires programming

DESIGNS WITH A SINGLE ARM

Fazzari and colleagues propose modifications to previously published phase II
designs. The modifications include: incorporating a patient population that is more
representative of the intended phase III trial population, by reducing the eligibility
restrictions and increasing the number of centres; increasing the sample size to
allow more accurate estimates of the treatment activity; using an outcome measure
that is more representative of that to be used in phase III, recommending a k-year
progression-free survival (PFS) or overall survival (binary) outcome measure for
advanced-stage disease populations; taking the upper limit of the 75% confidence
interval of the activity of previous treatments as the minimum activity required to be
observed to warrant moving to phase III. The methodology for the design of the study
is based on rejecting the minimum activity required from an x% confidence interval
around the estimate of treatment activity with, say, 80% probability. Sample size is
generated using Monte Carlo simulation which will require programming.
A’Hern (2001)

∙
∙

One-stage, binary outcome
Standard software available

A’Hern presents an adaptation of Fleming’s design (Fleming 1982). Calculation
of sample sizes and cut-offs is based on exact binomial distributions as opposed to
normal approximation. Trials based on exact distributions are typically larger than
those using the normal approximation; however, they avoid the possibility that confidence intervals around the estimate of activity at the end of the trial will incorrectly
contain the lower rejection proportion due to approximation to the normal distribution. As for Fleming, this design is widely used and programs are readily available
for its implementation. The choice between Fleming and A’Hern should be based on
the sample sizes and the requirement for exact testing.
Chang et al. (2004)

∙
∙

One-stage, binary outcome
Pascal programs noted as being available from authors

Chang and colleagues propose a design whereby the sample size, and thus the
test statistic, is calculated using exact unconditional methods. This design may be
used when the historical control data are based on only a few patients (say up to
120). The number of patients on which the historical data are based is required to be
known as analyses take into account the pooled variance of the historical control and
experimental data. Tables and software are available to calculate sample sizes.
Mayo and Gajewski (2004)

∙
∙

One-stage, binary outcome
Requires programming

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

Mayo and Gajewski propose sample size calculations for a single-arm single-stage
trial with binary outcome, using Bayesian informative priors (pessimistic/optimistic).
This is an extension of the two-stage designs proposed by Tan and Machin (2002).
Prior information regarding expected response rate and level of uncertainty in this
value is required to determine sample sizes using either the mode, median or mean
approach. Programming is required for the median and mean approaches, possible in
Matlab. Sample sizes will vary depending on the approach used.
Gajewski and Mayo (2006)

∙
∙

One-stage, binary outcome
Requires programming

Gajewski and Mayo describe Bayesian sample size calculations where conflicting
opinions on prior information can be incorporated. Information required to design
the trial includes prior distributions, cut-off for the posterior probability that the true
response rate is greater than some pre-specified value and an error term relating to a
small increase in the target response rate. Sample size calculation is iterative; therefore
some computation is required to identify the design characteristics, for which no
software is detailed but for which formulae are given to enable implementation.
This design differs from the earlier design proposed by Mayo and Gajewski (2004)
as it allows incorporation of pessimistic and optimistic priors, as opposed to one
informative prior.
Vickers (2009)

∙
∙

One-stage, binary outcome
Stata programs given in appendix to manuscript

Vickers proposes a design using historical control data to generate a statistical
prediction model for phase II trial. The observed trial data for the experimental
arm are then compared to the predicted results to give an indication of whether
patients treated with the experimental agents are doing better than expected, based
on the prediction model. The authors note that the methodology hinges on quality
historical control data relevant to the patient population under study. Step-by-step
methodology is presented which incorporates bootstrapping on both the historical
data set and the observed data set and a comparison of the predicted and actual
outcomes. Example Stata code is given in the appendix to the manuscript to allow
implementation of the statistical analysis, as well as assessment of power.

3.1.2

Continuous outcome measure

No references identified.

DESIGNS WITH A SINGLE ARM

3.1.3

Multinomial outcome measure

Zee et al. (1999)

∙
∙

One-stage, multinomial outcome
Requires programming

Zee and colleagues propose single-stage and multi-stage single-arm designs considering a multinomial outcome, in the context of incorporating progressive disease
as well as response into the primary outcome measure. Analysis is based on the number of responses and progressions observed, compared with predetermined stopping
criteria. A computer program written in SAS identifies the operating characteristics
of the designs. This is not noted as being available in the paper; however, detail is
given to allow implementation.
Lu et al. (2005)

∙
∙

One-stage, multinomial outcome
Programs may be available from authors

Lu and colleagues propose a design (one-stage or two-stage) to look at both
complete response (CR) and total response (or other such outcome measures whereby
observing one outcome implies the other outcome is also observed). The design
recommends a treatment for further investigation if either of the alternative hypotheses
is met (i.e. for CR or for total response) and rejects the treatment if neither is met.
The designs follow the general approach of Fleming’s single-stage (Fleming 1982)
or Simon’s two-stage (Simon 1989) approach whereby the number of CRs and total
responses are compared to identified stopping boundaries. Tables are provided for
some combinations of null and alternative hypotheses; however, formulae are given
and at the time of manuscript publication programs were in development. The design
differs from others in this section in that one outcome measure is a sub-outcome
measure of the other, whereas other designs consider discrete outcome measures
such as partial response (PR) versus CR.
Chang et al. (2007)

∙
∙

One-stage, multinomial outcome
Programs noted as being available from authors

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

both the response rate being above a pre-specified rate and the early progressive
disease rate being below a pre-specified rate. The outcomes follow a multinomial distribution. A SAS program is noted as being available from the authors to
identify designs.
Stallard and Cockey (2008)

∙
∙

One-stage, multinomial outcome
Programs noted as being available from author

Stallard and Cockey propose single-arm, one- and two-stage designs for ordered
categorical data, where the rejection region for the null hypothesis is defined based
on the likelihood ratio test. The null region over which the type I error is controlled
considers a weighting of the proportion of patients in each response category, in a
similar manner to that of Lin and Chen (2000). The focus of the paper is on response
with three levels; however, the design may be extended to more than three levels.
Programs are noted as being available from the first author to allow identification of
designs.

3.1.4

Time-to-event outcome measure

No references identified.

3.1.5

Ratio of times to progression

Mick et al. (2000)

∙
∙

One-stage, ratio of times to progression
Requires programming

Mick and colleagues propose a design based on the growth modulation index
(ratio of time to progression of experimental treatment relative to that on the patients’
previous course of anti-cancer treatment). The outcome measure is novel and the
authors justify its use for trials of cytostatic treatments where outcome measures such
as tumour response may not be appropriate. Various values of the growth modulation
index for null and alternative hypotheses should be considered to explore design
parameters, as appropriate for the setting of the study. Each patient acts as their
own control. Information is required for each patient on their time to progression on
previous treatment, and an estimate of the correlation between the two times is needed.
The design is identified via simulation, which allows investigation of the effect of the
correlation estimate on the overall design. Although software is not detailed as being
available, this has been implemented in Splus, and detail is provided to allow design
implementation.

DESIGNS WITH A SINGLE ARM

3.2
3.2.1

Two-stage designs
Binary outcome measure

Gehan (1961)

∙
∙
∙

Two-stage, binary outcome
Standard software available
Early termination for lack of activity

Gehan proposes one of the earliest designs to assess experimental treatments
in phase II trials. The methodology is based on the double sampling method and
considers a phase II trial composed of a ‘preliminary’ stage and a ‘follow-up’
stage. The preliminary stage assesses whether the treatment under investigation is
likely to be worth further investigation, using a confidence interval approach to
exclude treatments with response rates below those of interest from further investigation. The follow-up stage assesses the activity of the treatment with pre-specified
precision. The number of patients to be included in the follow-up stage is determined according to the number of responses observed during the first stage. The
proposed design is intended to completely reject inactive treatments quickly, such
that if the response rate of interest is excluded from the confidence interval at the
end of the first stage, the trial is terminated early. Otherwise the trial continues.
In the second stage the activity of the treatment is estimated with given precision, rather than providing decision criteria for continuing to a further trial. On
this basis, this design may be seen as an estimation procedure for initial proof
of concept trials rather than trials to determine whether or not to proceed to
phase III.
Fleming (1982)

∙
∙
∙

Two-stage, binary outcome
Standard software available for overall sample size
Early termination for activity or lack of activity

Fleming proposes a one-stage, two-stage and multi-stage design. The multi-stage
design addresses multiple testing considerations to allow early termination in case
of extreme results, employing the standard single-stage test procedure at the last
test. Tables are presented for specific design scenarios using the exact underlying
binomial probabilities rather than the normal approximation to these probabilities.
Programs are readily available to calculate the overall sample size for a one-stage
design (e.g. Machin et al. 2008), with sample sizes at each stage chosen to be approximately equal. Termination at the end of each stage is permitted for activity or lack
of activity.

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

Simon (1987)

∙
∙
∙

Two-stage, binary outcome
Requires programming
Early termination for lack of activity

Simon introduces a two-stage design that is single arm with a binary outcome
whereby the sample size is minimised under a pre-specified expected response rate,
not necessarily the null or alternative response rate. Where this expected response rate
corresponds with the null hypothesis response rate, this design is equivalent to the
optimal design proposed in the subsequent paper summarised below (Simon 1989).
The current design is optimised by keeping the size of the first stage small, making
the probability of rejecting an inactive drug high, and not allowing too high a sample
size in the second stage. Early termination is permitted at the end of stage 1 only
for lack of activity. A table is provided with limited design scenarios; however, the
designs detailed below (Simon’s optimal and minimax) are more widely used and
may be considered ahead of this earlier design.
Simon (1989)

∙
∙
∙

Two-stage, binary outcome
Standard software available
Early termination for lack of activity

Simon proposes a single-arm two-stage design based on minimising the expected
number of patients under the null hypothesis (optimal), as well as an additional
design that minimises the maximum sample size (minimax). This is a well-known
and widely used two-stage design, based on null and alternative response rates, power
and significance level, and the observed number of responses at the end of each stage
is used to assess stopping rules. The outcome of interest is binary and the trial may
only be terminated at the end of the first stage for lack of activity. Extensive tables are
provided for different design scenarios and software is readily available (e.g. Machin
et al. 2008).
Green and Dahlberg (1992)

∙
∙
∙

Two-stage, binary outcome
Requires programming
Early termination for lack of activity

The design described by Green and Dahlberg permits early termination for lack
of activity at the end of stage 1 when the alternative hypothesis is rejected at the 0.02
significance level. At the end of the second stage a significance level of 0.055 is used to
reject the null hypothesis and declare sufficient activity for further investigation. Some

DESIGNS WITH A SINGLE ARM

detail is given regarding stopping boundary and sample size calculation, although this
would need to be programmed and solved iteratively to find the most suitable design.
This paper also discusses adaptations to the designs of Gehan (1961), Fleming (1982),
and Simon (1989), in the cases where the final attained trial sample size differs from
the original planned design.
Heitjan (1997)

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∙
∙

Two-stage, binary outcome
Programs noted as being available from the author
Early termination for activity or lack of activity

Heitjan proposes a design whereby decision-making is based on the ability to
persuade someone with extreme prior beliefs that the treatment under investigation
is either active or not. This requires specification of extreme priors. For a sceptic,
the probability that the experimental treatment is better than the standard treatment
must be at least some pre-specified value (e.g. 70%) for the treatment to be declared
active (known as the ‘persuade the pessimist probability’ PPP), and for an enthusiast,
the probability that the experimental treatment is worse than the standard treatment
must be at least some pre-specified value (e.g. 70%) for the treatment to be declared
inactive (known as the ‘persuade the optimist probability’ POP). Timing of interim
analyses can either be based on numbers of patients or time during the trial. Sample
size is justified by assessing the operating characteristics and calculating PPPs and
POPs of the design under various scenarios. Programs are noted as being available
upon request from the author. Early termination is permitted for activity or lack of
activity.
Herndon (1998)

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∙
∙

Two-stage, binary outcome
Requires programming
Early termination for lack of activity

Herndon proposes a hybrid two-stage design that allows continuation of recruitment while the results of the first stage are being analysed. If the results of the first
stage indicate the treatment is inactive, accrual is suspended and data are re-analysed
including data from all patients recruited to that time point. Otherwise, the design
continues to target recruitment for the second stage. The sample sizes for the first
and second stages are chosen for practicality rather than via Simon’s optimal method,
with overall sample size calculated to maintain pre-specified type I and II errors for
study-specific null and alternative hypotheses. Critical values for suspending recruitment, reinitiating or terminating recruitment and for declaring the treatment worthy
of further investigation at the end of stage 2 are calculated. To identify the critical
values a numerical search is required, for which formulae are provided. If the stage

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

I results indicate re-analysis using all patients to that time point, analysis follows
similar methodology to that proposed by Green and Dahlberg (1992), detailed above,
as does the analysis of stage II.
Chen and Ng (1998)

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∙
∙

Two-stage, binary outcome
Programs noted as being available from authors
Early termination for lack of activity

Chen and Ng propose a flexible design that operates in the same manner as
Simon’s two-stage design (Simon 1989), but here the number of patients at the first
and second stages can vary by up to eight patients to allow a period of grace in
halting recruitment (in a similar manner to that described by Green and Dahlberg
1992, detailed above). A FORTRAN program is noted as being available from the
authors to enable implementation, and tables are given for some scenarios.
Chang et al. (1999)

∙
∙
∙

Two-stage, binary outcome
Requires programming
Early termination for activity or lack of activity

Chang and colleagues outline a design for continuous or binary outcomes that
takes into account the number of patients on whom historical control data are based.
This reflects the fact that the variances of the historical control data and the experimental data will differ. The trial may be terminated at the end of the first stage for
either activity or lack of activity. Algorithms are used to determine critical values for
stopping, and sample size is calculated by multiplying the single-stage sample size
(formulae provided) by between 1.02 and 1.05.
Hanfelt et al. (1999)

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∙
∙

Two-stage, binary outcome
Programs noted as being available from authors
Early termination for lack of activity

Hanfelt and colleagues propose a modification to Simon’s two-stage design
(Simon 1989) that minimises the median number of patients required under the
null hypothesis, as opposed to the expected number of patients. A program is noted
as being available from the authors that performs the design search. The design differs
very little to that of Simon, other than when the response rate of the treatment is much
less than the null hypothesis rate. Termination at the end of the first stage is for lack
of activity only.

DESIGNS WITH A SINGLE ARM

Shuster (2002)

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∙
∙

Two-stage, binary outcome
Requires programming
Early termination for activity or lack of activity

The minimax design proposed by Shuster follows the same format as, for example,
Simon’s design (Simon 1989), although it allows early termination for activity at the
end of the first stage, as well as for lack of activity. Sample sizes and cut-offs are
calculated based on exact type I and II errors, and the smallest expected maximum
sample size is calculated. The author shows that the proposed design generates the
smallest sample sizes under the null, alternative and maximum scenarios, compared
to Chang et al. (1987) and Fleming (1982). The author advises use of the proposed
minimax design when early termination for activity is beneficial (giving as an example
the setting of paediatric cancer). A table of specific design scenarios is presented;
otherwise the design will require programming.
Tan and Machin (2002)

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∙
∙

Two-stage, binary outcome
Standard software available
Early termination for lack of activity

Tan and Machin propose two Bayesian designs: the single threshold design (STD)
and the dual threshold design (DTD). The designs are intended to be user-friendly and
easily interpreted by those familiar with frequentist phase II designs. They provide
an alternative approach to the design, analysis and interpretation of phase II trial
data, allowing incorporation of relevant prior information and summarising results in
terms of the probability that a response proportion falls within a pre-specified region
of interest. The following design parameters are required: target response rate for
a new treatment; prior distribution for the experimental treatment being tested; the
minimum probability of the true response rate being at least the target response rate
at the end of stage 1 (for the STD, 𝜆1) and at the end of the study (𝜆2). For the DTD,
the lower response rate of no further interest is also required, and here 𝜆1 represents
the probability that the true response rate is lower than the rate of no further interest
at the end of stage 1.
The STD focuses on ensuring, at the end of the first stage, that the final response
rate of the drug has a reasonable probability of passing the target response rate at the
end of the trial. The DTD, however, focuses on ensuring, at the end of the first stage,
that the final response rate at the end of the trial is not below the response rate of no
further interest. Tables are given for a number of design scenarios and the designs
are compared with the frequentist approach of Simon (1989). Programs have been
developed and are available in Machin et al. (2008).

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

Case and Morgan (2003)

∙
∙
∙

Two-stage, binary outcome
Standard software available and programs noted as being available from authors
Early termination for lack of activity

Case and Morgan outline a design with survival outcomes which are dichotomised
to give survival probabilities at pre-specified time points of interest, incorporating all
available information. The design is aimed to avoid the drawbacks of extended followup periods and breaks in recruitment during follow-up between stages. The design
does not require a halt in recruitment between stages as Nelson–Aalen estimates
of survival are used to incorporate all survival information up to the time point of
interest, at the time of interim analysis. Early termination is permitted only for lack
of activity. FORTRAN programs are noted as being available upon request from the
authors, to identify the optimal design, and the proposed design is also available in
Machin et al. (2008).
Jung et al. (2004)

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∙
∙

Two-stage, binary outcome
Programs noted as being available from authors
Early termination for activity or lack of activity

Jung and colleagues propose a searching algorithm to identify admissible twostage designs based on Bayesian decision theory, incorporating a loss function which
is a weighted function of the expected number of patients and the maximum number
of patients required. A computer program, developed in Java and noted as being
available upon request from the authors, searches admissible designs (comparing the
expected loss to the Bayes risk) using information provided on the response rates
under null and alternative hypotheses, type I and II errors and maximum number
of patients available. Stopping rules are generated based on a minimum number of
responses required to be observed.
Lin and Shih (2004)

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∙
∙

Two-stage, binary outcome
Programs noted as being available from authors
Early termination for lack of activity

Lin and Shih propose an adaptive design which allows sample size to be adjusted
at the end of the first stage, to account for uncertainty in the response rate under the
alternative hypothesis. Two potential response rates are pre-specified at the design
stage, and the adjustment made based on these. Tables are provided and software is

DESIGNS WITH A SINGLE ARM

noted as being available from the authors to compute sample size and cut-offs that
are not displayed.
Wang et al. (2005)

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∙
∙

Two-stage, binary outcome
Requires programming
Early termination for lack of activity

Wang and colleagues propose a Bayesian version of Simon’s two-stage design
(Simon 1989), controlling frequentist type I and II error rates, as well as Bayesian
error rates measured using posterior distributions. The design therefore allows incorporation of commonly controlled error rates familiar with frequentists, as well as
enabling calculation of posterior probabilities regarding treatment activity. Stopping
at the end of stage I is permitted for lack of activity only. Sample sizes and stopping
boundaries for each stage are provided in tables for specific design scenarios, and the
design is compared with that of Simon (1989) and the STD and DTDs of Tan and
Machin (2002). The design requires programming to enable implementation.
Banerjee and Tsiatis (2006)

∙
∙
∙

Two-stage, binary outcome
Programs noted as being available from authors
Early termination for activity or lack of activity

Banerjee and Tsiatis propose an adaptive design that is similar to Simon’s optimal
design (Simon 1989); however, the sample size and decision criteria of the second
stage depend on the outcome of the first stage, and the trial may terminate at the
end of the first stage for either activity or lack of activity. The sample size and
decision criteria of the second stage are computed using Bayesian decision theory,
minimising the average sample size under the null hypothesis. The design offers
a small sample size reduction over Simon’s optimal design (3–5%); however, the
authors note potential difficulties in planning a trial where the total sample size is
unknown at the outset. Tables are given for various design scenarios, and software is
noted as being available on request.
Ye and Shyr (2007)

∙
∙
∙

Two-stage, binary outcome
Programs available on website
Early termination for lack of activity

The design proposed by Ye and Shyr follows that of Simon (1989) but is designed
to balance the number of patients investigated in each of the stages. Attention is

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

focused on a binary response outcome measure although the design may be extended
to multiple correlated outcome measures (where more than one outcome can occur
for one patient). Tables are provided with various design scenarios and software is
available at www.vicc.org/biostatistics/ts/freqapp.php (last accessed August 2013).
The authors note that when there are few patients available, Simon’s minimax
design would be preferable. If the optimal and minimax designs have dramatically
imbalanced sample sizes between the two stages then the proposed design may be
preferable; otherwise Simon’s optimal design can be used as this minimises the sample size under the null hypothesis. Termination at the end of the first stage is for lack
of activity only.
Litwin et al. (2007)

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∙
∙

Two-stage, binary outcome
Programs noted as being available from authors
Early termination for activity or lack of activity

Litwin and colleagues describe a design based on the outcome measure of PFS
at two set time points. In the second stage of the design the success rate of a binary
outcome measure at a set time point t2 is considered, which is dependent upon the
success rate of a, possibly different, binary outcome measure at an earlier set time
point t1 (assessed at the end of stage 1), for example, the progression-free rate at
time t2, dependent upon the progression-free rate at time t1. The design incorporates
the possibility of stopping for either activity or lack of activity at the end of the first
stage and proceeds as follows:
1. n1 patients are recruited to the study and followed to time t1 for PFS.
2. If there are too few patients who are progression-free at time t1 then the trial
is stopped early for lack of activity.
3. If there are sufficient patients who are progression-free at time t1 then accrual
continues to the second stage until a total of n2 patients are recruited. Patients
in the initial cohort who are progression-free at t1 continue on in the study.
4. At the end of the second stage (t2) all n2 – n1 patients from the second stage
and all those patients progression-free at t1 are evaluated at time t2.
Programs are noted as being available upon request from the authors.
Wu and Shih (2008)

∙
∙
∙

Two-stage, binary outcome
Requires programming for adaptations
Early termination for lack of activity

DESIGNS WITH A SINGLE ARM

Wu and Shih propose approaches to handling data that deviate from the prespecified Simon’s two-stage design (Simon 1989). The following scenarios are
considered:

∙

Simon’s design ‘interrupted’, such that there is additional evaluation at the
following times:
a. before completion of the first stage;
b. after the first stage but before completion of the second stage;
c. before completion of the first stage and again before completion of the
second stage.

∙

Simon’s design ‘abandoned’, that is, the first unscheduled assessment leads to
abandoning the original design and an adapted assessment schedule is developed.

Adaptations to stopping rules are presented as well as detail regarding adjusting
the p-value associated with decision-making under the deviated scenario. Adaptations
are based on the conditional probability of passing the first stage and the conditional
power of rejecting the null hypothesis assuming the study continues to its final stage.
No software is detailed; however, sufficient detail is given to allow the design to be
programmed for implementation.
Koyama and Chen (2008)

∙
∙
∙

Two-stage, binary outcome
Programs available on website
Early termination for lack of activity

Koyama and Chen detail an adaptation to Simon’s two-stage design (Simon
1989) to allow proper inference when the actual sample size at stage 2 deviates
from the planned sample size. The methodology allows computation of updated
critical values for the second stage, based on the number of responses observed
in the first stage, and adapted p-values, point estimates and confidence intervals,
incorporating conditional power. Software is available at http://biostat.mc.vanderbilt.
edu/wiki/Main/TwoStageInference (last accessed August 2013).
Chi and Chen (2008)

∙
∙
∙

Two-stage, binary outcome
Standard programs available as per Simon’s two-stage design (Simon 1989)
Early termination for activity or lack of activity

Chi and Chen propose a curtailed sampling adaptation to Simon’s two-stage
design (Simon 1989). The design allows earlier termination of the trial in the event that

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

the treatment is either very active or very inactive. Detail of the proposed adaptations
is presented and is easily implemented, using standard software to identify a design
via Simon’s methodology (Simon 1989). The design can offer substantial savings in
sample sizes when compared to continuing recruitment to the predetermined number
of patients under Simon’s design.
Sambucini (2008)

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∙
∙

Two-stage, binary outcome
Programs noted as being available
Early termination for lack of activity

Sambucini proposes a Bayesian design which represents a predictive version of
the STD proposed by Tan and Machin (2002), taking into account the uncertainty
about the data that have not yet been observed, to identify optimal two-stage sample
sizes and cut-off values. A ‘design’ prior and an ‘analysis’ prior are required to
be specified to compute prior predictive distributions and posterior probabilities of
treatment activity, respectively. A program written in R is available to determine
optimal two-stage designs.

3.2.2

Continuous outcome measure

Chang et al. (1999)

∙
∙
∙

Two-stage, continuous outcome
Requires programming
Early termination for activity or lack of activity

3.2.3

Multinomial outcome measure

Zee et al. (1999)

∙
∙
∙

Two-stage, multinomial outcome
Requires programming
Early termination for activity or lack of activity

DESIGNS WITH A SINGLE ARM

∙
∙
∙

Two-stage, multinomial outcome
Programs noted as being available from authors
Early termination for activity or lack of activity

Lin and Chen detail a design that considers both CRs and PRs in a trinomial
outcome, weighting CR as the more desirable outcome. Investigators must specify
overall response rates under the null and alternative hypotheses, and the proportion
that is attributable to CR. A weighted score is calculated at the end of each stage
and this is compared with predetermined cut-off boundaries as in Simon’s optimal
and minimax designs (to which this paper may be viewed as an extension) (Simon
1989). Tables are given for specific scenarios; however, programs are noted as being
available upon request from the authors.
Panageas et al. (2002)

∙
∙
∙

Two-stage, multinomial outcome
Programs noted as being available from authors
Early termination for lack of activity

Panageas and colleagues propose a single-arm two-stage design based on Simon’s
optimal design (Simon 1989), but with a trinomial outcome (e.g. CR vs. PR vs. nonresponse). The design requires null and alternative response rates to be specified for
both CR and PR, that is, improvements in both categories are required. The optimal
design is identified iteratively, to minimise the expected sample size and to satisfy
the type I and II error rates. A computer program is noted as being available from
the authors, with specific design scenarios presented in tables. There is a marginal
saving on sample size over Simon’s design (Simon 1989). The design differs from
that of Zee et al. (1999), detailed above, since early termination is permitted for lack
of activity only and does not incorporate weighting of the different outcomes.
Lu et al. (2005)

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∙
∙

Two-stage, multinomial outcome
Programs may be available from authors
Early termination for lack of activity

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

Lu and colleagues propose a design (one-stage or two-stage) to look at both CR
and total response (or other such outcome measures whereby observing one outcome
implies the other outcome is also observed). The design recommends a treatment
for further investigation if either of the alternative hypotheses is met (i.e. for CR
or for total response) and rejects the treatment if neither is met. The designs follow
the general approach of Fleming’s single-stage (1982) or Simon’s two-stage (Simon
1989) approach whereby the number of CRs and total responses are compared to
identified stopping boundaries. Tables are provided for some combinations of null
and alternative hypotheses; however, formulae are given and at the time of manuscript
publication programs were in development. The design differs from others in this
section in that one outcome measure is a sub-outcome measure of the other, whereas
other designs consider discrete outcome measures such as PR versus CR.
Chang et al. (2007)

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∙
∙

Two-stage, multinomial outcome
Programs noted as being available from authors
Early termination for activity or lack of activity

Chang and colleagues propose a single-stage and a two-stage design for window studies which aim to assess the potential activity of a new treatment in newly
diagnosed patients. Treatment is given to patients for a short period of time before
standard chemotherapy, and each patient is assessed for response or early progression (both binary outcome measures). The alternative hypothesis is based on both the
response rate being above a pre-specified rate and the early progressive disease rate
being below a pre-specified rate. The outcomes follow a multinomial distribution. A
SAS program is noted as being available from the authors to identify designs.
Goffin and Tu (2008)

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∙
∙

Two-stage, multinomial outcome
Programs noted as being available from authors
Early termination for lack of activity

Goffin and Tu outline an adaptation to the design proposed by Zee et al. (1999),
based on a simulation approach to determine design. The authors note that the previous
design of Zee was found to have lower power than intended (Freidlin et al. 2002;
Zee et al. 1999). In the proposed two-stage design decision criteria are based on
the proportion of patients with response and the proportion of patients with early
progressive disease, in an advanced disease setting. The alternative hypothesis is that
the response rate is sufficiently high or the early progressive disease rate is sufficiently
low. Simulation is used to determine the required stopping boundaries to satisfy prespecified design criteria. Programs are noted as being available upon request from
the authors. Early termination is permitted for lack of activity only.

DESIGNS WITH A SINGLE ARM

Kocherginsky et al. (2009)

∙
∙
∙

Two-stage, multinomial outcome
Programs available from website
Early termination for lack of activity

Kocherginsky and colleagues outline a design to consider the proportion of
patients achieving response and the proportion of patients not progressing early.
The alternative hypothesis being tested is that the response rate is sufficiently high or
the non-progression rate is sufficiently high. Sample size is calculated via numerical
searching, with the initial sample size estimate calculated following Simon’s twostage design (Simon 1989) based on the response rate limits. A numerical search is
then performed over all combinations of design parameters to determine stopping
rules, evaluated by assessing the probability of early termination and the probability
of rejecting the null hypothesis. The design incorporates a thorough assessment of
the operating characteristics over a range of response and progression rates, to guard
against unexpectedly high false-positive rates under certain parameters. Programs
written in R to implement the numerical search are noted as being available from
http://health.bsd.uchicago.edu/filestore/biostatlab/ (last accessed July 2013). Early
termination is permitted for lack of activity only.
Stallard and Cockey (2008)

∙
∙
∙

Two-stage, multinomial outcome
Programs noted as being available from author
Early termination for lack of activity

3.2.4

Time-to-event outcome measure

Case and Morgan (2003)

∙
∙
∙

Two-stage, time-to-event outcome
Standard software available and programs noted as being available from authors
Early termination for lack of activity

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

∙
∙
∙

Two-stage, time-to-event outcome
Programs noted as being available from authors
Early termination for activity or lack of activity

Litwin and colleagues describe a design based on the outcome measure of
progression-free survival at two set time points, that is, a binary outcome. In the
second stage of the design the success rate of a binary outcome measure at a set
time point t2 is considered, which is dependent upon the success rate of a, possibly
different, binary outcome measure at an earlier set time point t1 (assessed at the end
of stage 1), for example, the progression-free rate at time t2, dependent upon the
progression-free rate at time t1. The design incorporates the possibility of stopping
for either activity or lack of activity at the end of the first stage and proceeds as
follows:
1. n1 patients are recruited to the study and followed to time t1 for PFS.
2. If there are too few patients who are progression-free at time t1 then the trial
is stopped early for lack of activity.
3. If there are sufficient patients who are progression-free at time t1 then accrual
continues to the second stage until a total of n2 patients are recruited. Patients
in the initial cohort who are progression-free at t1 continue on the study.
4. At the end of the second stage (t2) all n2 – n1 patients from the second stage
and all those patients progression-free at t1 are evaluated at time t2.
Programs are noted as being available upon request from the authors.

3.2.5

Ratio of times to progression

No references identified.

DESIGNS WITH A SINGLE ARM

3.3
3.3.1

Multi-stage designs
Binary outcome measure

Herson (1979)

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∙
∙

Multi-stage, binary outcome
Programs noted as being available from author
Early termination for lack of activity

Herson describes a Bayesian multi-stage design that considers early stopping
rules based on the predictive probability that a treatment will not be successful at
the end of the phase II trial. Early termination is therefore only permitted for lack
of activity. The design incorporates investigators’ prior information on the response
rate of the experimental treatment and confidence in this prior information (via a
coefficient of variation). Early termination boundaries are calculated based on prespecified sample sizes ranging from 20 to 30 patients, and consideration is also given
to the expected sample size of a subsequent phase III trial. Programs are noted as
being available from the author.
Fleming (1982)

∙
∙
∙

Multi-stage, binary outcome
Standard software available for overall sample size
Early termination for activity or lack of activity

Fleming proposes a one-stage, two-stage and multi-stage design. The multi-stage
design addresses multiple testing considerations to allow early termination in the case
of extreme results, employing the standard single-stage test procedure at the last test.
Tables are presented for specific design scenarios using the exact underlying binomial
probabilities rather than the normal approximation to these probabilities. Programs
are readily available to calculate the overall sample size for a one-stage design (e.g.
Machin et al. 2008), with sample sizes at each stage chosen to be approximately
equal. Termination at the end of each stage is permitted for activity or lack of activity.
Bellissant et al. (1990)

∙
∙
∙

Multi-stage, binary outcome
Requires programming
Early termination for activity or lack of activity

Bellissant and colleagues apply the triangular test (TT) and sequential probability
ratio test (SPRT), previously used in phase III trials, to single-arm group-sequential

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

phase II trials with a binary outcome. An efficient score, Z, and Fisher’s information,
V, are calculated derived from the likelihood function. The log odds ratio statistic is used as the measure of the difference between the actual success rate and
the null hypothesis rate. Formulae are given for the calculation of Z and V as well
as for calculation of the stopping boundaries, whereby Z is seen as the difference
between observed and expected number of responses under the null hypothesis and
V as the variance of Z under the null hypothesis. Early termination is permitted for
either activity or lack of activity. Sample size is justified via the operating characteristics of the TT and SPRT, and group sizes and number of stages are arbitrary,
ranging from 5 to 15 in the examples. The design requires programming to enable
implementation.
Chen et al. (1994)

∙
∙
∙

Multi-stage, binary outcome
Requires programming
Early termination for lack of activity

Chen and colleagues propose a multi-stage design that is an extension of Gehan’s
two-stage design (Gehan 1961), where the chance of stopping early is increased if
the observed response rate is smaller than that of interest. It is noted that this design
is suitable for phase II trials that have high expected response rates, in contrast to
the design of Gehan where the chance of stopping a trial early is low if the response
rate of interest is above 0.3. Limited tables of designs are presented, therefore additional designs will require programming. Early termination is permitted for lack of
activity only.
Ensign et al. (1994)

∙
∙
∙

Multi-stage, binary outcome
Requires programming
Early termination for lack of activity

Ensign and colleagues propose a single-arm three-stage design that is an extension
to the two-stage design of Simon (1989). At the end of the first stage, the trial is
terminated if no responses are observed (i.e. for lack of activity). If at least one
response is observed, stages 2 and 3 are carried out as per Simon’s stages 1 and 2.
The sample sizes and cut-offs for stages 2 and 3 are determined to minimise the
expected sample size under the null hypothesis. A restriction is made that the first
stage must include at least five patients. Extensive tables are provided for designs
under differing scenarios; however, the design will need programming to enable
implementation outwith those provided.

DESIGNS WITH A SINGLE ARM

Thall and Simon (1994a)

∙
∙
∙

Multi-stage, binary outcome
Programs noted as being available from authors
Early termination for lack of activity

Thall and Simon present sample size calculations for their original Bayesian
continuous monitoring design (Thall and Simon 1994b). Adaptations to this design are
also provided. The impact of group-sequential monitoring, as opposed to continuous
monitoring, is assessed and it is found that assessment after every two, three or four
patients has little impact on results; however, reducing assessments much further can
increase the likelihood of inconclusive results. The first adaptation considers early
stopping boundaries for inconclusive results. The second adaptation considers early
termination for lack of activity, which considers only lower stopping boundaries.
Software is noted as being available upon request to compute and implement each
of these designs, including the original continuous monitoring design (Thall and
Simon 1994b).
Tan and Xiong (1996)

∙
∙
∙

Multi-stage, binary outcome
Programs available on website
Early termination for activity or lack of activity

Tan and Xiong propose a group-sequential (or continuous monitoring) design for
the assessment of a binary outcome in a single-arm trial, based on the sequential
conditional probability ratio test (SCPRT). The design is based around comparison to
a reference fixed sample size test (RFSST) such as that proposed by Fleming (1982),
and the results that this would achieve, since it is desirable to preserve the power of
this test while incorporating additional opportunities to terminate the trial early. The
proposed design provides similar power to the fixed sample size test, but allows more
opportunity to terminate the trial early (for activity or lack of activity). A FORTRAN
program is available via the website (http://lib.stat.cmu.edu/designs/scprtbin (last
accessed July 2013)) to compute the design characteristics.
Chen (1997)

∙
∙
∙

Multi-stage, binary outcome
Program noted as being available from author
Early termination for lack of activity

Chen proposes an extension to Simon’s minimax and optimal two-stage designs
(Simon 1989), simply incorporating an additional stage. Tables are provided with
designs under various scenarios, and a FORTRAN program is noted as being available

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

from the author for other scenarios. When compared to Simon’s design, the three-stage
design sometimes has smaller expected sample size; however, this is not consistent.
Compared to Ensign’s three-stage design (Ensign et al. 1994), the proposed design
does not make restrictions on the size and cut-off for the first stage.
Murray et al. (2004)

∙
∙
∙

Multi-stage, binary outcome
Requires programming
Early termination for activity or lack of activity

Murray and colleagues detail calculation of stopping rules based on confidence
interval estimation of the response rate at each stage. A table of specific design
scenarios is presented; however, the design requires programming to identify optimal
decision criteria for scenarios outwith the tables. The design is based on a prespecified fixed sample size (i.e. no sample size calculation is performed) and a fixed
number of stages (with fixed sample size at each stage), with type I and II errors
evaluated for the resulting design. Early termination is permitted for either activity
or lack of activity. The design may be used when only a small number of patients
are available for study (30 patients considered in the motivating example) and exact
binomial calculations are employed.
Ayanlowo and Redden (2007)

∙
∙
∙

Multi-stage, binary outcome
Requires programming
Early termination for lack of activity

Ayanlowo and Redden propose a stochastic curtailment design which is based
on the simple binomial test and considers the conditional probability of declaring a
treatment active at the end of the trial, conditional upon the responses observed to
date and the assumption that the alternative hypothesis is true. The design requires
programming to identify the points at which to conduct interim assessments. Sample
size determination is based on a binomial test. Stochastic curtailment adaptations to
Simon’s minimax and optimal design are also proposed (Simon 1989). While the
proposed designs provide more opportunity to stop a trial early due to an inactive
treatment, the authors suggest its use only when Simon’s minimax design is already
being considered, and when the trial is expected to recruit slowly and the outcome
may be observed relatively quickly.
Chen and Shan (2008)

∙
∙
∙

Multi-stage, binary outcome
Programs noted as being available from authors
Early termination for activity or lack of activity

DESIGNS WITH A SINGLE ARM

Chen and Shan outline a three-stage design, extending previous designs to allow
early termination for either activity or lack of activity (Chen 1997; Ensign et al.
1994; Simon 1989). Tables are given for optimal and minimax designs where the
difference in null and alternative hypothesis rates is 0.20 or 0.15, for a number of
scenarios. A C program is noted as being available from the authors to search for
designs under alternative scenarios. Comparing the proposed optimal and minimax
designs with those of Chen (1997), the designs presented in the current paper require
larger maximal sample size under the optimal design and similar maximal sample
size under the minimax design, but have a smaller average sample number in most
cases. Due to the ability to terminate early for either activity or lack of activity, the
probability of early termination at the first stage and overall is higher for the current
designs compared to those of Chen (1997).
Lee and Liu (2008)

∙
∙
∙

Multi-stage, binary outcome
Programs available from website
Early termination for lack of activity or activity

Lee and Liu outline a Bayesian group-sequential/continuous monitoring design
based on a binary outcome and the use of predictive probabilities (probability of a
positive result should the trial run to conclusion, given the interim data observed).
The design incorporates early termination for lack of activity, as well as activity. The continuous monitoring design is compared to Simon’s two-stage design
(Simon 1989). Under the proposed approach the probability of stopping the trial
early is higher, and in general, the expected sample size under the null hypothesis
is smaller. When assessing the design for robustness to deviation from continuous monitoring, although the type I error rate is inflated (usually less than 10%)
the design generally remains robust. The authors provide further considerations of
robustness to early termination, estimation bias and comparison to posterior probability designs. Software is available from https://biostatistics.mdanderson.org/Software
Download/SingleSoftware.aspx?Software_Id=84 (last accessed July 2013) to allow
implementation.

3.3.2

Continuous outcome measure

No references identified.

3.3.3

Multinomial outcome measure

Zee et al. (1999)

∙
∙
∙

Multi-stage, multinomial outcome
Requires programming
Early termination for activity or lack of activity

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

3.3.4

Time-to-event outcome measure

Cheung and Thall (2002)

∙
∙
∙

Multi-stage, time-to-event outcome
Programs noted as being available from authors
Early termination for activity or lack of activity

Cheung and Thall propose a Bayesian sequential-adaptive procedure for continuous monitoring, which may be extended to assessment after cohorts of more than
one patient, that is, multi-stage. The outcome measure of interest is a binary indicator of a composite time-to-event outcome, utilising all the censored and uncensored
observations at each interim assessment. Continuous monitoring based on the approximate posterior (CMAP) is used following Thall and Simon (1994b). The design can
incorporate multiple competing and non-competing outcomes. Early termination is
permitted for activity or lack of activity. R programs are noted as being available
from the authors to allow implementation of the design. This design enables data to
be incorporated on all patients at each interim assessment without all follow-up data
being obtained and may therefore be used when follow-up of each patient is for a
non-trivial period of time.

3.3.5

Ratio of times to progression

No references identified.

3.4 Continuous monitoring designs
3.4.1

Binary outcome measure

Thall and Simon (1994b)

∙
∙
∙

Continuous monitoring, binary outcome
Programs noted as being available from authors
Early termination for activity or lack of activity

Thall and Simon propose a Bayesian continuous monitoring design to assess the
binary outcome of response in a single-arm trial. Information required includes prior

DESIGNS WITH A SINGLE ARM

information on the standard treatment, required improvement due to the experimental
treatment and minimum and maximum boundaries on sample size. A flat prior is
assumed for the experimental treatment. Also required is a concentration parameter
for the experimental treatment, representing the amount of dispersion about the
mean of the experimental treatment. After the response outcome is observed on each
patient, the trial may be terminated for lack of activity, terminated for activity or
continued to the next patient (although this assessment is not required before the next
patient can be recruited). If the maximum sample size is obtained and neither of the
stopping boundaries for activity or lack of activity is crossed, the trial is declared
inconclusive. Stopping boundaries are calculated in terms of upper and lower posterior
probability limits, calculated by numerical integration. Designs should be assessed
by simulation to investigate the operating characteristics. Detail regarding software
and implementation is presented elsewhere (Thall and Simon 1994a).
Thall and Simon (1994a)

∙
∙
∙

Continuous monitoring, binary outcome
Programs noted as being available from authors
Early termination for lack of activity

Thall and Simon present sample size calculations for their original Bayesian continuous monitoring design (Thall and Simon 1994b) outlined above. Adaptations to
this design are also provided. The first adaptation considers early stopping boundaries
for inconclusive results. The second adaptation considers early termination for lack
of activity, which considers only lower stopping boundaries. Software is noted as
being available upon request to compute and implement the designs, including the
original continuous monitoring design (Thall and Simon 1994b).
Tan and Xiong (1996)

∙
∙
∙

Continuous monitoring, binary outcome
Programs available on website
Early termination for activity or lack of activity

Tan and Xiong propose a group-sequential (or continuous monitoring) design for
the assessment of a binary outcome in a single-arm trial, based on the SCPRT.
The design is based around comparison to a RFSST such as that proposed by
Fleming (1982), and the results that this would achieve, since it is desirable to
preserve the power of this test while incorporating additional opportunities to terminate the trial early. The proposed design provides similar power to the fixed
sample size test, but allows more opportunity to terminate the trial early (for
activity or lack of activity). A FORTRAN program is available via the website
(http://lib.stat.cmu.edu/designs/scprtbin (last accessed July 2013)) to compute the
design characteristics.

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

Chen and Chaloner (2006)

∙
∙
∙

Continuous monitoring, binary outcome
Programs noted as being available from authors
Early termination for lack of activity

Chen and Chaloner propose a stopping rule for a Bayesian continuous monitoring
design. Stopping rules are based on both the posterior probability that the failure rate
is unacceptably high and the posterior probability that the failure rate is acceptably
low, where these high and low values are derived from historical data. Patients are
recruited until either the stopping rules are met or a maximum sample size has been
recruited. Programs are noted as being available in R (via contacting the authors) to
enable computation of the stopping boundaries and operating characteristics based
on maximum sample size available, prior information on the experimental treatment,
null and alternative hypothesis rates and the upper and lower posterior probability
bounds. Early termination is permitted only for lack of activity.
Lee and Liu (2008)

∙
∙
∙

Continuous monitoring, binary outcome
Programs available from website
Early termination for lack of activity or activity

∙
∙
∙

Continuous monitoring, binary outcome
Programs available on website
Early termination for lack of activity or activity

DESIGNS WITH A SINGLE ARM

Johnson and Cook propose a Bayesian continuous monitoring design based
on formal hypothesis tests. They argue that, in contrast to Bayesian designs based
on posterior credible intervals, any misspecification of prior densities associated
with the alternative hypothesis cannot bias the trial results in favour of the null
hypothesis when the proposed formal hypothesis test approach is used. Analysis
is performed after data are available for each patient, and the trial may be terminated early for activity or lack of activity. Software is available from https://bio
statistics.mdanderson.org/SoftwareDownload/SingleSoftware.aspx?Software_Id=94
(last accessed July 2013) which allows the trial to be designed according to userspecified priors.

3.4.2

Continuous outcome measure

No references identified.

3.4.3

Multinomial outcome measure

No references identified.

3.4.4

Time-to-event outcome measure

Cheung and Thall (2002)

∙
∙
∙

Continuous monitoring, time-to-event outcome
Programs noted as being available from authors
Early termination for activity or lack of activity

Cheung and Thall propose a Bayesian sequential-adaptive procedure for continuous monitoring. The outcome measure of interest is a binary indicator of a composite
time-to-event outcome, utilising all the censored and uncensored observations at
each interim assessment. Continuous monitoring based on the approximate posterior
(CMAP) is used following Thall and Simon (1994b). The design can incorporate
multiple competing and non-competing outcomes. Early termination is permitted for
activity or lack of activity. R programs are noted as being available from the author
to allow implementation of the design. This design enables data to be incorporated
on all patients at each assessment without all follow-up data being obtained and may
therefore be used when follow-up of each patient is for a non-trivial period of time.
Thall et al. (2005)

∙
∙
∙

Continuous monitoring, time-to-event outcome
Programs noted as being available from authors
Early termination for activity or lack of activity

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

Thall and colleagues propose Bayesian continuous monitoring designs that incorporate three time-to-event outcomes (death, disease progression and SAE). Various
amendments to the design are proposed, including randomisation, frequent interval
monitoring, alternative distribution assumptions and incorporation of interval censoring for disease progression. The trial may be stopped early for lack of activity or
for activity. Simulations are performed to establish operating characteristics of the
designs. Programs are noted as being available from the authors upon request.
Johnson and Cook (2009)

∙
∙
∙

Continuous monitoring, time-to-event outcome
Programs available on website
Early termination for lack of activity or activity

3.4.5

Ratio of times to progression

No references identified.

3.5 Decision-theoretic designs
3.5.1

Binary outcome measure

Sylvester and Staquet (1980)

∙
∙
∙

Decision-theoretic, binary outcome
Requires programming
Early termination for activity or lack of activity

Sylvester and Staquet outline a decision-theoretic design whereby the sample
size and cut-off boundaries for decision-making in the phase II trial are calculated
based on the number of patients who would be expected to receive the experimental
treatment in a subsequent phase III trial, as well as prior probabilities of the response
proportions of the experimental treatment in the phase II trial. There are examples

DESIGNS WITH A SINGLE ARM

of specific design scenarios; however, the design would require programming to
enable implementation. Decision criteria are based on observing a given number of
responses. The design allows incorporation of interim assessments, at which the trial
may be terminated early for either activity or lack of activity.

3.5.2

Continuous outcome measure

No references identified.

3.5.3

Multinomial outcome measure

No references identified.

3.5.4

Time-to-event outcome measure

No references identified.

3.5.5

Ratio of times to progression

No references identified.

3.6

Three-outcome designs

3.6.1

Binary outcome measure

Lee et al. (1979)

∙
∙
∙

Three-outcome design, binary outcome
Requires programming
Early termination for activity or lack of activity

Lee and colleagues present a two-stage, three-outcome design whereby the available sample size is pre-specified based on non-statistical considerations such as
patient availability, and the optimal design is identified based on given constraints.
The design is based on determining whether the true response rate is above or below
a single pre-specified response rate, incorporating the possibility to declare an inconclusive result. Tables are presented for a target 20% response rate only, with upper
and lower limits of 30% and 10%, respectively, for determining activity, lack of
activity or an inconclusive result. The paper is therefore somewhat impractical for
designs beyond this specific setting, without further work to implement for other
scenarios. The design may be seen to complement the confidence interval approach
to estimating a response rate with given precision.

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

Storer (1992)

∙
∙
∙

Three-outcome design, binary outcome
Programs noted as being available from author
Early termination for activity or lack of activity

Storer proposes a three-outcome design that is an adaptation to single-, two- and
multi-stage designs such as those described by Fleming (1982). The event rate of
uncertainty is taken to be around the midpoint between the event rate of no interest
and the event rate of interest. As described in Chapter 2, various error rates are
required to be specified. Here the probabilities of concluding in favour of either the
null or alternative hypothesis when in fact the true response rate lies within the region
of uncertainty are required to be specified. These error rates are set to be equal under
this design. Programs are noted as being available to identify the design, upon request
from the author. Early termination is permitted for activity or lack of activity in the
two- and multi-stage designs.
Sargent et al. (2001)

∙
∙
∙

Three-outcome design, binary outcome
Requires programming; programs may be available upon request
Early termination for lack of activity

Sargent and colleagues propose a single-stage (and two-stage) design with three
possible outcomes. As described in Chapter 2, various error rates are required to be
specified, corresponding to differing regions of the distribution curves presented in
Figure 2.2. Here specific probabilities for concluding uncertainty are specified under
both the null and alternative hypotheses (𝜆 and 𝛿, respectively, in Figure 2.2), and
these may differ. Tables and formulae are provided for sample size and stopping rule
calculation. The design requires programming; however, programs may be available
upon request from the authors. Under the two-stage design, early termination is for
lack of activity only.

3.6.2

Continuous outcome measure

No references identified.

3.6.3

Multinomial outcome measure

No references identified.

3.6.4

Time-to-event outcome measure

No references identified.

DESIGNS WITH A SINGLE ARM

3.6.5

Ratio of times to progression

No references identified.

3.7

Phase II/III designs

There are no phase II/III designs listed in this chapter since these designs require a
control arm to be incorporated in the phase II trial, to enable a seamless transition to
phase III.

Designs for single experimental
therapies including
randomisation
Sarah Brown

The designs included in this chapter incorporate randomisation to a control arm with
the intention of a formally powered statistical comparison between the experimental
and control arms, as well as designs where incorporation of randomisation is primarily
to provide a calibration arm, with no statistical comparison formally powered. The
distinction between these approaches is presented for each design listed.

4.1 One-stage designs
4.1.1

Binary outcome measure

Herson and Carter (1986)

∙
∙
∙

One-stage, binary outcome
No formally powered statistical comparison between arms
Requires programming

Herson and Carter consider the inclusion of a randomised calibration group
in single-stage phase II trials of a binary endpoint, in order to reduce the risk of
A Practical Guide to Designing Phase II Trials in Oncology, First Edition.
Sarah R. Brown, Walter M. Gregory, Chris Twelves and Julia Brown.
© 2014 John Wiley & Sons, Ltd. Published 2014 by John Wiley & Sons, Ltd.

RANDOMISED DESIGNS FOR SINGLE EXPERIMENTAL THERAPIES

false-negative decision-making. Patients are randomised between current standard
treatment (calibration group) and the treatment under investigation. Results of the
calibration group are intended largely to assess the credibility of the outcome in the
experimental arm, that is, not for formal comparative purposes. Decision criteria are
based primarily on the experimental arm results; however, outcomes in the calibration
arm are also considered to address the initial assumptions made regarding the current
standard treatment. Thus the trial essentially constitutes two separate designs, one for
the experimental arm and one for the calibration arm. Due to the assessment of the
control arm results, the overall sample size of the trial may be between three and five
times that of a non-calibrated design. An example is provided; however, the design
will require programming.
Thall and Simon (1990)

∙
∙
∙

One-stage, binary outcome
No formally powered statistical comparison between arms
Requires programming

Thall and Simon outline a design that incorporates historical data, including
variability, into the design of the trial. A specific proportion of patients are randomised
to a control arm dependent upon the amount of historical control data available, the
degree of both inter-study and intra-study variability and the overall sample size of
the phase II study being planned (following formulae provided). The inclusion of a
sample of patients randomised to a control arm allows the precision of the response
rate in the experimental arm at the end of the trial to be maximised, relative to
the control. Sample size is determined iteratively and the design would need to be
programmed to allow implementation.
Stone et al. (2007b)

∙
∙
∙

One-stage, binary outcome
Formally powered statistical comparison between arms
Standard software available

Stone et al. discuss the use of progressive disease rate at a given time point (as
well as overall progression-free survival) as an outcome measure in randomised phase
II trials of cytostatic agents. Formal comparison between the experimental treatment
and the control treatment is performed for superiority; however, larger type I error
rates than would be used in phase III are incorporated, and large treatment effects
are targeted. The use of relaxed type I errors and large targeted treatment effects
contribute to reduced sample sizes compared to phase III trials, and may therefore be
deemed more realistic for phase II trials.

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

4.1.2

Continuous outcome measure

Thall and Simon (1990)

∙
∙
∙

One-stage, continuous outcome
No formally powered statistical comparison between arms
Requires programming

Thall and Simon outline a design that incorporates historical data, including
variability, into the design of the trial. A specific proportion of patients are randomised
to a control arm dependent upon the amount of historical control data available, the
degree of both inter-study and intra-study variability and the overall sample size of
the phase II study being planned (following formulae provided). The inclusion of a
sample of patients randomised to a control arm allows the precision of the outcome
estimate in the experimental arm at the end of the trial to be maximised, relative to
the control. Sample size is determined iteratively and the design would need to be
programmed to allow implementation.
Chen and Beckman (2009)

∙
∙
∙

One-stage, continuous outcome
Formally powered statistical comparison between arms
Programming code provided

Chen and Beckman describe an approach to a randomised phase II trial design
that incorporates optimal error rates. Optimal type I and II errors for the design are
identified by means of an efficiency score function which is based on initial proposed
error rates and the ratio of sample sizes between phases II and III. Sample size
calculation is performed using standard phase III-type approaches using the optimal
identified type I and II errors. Formal comparison with the control arm is incorporated.
The design considers cost efficiency of the phase II and III trials, on the basis of the
ratio of sample sizes between phases II and III and the a priori probability of success
of the investigational treatment. An R program is provided in the appendix of the
manuscript to identify optimal designs.

4.1.3

Multinomial outcome measure

No references identified.

4.1.4

Time-to-event outcome measure

Simon et al. (2001)

∙
∙
∙

One-stage, time-to-event outcome
Formally powered statistical comparison between arms
Standard software available

RANDOMISED DESIGNS FOR SINGLE EXPERIMENTAL THERAPIES

Simon and colleagues propose what is termed a randomised ‘phase 2.5’ trial
design, incorporating intermediate outcome measures such as progression-free survival. The design takes the approach of a phase III trial design, with a formally
powered statistical comparison with the control arm for superiority. It incorporates
a relaxed significance level, large targeted treatment effects and intermediate outcome measures, resulting in more pragmatic and feasible sample sizes than would be
required in a phase III trial. The design is straightforward, following the methodology
of phase III trials; however, it is important to note that this should only be used where
large treatment differences are realistic and should not be seen as a way to eliminate
phase III testing.
Stone et al. (2007b)

∙
∙
∙

One-stage, time-to-event outcome
Formally powered statistical comparison between arms
Standard software available

Stone et al. discuss the use of progressive disease rate at a given time point, as
well as overall progression-free survival, as an outcome measure in randomised phase
II trials of cytostatic agents. Formal comparison between the experimental treatment
and the control treatment is performed for superiority; however, larger type I error
rates than would be used in phase III are incorporated, and large treatment effects
are targeted. The use of relaxed type I errors and large targeted treatment effects
contribute to reduced sample sizes compared to phase III trials, and may therefore be
deemed more realistic for phase II trials. This reflects the designs described above
by Simon et al. in the setting of time-to-event outcomes, which are described by the
authors as ‘phase 2.5’ designs (Simon et al. 2001).
Chen and Beckman (2009)

∙
∙
∙

One-stage, time-to-event outcome
Formally powered statistical comparison between arms
Programming code provided

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

4.1.5

Ratio of times to progression

No references identified.

4.2 Two-stage designs
4.2.1

Binary outcome measure

Whitehead et al. (2009)

∙
∙
∙
∙

Two-stage, binary outcome
Formally powered statistical comparison between arms
Requires programming
Early termination for activity or lack of activity

Whitehead and colleagues outline a randomised controlled two-stage design with
normally distributed outcome measures that may be extended to the setting of binary
and ordinal outcomes. The design allows early termination for activity, or lack of
activity, and incorporates formal comparison between experimental and control arms.
At the interim assessment, which takes place after approximately half the total number
of patients have been recruited, sample size re-estimation may be incorporated if
necessary. The methodology employs approximations to the normal distribution since
sample sizes are generally large enough. No software is detailed as being available
to identify designs; however, programming is noted as being possible in SAS, and
detail is provided to allow its implementation. Simulation is also required to evaluate
potential designs.
Jung (2008)

∙
∙
∙
∙

Two-stage, binary outcome
Formally powered statistical comparison between arms
Programs noted as being available from author
Early termination for lack of activity

Jung proposes a randomised controlled extension to Simon’s optimal and minimax
designs (Simon 1989) in the context of a binary outcome measure (e.g. response). The
experimental arm is formally compared with the control arm and declared worthy of
further investigation only if there are sufficiently more responders in the experimental
arm. Extensive tables are provided, and programs to identify designs not included in
tables are noted as being available upon request from the author. Extensions to the
design include unequal allocation, strict type I and II error control and randomisation
to more than one experimental arm.

RANDOMISED DESIGNS FOR SINGLE EXPERIMENTAL THERAPIES

Jung and George (2009)

∙
∙
∙
∙

Two-stage, binary outcome
Formally powered statistical comparison between arms
Requires minimal programming
Early termination for lack of efficacy

Jung and George propose methods of comparing treatment arms in a randomised
phase II trial, where the intention is either to determine whether a single treatment
is worthy of evaluation compared to a control or to select one treatment from many
for further evaluation. The phase II design for a single experimental treatment versus control is initially based on the evaluation of the control and experimental arms
independently following Simon’s two-stage design (Simon 1989), or similar. The
experimental treatment must first be accepted via this evaluation, that is, compared
to historical control rates, and is then formally compared with the concurrent control arm. The experimental treatment is deemed worthy of further evaluation if the
treatment difference between the two arms is above some pre-defined value. No software is detailed; however, detail is given which should allow implementation, and
sufficient examples are also provided. The initial two-stage design can be calculated
using standard software available for Simon’s two-stage design.

4.2.2

Continuous outcome measure

Whitehead et al. (2009)

∙
∙
∙
∙

Two-stage, continuous outcome
Formally powered statistical comparison between arms
Requires programming
Early termination for activity or lack of activity

Whitehead and colleagues outline a randomised controlled two-stage design with
normally distributed outcome measures. The design allows early termination for
activity, or lack of activity, and incorporates formal comparison between experimental
and control arms. At the interim assessment, which takes place after approximately
half the total number of patients have been recruited, sample size re-estimation may be
incorporated if necessary. The methodology employs approximations to the normal
distribution since sample sizes are generally large enough. No software is detailed as
being available to identify designs; however, programming is noted as being possible
in SAS, and detail is provided to allow its implementation. Simulation is also required
to evaluate potential designs. The authors note that the design may be extended to
binary and ordinal outcome measures.

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

4.2.3

Multinomial outcome measure

Whitehead et al. (2009)

∙
∙
∙
∙

Two-stage, multinomial outcome
Formally powered statistical comparison between arms
Requires programming
Early termination for activity or lack of activity

Whitehead and colleagues outline a randomised controlled two-stage design with
normally distributed outcome measures, which may be extended to binary and ordinal
outcome measures. The design allows early termination for activity, and lack of
activity, and incorporates formal comparison between experimental and control arms.
At the interim assessment, which takes place after approximately half the total number
of patients have been recruited, sample size re-estimation may be incorporated if
necessary. The methodology employs approximations to the normal distribution since
sample sizes are generally large enough. No software is detailed as being available
to identify designs; however, programming is noted as being possible in SAS, and
detail is provided to allow its implementation. Simulation is also required to evaluate
potential designs.
Sun et al. (2009)

∙
∙
∙
∙

Two-stage, multinomial outcome
Formally powered statistical comparison between arms
Software noted as being available from author
Early termination for lack of activity

Sun and colleagues propose a randomised two-stage design based on Zee’s singlearm multi-stage design with multinomial outcome measure (Zee et al. 1999), adjusting
the rules such that a sufficiently high response rate or a sufficiently low early progressive disease rate should warrant further investigation of the treatment. Optimal
and minimax designs are proposed following the methodology of Simon (1989).
Differences in response and progressive disease rates between control and experimental arms are compared, and the authors note that the intention of the phase
II trial is to screen for potential efficacy as opposed to identifying statistically
significant differences. An extension is also proposed to the multi-arm selection
setting. Detail is given regarding how to implement the designs in practice, and
software is noted as being available by contacting the first author to allow identification of designs. The design recommends a treatment for further investigation
when the response rate is sufficiently high, or the early progressive disease rate is
sufficiently low. Early termination is permitted for lack of activity only. The authors

RANDOMISED DESIGNS FOR SINGLE EXPERIMENTAL THERAPIES

also note that the design may be extended to studies monitoring safety and efficacy
simultaneously.

4.2.4

Time-to-event outcome measure

No references identified.

4.2.5

Ratio of times to progression

No references identified.

4.3
4.3.1

Multi-stage designs
Binary outcome measure

No references identified.

4.3.2

Continuous outcome measure

Cronin et al. (1999)

∙
∙
∙
∙

Multi-stage, continuous outcome
Formally powered statistical comparison between arms
Standard software available for sample size
Early termination for activity or lack of activity

Cronin and colleagues propose a Bayesian design for monitoring of phase II trials.
The design incorporates both sceptical and indifferent priors at each of the interim
analyses, according to the hypothesis being tested. Early termination is permitted for
activity or lack of activity, and as such, priors differ at interim and final analysis.
Posterior distributions are updated at each analysis. When compared with frequentist
group-sequential methods, the proposed Bayesian methods performed at least as well
for the main purpose of detecting ineffective treatments early. The Bayesian method
was slowest to stop when the treatment had clear biological activity. The authors
note that the Bayesian method provides flexibility to make changes to outcome
measures, analyses and original trial plans at interim analyses without introducing
theoretical statistical complications. Standard software is available for sample size
calculation.

4.3.3

Multinomial outcome measure

No references identified.

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

4.3.4

Time-to-event outcome measure

No references identified.

4.3.5

Ratio of times to progression

No references identified.

4.4 Continuous monitoring designs
4.4.1

Binary outcome measure

No references identified.

4.4.2

Continuous outcome measure

No references identified.

4.4.3

Multinomial outcome measure

No references identified.

4.4.4

Time-to-event outcome measure

Thall et al. (2005)

∙
∙
∙
∙

Continuous monitoring, time-to-event outcome
Formally powered statistical comparison between arms
Programs available from authors
Early termination for activity or lack of activity

Thall and colleagues propose Bayesian continuous monitoring designs that incorporate three time-to-event outcomes (death, disease progression and serious adverse
event). Various amendments to the initial proposed single-arm continuous monitoring design assuming exponential distribution are proposed (Cheung and Thall
2002), including randomisation, frequent interval monitoring, alternative distribution
assumptions and incorporation of interval censoring for disease progression. The trial
may be stopped early for lack of activity or for activity. Simulations are performed
to assess the performance of the design. Programs are noted as being available from
the authors upon request.

4.4.5

Ratio of times to progression

No references identified.

RANDOMISED DESIGNS FOR SINGLE EXPERIMENTAL THERAPIES

4.5

Three-outcome designs

4.5.1

Binary outcome measure

Hong and Wang (2007)

∙
∙
∙
∙

Three-outcome design, binary outcome measure
Formally powered statistical comparison between arms
Programs noted as being available from authors
Early termination for lack of activity

Hong and Wang detail both a single-stage and a two-stage three-outcome design
which extend that of Sargent et al. (2001) (Chapter 3) to a randomised comparative
design. The region of uncertainty falls around the middle region between the null
hypothesis that the difference in response rates between the arms is zero and the
alternative hypothesis that the difference is delta. In the two-stage design the trial
may only be terminated at the end of the first stage for lack of activity. A SAS program
to identify the design is noted as being available on request from the authors.

4.5.2

Continuous outcome measure

No references identified.

4.5.3

Multinomial outcome measure

No references identified.

4.5.4

Time-to-event outcome measure

No references identified.

4.5.5

Ratio of times to progression

No references identified.

4.6
4.6.1

Phase II/III designs
Binary outcome measure

Storer (1990)

∙
∙
∙
∙

Phase II/III, binary outcome
No formal comparison with control in phase II
Standard software available for phase II, phase III requires programming
No early termination during phase II

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

Storer proposes a phase II/III design with the same binary outcome at both stages.
This corresponds to a single-arm phase II design (e.g. A’Hern 2001) embedded in a
randomised phase III trial (i.e. randomisation takes place in phase II but the design
and primary decision-making are based on a single-arm design). The phase II decision
criteria are based on the results of the experimental arm only, as opposed to comparing
activity between the experimental and control arms. Sample size calculations for the
phase II aspect may be performed using standard available software for one-stage
designs, based on numerical searching to satisfy given type I and II errors and null
and alternative hypothesis response rates. Standard approaches to phase III sample
size calculation are used, with formulae provided to incorporate an adjustment for
the phase II/III design. This design may be used as a basis for phase II/III designs
whereby any single-arm phase II design is embedded in a phase III trial, including
where the outcome measure at phase III differs to that at phase II.
The design described above uses the same outcome measure at phase II as it does
at phase III. Although this may be seen as seamless phase II/III approach, in effect
it reflects a phase III trial with an early interim analysis on the primary outcome
measure (albeit based on a single-arm design). In this setting, consideration should
be given to the most appropriate outcome measure to use for both the phase II and
phase III primary outcome. It is rare that efficacy in the phase III setting could be
claimed on the basis of a binary outcome; rather, a time-to-event outcome is usually
required in phase III trials.
Lachin and Younes (2007)

∙
∙
∙
∙

Phase II/III, binary outcome
Formally powered statistical comparison between arms
Requires programming
No early termination during phase II

Lachin and Younes outline a phase II/III design that incorporates different outcome measures at phases II and III (with phase II being a shorter term outcome
measure). Joint distributions for the phase II and III outcomes are calculated, and
the design operating characteristics and sample sizes are calculated via iteration and
numerical integration. An estimate of the correlation between the two outcome measures is required. The design preserves the type I and II error rates, and patients
randomised during phase II are included in the phase III analysis. Analysis of the
phase II outcome measure considers a formal comparison for lack of activity only (or
excessive toxicity). Software is not detailed as being available; therefore, this design
would require programming to allow implementation.
Chow and Tu (2008)

∙
∙

Phase II/III, binary outcome
Formally powered statistical comparison between arms

RANDOMISED DESIGNS FOR SINGLE EXPERIMENTAL THERAPIES

∙
∙

Requires programming
No early termination during phase II

Chow and Tu present sample size formulae for seamless adaptive phase II/III
designs where the outcome measures at each phase differ, but the outcome measure
distributions remain the same (e.g. binary outcome in phase II, binary outcome in
phase III). This design is based on two separate studies, with differing endpoints and
durations, which are then combined. Data from patients in the phase II trial are used
to predict the phase III endpoint, for those patients, rather than continuing to follow
patients to observe the phase III endpoint. These data are then combined with the
data from the phase III trial. The relationship between the outcome measures at each
phase is required to be known and well established. This is an essential component
due to the predictive nature of the design. The design will require programming to
enable implementation.

4.6.2

Continuous outcome measure

Liu and Pledger (2005)

∙
∙
∙
∙

Phase II/III, continuous outcome
Formally powered statistical comparison between arms
Requires programming
No early termination during phase II

Liu and Pledger detail a phase II/III design for a single experimental treatment compared to a control, as well as outlining a design in the dose-finding
context. In the single experimental treatment setting, the experimental treatment
is compared with the control treatment at the end of the phase II trial, based on
the short-term continuous outcome measure associated with the phase II trial. At
this stage, there is no break in recruitment during the analysis, and the sample
size for the phase III trial may be modified to allow estimation of the standard
deviation of the phase III outcome measure. Different phase II and III outcome
measures are used. At the end of the trial, the test statistics from the first and second stages (i.e. phases II and III) are combined. The treatment effect required to be
observed is the same for both short- and long-term outcome measures and needs to
be pre-specified, along with prior information on probability of success and standard deviation for each outcome measure. This information is used to generate the
operating characteristics of the design. Formulae are given which would need to
be implemented in order to identify the design. The design offers flexibility in that
the second-stage (phase III) sample size may be calculated based on updated data
from the first stage (phase II), and adaptation rules do not need to be specified
in advance.

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

Lachin and Younes (2007)

∙
∙
∙
∙

Phase II/III, continuous outcome
Formally powered statistical comparison between arms
Requires programming
No early termination during phase II

∙
∙
∙
∙

Phase II/III, continuous outcome
Formally powered statistical comparison between arms
Requires programming
No early termination in phase II

4.6.3

Multinomial outcome measure

No references identified.

RANDOMISED DESIGNS FOR SINGLE EXPERIMENTAL THERAPIES

4.6.4

Time-to-event outcome measure

Lachin and Younes (2007)

∙
∙
∙
∙

Phase II/III, time-to-event outcome
Formally powered statistical comparison between arms
Requires programming
No early termination during phase II

∙
∙
∙
∙

Phase II/III, time-to-event outcome
Formally powered statistical comparison between arms
Requires programming
No early termination in phase II

4.6.5

Ratio of times to progression

No references identified.

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

4.7 Randomised discontinuation designs
4.7.1

Binary outcome measure

Kopec et al. (1993)

∙
∙
∙
∙

Randomised discontinuation, binary outcome
Formally powered statistical comparison between arms
Requires programming (can incorporate standard software)
No early termination

Kopec et al. introduce the randomised discontinuation design. All eligible patients
are initially treated with the investigational treatment for a pre-defined period of
time. At this time, all patients are assessed for response to treatment. Treatment
‘responders’ are randomised to either continue with the investigational treatment or
to discontinue the investigational treatment (and instead receive a placebo or current
standard treatment). A formal comparison is made between the experimental and
control arms at the end of the second stage (i.e. after randomisation). Formulae for
the calculation of response proportions are provided and are based on the sample
size needed for the randomised phase to assess relative activity. The design would
therefore need programming. Analysis may also be adapted to incorporate data from
patients in the first stage, to adapt the response requirements for randomisation, for
example, to incorporate patients with stable disease or greater, as detailed by Rosner
et al. (2002). Alternatively, patients achieving response may continue with treatment,
those with progressive disease discontinue treatment and those with stable disease
are randomised (Stadler 2007). The current design, incorporating randomisation of
patients who are responding to treatment, may be more applicable to other disease
areas where life-threatening consequences of discontinuing treatment may be less
immediate, and there are fewer potential ethical implications associated with this.

4.7.2

Continuous outcome measure

No references identified.

4.7.3

Multinomial outcome measure

No references identified.

4.7.4

Time-to-event outcome measure

No references identified.

4.7.5

Ratio of times to progression

No references identified.

Treatment selection designs
Sarah Brown

The designs described within this chapter specifically address the question of treatment selection, that is, randomisation to multiple experimental treatment arms is
incorporated. It is, however, also possible to consider treatment selection using singlearm or randomised phase II designs described in Chapters 3 and 4. In this respect the
aim is to show that each experimental treatment has sufficient activity (and tolerability, if appropriate) before performing treatment selection. Treatment selection from
those experimental arms found to be sufficiently active (and tolerable if appropriate)
may then take place, for example, using selection designs such as those described
by Sargent and Goldberg (2001) or Simon et al. (1985) (see Section 5.2.1 for further
details). These designs select the most active treatment with a pre-specified probability of correct selection, according to the difference in activity observed between the
experimental arms. Such an approach, combining these selection designs with other
phase II designs, ensures that the treatments considered for selection have already
passed pre-specified minimum activity criteria (and possibly tolerability criteria),
prior to selection. Steinberg and Venzon provide an example of such an approach,
as described in Section 5.2.2 (Steinberg and Venzon 2002). The efficiency of such
an approach, as compared with the alternative treatment selection designs described
within this chapter, should be considered in further detail on a trial-specific basis.
The designs within this chapter are organised as follows. First, designs including
a control arm are described in Section 5.1, organised by design category and by
outcome measure distribution. Second, in Section 5.2, designs that do not include
a control arm are presented, again by design category and by outcome measure.
Treatment selection designs that incorporate both activity and toxicity are presented
separately in Section 6.4.
A Practical Guide to Designing Phase II Trials in Oncology, First Edition.
Sarah R. Brown, Walter M. Gregory, Chris Twelves and Julia Brown.
© 2014 John Wiley & Sons, Ltd. Published 2014 by John Wiley & Sons, Ltd.

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

5.1 Including a control arm
5.1.1

One-stage designs

5.1.1.1

Binary outcome measure

No references identified.
5.1.1.2

Continuous outcome measure

No references identified.
5.1.1.3

Multinomial outcome measure

Whitehead and Jaki (2009)

∙
∙
∙
∙

One-stage, multinomial outcome, control arm
Formal comparison with control for selection
Programs noted as being available from authors
No early termination

Whitehead and Jaki propose one- and two-stage designs for phase II trials based
on ordered category outcomes, when the aim of the trial is to select a single treatment
to take forward to phase III evaluation. The design is randomised to incorporate a
formal comparison with a control arm, and hypothesis testing is based on the Mann–
Whitney statistic. The treatment identified with the smallest p-value indicating a
treatment effect is selected as the treatment to take forward for further investigation.
Details of sample size and critical value calculation are provided, and R code is noted
as being available from the authors to allow implementation. Specification of the
worthwhile treatment effect and the small positive treatment effect that is not worth
further investigation are required to be specified.
5.1.1.4

Time-to-event outcome measure

No references identified.
5.1.1.5

Ratio of times to progression

No references identified.

5.1.2

Two-stage designs

5.1.2.1

Binary outcome measure

Jung (2008)

∙
∙

Two-stage, binary outcome, control arm
Formal comparison with control for selection

TREATMENT SELECTION DESIGNS

∙
∙

Programs noted as being available from author
Early termination for lack of activity

Jung proposes a randomised controlled extension to Simon’s optimal and minimax designs (Simon 1989), considering a binary outcome measure and incorporating
early termination for lack of activity. The experimental arms are compared with
the control arm at the end of stage 1 and treatments may be dropped for lack of
activity. More than one experimental arm may therefore be taken forward to stage
2. If no treatments show improved activity over the control arm at the end of stage
1 the trial may be terminated for lack of activity. At the end of stage 2, all arms
that pass the stage 2 cut-off boundaries compared to control are deemed worthy of
further investigation. The selection design is an extension to the design described
comparing a single experimental arm with a control. In the selection design the
family-wise error rate, the probability of erroneously accepting an inactive treatment, is controlled. Programs to identify designs are available upon request from
the author.
Jung and George (2009)

∙
∙
∙
∙

Two-stage, binary outcome, control arm
Formal comparison with control for selection
Requires minimal programming
Early termination for lack of activity

Jung and George propose methods of comparing treatment arms in a randomised
phase II trial, where the intention is either to select one treatment from many for
further evaluation or to determine whether a single treatment is worthy of evaluation
compared to a control. The phase II design is based on a k-armed trial (with or without a control arm for selection) with each arm designed for independent evaluation
following Simon’s two-stage design (Simon 1989), or similar, based on historical control data, that is, no comparison is made with the control arm at this stage. Different
designs (i.e. the same two-stage design but with different operating characteristics)
may be used for different arms in the independent evaluation if deemed necessary.
A treatment must be accepted via the independent evaluation before it can be considered for selection, at which point comparisons may be made with the control
arm. p-Values are calculated to represent the probability that the difference between
the arms being compared is at least some pre-defined minimal accepted difference,
given the actual difference observed. The outcome measure used to select the better
treatment is the same outcome measure used for evaluation of each arm independently, for example, tumour response. No software is detailed; however, detail is
given which should allow implementation, and sufficient examples are also provided.
The initial two-stage design can be calculated using software available for Simon’s
two-stage design.

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

5.1.2.2

Continuous outcome measure

Levy et al. (2006)

∙
∙
∙
∙

Two-stage, continuous outcome, control arm
No formal comparison with control for selection
Requires programming
No early termination; treatment selection at the end of stage 1

Levy et al. propose a randomised two-stage futility design incorporating treatment
selection at the end of the first stage. At the end of the first stage the ‘best’ treatment is
selected based on the treatment with the highest/lowest (‘best’) mean outcome, that is,
no comparison with control is made here. Sample size for the first stage is calculated
to give at least 80% probability of correct selection. Patients then continue to be
randomised between control and the selected treatment, and data from the first stage
is incorporated into the second-stage futility analysis, incorporating a bias correction.
The null hypothesis is that the selected treatment reduces the mean response by at
least x% compared to control; the alternative hypothesis is that the selected treatment
reduces the mean response by less than x% compared to control (reflecting a futility
design). Sample size and power calculation details are provided in appendices.
Shun et al. (2008)

∙
∙
∙
∙

Two-stage, continuous outcome, control arm
No formal comparison with control for treatment selection
Requires programming
No early termination at the end of stage 1

Shun et al. propose a phase II/III or two-stage treatment selection design where
a single treatment is selected from two at the end of the first stage. Randomisation
incorporates a control arm, with the intention of formal comparison at the end of the
second stage only, that is, no formal comparison for treatment selection. Treatment
selection is based on the experimental treatment with the highest/lowest (‘best’)
mean outcome. A normal approximation approach is proposed to avoid complex
numerical integration requirements. The design assumes that the treatment effects
of the experimental treatments are not the same. The practical approach to timing
of interim analysis addresses the need to perform this early in order to avoid type
I error inflation and the need to perform this late enough such that there is a high
probability of correctly selecting the better treatment. No software is noted as being
available; however, detail is provided to allow implementation and a detailed example
is given. The authors note that this design can be extended to binary and time-toevent outcome measures if the correlation between the final and interim test statistics
is known.

TREATMENT SELECTION DESIGNS

5.1.2.3

Multinomial outcome measure

Sun et al. (2009)

∙
∙
∙
∙

Two-stage, multinomial outcome, control arm
Formal comparison with control
Software noted as being available from author
Early termination for lack of activity; early treatment selection

Sun and colleagues propose a randomised two-stage design based on Zee’s singlearm multi-stage design with multinomial outcome measure (Zee et al. 1999), adjusting
the rules such that a sufficiently high response rate or a sufficiently low early progressive disease rate should warrant further investigation of a treatment. Optimal and
minimax designs are proposed following the methodology of Simon (1989), incorporating comparison with a control arm. Differences in response and progressive
disease rates between control and experimental arms are compared. The authors note
that the intention of the phase II trial is to screen for potential efficacy as opposed
to identifying statistically significant differences compared with control. Patients are
randomised between multiple experimental treatments and a control arm. At the end
of the first stage only those treatments that pass the stopping boundaries for both
response and progressive disease are continued to the second stage. If there is clear
evidence that one treatment is better than the other, selection may take place at the
end of the first stage. If, at the end of the second stage, there is no clear evidence
that one experimental treatment is better than the other both arms may be considered
for further evaluation. Detail is given regarding how to implement the designs in
practice, and software is noted as being available by contacting the first author to
allow identification of designs. The authors also note that the design may be extended
to studies monitoring safety and efficacy simultaneously.
Whitehead and Jaki (2009)

∙
∙
∙
∙

Two-stage, multinomial outcome, control arm
Formal comparison with control for selection
Programs noted as being available from authors
No early termination

Whitehead and Jaki propose one- and two-stage designs for phase II trials based
on ordered category outcomes, when the aim of the trial is to select a single treatment
to take forward to phase III evaluation. The design is randomised to incorporate a
formal comparison with a control arm, and hypothesis testing is based on the Mann–
Whitney statistic. In the two-stage design, treatment selection takes place at the end of
stage 1 whereby the treatment with the smallest p-value indicating a treatment effect is
selected as the treatment to take forward to stage 2. In stage 2, patients are randomised
between the selected treatment and control only. The final analysis at the end of stage

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

2 is based on all data available on patients in the control arm and the selected treatment
arm. Details of sample size and critical value calculation are provided, and R code
is noted as being available from the authors to allow implementation. Specification
of the worthwhile treatment effect and the small positive treatment effect that is not
worth further investigation are required to be specified.
5.1.2.4

Time-to-event outcome measure

No references identified.
5.1.2.5

Ratio of times to progression

No references identified.

5.1.3

Multi-stage designs

5.1.3.1

Binary outcome measure

No references identified.
5.1.3.2

Continuous outcome measure

Cheung (2009)

∙
∙
∙
∙

Multi-stage, continuous outcome, control arm
Formal comparison with control for treatment selection
Requires programming
Early treatment selection and early termination for lack of activity

Cheung describes an adaptive multi-arm, multi-stage selection design incorporating a control arm and considering a normally distributed outcome measure. Two
multi-stage procedures are proposed: an extension of the sequential probability ratio
test (SPRT) with a maximum sample size and a truncated sequential elimination
procedure (ELIM). The SPRT method allows early selection of a treatment when
there is evidence of increased activity compared to control, whereas the ELIM procedure also allows early termination of arms for lack of activity. The proposed
procedures are compared with single-arm trials and the ELIM procedure is recommended over these, incorporating sample size reassessment at interim analyses.
Cohort sizes between interim assessments may range from 1 to 10 with little impact
on the design’s operating characteristics. Sample size formulae are provided which
will require implementing in order to identify the trial design.
5.1.3.3

Multinomial outcome measure

No references identified.

TREATMENT SELECTION DESIGNS

5.1.3.4

Time-to-event outcome measure

No references identified.
5.1.3.5

Ratio of times to progression

No references identified.

5.1.4

Continuous monitoring designs

No references identified.

5.1.5

Decision-theoretic designs

No references identified.

5.1.6

Three-outcome designs

No references identified.

5.1.7

Phase II/III designs – same primary outcome measure at
phase II and phase III

The designs outlined within this section incorporate the same primary outcome
measure for phase II assessment as that used for phase III. Although this may be
seen as a seamless phase II/III approach, in effect it reflects a phase III trial with an
early interim analysis on the primary outcome measure. In this setting, consideration
should be given to the most appropriate outcome measure to use for both the phase II
and phase III primary outcome. It is rare that efficacy in the phase III setting could
be claimed on the basis of, for example, a binary outcome; rather, a time-to-event
outcome is usually required in phase III trials.
5.1.7.1

Binary outcome measure

Bauer et al. (1998)

∙
∙
∙
∙

Phase II/III, binary outcome, control arm
Formal comparison with control for treatment selection
Programs noted as being available from authors
Early termination for efficacy at the end of phase II

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

design according to various operating characteristics and the performance of different
designs. A program is detailed (the focus of the manuscript) to allow implementation,
which is noted as being available on request from the authors. At the end of the first
stage the stage 1 hypothesis is tested, generating a p-value p1. At the end of the second
stage the stage 2 hypothesis is tested using only data obtained from patients in stage
2, generating a p-value p2. The overall hypothesis is then tested combining p1 and
p2 using Fisher’s combination test (Fisher 1932). Application is given to phase II/
III, with treatment selection at the end of stage 1: if the p-value is significant that at
least one of the treatments is superior then the treatment with the ‘best’ outcome is
considered in phase III. The trial may also terminate early for efficacy at the end of
stage 1 if the p-value is significant at the stage 2 significance level.
Bauer and Kieser (1999)

∙
∙
∙
∙

Phase II/III, binary outcome, control arm
Formal comparison with control for treatment selection
Programs noted as being available from author
Early termination for efficacy at the end of phase II

Bauer and Kieser detail a design that incorporates formal comparison of each of
the experimental arms with the control at the end of phase II (as well as testing whether
any of the treatments are superior to control). The same primary outcome measure is
used in both phases II and III. A fixed sample size is used for phase II, however the
phase III sample size can be updated adaptively at the end of phase II. Stopping at the
end of phase II is permissible for either lack of efficacy or early evidence of efficacy.
The design also allows more than one treatment to be taken forward to phase III. At
the end of phase II the sample size may be re-estimated and the test statistics to use
at phase III are determined, according to the number of treatments taken forward and
the hypotheses to be tested. The decision criterion at the end of phase III is based on
Fisher’s combination test (Fisher 1932) whereby the p-values from both phases are
combined (as opposed to combining data from all patients). Simulation is required
as detailed in Bauer et al. (1998), as above. Examples are given in the dose-finding
setting and the authors note that the main advantage of this design is its flexibility and
its control of the family-wise error rate. The design is similar to that detailed above
(Bauer et al. 1998) with the exception that the current paper gives more detail relating
to multiple comparisons between experimental treatments and control arm. When
considering either of these two designs, it is advised that both papers be considered
together since the software detailed in Bauer et al., above, is required to identify the
design proposed here.
Stallard and Todd (2003)

∙
∙

Phase II/III, binary outcome, control arm
Formal comparison with control for treatment selection

TREATMENT SELECTION DESIGNS

∙
∙

Programs noted as being available from authors
Early termination for efficacy at the end of phase II

Stallard and Todd propose a design whereby patients from phase II are incorporated in the phase III analysis, and treatment selection at the end of phase II is based
on the treatment with the largest test statistic using efficient scores and Fisher’s information. A formal comparison is made between the selected treatment and control,
and the trial may be terminated early for lack of efficacy or superiority at this stage.
The type I error in the final phase III analysis is adjusted for the treatment selection
in phase II. Overall sample size and phase II sample size are computed according to
group-sequential phase III designs such as those described by Whitehead (1997). A
computer program is noted as being available from the authors to calculate power for
stopping boundaries, according to pre-specified group sizes. The authors note that
the design is useful when one treatment is likely to be much better than the others at
phase II, as opposed to taking multiple treatments to phase III. Consideration should
also be given to the timing of the first interim analysis (i.e. phase II assessment).
Too early and there is too little information, too late and there are too many patients
enrolled and thus potentially wasted resources.
Kelly et al. (2005)

∙
∙
∙
∙

Phase II/III, binary outcome, control arm
Formal comparison with control for treatment selection
Requires programming
Early termination for efficacy and lack of efficacy during phase II

Kelly and colleagues propose an adaptation to the design proposed by Stallard and
Todd (detailed above), such that more than one treatment may be selected at multiple
stages within the phase II part of the trial. Treatments are evaluated for selection
using Fisher’s information and an efficient score statistic which may be applied to
continuous, binary and failure time data. p-Values are calculated at each stage for
comparison of the best treatment with control. Only treatments within a pre-specified
margin of the efficient score statistic of the best treatment are continued to the next
stage, and all other treatments are dropped. Patients are randomised between control
and each of the treatments under investigation at each stage. The trial may stop for
efficacy or lack of efficacy at each stage. The example given is based on the use
of the triangular test described by Whitehead (1997), which uses expected Fisher’s
information to calculate operating characteristics.
Wang and Cui (2007)

∙
∙

Phase II/III, binary outcome, control arm
No formal comparison with control in phase II

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

∙
∙

Requires programming
No early termination during phase II

Wang and Cui outline a design whereby patients are randomised to each of
the experimental treatments under investigation and a control arm, using responseadaptive randomisation (the paper is written in the context of dose selection but
could be applied to treatment selection). The allocation ratios are calculated based on
distance conditional powers (i.e. the probability that the event rate for the treatment
under investigation is larger than some pre-specified fixed rate, based on the observed
data and the fact that some patients will not yet have had their outcome observed).
The treatment to which most patients have been randomised is deemed the most
efficacious at the end of the recruitment period. This selected treatment is then
formally compared with the control treatment, forming the phase III comparison.
This design uses binary outcome measures such as treatment response, for both the
phase II treatment selection and the phase III formal comparison; although it is noted
that continuous outcomes may be used. Simulation is required to investigate the
design parameters, with sample size calculated based on the phase III comparison.
The design may be implemented with the development of programs based on formulae
provided.
5.1.7.2

Continuous outcome measure

Bretz et al. (2006)

∙
∙
∙
∙

Phase II/III, continuous outcome, control arm
Formal comparison with control for treatment selection
Minimal programming required
Early termination for efficacy or lack of efficacy at the end of phase II

Bretz and colleagues outline a phase II/III design which allows treatment selection
at the interim assessment (i.e. at the end of phase II). The design allows data from
the first stage to be incorporated into the final analysis. Formal comparisons between
control and experimental treatments are performed at the end of each stage. Early
termination is permitted at the end of the first stage (i.e. at the end of phase II) for
lack of efficacy or for early evidence of efficacy. Also at this time, if the study is to
be continued to phase III, adaptations to the design of the trial may be made such as
sample size reassessment based on the data observed to date. Final analysis includes
data from both stages, with decision criteria based on a combination of test results
(i.e. using methods such as Fisher’s product test of the conditional error function).
The closure principle is incorporated, such that a hypothesis is only rejected if it
and all associated intersection hypotheses are also rejected. Sample size formulae are
given to allow calculation. The design may be extended to multiple stages, in which
case early termination during the phase II aspect may be incorporated.

TREATMENT SELECTION DESIGNS

Bauer et al. (1998)

∙
∙
∙
∙

Phase II/III, continuous outcome, control arm
Formal comparison with control for treatment selection
Programs noted as being available from authors
Early termination for efficacy at the end of phase II

Bauer and colleagues outline a simulation program for an adaptive two-stage
design with application to phase II/III and dose finding. Two outcomes may be considered, with one primary variable on which formal hypothesis testing is performed
and the other for which adaptations at the end of the first stage may be based on.
The outcomes may be binary or continuous, or a combination. The same primary
outcome measure is used at each analysis. Simulation is required to identify the best
design according to various operating characteristics and the performance of different
designs. A program is detailed (the focus of the manuscript) to allow implementation,
which is noted as being available on request from the authors. At the end of the first
stage the stage 1 hypothesis is tested, generating a p-value p1. At the end of the
second stage the stage 2 hypothesis is tested using only data obtained from patients in
stage 2, generating a p-value p2. The overall hypothesis is then tested combining p1
and p2 using Fisher’s combination test (Fisher 1932). Application is given to phase
II/III, with treatment selection at the end of stage 1: if the p-value is significant that
at least one of the treatments is superior then the treatment with the ‘best’ outcome
is considered in phase III. The trial may also terminate early for efficacy at the end
of stage 1 if the p-value is significant at the stage 2 significance level.
Bauer and Kieser (1999)

∙
∙
∙
∙

Phase II/III, continuous outcome, control arm
Formal comparison with control for treatment selection
Programs noted as being available from author
Early termination for efficacy at the end of phase II

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

(Fisher 1932) whereby the p-values from both phases are combined (as opposed to
combining data from all patients). Simulation is required as detailed in Bauer et al.
(1998), as above. Examples are given in the dose-finding setting and the authors
note that the main advantage of this design is its flexibility and its control of the
family-wise error rate. The design is similar to that detailed above (Bauer et al. 1998)
with the exception that the current paper gives more detail relating to the multiple
comparisons between experimental treatments and control arm. When considering
either of these two designs, it is advised that both papers be considered together since
the software detailed in Bauer et al., above, is required to identify the design proposed
here.
Stallard and Todd (2003)

∙
∙
∙
∙

Phase II/III, continuous outcome, control arm
Formal comparison with control for treatment selection
Requires programming
Early termination for efficacy and lack of efficacy during phase II

TREATMENT SELECTION DESIGNS

using Fisher’s information and an efficient score statistic which may be applied to
continuous, binary and failure time data. p-Values are calculated at each stage for
comparison of the best treatment with control. Only treatments within a pre-specified
margin of the efficient score statistic of the best treatment are continued to the next
stage, and all other treatments are dropped. Patients are randomised between control
and each of the treatments under investigation at each stage. The trial may stop for
efficacy or lack of efficacy at each stage. The example given is based on the use
of the triangular test described by Whitehead (1997), which uses expected Fisher’s
information to calculate operating characteristics.
Wang (2006)

∙
∙
∙
∙

Phase II/III, continuous outcome, control arm
Formal comparison with control for treatment selection
Requires programming
Early termination for efficacy at the end of phase II

Wang proposes an adaptive design with treatment selection at the end of phase
II. Patients are randomised between control and each of the experimental treatments
under investigation in phase II. The design controls the overall type I error and allows
the conditional error function of the phase III trial to depend on the data observed
during phase II. Maximum sample sizes are required to be specified and simulations
performed to evaluate expected sample size. The identification of the optimal design
requires detailed numerical integration. At the end of the first stage the treatment with
the largest test statistic is selected to take forward to phase III; however, the trial could
also be stopped at this point (i.e. at the end of phase II) for efficacy or lack of efficacy.
There is formal comparison between each of the experimental arms and the control
arm at the end of phase II, and as long as at least one experimental treatment has
sufficient activity, a treatment is selected for further testing in phase III (or selected
as being superior if significant enough). The design has been implemented in R and
formulae are given to allow this to be implemented in other software, therefore the
design would need programming.
Wang and Cui (2007)

∙
∙
∙
∙

Phase II/III, continuous outcome, control arm
No formal comparison with control in phase II
Requires programming
No early termination during phase II

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

on distance conditional powers (i.e. the probability that the treatment effect for the
treatment under investigation is larger than some pre-specified fixed value, based on
the observed data and the fact that some patients will not yet have had their outcome
observed). The treatment to which most patients have been randomised is deemed the
most efficacious at the end of the recruitment period. This selected treatment is then
formally compared with the control treatment, forming the phase III comparison.
This design as detailed uses binary outcome measures such as treatment response, for
both the phase II treatment selection and the phase III formal comparison, although it
is noted that continuous outcomes may be used. Simulation is required to investigate
the design parameters, with sample size calculated based on the phase III comparison.
The design may be implemented with the development of programs based on formulae
provided.
Shun et al. (2008)

∙
∙
∙
∙

Phase II/III, continuous outcome, control arm
No formal comparison with control for treatment selection
Requires programming
No early termination at the end of phase II

Shun et al. propose a phase II/III or two-stage treatment selection design where
a single treatment is selected from two at the end of the first stage. Randomisation
incorporates a control arm, with the intention of formal comparison at the end of the
second stage only, that is, no formal comparison for treatment selection. Treatment
selection is based on the experimental treatment with the highest/lowest (‘best’)
mean outcome. A normal approximation approach is proposed to avoid complex
numerical integration requirements. The design assumes that the treatment effects of
the experimental treatments are not the same. The practical approach to timing of
interim analysis addresses the need to perform this early in order to avoid type I error
inflation, and the need to perform this late enough such that there is a high probability
of correctly selecting the better treatment. No software is noted as being available;
however, detail is provided to allow implementation and a detailed example is given.
The authors note that this design can be extended to binary and time-to-event outcome
measures if the correlation between the final and interim test statistics is known.
5.1.7.3

Multinomial outcome measure

Whitehead and Jaki (2009)

∙
∙
∙
∙

Phase II/III, multinomial outcome, control arm
Formal comparison with control for selection
Programs noted as being available from authors
No early termination during phase II

TREATMENT SELECTION DESIGNS

Whitehead and Jaki propose one- and two-stage designs for phase II trials based
on ordered category outcomes, when the aim of the trial is to select a single treatment
to take forward to phase III evaluation. The authors note that the two-stage design
detailed may be applied to the phase II/III setting, although refinements to the design
may be required including the use of different outcome measures for treatment selection and final analysis. The design is randomised to incorporate a formal comparison
with a control arm, and hypothesis testing is based on the Mann–Whitney statistic.
In the phase II/III setting, treatment selection takes place at the end of stage 1, that
is, phase II, whereby the treatment with the smallest p-value indicating a treatment
effect is selected as the treatment to take forward to stage 2, that is, phase III. Early
termination for lack of activity is permitted at the end of phase II. During phase III,
patients are randomised between the selected treatment and control only. The final
analysis at the end of phase III is based on all data available on patients in the control arm and the selected treatment arm. Details of sample size and critical value
calculation are provided, and R code is noted as being available from the authors
to allow implementation. Specification of the worthwhile treatment effect and the
small positive treatment effect that is not worth further investigation are required to
be specified.
5.1.7.4

Time-to-event outcome measure

Bauer and Kieser (1999)

∙
∙
∙
∙

Phase II/III, time-to-event outcome, control arm
Formal comparison with control for treatment selection
Programs noted as being available from author
Early termination for efficacy at the end of phase II

Bauer and Kieser detail a design that incorporates formal comparison of each
of the experimental arms with the control at the end of phase II (as well as testing
whether any of the treatments are superior to control). The same primary outcome
measure is used in both phases II and III. A fixed sample size is used for phase II,
however the phase III sample size can be updated adaptively at the end of phase
II. Stopping at the end of phase II is permissible for either lack of efficacy or early
evidence of efficacy and is based on p-value calculation. The design also allows more
than one treatment to be taken forward to phase III. At the end of phase II the sample
size may be re-estimated and the test statistics to use at phase III are determined,
according to the number of treatments taken forward and the hypotheses to be tested.
The decision criterion at the end of phase III is based on Fisher’s combination test
(Fisher 1932) whereby the p-values from both phases are combined (as opposed to
combining data from all patients). Simulation is required as detailed in Bauer et al.
(1998). Examples are given in the dose-finding setting and the authors note that the
main advantage of this design is its flexibility and its control of the family-wise error
rate. When considering this design, it is advised that the detail provided by Bauer et al.

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

(1998) also be reviewed since this paper outlines the software required to identify the
design proposed here.
Stallard and Todd (2003)

∙
∙
∙
∙

Phase II/III, time-to-event outcome, control arm
Formal comparison with control for treatment selection
Programs noted as being available from authors
Early termination for efficacy at the end of phase II

∙
∙
∙
∙

Phase II/III, time-to-event outcome, control arm
Formal comparison with control for treatment selection
Requires programming
Early termination for efficacy and lack of efficacy during phase II

TREATMENT SELECTION DESIGNS

of the triangular test described by Whitehead (1997), which uses expected Fisher’s
information to calculate operating characteristics.
5.1.7.5

Ratio of times to progression

No references identified.

5.1.8

Phase II/III designs – different primary outcome
measures at phase II and phase III

The literature described within this section considers designs whereby different primary outcome measures are used for phase II and for phase III. Here the phase II
primary outcome measure should be selected based on the discussions provided in
Chapter 2, as this is not intended to be used for phase III decision-making.
5.1.8.1

Binary outcome measure

Todd and Stallard (2005)

∙
∙
∙
∙

Phase II/III, binary outcome, control arm
Formal comparison with control for treatment selection
Programs noted as being available from the authors
No early termination during phase II

Todd and Stallard describe a design where treatment selection occurs at the
first interim assessment (phase II) based on comparison of a short-term outcome
measure for each of the treatments versus control. Patients are randomised to
each of the experimental treatments and control during phase II, and then to the
selected treatment and the control during phase III. Phase III is carried out in a
group-sequential manner, with the experimental treatment compared to control in
terms of a longer term outcome measure. Selection at phase II is based on the
treatment with the largest test statistic, that is, there is formal comparison with
control but the study may only be terminated for lack of activity at this stage. The
trial protocol remains the same throughout the study; therefore, patients in phase II
can be incorporated in phase III. Required treatment effects (clinically significant),
treatment effects that are still desirable but not clinically significant and expected
correlation between phase II and III outcome measures are all required to identify
the complete phase II/III design. Formulae are given and programs are noted as
being available from the authors to calculate stopping boundaries.
5.1.8.2

Continuous outcome measure

Todd and Stallard (2005)

∙
∙

Phase II/III, continuous outcome, control arm
Formal comparison with control for treatment selection

100

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

∙
∙

Programs noted as being available from authors
No early termination during phase II

Todd and Stallard describe a design where treatment selection occurs at the
first interim assessment (phase II) based on comparison of a short-term outcome
measure for each of the treatments versus control. Patients are randomised to each
of the experimental treatments and control during phase II, and then to the selected
treatment and the control during phase III. Phase III is carried out in a groupsequential manner, with the experimental treatment compared to control in terms of
a longer term outcome measure. Selection at phase II is based on the treatment with
the largest test statistic, that is, there is formal comparison with control but the study
may only be terminated for lack of activity at this stage. The trial protocol remains
the same throughout the study; therefore, patients in phase II can be incorporated in
phase III. Required treatment effects (clinically significant), treatment effects that are
still desirable but not clinically significant and expected correlation between phase II
and III outcome measures are all required to identify the complete phase II/III design.
Formulae are given and programs are noted as being available from the authors to
calculate stopping boundaries.
Liu and Pledger (2005)

∙
∙
∙
∙

Phase II/III, continuous outcome, control arm
Formal comparison with control for treatment selection
Requires programming
No early termination during phase II

Liu and Pledger detail a phase II/III design in the dose-finding context where
patients are randomised to different doses and a placebo–control with the intention
of dose selection, as well as an adaptive two-stage phase II/III design where the
intention of phase II is to determine whether or not to continue to phase III, for a
single experimental treatment. Short-term continuous outcome measures are used at
the end of phase II to ‘prune’ the doses and to perform sample size adjustment for
the second stage (phase III), and long-term continuous outcome measures are used to
estimate the dose–response curve to calculate trend statistics for the analysis of the
phase III (and also at the end of phase II). Patients continue to be randomised to all
doses for a short period of phase III during the first analysis for dose selection at the
end of phase II (i.e. there is no break in recruitment for phase II analysis), at which
point more than one dose may be carried forward. The treatment effect required to be
observed is the same for both short- and long-term outcome measures and needs to be
pre-specified, along with prior information on probability of success for each dose,
standard deviation for each outcome measure, the time period between enrolment of
the first patient and the first analysis and the likely recruitment in this period. This
information is used to generate the operating characteristics of the design. Formulae
are given which would need to be implemented in order to identify the design. The

TREATMENT SELECTION DESIGNS

101

design offers flexibility in that the second stage (phase III) sample size may be
calculated based on updated data from the first stage (phase II), and adaptation rules
do not need to be specified in advance.
Shun et al. (2008)

∙
∙
∙
∙

Phase II/III, continuous outcome, control arm
No formal comparison with control for treatment selection
Requires programming
No early termination at the end of phase II

Shun et al. propose a phase II/III or two-stage treatment selection design where
a single treatment is selected from two at the end of the first stage (i.e. phase II).
Randomisation incorporates a control arm, with the intention of formal comparison at
the end of the second stage only, that is, no formal comparison for treatment selection.
Treatment selection is based on the experimental treatment with the highest/lowest
(‘best’) mean outcome. A normal approximation approach is proposed to avoid
complex numerical integration requirements. Where a different outcome measure is
used during phase II for treatment selection, the correlation between the phase II
and III outcome measures must be specified. The design assumes that the treatment
effects of the experimental treatments are not the same. The practical approach to
timing of interim analysis addresses the need to perform this early in order to avoid
type I error inflation, and the need to perform this late enough such that there is a
high probability of correctly selecting the better treatment. No software is noted as
being available; however, detail is provided to allow implementation and a detailed
example is given. The authors note that this design can be extended to binary and
time-to-event outcome measures if the correlation between the final and interim test
statistics is known.
5.1.8.3

Multinomial outcome measure

No references identified.
5.1.8.4

Time-to-event outcome measure

Royston et al. (2003)

∙
∙
∙
∙

Phase II/III, time-to-event outcome, control arm
Formal comparison with control for treatment selection
Some programming required before using standard software
No early termination during phase II

Royston and colleagues outline a multi-arm, two-stage design aimed at identifying treatments worthy of further consideration at the end of the first stage by

102

A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

comparing each treatment with a control arm using an intermediate outcome measure
of treatment activity. Only those treatments showing sufficient improvement in activity over control are continued to the second stage, at the end of which the treatments
are each compared with control using an outcome measure of primary interest (i.e.
different to that used at the end of the first stage). Data from both stages of the trial
are incorporated in the final analysis at the end of stage 2. The design may be seen
to reflect a seamless phase II/III design with treatment selection at the end of phase
II, allowing more than one treatment to be continued into phase III. In evaluating
the operating characteristics of the design, an estimate of the correlation between the
treatment effects on the intermediate and final outcome measures is required. The
authors propose an empirical approach to identifying this correlation using bootstrap
resampling of previous data sets, thus the design requires data of this type to be
available in order to allow implementation.
Todd and Stallard (2005)

∙
∙
∙
∙

Phase II/III, time-to-event outcome, control arm
Formal comparison with control for treatment selection
Programs noted as being available from authors
No early termination during phase II

Todd and Stallard describe a design where treatment selection occurs at the
first interim assessment (phase II) based on comparison of a short-term outcome
measure for each of the treatments versus control. Patients are randomised to
each of the experimental treatments and control during phase II, and then to the
selected treatment and the control during phase III. Phase III is carried out in a
group-sequential manner, with the experimental treatment compared to control in
terms of a longer term outcome measure. Selection at phase II is based on the
treatment with the largest test statistic, that is, there is formal comparison with
control but the study may only be terminated for lack of activity at this stage. The
trial protocol remains the same throughout the study therefore patients in phase II
can be incorporated in phase III. Required treatment effects (clinically significant),
treatment effects that are still desirable but not clinically significant and expected
correlation between phase II and III outcome measures are all required to identify
the complete phase II/III design. Formulae are given and programs are noted as
being available from the authors to calculate stopping boundaries.
5.1.8.5

Ratio of times to progression

No references identified.

5.1.9

Randomised discontinuation designs

No references identified.

TREATMENT SELECTION DESIGNS

5.2

103

Not including a control arm

5.2.1

One-stage designs

5.2.1.1

Binary outcome measure

Whitehead (1985)

∙
∙
∙

One-stage, binary outcome, no control arm
Requires programming
No early termination

Whitehead discusses a phase II selection design when there are a number of
treatments available for study, currently and expected in the near future, and a fixed
number of patients available over a period of time. Patients are randomised to the
treatments currently available and new treatments may be entered as they become
available. A given number of patients are recruited to each treatment and analysis takes
place when all treatments have been considered. The design, for which no software
is detailed but for which formulae are given to allow implementation, identifies the
optimal number of treatments (t) and patients per treatment (n) such that nt = total
number of patients available. The examples given consider trials including around
10 treatments, 6 patients per treatment, that is, 60 patients in total. Analysis takes
the form of an appropriate statistical model, fitting treatment as a covariate and
incorporating other prognostic variables as necessary. The treatment with the largest
estimated beneficial effect is then selected for further investigation in phase III. The
design allows modification such that more than one treatment may be taken forward
and such that cut-off boundaries may be incorporated to ensure a pre-specified level
of success. Any outcome measure distribution may be considered. No control patients
are incorporated and no assessment of risk of a false-negative result is considered.
It is noted that when only a few treatments are to be tested and when the number of
patients available is plentiful, this design may be less appropriate.
Simon et al. (1985)

∙
∙
∙

One-stage, binary outcome, no control arm
Software available
No early termination

Simon et al. detail a selection procedure based on correctly selecting the treatment
with the higher event rate when the difference in event rates is at least d, some prespecified amount. The design proposed will always select a treatment, even if the
differences are 25% intolerable, is taken
to be unacceptable and would lead to a recommendation of rejecting the dosing
combination. A tolerability rate of 90% is targeted with this regimen, that is, 10%
intolerability, a relative reduction of 50% compared to historical control data, deemed
clinically relevant.
After discussion with the clinicians it was agreed that the trial should be designed
with 90% power and 10% type I error rates for both activity and tolerability (i.e. 10%
chance that a dosing schedule is deemed active when in fact the response rate is <20%
and 10% chance a dosing schedule is deemed tolerable when in fact tolerability is
<75%). Implementing this design using software provided by Machin et al. (2008),
the corresponding design is as follows, for each arm separately.

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A PRACTICAL GUIDE TO DESIGNING PHASE II TRIALS IN ONCOLOGY

∙

Stage 1: Recruit 20 patients and follow up to observe response and tolerability.
If at least 4/20 patients achieve a response and at least 15/20 patients are able
to tolerate treatment, continue to stage 2. If there are three or fewer patients
who do not achieve a response, the dosing schedule is terminated early for lack
of activity; if there are 14 or fewer patients who are able to tolerate treatment,
the dosing schedule is terminated early for non-tolerability.

∙

Stage 2: Recruit a further 24 patients to a total of 44 in each arm. Follow up to
observe response and tolerability. If at least 13/44 patients achieve a response
and at least 36/44 patients are able to tolerate treatment, the dosing schedule is
deemed sufficiently active and tolerable. If there are 12 or fewer patients who
do not achieve a response, the dosing schedule is rejected for lack of activity;
if there are 35 or fewer patients who are able to tolerate treatment, the dosing
schedule is rejected for non-tolerability.

If only one of the dosing schedules successfully passes stage 2, this dosing
schedule will be selected for further investigation. In the case where both dosing
schedules successfully pass stage 2 and are deemed sufficiently active and tolerable to warrant further investigation, the selection criteria of Sargent and Goldberg
are applied, as previously described. It was agreed that the dosing schedule with
the higher PFS rate at 12 months should be selected only when the difference in
12-month PFS rates between the two arms is greater than 5%. A 25% PFS rate at
12 months with dose 1 and a 35% PFS rate with dose 2 were hypothesised based
on previously published data for drug D. With 44 patients per arm and observed
PFS rates of 25% and 35% in the dose 1 and 2 arms, respectively, the study would
correctly select the dose schedule with higher PFS rate with 81% probability (assuming that in 50% of ambiguous cases the correct treatment would be selected), based
on PFS alone. If the difference is less than 5%, alternative selection criteria may
be considered.
Patients will be randomised on a 1:1 basis to receive either DTD (dose 1) or DTD
(dose 2), with a maximum of 88 patients randomised (44 per arm).

Summary
This trial has been designed to select the best dosing schedule of a cytotoxic agent,
drug D, when given in combination with thalidomide and dexamethasone in patients
with relapsed refractory multiple myeloma. Sufficient activity and tolerability of
dose 1 and dose 2 are initially incorporated to select between the two doses, with
additional, secondary, selection only in the case where both dosing schedules are
found sufficiently active and tolerable. Schedule selection is then determined on the
basis of progression-free survival.
By taking into account therapeutic considerations associated with the drug,
the patient population and available historical control data and taking pragmatic
approaches to trial design, the specific design criteria associated with each of the

Primary aim dose
selection

Patients with
relapsed/
refractory
multiple myeloma

Rationale
behind
selection

Two dosing
schedules for
consideration

Two experimental
arms

Number of
experimental
treatment arms

Need to show
both sufficiently
active and
tolerable

Drug D is
expected to have
associated
cumulative
toxicities

Activity and
toxicity

Primary outcome
of interest

Non‐tolerability of
first two cycles is
an early indication
of future
tolerability issues

Response
recommended as
benchmark
outcome in this
setting

Drug D expected
to induce
response in
combination with
thalidomide and
dexamethasone

Dual binary –
response and
tolerability of at
least two cycles

Outcome
measure and
distribution

Subsequent phase
II trial in de novo
setting to include
randomisation to
control

One interim
assessment
deemed sufficient

Necessary to
include early
evaluation of
activity and
tolerability

Primary aim to
select most active
and tolerable
dose
Historical control
data on less
heavily pretreated
patients

Two stage

Design category

Randomisation to
experimental
arms only

Randomisation

Figure 11.1 Summary of decision process in designing phase II trial of drug D in multiple myeloma.

No validated
biomarkers
associated with
drug D or disease

Associated
cumulative
toxicities

Optimal dose
unclear

Intention to take
the combination
forward into study
of newly
diagnosed
patients

Proof of concept

No selection,
therapeutic
considerations
below

Selection from
flow diagram

Drug D is a
cytotoxic agent,
expected to
induce response

Primary aim of
trial

Therapeutic
considerations

Point of
consideration

Pragmatic
decision for
purpose of
example

Available software

Robust to
misspecification
of relationship
between activity
and tolerability

Two‐stage
activity and
tolerability with
secondary
schedule
selection

Practical
considerations

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eight elements featured in Figure 2.1 and described in Chapter 2 are summarised in
Figure 11.1. Working through the thought process and taking an iterative approach
to the design of the trial, with ongoing discussion between the clinician and statistician, we have designed a randomised, phase II selection trial, for the selection of the
optimal dose of drug D in combination with thalidomide and dexamethasone (DTD)
in patients with relapsed refractory multiple myeloma.

Targeted therapy for advanced
colorectal cancer
Matthew Seymour and Sarah Brown

Drug E is a monoclonal antibody therapy targeting a cell surface receptor, ‘Receptor
X’, that is known to be involved in cell growth from some cancers. Retrospective
studies have shown that Receptor X is strongly expressed in around 5% of colorectal
cancers, and it is now hypothesised that drug E, given in combination with current
standard chemotherapy, will improve efficacy for patients with X-positive advanced
colorectal cancer (aCRC) after failure of first-line chemotherapy. Receptor X is not
routinely measured in aCRC, so there are only limited historical data from previous
trials on which to base the expected control outcomes in this specific group. Phase
III clinical data are available for the efficacy of drug E in other solid tumours where
Receptor X is more commonly expressed, and it is hoped that a similar treatment
effect will occur in X-positive aCRC. Drug E has demonstrated an acceptable toxicity
profile in studies in other disease areas. A phase II trial of drug E in combination
with standard second-line chemotherapy, for Receptor-X-positive aCRC patients, is
proposed to determine whether to proceed to a larger phase III trial.

Stage 1 – Trial questions
Therapeutic considerations
Mechanism of action: Drug E is a monoclonal antibody directed against Receptor X.
It is believed to be primarily cytostatic as a single agent, but to act synergistically
A Practical Guide to Designing Phase II Trials in Oncology, First Edition.
Sarah R. Brown, Walter M. Gregory, Chris Twelves and Julia Brown.
© 2014 John Wiley & Sons, Ltd. Published 2014 by John Wiley & Sons, Ltd.

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with standard cytotoxic chemotherapy. In the setting of second-line treatment for
aCRC, classical cytotoxic chemotherapies are associated with low response rates due
to high levels of tumour resistance. It is, therefore, unrealistic to expect the addition
of drug E to chemotherapy to induce a high response rate. An assessment of disease
control, that is, progression-free survival (PFS), offers a more realistic measure of
the efficacy of this combination in this setting.
Aim of treatment: The ultimate aim of second-line treatment of patients with
advanced disease is to prolong overall survival. An early indicator of treatment
activity is the ability to prolong PFS, as discussed above.
Single or combination therapy: Drug E is given in combination with standard
second-line chemotherapy; to be relevant, therefore, the activity of the combination
therapy would need to be greater than that of chemotherapy alone.
Biomarkers: Drug E targets the specific cell surface receptor, Receptor X, so the
trial will be focused specifically on patients with X-positive tumours. On the basis of
evidence in other disease areas, the drug is not expected to improve clinical outcomes
in patients with X-negative tumours; these patients will, therefore, be excluded. There
are no validated biomarkers associated with aCRC which may provide an alternative
assessment of therapeutic activity.

Primary intention of trial
There is confirmed clinical evidence of efficacy of drug E in other solid tumours
(breast and gastrointestinal cancer). Owing to the small population of patients available, the current phase II trial is designed to deliver proof of concept in this targeted
population of patients and a go/no-go decision for a subsequent phase III trial. It is
important to consider the most efficient trial designs due to the rarity of the target
population, as well as the length of time required for a drug to move from phase II
to phase III then into routine clinical practice. A pragmatic approach to designing
trials in these settings is essential, to ensure reliable and robust trial design, whilst
maintaining an efficient and achievable drug development pathway.

Number of experimental treatment arms
There is only one experimental treatment under investigation, so a selection trial is
not required.

Primary outcome of interest
Drug E has shown an acceptable toxicity profile in multiple studies in other solid
tumours. The current combination in aCRC is expected to have only minimal additional toxicity or functional deficit. While toxicity will form a secondary endpoint of
the phase II trial, the primary outcome of interest is activity.

TARGETED THERAPY FOR ADVANCED COLORECTAL CANCER

187

Stage 2 – Design components
Outcome measure and distribution
In this heavily pre-treated population of patients, response rates to chemotherapy
are historically low and the addition of drug E is not expected to induce a high
response rate. The use of PFS as an indicator of activity may, therefore, be more
appropriate and clinically relevant. PFS is strongly correlated with overall survival in
patients with aCRC (Buyse et al. 2007), albeit predominantly in the setting of trials
of chemotherapeutic agents.
Chemotherapy plus drug E will be given for an initial period of 12 weeks, reflecting the initial treatment period of standard chemotherapy. After this point, patients
who have not progressed will continue to receive drug E until progression. Assessments of disease status via CT scan will be carried out approximately 12-weekly
until disease progression. Median PFS with standard chemotherapy is approximately
4.8 months in patients with advanced colorectal cancer following first-line therapy,
but data specifically for patients with X-positive colorectal cancer are limited (see
Section 12.4 for further details). This population of patients represents a rare subgroup of aCRC patients, so recruitment to the study will likely be slow. A binary
outcome dichotomising PFS at a single time point (i.e. the proportion of patients free
of disease progression at a specific time point) is worthy of consideration due to the
long period of recruitment and the requirement otherwise for all patients to be followed up to disease progression. If inclusion of interim assessments during the trial
is being considered, however, the requirement to wait for all patients to be followed
up to the specific time point of interest before this can take place may be impractical.
The use of all time-to-event data up to and including the specific time point may be
considered a possibility in this setting. Conversely, PFS will be limited and the use
of a time-to-event outcome (i.e. overall PFS) may be preferable since this incorporates all available information from the trial and will further facilitate design of the
potential phase III trial that would have a time-to-event primary outcome measure.

Randomisation
Drug E is to be given in combination with standard chemotherapy. It is important
that any possible additional activity observed with the combination can reasonably
be attributed to the addition of drug E. In the absence of reliable historical control
data for this population of patients with X-positive aCRC, randomisation should be
incorporated to provide robust and reliable results. Randomisation will increase the
number of patients required with what is a rare sub-type of a more common cancer, so
it is also important to minimise the sample size in other ways. Since the trial is being
designed to provide sufficient data to determine whether to progress to a phase III trial,
randomisation is essential despite its impact on patient numbers. A key consideration
is the incorporation, or otherwise, of formal statistical comparison with control. While
this is preferable for the purpose of making a stop/go decision, to sufficiently power
such a comparison with an acceptable type I error rate may be prohibitive within

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such a rare population. On the other hand, an additional consideration is the targeted
treatment effect with the experimental treatment. In studies adding drug E to standard
chemotherapy in other disease areas, hazard ratios of between 0.5 and 0.7 have been
observed. When such large treatment effects are realistic, it may be feasible to perform
formal statistical comparisons between experimental and control arms, with limited
sample sizes.
Randomisation will, therefore, be incorporated, and the feasibility of including
a formally powered comparison with a control will be considered, with regard to
impact on sample size. Should drug E show a sufficient level of activity, a subsequent
randomised phase III trial with multiple interim assessments for lack of efficacy is
envisaged.

Design category
Especially where historical data may be unreliable it is important to consider multiple
scenarios when choosing the statistical design, to assess how robust each design is if
outcomes in either treatment arm are not as expected. For example, if activity in the
control arm is uncertain, how well do the different trial designs cope with an underor over-estimation of this activity?
Rejected designs:
i. Decision-theoretic approaches to trial design incorporate information on number of patients to be treated in future phase III trials, number of patients
potentially benefitting from future treatment and costs of treatment. In this
particular setting, the costs associated with the current treatment are expected
to change in the near future due to patent expiry. The data are, therefore, not
reliable for the purpose of a decision-theoretic design and this design was
deemed inappropriate.
ii. Randomised discontinuation designs were also rejected, on the basis that the
initial assessment of treatment activity is carried out on completion of the first
block of combination treatment, after which treatment is with single agent drug
E only. Although it may be possible for all patients to receive initial treatment
with drug E plus chemotherapy, to randomise patients free of progression
at 12 weeks to drug E versus no treatment is not the central question here.
Rather, the trial is designed to address the treatment schedule as a whole, that
is, initial combination therapy followed by single-agent maintenance therapy,
compared with chemotherapy alone, so a randomisation discontinuation design
was rejected.
iii. Due to the rarity of the subgroup of patients considered in this trial, and the
potential subsequent phase III trial, seamless phase II/III designs were deemed
inappropriate given the uncertainty regarding feasibility of recruiting large
numbers of patients.
iv. Studies in other solid tumours have shown large treatment effects, with hazard ratios in the region of 0.5–0.7 with the addition of drug E to standard

TARGETED THERAPY FOR ADVANCED COLORECTAL CANCER

189

chemotherapy. With the addition of this monoclonal antibody to current
standard chemotherapy, there is no reason to expect that toxicity will be
reduced (although neither is it expected that significant additional toxicities
will emerge), and the combination therapy will ultimately be more costly than
standard chemotherapy alone. A three-outcome design which enables alternative outcome measures such as toxicity and cost to be considered in the event
that the treatment effect is inconclusive (i.e. it lies within a ‘grey area’ between
declaring the treatment worthy of further investigation and not worthy of further investigation) is not appropriate here since we do not expect either of these
measures to be reduced with the use of drug E.
v. As previously noted, the proportion of aCRC patients with X-positive disease
is low; therefore, recruitment is expected to be relatively slow. The ability
to build in early stopping boundaries for lack of activity is beneficial in this
setting due to the potentially prolonged period of recruitment. On this basis
two-stage designs were felt preferable to one-stage designs that do not incorporate formal interim assessment and the opportunity for early cessation. The
use of a multi-stage design, or a continuous monitoring design, was considered but a single interim assessment was considered sufficient provided
recruitment could continue during the stage 1 analysis as the eligible patient
population is small and it is important not to ‘lose’ potential patients due to a halt
in recruitment.
Candidate designs: Two-stage designs were considered as potential designs for
the trial.

Possible designs
We have determined that the phase II trial will be a randomised trial, addressing both
the proof of concept of drug E in combination with standard chemotherapy and the
decision to proceed or not to phase III, on the basis of activity alone. This will be
assessed using the time-to-event outcome measure of PFS, either incorporating all
available data on PFS or enabling all available data up to and including a specific
time point to be incorporated. Thus we consider designs listed under time-to-event
outcome measures only. A two-stage statistical design will be used. Inclusion of
randomisation for the purpose of formally powered statistical comparison will be
addressed by taking a pragmatic approach to the necessary sample size in the context
of the target population being small but the potential treatment effect large. Singlearm designs which enable randomisation for the purpose of calibration only, as well
as randomised designs incorporating formally powered comparison, are therefore
considered. Designs are identified from Chapter 3, single-arm trial designs that are
adapted to include a randomised reference arm, or from Chapter 4.
Reviewing the available designs in Chapters 3 and 4 which fit these design
parameters, the following designs may be considered for this trial. Discussion as to
selecting between these specific designs is given in the next section.

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From Chapter 3
i. Case and Morgan (2003)
ii. Litwin et al. (2007)
Although there are no two-stage designs listed in Chapter 4 with time-to-event endpoints, the principles of, for example, Herson and Carter (1986) or Buyse (2000) may
be incorporated into the designs listed above, to assess the credibility of the outcome
in the experimental arm. Alternatively, the one-stage designs from Chapter 4 noted
below may be considered, with an adaptation to incorporate an interim assessment
for lack of activity:
iii. Stone et al. (2007b) and Simon et al. (2001)
iv. Chen and Beckman (2009)

Stage 3 – Practicalities
Practical considerations for selecting between designs
We now consider each of the above designs in turn.
i. The design proposed by Case and Morgan incorporates a time-to-event outcome measure whereby all information available at the time of the interim
analysis is included. This is achieved by identifying a specific time point of
interest at which the probability of PFS is assessed, in other words, a binary
outcome derived from the time-to-event outcome incorporating all available
data, including those patients with follow-up to less than the time point of
interest. This design does not require a halt to recruitment. Standard programs
are available for this design. Although a control arm may be included for the
purpose of calibration, this does not power the study for formal comparison of
the arms.
ii. The design of Litwin et al. is based on a time-to-event outcome measure at two
specific time points, that is, a binary outcome. This design does not incorporate
data for patients who have not yet been followed up to the specific time point
of interest at the interim assessment, and is therefore not considered further.
iii. Stone and colleagues describe a phase II design which is formally powered
to compare the experimental arm with the control arm, using relaxed type
I errors and potentially targeting large treatment effects. This reflects the
designs described by Simon in the setting of time-to-event outcomes, which
are described by the authors as ‘phase 2.5 screening’ designs, due to the
use of phase III-type designs but with type I error rates typically associated
with phase II trials (Simon et al. 2001). By incorporating a formally powered
statistical comparison with the control arm, the sample size of the trial will
inevitably increase. This should, however, be weighed against the reliability of

TARGETED THERAPY FOR ADVANCED COLORECTAL CANCER

191

the decision-making criteria and compared with that for the non-comparative
phase II design described in (i) above. Standard software is available for this
design.
iv. Chen and Beckman describe an approach to a randomised phase II trial design
that incorporates the ratio of sample sizes between phases II and III. Optimal
type I and II errors for the design are identified by means of an efficiency
score function. Formal comparison with the control arm is incorporated. The
design considers cost efficiency of the phase II and III trials based on the
ratio of sample sizes between phases II and III and the a priori probability of
success of the investigational treatment, to determine the sample size for phase
II. Sufficient detail is provided within the paper to allow implementation and
an R program is provided to identify optimal designs. At this stage, however,
the design of the potential phase III trial is unclear, since the phase II study
is designed in part to provide data on feasibility of recruitment with such a
rare subgroup of patients. The design of Chen and Beckman is, therefore, not
considered further.
To distinguish between the designs incorporating no formal comparison (Case
and Morgan 2003) versus formal comparison (Stone et al. 2007b), we consider below
the required sample sizes, bearing in mind the need to include an interim assessment
for lack of activity using the design of Stone et al.

Proposed trial design
The primary assessment of activity is based on PFS. The trial is designed for
patients with X-positive aCRC after failure of first-line chemotherapy. It is anticipated that approximately 30% of patients will have progressed on first-line therapy;
for these patients the estimated median PFS with standard second-line chemotherapy is 2.6 months (Sobrero et al. 2008). The remaining 70% of patients are
expected to have progressed during a treatment break, or on intermittent therapy,
with first-line chemotherapy; the estimated median PFS for these patients treated
with standard ‘re-challenge’ chemotherapy is 5.7 months (Adams et al. 2011). It is
acknowledged that the standard chemotherapy may, therefore, differ between these
two groups of patients. The expected median PFS of patients after first-line therapy in the current trial is approximately 4.8 months since we have no evidence
that Receptor X status is prognostic of outcome. In other disease areas, a reduction in hazard rate for PFS of 30–50% has been observed with the addition of
drug E to chemotherapy. In the current setting, a hazard ratio of 0.6 is targeted
(i.e. a reduction in hazard rate of 40%) with the addition of drug E to standard
chemotherapy. This corresponds to a targeted median PFS of 8 months in the experimental arm.
The design of Case and Morgan requires a specific time point at which to assess
the progression-free probability; we select the 24-week time point. Corresponding

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expected PFS probabilities at 24 weeks (5.5 months) post-randomisation are 45.2% in
the control arm (i.e. a probability of progression that would not be of further interest)
and 62.1% in the experimental arm (i.e. a probability of progression worthy of further
investigation).
We assume that patients are to be recruited over no more than a 3-year period
as more protracted recruitment risks loss of engagement from investigators and the
potential that the clinical question behind the trial will have changed if other new
treatments have become available. Power of 80% is selected to detect the targeted
treatment effect, with a 10% one-sided type I error for incorrectly declaring the
addition of drug E to standard chemotherapy worthy of further investigation.
Under the design of Case and Morgan we would require 51 patients in the experimental arm, with an interim analysis taking place after 23 patients are recruited,
not accounting for dropout. This is based on minimising the expected duration of
accrual under the null hypothesis (Case and Morgan 2003). In order to incorporate
randomisation to a reference arm a 1:1 randomisation would simply double the sample size. Alternatively, an imbalanced randomisation such as 2:1 in favour of the
experimental arm may be favoured in this setting where the specific population of
patients is rare. This will provide sufficient data in the experimental arm whilst also
guarding against selection bias. It retains a reference arm against which the control
arm assumptions may be informally compared, but the design is not powered for
formal statistical comparison between the arms. In this particular example, including a 2:1 randomisation between standard chemotherapy plus drug E and standard
chemotherapy alone without formal statistical comparison, a total of up to 77 patients
will be recruited (assuming successfully passing stage 1; chemotherapy plus drug E
n = 51, chemotherapy alone n = 26).
Under the design of Stone et al., we would require 40 patients per arm, that is, a
total of 80 patients, assuming all patients are followed up until disease progression
and for a minimum of 6 months. An interim assessment for lack of activity, based
on the design of Gehan (1961), would be incorporated to enable early termination of
the trial in the event that the PFS probability at 24 weeks post-randomisation is not
sufficiently large enough in the experimental arm, to warrant continuation.
Comparing the two designs, we can see that the inclusion of formal comparison
between the arms increases the required sample size only marginally in this setting. This is because the design of Stone et al. considers all the time-to-event data
through the 3 years of recruitment and additional follow-up, whereas the design of
Case and Morgan, although taking into account the time-to-event data prior to the
24-week time point, focuses on the survival probabilities at 24 weeks. The inclusion of the additional data under the design of Stone et al. makes this a feasible
approach in this particular setting with a long recruitment period and a large targeted treatment effect. Additionally, the inclusion of a formally powered statistical
comparison between treatment arms is more robust to uncertainty in the estimation
of activity of the control arm, at the design stage. This trial would therefore require
approximately 1600 patients to be screened over 3 years to identify 80 patients with
X-positive aCRC.

Targeted, rare
population

Patients with
Receptor-Xpositive
advanced
colorectal cancer
requiring
second-line
chemotherapy

Rationale
behind
selection

Subsequent
study would
formally
compare with
standard
chemotherapy

Only one
experimental
treatment for
consideration

One
experimental
arm

Number of
experimental
treatment arms

Expected to have
minimal toxicity
/functional
deficit

Drug E has an
acceptable
toxicity profile in
other disease
areas

Activity

Primary
outcome of
interest

Patients receive
experimental
treatment until
disease
progression
therefore would
be followed up

Heavily pretreated
population,
therefore high
response rates
unrealistic

The addition of
drug E to
standard
chemotherapy
aims to delay
disease
progression

Time-to-event –
progression-free
survival

Outcome
measure and
distribution

Require interim
assessment for
lack of activity

Rare disease
subgroup;
pragmatic
approach to trial
design needed
Large treatment
effect targeted,
therefore formal
comparison may
not be
prohibitive

Small population
of patients, may
be difficult to
recruit

Two-stage

Design category

Drug E given in
combination
with standard
chemotherapy

Randomisation
to a control arm
with OR without
formal
comparison

Randomisation

Enable formal
comparison –
more robust

Allows
incorporation of
all progression
-free survival
data

Software
available to
implement

Formal
comparison with
control, with
interim
assessment

Practical
considerations

Figure 12.1 Summary of decision process in designing phase II trial of drug E in Receptor-X-positive advanced colorectal cancer.

Given with
standard
chemotherapy
may delay
disease
progression

Drug E is a
monoclonal
antibody
directed against
Receptor-X

Proof of concept
and go/no-go
decision for
phase III

No selection,
therapeutic
considerations
below

Selection
from flow
diagram

Proof of concept
data available in
other solid
tumours only

Primary aim of
trial

Therapeutic
considerations

Point of
consideration

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Summary
This trial has been designed to assess the activity of the addition of a monoclonal
antibody, drug E, to standard chemotherapy in patients with Receptor-X-positive
aCRC. By taking into account therapeutic considerations associated with the drug, the
rare patient population and mechanistic considerations associated with appropriate
outcome measures in aCRC, we addressed the trial-specific design requirements
through each of the three stages featured in Figure 2.1 and described in Chapter 2,
as summarised in Figure 12.1. Working through the thought process with ongoing
discussion between the clinician and statistician, we have designed a randomised,
controlled, two-stage trial, with PFS as the primary phase II outcome measure for
the assessment of chemotherapy plus drug E in Receptor-X-positive aCRC patients.
The trial is designed to provide both proof of concept data and a go/no-go decision
regarding whether or not to proceed to a larger randomised phase III trial.

Phase II oncology trials:
Perspective from industry
Anthony Rossini, Steven Green and William Mietlowski

13.1 Introduction
In oncology clinical development, phase II has the widest range of possible goals
which can be addressed at this stage. In contrast, there is general agreement for what
is to be done at phase I and phase III. Phase I generates the initial data used to select
a dose which can be used relatively safely in a larger population. Likewise, phase
III studies aim to establish evidence justifying efficacy and safety enabling health
authority approval. Generally, these designs focus on clinically relevant survival and
event-time endpoints. Phase II trials, on the other hand, have the simple but ill-defined
mission of providing evidence for one or more of the many possible strategic paths
between these two phases. Specifically, the phase II programme must bridge between
the current knowledge about the initially established dosing regimen and the phase III
design to support registration. There are many possible paths, representing the many
approaches to learning about how to use a compound to treat cancer. The diversity
of clinical development paths can also be deduced from the range of clinical trial
designs described in this book. This chapter will focus on selecting phase II designs
originating in response to strategies embodied in a commercially oriented clinical
development plan (CDP).
Commercially sponsored trials are a component of a pre-specified, evolving,
comprehensive CDP. A CDP can be formally thought of as a document which frames
the development of a compound in terms of medical indications, staging of activities
A Practical Guide to Designing Phase II Trials in Oncology, First Edition.
Sarah R. Brown, Walter M. Gregory, Chris Twelves and Julia Brown.
© 2014 John Wiley & Sons, Ltd. Published 2014 by John Wiley & Sons, Ltd.

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and collection of data for justifying registration across possible indications. This
contains justification for components which the development team considers essential
to develop the compound. The choice of trial designs should address the CDP’s
objectives, conditional on previous results. The goal of the CDP is to provide a
roadmap of activities to efficiently either deliver a commercially viable product or
terminate development early for futility and/or safety issues. A commercially viable
product requires both regulatory approval and agreement by payers to reimburse.
The selection process described in this chapter takes into account pharmaceutical
drug development challenges and drivers. These frame the constraints and requirements which inform the selection of the phase II design(s). The source for these
challenges arise both internally and externally and relate to both scientific and operational considerations. Internal clinical development decisions which impact phase
II include timing and prioritisation of the compound in relation to other compounds
in the portfolio. External clinical constraints and drivers include current medical
practice, payer approaches and competition from external compounds. Constraints
include both financial resources and shared internal specialised employee skills which
are in limited supply and required for more sophisticated designs. Some parts of this
chapter are forward looking and represent practices which are not yet incorporated.
Other parts are retrospective and may be suboptimal or obsolete due to recent statistical, clinical or regulatory landscape changes. This chapter just reflects a snapshot
in time of current thinking.
Multiple options often exist for clinical development strategies at the planning
stage for the phase II programme, with acceleration and hesitation pressure coming
from both the development team and the external environment. The selection of one
or more strategies in the face of uncertainty informs the choice of phase II design(s)
to be implemented. The range of strategic goals that are addressed in this chapter
consists of those for potential registration, establishing exploratory activity, regimen
selection, prediction of phase III success, safety trials and prospective identification
of targeted populations. We next describe some of the commercial challenges and
drivers before discussing strategic considerations and how they can inform study
design selection.

13.2 Commercial challenges, drivers
and considerations
The environment for commercial clinical drug development can change frequently,
making fixed as well as long-term planning difficult. New information arises regarding science, competitors, regulators and payer organisation; payer organisation can
cause an extreme change in plans, from rapid acceleration to a complete halt of the
programme. In addition, corporate philosophy and goals, as well as organisational
structure, can also impact a development programme’s strategy.
Competition, both internal and external, is a difficult factor to manage. Competition can take the form of internal competition between indications for a compound’s

PERSPECTIVE FROM INDUSTRY

197

resources, as well as between compounds which address the same family of indications. The CDP should outline how to address this.
The approach in this chapter naturally emphasises strategic goals based on commercial experience. These strategic goals reflect both common, clinical and scientific
goals and relevant corporate financial opportunities and challenges, since maintaining
positive cash flow, and the extent of that income source, will dictate potential opportunities and risks. For any publicly traded company, the value of the investigational
portfolio is intrinsically incorporated into the value of the stock price. A failed phase
III trial can strongly influence the stock price of a company if this compound reflects
a sizable portion of the stock price as well as an erosion of confidence in the company
to register drugs. Decisions which benefit the company are at the level of the clinical
trial, such as minimising patients who are exposed to toxic drugs via careful sample
size determination and interim analyses. Other decisions at the strategic level, including selection of drugs with most appropriate benefit/risk balance, and the efficient
development of viable therapies also benefit both patients and society as a whole.
While this could be done formally using a decision-theoretic framework, it is often
informally managed.

13.3 Selecting designs by strategy
The CDP provides guidance in terms of overall goals and approaches for clinical
development. Since it has a strategic focus for approaching clinical development,
a selection of trial designs based on strategic deliverables is simpler for teams to
use. We first give some examples of overall programme-level strategies that could
be under consideration, before moving forward with how a few common phase II
strategies are addressed.
Overall programme strategies are described differently from, and yet contain,
the phase II strategies which are being considered. For example, one increasingly popular development strategy is to target a rare but well-characterised
oncological indication, register the compound for treatment in that setting and then
construct a series of interrelated development programmes to expand into different
indications. These expanded indications are selected by considering the targets which
represent a component of the tumour, unlike the original indication where the target is found more homogenously across the whole tumour. Another strategy is to
leverage chemical synergies and initially target a medium-sized indication based on
initial pre-clinical and phase I results, combined with how they may relate to existing
medical practice and needs. Other common strategies include pairing new treatments
with existing ones for combination therapies, as well as including in the initial plans
a focus on setting up a possible diagnostic/compound combination.
Phase II studies address the middle stage of these strategies. For each example
given above, multiple questions could be addressed depending on the specific tactical
implementation of the global CDP strategy. The rest of this section focuses on the
phase II-specific strategic aspects.

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13.3.1

Basic strategies addressed by phase II studies

The summary within Table 13.1 illustrates some examples of matching trial design
options to development strategies. For each strategy, multiple phase II designs are
observed to have been employed, and some of these designs can be seen to have
addressed multiple strategic objectives. This table is just a historical view; proper
due diligence requires searching the literature for improvements and newer designs
which may include any of those listed within Chapters 3–7, understanding available
data in the specific setting and the current state of regulatory requirements and payer
opinions. Based on an internal review of phase II experiences, we have identified six
strategic goals that have occurred with high frequency, specifically:
1. Determination of activity for registration
2. Determine exploratory activity
3. Selection of regimen (single and combination agents)
4. Prediction of phase III success
5. Safety characterisation
6. Prospective identification of target populations
A clinical development programme can have multiple phase II trials, sometimes
answering the same strategic question on a different topic (different safety foci,
different subgroups to characterise). Alternatively, a single phase II trial can address
multiple goals. We now cover each strategy and describe considerations as well as
some of the trial design features which are of increasing importance for each particular
strategy.

13.3.2

Potential registration

The first strategic goal discussed is the accommodation of possible registration based
on strong positive early results. This could be considered a feasible strategic goal
based on pre-clinical data, phase I study results and the overall scientific and medical
rationale for development. The considerations in this section are primarily applicable
to situations when conditional or accelerated approval is based solely on phase
II or earlier trial data. Although this section primarily relates to trials designed for
registration, it also applies to registration from trials in which overwhelming evidence
of efficacy was observed although not planned for registration. Registration trials
designed to meet the usual requirement of ‘an adequate and well-controlled study’
are out of scope for this section; for example, we do not cover intended phase III
trials powered to detect clinically meaningful differences at the one-sided 2.5% level
of significance.
13.3.2.1

Regulatory considerations

This strategic goal intersects regulatory and statistical considerations. It is critical
to remember that the regulatory environment is constantly changing and requires

Determine best regimen
(possibly a combination)
for subsequent randomised
controlled trial

Two-stage design, single arm
(Simon and Bayesian based)
Randomised phase II
Single-arm multinomial
Randomised two-stage multinomial
Randomised discontinuation
Growth modulation index (GMI)
(intra-patient PFS)
Randomised Simon two stage
Randomised selection (Bayesian
and frequentist) with and without
control group
Randomised (combination add-on
vs. SOC)
Randomised modified factorial (no
control group)
Randomised factorial (add-on with
SOC)

Determine biological activity
using a quick, intermediate
endpoint

Several potential regimens
(doses, schedules,
formulations, etc.) for
possible combination
development

Single-stage and two-stage
single-arm design
Randomised phase II

Determine potential for phase
II-based registration
(endpoint to confer clinical
benefit)

Regimen likely to be active in
an unmet medical need
without approved or
available therapy, no major
safety issues
Phase I data available, dose
known but activity in
indication to be shown, not
suitable for phase II
registration, no major
safety issues

Major designs

Main goal of phase II study

Known at phase II planning

Table 13.1 Roadmap for phase II: strategic situations.

(continued)

Overall tumour response rate
(CR/PR)
PFS, tumour markers, imaging
‘wet’ biomarker
Multinomial (CR/PR, SD, early
PD)
Duration of SD
GMI response rate (GMI ≥ 1.33)
Overall tumour response rate
PFS
Possibly pharmacodynamics

Overall tumour response rate
(e.g. durable CR)
PFS, OS (overwhelming
evidence of efficacy)

Major endpoints (most common)

Determine likelihood of
success in phase III using
suitable endpoint and
patient population in phase
II study
Better characterise safety
profile, especially major
safety issue(s), include
safety as co-primary
endpoint
Determine appropriate patient
subpopulation for phase III
trial

Regimen, indication known,
important to reduce risk in
phase III; not suitable for
phase II registration, no
major safety issues
Potential major safety
issue(s) representing
possible ‘no/go’

Safety and efficacy (usually
overall tumour response rate)

Extension of two-stage designs
where safety and efficacy are
co-primary endpoints
Seamless phase I/II
Randomised phase II
Adaptive targeted two-stage
design
‘Basket of indication’ design
Stratification and enrichment
designs

Overall tumour response rate
PFS
Pharmacodynamics

Phase III endpoints PFS, OS,
response rates
(haematological
malignancies)

Major endpoints (most common)

Randomised phase II
(Bayesian-based predictive
probability of success)

Major designs

Entries given in Bold, used in Novartis trials, italics, used in other pharma, bold italics, academic trials or literature.

Regimen, indication known
but not suitable for phase II
registration, no major
safety issues,
heterogeneous populations
defined by molecular
markers, histology, prior
treatment paradigms

Main goal of phase II study

Known at phase II planning

Table 13.1 (Continued)

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regular review during the overall clinical development process. For phase II trials
designed for registration, it is even more critical to review the most current regulatory
guidance and recent relevant regulatory events, and regulatory affairs specialists need
to be involved in design discussions.
Although regulatory approval based solely on phase II data still remains possible
in both the United States and European Union (EU), its applicability may now be
confined to indications for which there is no approved or available therapy and will
likely require demonstration of clear clinical benefit and efficacy. One necessary but
not sufficient programme-related requirement is that the accelerated approval (phase
II) trial must be part of a well-conceived and comprehensive CDP. This CDP should
include at least two randomised phase III trials for the registered indication which
are planned as part of a post-marketing approval requirement. These phase III trials
should be enrolling patients at the time of accelerated approval. The conditional marketing authorisation approval process in the EU is analogous to accelerated approval
in the United States. However, it must be renewed on an annual basis. This renewal
requires timely completion of studies demonstrating clinical benefit. Health authority
meetings should be planned to confirm the adequacy of the registration plan including
post-marketing approval commitments. For example, registration using single-arm
trials based on objective tumour response rate may require evidence of strong positive benefit/risk, require documentation of unmet medical need or represent a rare
indication.
If the planned phase II study for monotherapy or combination studies is intended
for potential registration, this should be confirmed with the health authorities prior
to the start of the study, for example, at the end of a phase I meeting. The briefing
documents should also contain a detailed description of the planned phase II trial
(detailed protocol synopsis), an overall CDP which includes concrete and viable
plans for post-approval confirmatory trial(s) and a discussion about the total number
of patients in the proposed submission to monitor safety (i.e. the size of the safety
database). At the present time, the protocol would need to be submitted for an FDA
Special Protocol Assessment (SPA), with content of the briefing documents similar
to those prepared to discuss phase II-based registration with the Committee for
Medicinal Products for Human Use (CHMP). They should provide evidence that the
planned development would meet the requisite statutory requirements for conditional
approval or approval under exceptional circumstances. For a single-arm trial, the
absolute minimum evidence could be, for example, clear documentation that the
investigated indication represents an unmet medical need (e.g. documentation that
patients had progressive disease under standard of care) or represents a rare indication
for which a randomised controlled trial is not feasible. Clearly, more evidence will
be warranted if there are questions from regulators or others who are weighing the
quality of the evidence.
While it is possible for a randomised controlled phase II trial to demonstrate
overwhelming evidence of efficacy, the standards are rather stringent (see Section
13.3.2.2). The screening randomised phase II trial should incorporate the same degree
of rigour as the planned phase III trials. Ideally, it should use the same endpoint and
patient population as the planned phase III trials.

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Statistical considerations

The statistical considerations can be discussed in relation to the planned role of phase
II in the development strategy, that is, whether the phase II trials are specifically
targeted for accelerated approval and/or conditional registration.
Trials planned for registration (accelerated approval and/or conditional registration) Regulatory and medical considerations generally drive the potential for
accelerated registration. The study designs commonly considered arise from the
unmet medical need/rare indication setting and include single-arm designs based on
objective tumour response, randomised uncontrolled phase II trials (e.g. two different
doses) and randomised controlled studies for rare diseases (if feasible). The singlearm design may have one stage (if early termination for lack of efficacy is not a
concern because of phase I activity) or two stages (if early termination for futility is
a requirement).
Although statistical methodology is used to design the pivotal phase II study, drive
sample size considerations and provide operating characteristics, successful statistical
results may only be necessary and not sufficient for health authority approval. In the
uncontrolled setting, clinical considerations for the overall benefit/risk are critical
considerations.
As the CHMP guidance (EMEA/357981/2005) stipulates, statistical support is
required to provide justification for ‘approval based on exceptional circumstances’.
Some of this is used to characterise the context of the design and indication; for
example, the sponsor’s inability to provide comprehensive efficacy and safety information because the rarity of the indication must be established. Evaluation of sample
size requirements under various statistical scenarios may prove necessary to support
an exceptional circumstances claim. Relevant EMA guidance such as the CHMP
guidance on small populations, and the EMA workshop on methodological aspects
of clinical trials for efficacy evaluations in small populations, should be referenced
for possible alternative designs.
Trials not planned for registration but overwhelming evidence of efficacy
observed In addition to phase II trials planned for registration, it may be possible for a randomised controlled phase II trial designed for screening agents for
subsequent phase III studies to provide overwhelming evidence of efficacy that might
lead to registration. For example, if the primary efficacy endpoint and patient population match what is planned for phase III, a strong positive outcome may render a
subsequent randomised controlled trial difficult to recruit and potentially unethical.
With respect to design characteristics, it has been suggested that the boundaries used
for interim monitoring of a randomised phase III trial be employed to determine
overwhelming evidence of efficacy from a randomised phase II trial. For example,
if there are one-quarter the number of events in the randomised phase II trial as
compared to a randomised phase III trial, then a one-sided p-value <0.00003 would
be required to claim efficacy, assuming O’Brien–Fleming boundaries are used for
interim monitoring at 25% of the information.

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Implementation and design should address the exceptional circumstances upon
which the argument for registration is based. The impact on trial operations based
on different outcomes must be contemplated. The regulatory acceptance of a claim
based on a randomised controlled phase II trial not primarily or originally intended
for submission but in which overwhelming evidence of efficacy was observed might
be enhanced by pre-specifying this in the protocol. In this situation, consider providing a potential strategy for confirming an effect and for generating adequate safety
information.

13.3.3

Exploratory activity

The goal of exploratory activity trials (phase IIa) is to collect efficacy data to use in
planning for (or against) future randomised controlled trials. The phase IIa criteria
should be explicitly defined and reflect the competitive environment and the appropriate level of evidence to decide on the merits of a subsequent larger randomised
controlled trial at a particular level of risk.
Risk calculations must, at least implicitly, incorporate expected returns. From a
pharmaceutical company perspective, the cost of not continuing development of a
‘good’ drug, in terms of expected future sales, might be much greater than continuing
with a bad drug. On one side, continuing development of a ‘bad’ drug results in
losses from the failed phase III trial as well as the lost opportunity of reallocating
resources for better drugs. On the other, potential profit from a new successful drug
could outweigh the potential losses from continuing with a useless or harmful drug;
this can encourage continuing development in the case of uncertainty.
If they exist, short-term endpoints which are well correlated with the primary
endpoint for registration should be considered as discussed in Chapter 2. This is still
true even if they are not causally related to the registration endpoint. This data can
help support a no-go decision (termination of development for the specific indication).
In addition, a successful phase IIa trial may use the results from these endpoints to
reassess the proposed future trial designs within the CDP.
Both single-arm and randomised trial designs (especially for combination agents)
may be used for phase IIa trials.
Bayesian and frequentist methods have been proposed for phase IIa trials. For
frequentist designs, the power of the pre-specified success criteria is key, since a
negative trial for the phase IIa endpoint may terminate an indication’s development.
As discussed above, the risks involved in termination of a development programme
require careful consideration. A greater type I error rate, increasing the tolerance for
allowing a poor development programme to continue, may be tolerated in this phase
IIa setting. For example, one-sided type I error rates as high as 20% have been used
for randomised phase IIa trials and one-sided type I error rates as high as 10% have
been used for internal single-arm phase IIa trials.
Bayesian methods can incorporate relevant historical information in a straightforward manner if it exists (Neuenschwander et al. 2010). Attention and preparation
should be given to prepare for concerns regarding the selection of historical data (prior
sensitivity) and operating characteristics under different scenarios, as previously

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discussed in Chapter 2. However, reliable historical data for the phase IIa study might
not be available. If the trial relies on a functional imaging or molecular biomarker
or is limited to a targeted subpopulation, this information may not be available for
the standard of care. In other settings where historical information for the phase IIa
endpoint may be available, there may be concerns about inter-trial variability that
would indicate the need for a randomised phase IIa trial. Historical information is not
necessarily usable on a one-to-one substitution basis as a replacement for including
a control (active or placebo) arm in the study. In particular, a phase IIa trial for
a combination of a new drug added to a standard of care should be a randomised
comparison with the standard of care alone. One advantage to the Bayesian analysis
approach is that it can also provide estimates of the predictive probability of success
(PoS) in later trials. For further discussion of PoS refer to section 13.3.5.
Finally, we reiterate that data on potential phase III endpoints to support future
trial planning and programme-level decision-making should be collected even though
a short-term endpoint was chosen to design the phase IIa trial.

13.3.4

Regimen selection

Selection of a regimen for single-agent therapies tends to follow two strategies.
If there is sufficient evidence of activity in all proposed experimental regimens, a
randomised selection design without a control group may be used. Selection designs
try to determine the best regimen when several competing regimens are candidates for
a subsequent randomised controlled trial to study only the best regimen. For example,
there may be questions about the most appropriate dose, schedule, sequence and/or
formulation to compare with the standard of care. This aims to have a high chance
of selecting the best regimen (if it exists) for a subsequent randomised controlled
trial without requiring additional subjects in a placebo arm for comparison. The
other common design strategy is to incorporate historical or concurrent controls
in a traditional comparison design, potentially with the facility to drop ineffective
regimens early. Historical controls should be carefully considered for relevance, as
temporal changes in standard of care could increase bias, variance or both. Concurrent
controls may be required due to insufficient information on activity. Chapter 5 in this
book summarises additional design possibilities.
If there is a marked difference in response based on dose or regimen, selection
designs are straightforward for comparing regimes of a single compound. However,
it can be a valuable tool to select across compounds at the same stage of development.
In this instance, there are many challenges to implementing the first strategy within
a company. In many pharmaceutical companies, project teams are usually set up to
develop individual drugs or drugs from the same family. Successful implementation
for cross-compound selection would require either close collaboration across teams
or an integrated indication team approach to development. This also applies to the
selection stage in the development of combination therapies
13.3.4.1

Adaptive designs and selection

Regimen selection during the phase II part of an adaptive phase II/III design is
one of the common adaptations cited by the proponents of the design. There are

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many positive aspects for these designs which are found in the literature. To balance
out that view, we point out that the greatest obstacles to implementation of such
an adaptive phase II/III design are primarily logistic. For example, there must be
adequate firewalls in place to keep the project team blinded to the phase II results,
detailed pre-specified decision rules for selecting the best regimen to be chosen by
an independent group, usually a data monitoring committee (DMC), and one or more
meetings with the health authorities. The potential advantages from using an adaptive
phase II/III design with regimen selection during the phase II part should be weighed
against the intensive and time-consuming study start-up activities. There may also be
increased monitoring, more complex randomisation and potential issues concerning
operational bias. In addition, from a corporate perspective, the main decision-making
is allocated to an external DMC which reduces the flexibility, in case of surprising
internal or external results which result in requiring major trial changes. As a result
phase II/III trials can have drawbacks when there is not so much existing knowledge
about the drug, target population and indication.

13.3.4.2

Dose selection for combination therapies

Combination therapies require additional critical consideration. Different agents are
often at different stages of development. Seldom do the agents have equal amounts
of prior information from internal clinical studies.
The intentional drug–drug interaction leads to considering a few subsequent
points. With respect to safety there may be a synergistic effect of the combination of
drugs leading to a higher incidence of severe acute and delayed toxicity relative to the
single-agent therapies, even if full doses were tolerable according to the individual
phase I studies. In addition, identifying predictive biomarkers for patient stratification
may be more challenging in the combination setting. For combinations where one or
more agent has been approved, the selection of the approved agent as a component
of the treatment should take into account the relative frequency of usage of this
agent globally as well as the pre-clinical and phase I evidence supporting the usage
of the combination with the investigational agent. For registration of a combination
therapy of two or more investigational agents the contribution to efficacy of each
component generally needs to be quantified to show evidence that any observed
clinical benefit is not entirely attributable to only one of the two single agents.
Contributions of the components might be demonstrated in phase II based on a
surrogate or pharmacodynamic marker using a factorial design (U.S. Department of
Health and Human Services 2013).
Regimen selection in the setting of combination therapies with two or more
experiment compounds increases complexity. Three possible settings are (i) combination of an investigational agent(s) with a standard of care; (ii) combination of
two (or more) investigational agents in an indication without a standard of care; and
(iii) combination of two (or more) investigational agents compared to a standard of
care. In all three settings we currently consider only randomised trial designs. Van
Glabbeke et al. (2002) claimed that ‘non-randomised Phase II studies of drug combinations are often meaningless, sometimes misleading’. They gave two examples

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where use of non-randomised phase II combination studies may have led to misleading development. The first was a study on dose-intensive chemotherapeutic regimens
for intermediate- and/or high-grade non-Hodgkin’s lymphoma. Here, five subsequent
randomised trials versus a CHOP (or CHOP-like control) all showed no objective
benefit but greater toxicity and toxic death rates relative to the standard arm. The
second was an autologous bone marrow transplantation (BMT) for breast cancer. In
this case, a definitive randomised phase III trial had accrual problems because of the
reports of uncontrolled phase II trials.

13.3.5

Phase II to support predicting success in phase III

Predicting success in phase III is an important strategic consideration for the drug
industry. In general, despite all of the introduced improvements in clinical development, the rate of phase III failures is still high, and it is common for management to
be continually surprised by this. One of the reasons for this strategic goal is to manage
expectations on what will be obtained from phase III trials, and therefore using previous data to predict the likelihood of ‘success’ is very appealing. If there is still a lot
of uncertainty following phase II, then management must be aware of this so they can
make appropriate planning decisions. At the end of the day companies can live with
risk of ‘failure’ if it is well managed and spread appropriately across the portfolio.
Prospective thinking about the future success of a trial is an important part
of good decision-making. Considerations of probability of success (PoS) comprise
qualitative as well as quantitative aspects. There are various important qualitative
considerations, such as the choice of endpoint, patient population, disease setting
and dosing schedule. In order to be reasonably well calibrated, calculations of the
PoS should include all relevant sources of uncertainty. These comprise uncertainties
regarding the future data, the true underlying parameter of interest (e.g. a progressionfree survival (PFS) hazard ratio), between-trial heterogeneity and the relationship
between different endpoints in phases II and III.
From a predictive point of view, the most informative phase II design is a randomised design with the same endpoint (PFS or overall survival (OS)) as in phase III.
For such a design, and a reasonably promising effect estimate in phase II (e.g. HR of
0.7 to 0.75), the PoS in phase III is approximately 60–70%. If a different endpoint is
considered for phase II, collecting information on the phase III endpoint, if feasible,
will be important. In summary,

∙

not acknowledging relevant uncertainties leads to an overly optimistic estimate
for the PoS in phase III;

∙

the largest uncertainties should be accounted for since they have the largest
impact;

∙

a good outcome in phase II does not necessarily lead to higher probabilities of
success, in particular if between-trial heterogeneity is large.

A good quantitative estimate for the PoS is an important input for decisionmaking. For example, in a multi-stage trial this probability may inform decisions at

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interim to stop the trial early. Or, at the end of a phase II trial, the decision to go to
phase III may be easier if the chance to be successful is reasonably high. However,
formal quantifications of the PoS have not been used systematically in the past, for
various reasons:
1. An assessment of the PoS in a future trial requires an understanding of future
data, that is, a prediction for the data in the upcoming trial.
2. The inherent difficulty to make predictions. This is due to the fact that extrapolations are required from current data to future data, which are based on
assumptions that are essentially unverifiable at the time when the prediction is
made. The standard assumption is that the future will be identical to the past.
To relax this fairly strong assumption means to introduce other assumptions
that may be equally difficult to justify.
3. The need to think (before starting phase II) about the design of the phase III
trial.
4. Technical difficulties that are of a purely statistical or computational nature.
Points 1 and 2 above are scientifically challenging. Predictions are one variant of
the problem of induction (Hacking 2001), one of the most difficult problems in the
empirical sciences. Predictions are inductive in the sense that there is no logical (or
deductive) way that allows to reliably extrapolate (1) from partial to full information
or (2) from the past to the future. The statistical/probabilistic approach to induction
provides a quantitative framework that combines mathematical rigour with good
judgement, the latter depending on the given context. To prospectively think about
upcoming phase III trials, point 3, can be quite a challenge too, as it requires teams to
think beyond phase II and may imply the involvement of health authorities at a fairly
early stage.
Predictive problems in clinical trials arise in different ways:
1. The least controversial prediction problem is within-trial prediction for the
same endpoint. This type of prediction may be of relevance at an interim stage
of a phase IIa study. For example, in a multi-stage single-arm phase II trial,
a prediction from the data on objective response rate (ORR) available at the
first stage can be used to calculate the predictive distribution for the remaining
data, from which the PoS for phase II can be obtained. This probability can
be used to stop the trial, for futility and/or early success. Note that within-trial
prediction is relatively straightforward only under the assumption that there
is homogeneity over the different stages of the trial with regard to all relevant
factors that may influence the outcome of the trial.
2. Between-trial prediction for the same endpoint is more difficult, because
(in its simplest form) it critically depends on the assumption that all relevant
factors that may influence the outcome are equal (or at least sufficiently similar)
for both trials. For example, in a randomised phase II trial using a time-to-event

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endpoint (e.g. a PFS hazard ratio), the data at the end of the trial can be used
to predict data for an upcoming phase III trial of given design.
3. The quality of between-endpoint prediction depends on how predictive one
endpoint is for the other. For example, PFS data may be collected in a randomised phase II trial, but OS will be used in phase III. Clearly, a proper
prediction for PoS in phase III depends on a good understanding of the degree
of correlation between PFS and OS. Therefore lack of knowledge between
the endpoints adds to the uncertainty about the prediction and increases the
challenges of planning across the portfolio, since risks of phase III failure are
less known.
The different types of extrapolations may arise in combination. For example, in a
phase II study with PFS as the primary endpoint, some limited information about OS
may be available. For this situation, between-trial (for PFS) and between-trial as well
as between-endpoint considerations (for OS) will influence the PoS in phase III. The
level of uncertainty due to different endpoints depends also on the disease setting.
Prediction of future results in the context of clinical trials is an important use of
early phase data and, as noted in this section, requires some attention to detail.

13.3.6

Phase II safety trials

Historically, within the drug industry, trials set up to specifically look at some aspect
of safety have been relatively uncommon and have often been motivated as a result
of health authority concerns. The evolving regulatory and reimbursement landscape
has changed the playing field, and this drives development towards a situation where
safety and specific risks are assessed in a proactive ongoing basis. It is assumed that
the frequency of such studies will likely increase.
Although safety information is constantly monitored in all trials, sample size
determination is usually based upon efficacy, and formal early stopping rules related
to safety issues usually are not always clearly specified in phase II. Safety should be
investigated as a co-primary endpoint when the study drug shows some preliminary
efficacy but major safety concerns in the early stage of the development, or if the
experimental treatment has similar efficacy as the standard but may have a substantial
improvement of safety.
There are many advantages of collecting and studying safety data in phase II trials.
For example, the safety data from phase II trials are collected in a more specific and
controlled setting. Safety profiles in the targeted population(s) can provide further
insight into the safety and efficacy relationship of the studied drug. Another example
is that long-term toxicities or safety trends can be collected and studied. Phase I
oncology trials usually have short duration and focus on the toxicities occurred in
the first cycle in order to determine the maximum tolerated dose (MTD), and further
recommended phase II dose. Finally, a control arm can be included to compare the
safety profile of an investigational drug with the control of interest. Most of the
time, the control could be a standard of care that is available to the general patient
population.

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The designs with both safety and efficacy as co-primary endpoints include, but
are not limited to, Bryant and Day (1995), Conaway and Petroni (1995) and Thall and
Cheng (2001) are discussed in more detail in Chapter 6. Additionally Hoering et al.
(2011) consider this in the phase I/II setting. One practical problem with many of
these designs is that defining toxicity as a binary variable can be clinically challenging
when several toxicities of various grades are of interest.

13.3.7

Prospective identification of target populations

The increasing awareness that cancers are actually very heterogeneous has driven the
development of targeted therapies which are effective in clearly defined and diagnosed populations. Although the number of potential patients may be reduced, this
possible income loss can be balanced out by both a more powerful and stronger
treatment effect (smaller and faster trials) and the likelihood of possible earlier
approval where the additional time on the market can lead to increased income.
A related challenge for pharmaceutical companies is that in many countries reimbursement must be justified, in that the payers require evidence for the population
which will benefit most. Therefore, from a drug company point of view there is a
financial imperative to ensure that the right set of patients are treated and that an
appropriate level of evidence of efficacy is provided to the health authorities in this
population.
Heterogeneity in treatment outcome is a common phenomenon in phase II clinical
trials, perhaps more so than in phase III. Sources of heterogeneity of clinical outcome
in response to an experimental treatment in phase II experiments can often be anticipated. The use of biomarkers can be one attempt to prospectively account for and
control the variation. Without successful accommodation, the impact of unaccounted
heterogeneity can lead to biased inferences. This can result in the early rejection of
effective therapeutics or improper planning and failure in phase III experiments.
Two main design strategies, stratification and enrichment, are used (sometimes
together) to prospectively account for such heterogeneity, as has previously been
introduced in Chapter 2. First, enrichment strategies limit trial enrolment to patients
with specific marker profiles. These should be used carefully and only in the presence
of substantial contextual evidence that the study drug will be ineffective in the
excluded patient subgroups. Second, stratification strategies enrol all comers but
assess treatment effects separately in mutually exclusive subgroups. Such studies
should be sized adequately to provide valid inferences about the effect (often benefit–
risk) within each subgroup. For both of these approaches, adaptive and Bayesian
variations of these strategies may be more informative and allow greater flexibility,
although requiring considerable upfront investment for planning and implementation.
The choice of a phase II design depends on the nature of the marker(s) likely
to affect treatment outcome in any given setting. Markers (single traits or signatures
of traits) that are informative for clinical outcome can be broadly categorised as
predictive, which are those that separate different populations in terms of the clinical
outcome of interest in response to a particular treatment; or prognostic, those that
separate different populations in terms of the clinical outcome of interest irrespective

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of the treatment; or predictive–prognostic, when both predictive and prognostic effects
are observed.
Traditional approaches may be inadequate for a number of reasons. The main
issue with traditional ‘all-comers’ designs is that they exercise no control on the
subgroup composition of the set of patients studied. When the studied treatment is
effective only in selected subgroups, the measured treatment effect is diluted and can
lead to misleading conclusions and costly errors in development. This is particularly
true for targeted agents.
For multiple reasons it is often not possible to retrospectively calculate accurate
estimates of treatment effects within subgroups of interest (e.g. patients with a certain
biomarker-positive status). Sample sizes of phase II cancer trials are often fairly small,
so that there may be too few patients in a given subgroup (e.g. rare mutations) to draw
reliable inference. Furthermore, without prospective planning important predictive
traits may be confounded with other predictive/prognostic traits.
In comparative assessment of treatment benefit, randomisation can be used to
achieve balance between treatment arms. However, in the case of predictive markers, without appropriate stratification there may still be important imbalances and
confounding of effects due to small sample sizes, and the trial may therefore yield
insufficient information to identify important subgroups.
For genetic and molecular markers, it is assumed that assays are available and have
reasonable turnaround time to allow each patient’s marker status to be established
upfront (i.e. before enrolment or start of treatment). Definition of indications and
hence designs for identifying indications are based on classification of biomarker
status into a few discrete categories (typically a dichotomy). Thus, while biomarker
status may be continuous, in most cases appropriate thresholds for classification need
to be established prior to implementing the proposed strategies.
The relative merits of the proposed strategies need to be assessed at the outset and
can be measured in terms of numbers of patients, time to completion of the trial or the
cost of the trial. These merits are impacted by factors including the relative treatment
effect in the biomarker-defined subgroups, the prevalence of these subgroups and the
accuracy and cost of the diagnostic and treatment. Phase II designs which may be
appropriate in the context of targeted subgroups are outlined in Chapter 7.
As a final note, when indications are based on levels of predictive biomarkers,
co-development of reliable diagnostics for patient selection should start early. Failure
to start early enough will increase risk due to the need to bridge between a clinical
trial assay and a clinically and analytically validated diagnostic system.

13.4 Discussion
This chapter is intended to provide a strategic overview of programme-level decisionmaking and the need to tailor phase II designs according to the CDP. It is also intended
to complement the other chapters in this book. By refining the strategic boundaries of
what the trial should support, and then working to select the best of the implementable
designs, this will result in more efficient trials which have a better chance to provide

PERSPECTIVE FROM INDUSTRY

211

answers. Sometimes these trials will be shorter or smaller, but hopefully they will
always be more decisive trials.
Phase II clinical trials play a critical role in understanding better how the compound can be used to maintain or improve the health of a patient. During times of
rapid discovery of possible therapies, phase II trials can sometimes be viewed negatively, as an attempt to correct early mistaken decisions about the indicated use of
the compound. During times when few compounds are being discovered, they can be
seen as an opportunity and means to patiently increase the probability of finding a
commercially viable and profitable niche for the compound. The challenge in understanding the huge diversity of designs, along with the ever-evolving commercial and
medical landscape, makes the approach for proper selection interesting and difficult.
Disclaimer: The opinions expressed in this chapter are solely those of the authors
and not necessarily those of Novartis. Novartis does not guarantee the accuracy or
reliability of the information provided herein.

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Index
Academia, 4–5
Accelerated approval, 176, 198, 201,
202
Activity, exploratory, 196, 198,
203–204
A’Hern
(2001), 37, 155–160
(2004), 131–132
Alpe-Adria Thoracic Oncology
Multidisciplinary (ATOM) group,
162
Alternative hypothesis, 30, 157, 158,
160
Androgen deprivation, 163, 165,
171
Average sample number (ASN), 28, 59,
127
Ayanlowo and Redden (2007), 58
Banerjee and Tsiatis (2006), 47
Bauer et al. (1998), 89, 93
Bauer and Kieser (1999), 90, 93, 97
Bayesian, 27, 33, 38, 45–47, 50, 55, 57,
59–64, 75, 76, 109, 110, 122,
123–126, 129, 130, 135–140, 156,
178, 181, 203, 204, 209
Bellissant et al. (1990), 55
Binary outcome, 19–20, 36–50, 54–66,
68–69, 72–73, 77–79, 82, 84–85,
89–92, 99, 103–104, 106–108,
111, 112–121, 122–124, 125–128,

131–136, 138–139, 143–145, 148,
153–154, 165, 176, 181
Biomarker, 7, 10, 15–16, 17, 20, 33, 34,
133–135, 163–173, 203, 205,
209–210
Bretz et al. (2006), 92
Bryant and Day (1995), 118, 178–181
Case and Morgan (2003), 46, 53,
190–192
Categorical data, see Multinomial
outcome
Chang et al.
(1999), 44, 50
(2004), 37, 155–160
(2007), 39, 52
Chen (1997), 57
Chen and Beckman (2009), 70–71,
145–147, 190–192
Chen and Chaloner (2006), 62
Chen et al. (1994), 56
Chen and Ng (1998), 44
Chen and Shan (2008), 58
Cheung (2009), 88
Cheung and Thall
(2002), 60, 63, 109–110
Chi and Chen (2008), 49
Chow and Tu (2008), 78, 80–81,
145–147
Clinical development plan (CDP),
195–197, 201, 203, 210

228

INDEX

Colorectal cancer, 11, 185–194
Combination therapy, 7, 15, 22, 24, 31,
142–150, 151–162, 174–184,
185–194, 197, 198, 203–205
Committee for Medicinal Products for
Human Use (CHMP), 201, 202
Conaway and Petroni
(1995), 117, 119, 122, 178–181
(1996), 117, 119, 178–181
Confidence intervals, 37, 41, 49, 58, 65,
156
Continuous monitoring, 26, 29, 60–64,
76, 89, 109–110, 125–130, 132,
133, 138–140, 154, 166, 177, 189
Continuous outcome, 18–20, 38, 50,
59, 63, 65, 66, 70, 73, 75, 76, 77,
79–80, 82, 84, 86, 88, 92–96,
99–101, 104, 108, 109, 111, 165,
167, 168
Control arm, 16, 17, 22, 23, 24–26, 31,
34, 68–82, 83–102, 112–116, 126,
128–129, 146–147, 153–154,
157–160, 166–173, 176, 187, 190,
194, 201, 202, 204, 208
Correlation, 19, 34, 40, 78, 80, 81, 86,
96, 99, 100, 101, 102, 117, 119,
122, 128, 147, 148, 165, 179, 208
Costs of treatment, 29, 144, 154, 167,
177, 188
Critical values, 43, 44, 49, 50, 84, 88,
97. See also Stopping boundaries
Cronin et al. (1999), 75
Cytostatic therapies, 14, 18, 20, 21, 22,
25, 40, 69, 71, 141, 185. See also
Targeted therapies
Cytotoxic therapies, 2, 4, 5, 14, 15, 19,
22, 24, 151–153, 176, 186
de Boo and Zielhuis (2004), 126
Decision making, 4, 5, 15, 16–17, 18,
19, 22–25, 27, 28, 29, 30, 35,
143–147, 152–158, 164, 166, 167,
168, 178, 186, 187, 189, 191,
196–197, 203, 204, 205, 206
Decision-theoretic, 26, 29–30, 64, 89,
110, 144, 154, 167, 177, 188, 197

Dexamethasone, 174–184
Docetaxel, 151–162
Dose finding, 4, 79, 89, 90, 93, 94, 97,
100
Dose response, 4, 100
Drug development, 1–6, 16, 19, 166,
171, 186, 196
Dual threshold design, 45
Early termination, 27–29, 31, 34–35,
144, 154, 166–168, 169, 170,
179–180, 192, 202
Effect size, 10
Efficacy, 1–4, 15, 78, 87, 89, 90–95, 97,
98, 110, 115, 129, 145, 170, 185,
186, 188, 198, 201–203, 205, 208,
209
Eligibility criteria, 32, 37 148, 167
Enrichment, 7, 10, 16, 22, 27, 32, 33,
142, 152, 164, 175, 209
Ensign et al. (1994), 56
European Medicines Agency (EMEA),
202
Event-free survival, 142–143, 148, 175
False negative result, 5, 6, 16, 23
False positive result, 5, 23, 35
Fazzari et al. (2000), 36, 155–160
Fixed sample, 27, 29, 57, 58, 61, 90,
93, 97, 127, 128
Fleming (1982), 36, 41, 55, 155–160
Follow-up, 21, 28, 32, 41, 46, 54, 60,
63, 109, 110, 143, 147, 148,
165–167, 171, 190, 192
Food and Drug Administration (FDA),
176, 201
Frequentist, 45, 47, 75, 181, 203
Funding, 31
Futility, 86, 147, 169, 171, 196, 202,
207
Gajewski and Mayo (2006), 38,
155–160
Gefitinib, 6, 151
Gehan (1961), 41
Goffin and Tu (2008), 52

INDEX

229

Goldman (1987), 127
Goldman and Hannan (2001), 127
Go/no-go, 4, 5, 15, 16, 142–144, 152,
154, 164, 167, 168, 178, 186
Green and Dahlberg (1992), 42
Group sequential, 26, 28, 55, 57, 59,
61, 62, 75, 91, 94, 98, 99, 102,
122, 125, 136, 138, 170, 171.
See also Multi-stage
Growth modulation index, 21, 40,
199

Jin (2007), 118, 120, 178–181
Johnson and Cook (2009), 62, 64
Jones and Holmgren (2007), 134
Jung (2008), 72, 84
Jung et al. (2004), 46
Jung and George (2009), 73, 85, 107

Hanfelt et al. (1999), 44
Head and neck cancer/head and neck
squamous cell carcinoma
(HNSCC), 11, 19, 141–150
Heitjan (1997), 43
Herndon (1998), 43
Herson (1979), 55
Herson and Carter (1986), 68,
145–147, 155–160
Historical control data, 15, 16, 17, 19,
21, 22, 23, 24, 25, 26, 33, 34, 37,
38, 44, 50, 62, 69, 70, 73, 85, 107,
123, 125, 141, 151, 153, 156, 157,
160, 177, 178, 179, 181, 185, 187,
188, 203, 204
Hong and Wang (2007), 77, 155–160

Lachin and Younes (2007), 78, 80–81,
145–147
Le Blanc et al. (2009), 136, 138
Lee et al. (1979), 65
Lee and Liu (2008), 59, 62
Levy et al. (2006), 86, 168–170
Lin and Chen (2000), 51
Lin and Shih (2004), 46
Litwin et al. (2007), 48, 54, 190–192
Liu and Pledger (2005), 79, 100,
168–170
Logan (2005), 107
London and Chang (2005), 132–133
Lu et al. (2005), 39, 51

Implementation, 9, 10, 27, 147, 156,
191, 197, 203–205, 209
Independent data monitoring
committee, 170, 205
Independent review, 19
INTACT1, 6
INTACT2, 6
Interactions, 136, 137, 139, 140, 205
Interim analysis, 27, 28, 31, 32, 54, 78,
86, 89, 91, 94, 96, 98, 101, 110,
170, 171, 177–180, 187–192, 197,
202, 207
International Conference on
Harmonization (ICH), 3, 4
Interpreting trial results, 7, 16, 22, 24,
25, 45, 153
Ivanova et al. (2005), 128

Kelly et al. (2005), 91, 94, 98
Kocherginsky et al. (2009), 53
Kopec et al. (1993), 82
Koyama and Chen (2008), 49

Mayo and Gajewski (2004), 37,
155–160
Mechanism of action, 2, 4, 7, 14, 15,
18, 20, 141, 152, 164, 174, 185
Methodology for the Development of
Innovative Cancer Therapies
(MDICT) Task Force, 7, 32
Mick et al. (2000), 40
Minimax design, 42, 45, 48, 51, 57, 58,
59, 72, 74, 85, 87, 114, 129
Misspecification, 23, 34, 117–122,
179–181
Molecular targeted agents, 27, 141,
148. See also Targeted therapies
Monoclonal antibody therapy, 14, 15,
16, 185–194
Multi arm, 17, 26, 83, 163–173,
174–184, 204–205. See also
Treatment selection

230

INDEX

Multinomial outcome, 20, 39–40,
50–53, 59–60, 63, 65, 66, 70,
74–76, 77, 80, 82, 84, 87, 88,
96–97, 101, 105, 108, 109, 111,
114, 128
Multiple myeloma, 11, 174–184
Multi-stage, 26–29, 55–60, 66, 75, 88,
91, 92, 94, 98, 108–109, 115–117,
122–125, 129, 135–138, 144, 154,
166, 177, 178, 189, 206, 207
Murray et al. (2004), 58
National Cancer Institute, 7, 16
Non-small cell lung cancer (NSCLC),
6, 11, 151–162, 164, 166
Null hypothesis, 28, 30–31, 156–158,
160, 192
Objective response, 6, 207
Objectives, 3–5, 7, 196, 198
One-sided test, 148, 158, 160, 170, 192,
198, 202, 203
One-stage, 26–29, 36–40, 68–71, 78,
84, 103–105, 112–113, 117–118,
126, 131–132, 144, 145, 154–158,
160, 167, 169, 177, 189, 190, 202
Operating characteristics, 27–29, 35,
158–160
Optimal design, 42, 47, 48, 51, 52, 57,
58, 59, 72, 74, 85, 87, 114, 129
Ordered categorical outcome, see
Multinomial outcome
Overall survival, 3, 14, 142, 153, 156,
163, 165, 175, 176, 186, 187,
206
Panageas et al. (2002), 51
Patient population, 10, 14, 16, 19, 22,
23, 24, 25, 29, 31–33, 131–140,
141, 145, 148, 151, 160, 164, 166,
170, 171, 176–177, 181, 182, 186,
187–189, 192, 201, 202, 203, 205,
206, 208, 209–210
Pharmaceutical industry, 1, 4, 5,
195–211

Phase 2, 5, 71, 146, 190
phase I, 1, 2, 4, 6, 16, 17, 163, 175,
195, 197, 198, 200–202, 205, 208
Phase II/III, 26, 31, 32, 67, 77–88,
89–102, 110, 111, 144–150, 154,
166, 167–173, 177, 188, 204, 205
phase IIa, 4, 16, 19, 22, 24, 203, 204,
207
phase IIb, 4, 15–17, 19, 22, 24
phase III, 1–7, 14–19, 22, 23, 25–32,
35, 141–150, 163–173, 185–191,
195–198, 201–204, 206–209
phase IV, 1
Phases of drug development
Power, 23–25, 33, 35, 148, 160, 170,
187, 190, 192, 203
Practicalities, 8, 10, 12, 33–35,
146–148, 155–158, 168–170,
178–181, 190–191
Prediction (of outcomes), 38, 79, 80,
81, 147, 156–157, 196, 206–208,
209
Primary aim, 5, 16, 18, 24, 35,
142–143, 152, 164, 175, 186
Primary endpoint, 15–16, 17, 18–21,
24, 29, 30, 31, 34, 142–143, 145,
148, 152–153, 164–166, 175–178,
186–187, 203, 208
Probability of success (PoS), 200, 204,
206
Programming, 34, 147, 156–158, 169,
170, 179–180
Progression-free survival, 14, 20–22,
26, 29, 37, 48, 54, 69, 71, 153,
175, 181, 182, 186, 187, 189–192,
199, 200, 206, 208
Proof of concept, 3–5, 15–17, 24, 27,
41, 142, 143, 152, 154, 164, 175,
177, 186, 189, 194
Prostate cancer, 11, 163–173
Prostate Specific Antigen (PSA),
163–167, 169–173
Protocol, 145, 168, 201, 203
Publication guidance, 6–7
Pusztai et al. (2007), 133

INDEX

Radiotherapy, 141–150
Randomisation, 7, 8, 12, 15–17, 21–26,
31, 32–33, 68–82, 83, 86, 92, 95,
108, 111, 143, 145, 146, 147,
153–155, 159, 160, 165–166, 168,
171, 176–177, 187–189, 192, 205,
210
Randomised discontinuation, 7, 24, 26,
32–33, 82, 102, 111, 144, 154,
167, 177, 188, 199
rare, 187–191
Ratio of times to progression, 21, 40,
54, 60, 64, 65, 67, 72, 75–77, 81,
82, 84, 88, 89, 99, 102, 105, 108,
109, 110, 111
RECIST criteria, 18, 19
Recommended phase II dose, 2, 16,
208
Recruitment, 28, 29, 31, 32, 145–148,
166–167, 187–192
Reference arm, 25, 189, 192
Region of uncertainty, 30, 66, 77, 155,
158
Registration trials, 163, 195, 196,
198–203
Regulatory considerations/
requirements, 4, 196, 198, 201,
202
Response, 3, 6, 19, 20, 22, 23, 24, 25,
29, 30, 34, 152, 153, 155,
157–162, 176–182, 186, 187, 199,
200, 201, 202, 204, 207
Royston et al. (2003), 101
Safety, 21, 27, 30, 34, 154, 155, 164,
166, 170, 195, 196, 201, 203, 205,
208
Sambucini (2008), 50
Sample size, 1, 9, 23, 25–28, 30, 33,
35, 153, 154, 156, 157, 158, 160,
169, 170, 180, 187–192, 197, 202,
208, 210
Sargent et al. (2001), 66, 155–160
Sargent and Goldberg (2001), 104,
178–182

231

Screening, 3, 22, 146, 156, 190, 201,
202
Selection bias, 21, 22, 25, 153, 160,
192
Sequential probability ratio test
(SPRT)/Sequential conditional
probability ratio test (SCPRT),
55–57, 61, 88, 127–128
Shun et al. (2008), 86, 96, 101,
168–170
Shuster (2002), 45
Significance level, 25, 148, 150, 170,
198. See also Type I error
Simon
(1987), 42
(1989), 42
Simon et al.
(1985), 103
(2001), 70, 145–147, 190–192
Simulation, 9, 23, 34, 148
Single arm, 6–10, 17, 23–25, 27, 30, 34,
36–67, 78, 83, 117–140, 153–157,
178, 179, 189, 199, 201–203, 207
Single threshold design, 45, 50
Software, 9, 34, 147, 156–158, 169,
170, 179, 180, 181
Stallard and Cockey (2008), 40, 53
Stallard and Todd (2003), 90, 94, 98
Statistical analysis, 27, 28, 31,
146–147, 167, 169, 204
Steinberg and Venzon (2002), 106
Stochastic curtailment, 58
Stone et al. (2007b), 69, 71, 145–147,
155–160, 190–192
Stopping rules/boundary, 27, 28, 29,
30, 31, 160, 171, 189, 208
Storer (1990), 66, 77, 145–147,
155–160
Stratified designs, 10, 33, 131–140,
200, 205, 209
Subgroups, 9, 10, 15, 17, 33, 131–140,
209, 210
Sun et al. (2009), 74, 87, 114, 128
Surrogate endpoints, 19, 163, 165, 175,
176, 205

232

INDEX

Sylvester and Staquet (1980), 64
Systematic review, 6–7, 10
Tan and Machin (2002), 45
Tan and Xiong (1996), 57, 61
Targeted subgroups, 9, 15, 26, 32, 33,
131–140, 185–192, 196, 203, 208,
210
Targeted therapies, 2, 3, 4, 5, 7, 10, 14,
15, 16, 18, 20, 21, 22, 25, 32, 33,
141–150, 163–173, 185–192,
209–210
Thalidomide, 174–184
Thall and Cheng
(1999), 112–113
(2001), 114–116, 120–121, 123–124,
178–181
Thall et al.
(1996), 122, 125
(2000), 108
(2003), 124, 126, 135, 137–139
(2005), 63, 76
Thall and Simon
(1990), 69–70, 145–147, 155–160
(1994a), 57, 61
(1994b), 60
Thall and Sung
(1998), 123, 125, 129–130, 178–181
Thought process, 7–14, 35, 150, 162,
173, 184, 194
Three-outcome, 26, 30, 65–66, 77, 89,
110, 144, 154–162, 167, 177, 189
Time to event outcome, 20, 21, 40,
53–54, 60, 63–64, 65, 66 70–71,
75–78, 81, 82, 84, 88, 89, 97–99,
101–102, 105, 108–111, 113, 115,
116, 121, 124, 137–140, 143–146,
148 187, 189, 190, 192
Time to progression, 20, 40
Time to treatment failure, 20
Todd and Stallard
(2005), 102, 99, 168–170
Toxicity, 1, 2, 7, 9, 15, 18, 19, 21, 27,
29, 34, 112–130, 135, 137, 139,

140, 142, 151, 152, 163–165,
175–184, 185–186, 189, 205, 206,
209
Trade-off, 15, 18, 25, 113–124,
178–180
Treatment selection, 4, 7, 9, 17, 26,
83–111, 128–130, 163–173,
174–184, 197, 198, 204–205
Triangular test, 55, 91, 95, 99
Tumour response, 3, 14, 18, 19, 20, 40,
152, 153, 199, 200, 201, 202.
See also Response
Tumour size/volume, 14, 19, 20
Two-sided test, 35, 150
Two-stage, 7, 10, 27–29, 33, 41–54,
72–74, 77, 84–87, 106–108,
114–115, 118–122, 128, 132–135,
138, 143, 154, 166–173, 177–184,
189–194, 199, 200, 202
Type I error, 23, 25, 30, 31, 35,
146–147, 157–158, 160, 180–181,
187, 190–192, 203
Type II error, 23, 30, 133. See also
Power
Vickers (2009), 38, 155–160
Wang (2006), 95
Wang and Cui (2007), 91, 95
Wang et al. (2005), 47
Wathen et al. (2008), 136–137,
139–140
Weiss and Hokanson (1984), 106
Whitehead (1985), 103–105
Whitehead (1986), 111
Whitehead and Jaki (2009), 84, 87,
96
Whitehead et al. (2009), 72–74
Wu and Liu (2007), 121, 178–181
Wu and Shih (2008), 48
Ye and Shyr (2007), 47
Zee et al. (1999), 39, 50, 59

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