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A comparison of methods for estimating survival probabilities in two stage phase III randomized clinical trials

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A comparison of methods for estimating survival probabilities in two stage phase III randomized clinical trials

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A COMPARISON OF METHODS FOR ESTIMATING SURVIVAL
PROBABILITIES IN TWO STAGE PHASE III RANDOMIZED
CLINICAL TRIALS

by
Ying Wang

A Dissertation Presented to the
FACULTY OF THE GRADUATE SCHOOL
UNIVERSITY OF SOUTHERN CALIFORNIA
In Partial Fulfillment of the
Requirement for the Degree
DOCTOR OF PHILOSOPHY
(BIOSTATISTICS)

May 2009

Copyright 2009 Ying Wang

ii
Dedication

To my grandparents Cuizhuo Zhang, Min Jin, Guangzu Liu, and Boyuan
Wang. Without their love, inspiration, and spiritual support the completion of such
task would be unthinkable. I would also like to dedicate this thesis to my parents
Rongfeng Liu and Jun Wang, for their continuous love and patience in
accompanying me through this journey.

iii
Acknowledgements

First of all my most sincere gratitude goes to my mentors and co-chairs Dr.
Stanley P. Azen and Dr. Richard Sposto. Their advice and guidance helps to shape
the final product of my doctorate research and also enriches my academic
experience at USC. Secondly my special thanks to committee members Dr. Daniel
Stram, Dr. Anny Xiang, and Dr. Rand Wilcox whose suggestions push my research
to a new level.

I would also like to show my profound appreciation to Dr. Fred R. Sattler,
Dr. Leslie Bernstein, Dr. Todd E. Schroeder, Dr. Bryan M. Langholz, and Dr.
Florence Clark, who granted me opportunities to work on projects in many fields of
medical research and public health. Without their support and expertise my
experience at USC would not be as enlightening and gratifying.

In addition I want to give special recognition to Children’s Oncology Group
for their permission to use published trials as application data for testing
methodology and also for providing analytical dataset.

Many thanks to our academic advisor Mary Trujillo, our brilliant IT
professionals George Martinez and John Morris for their assistance and dedicated
work throughout my years with the department.

iv
In addition I can never give enough thanks to many of my USC friends and
colleagues for their encouragement, company, and hours of discussion about
interesting statistical questions and my dissertation work. The list includes but not
limited to Miwa Kawakubo, Jane Sullivan-Halley, Cher Dallal, Chris Hahn,
Deborah Mandal, Mei-Ying Lai, Xuejuan Jiang, Tim Triche, Huan Pablo Lewinger,
Tommy Ly, Sylvia Tan, Terri Johnson, Claudia Lam, Kelly Tsai, Naoko Kono, and
You-Jin Hong.

Last but not least special thanks to my long-time friends and family
members including Bin Wang, Liusu Wang, Jinlong Liu, Songling Guo, Shaoming
Zhang, Bing Bai, Hua Wang, Linda Eiler, Lila, and Mike J Bowers for their love
and being wonderful spirit in my life.

v
Table of Contents

Dedication ii
Acknowledgements iii
List of Tables vii
List of Figures viii
Abstract ix
Chapter 1: Introduction 1

Chapter 2: Background 3
2.1 Two stage design schema and stochastic processes 3
2.2 Two stage design randomized COG trials 9
2.3 Study endpoints and ITT analysis in two stage design 14
2.4 Types of study dropouts in two stage design 16
2.5 Naïve Estimators 19
2.6 Analytical Approach and IPW Estimator 23
2.7 Bootstrap Approach and the Proposed Estimator 26
2.8 Global Test 27
2.9 Summary 29

Chapter 3: Methods and Survival Estimators 30
3.1 Basic assumptions and common notations 31
3.2 Kaplan-Meier Estimator and Greenwood Formula 33
3.3 Naïve Estimators 34
3.4 Analytical Approach and IPW Estimator 36
3.5 Properties of IPW Estimator 40
3.6 Bootstrap Approach and Proposed Estimator 48
3.7 Modified IPW Estimator 53

Chapter 4: Simulation Studies 54
4.1 Simulation considerations for comparing survival estimators 55
4.2 Simulation Studies I – IV 59
4.3 Simulation studies V and VI 65
4.4 Summary of simulation studies 67

vi
Chapter 5: Data Analysis of COG trials 68
5.1 Statistical analysis for high-risk neuroblastoma trial 69
5.2 Statistical analysis for B NHL and B ALL trial 72

Chapter 6: Hypothesis Test 76
6.1 Global Test Statistic 76
6.2 Global test based on log transformation 77
6.3 Simulation studies and results 80

Chapter 7: Discussion 87
7.1 Strength and limitations of proposed methods 89
7.2 Limitations of Analytical Approach 93
7.3 Strength and limitations of simulation studies 94
7.4 Strength and limitations of proposed global test 96

Bibliography 99

Appendix A 101
Appendix B 106
Appendix C 115
Appendix D 121

vii
List of Tables

Table 1: Parameters for basic simulation studies 59
comparing survival estimators

Table 2: Basic simulation I: compare survival estimators 61
for 1:1 randomization

Table 3: Basic simulation II: compare survival estimators 62
for 3:1 randomization

Table 4: Basic simulation III: compare survival estimators 63
for 1:3 randomization

Table 5: Basic simulation IV: compare survival estimators 64
for heavy tail model

Table 6: Simulation study V: 10,000 simulations for variance 66
estimate of IPW Estimator

Table 7: Simulation study VI: bootstrap variance estimate 66
of IPW Estimator

Table 8: High-risk neuroblastoma trial (CCG3891): compare 72
3-year event-free survival estimates

Table 9: B NHL (B ALL) trial (CCG 5961): compare 75
4-year event-free survival estimates

viii
List of Figures

Figure 1: 2×2 two stage design study diagram with treatment 4
A (A
1
A
2
) and treatment B (B
1
B
2
)

Figure 2: Cancer treatment cycles and candidacy for randomization 7
Figure 3: Treatment regimens for high-risk neuroblastoma among 10
children and adolescences

Figure 4: Treatment regimens for Non-Hodgkin lymphoma and Acute 12
Lymphoblastic Leukemia among children and adolescents

Figure 5: Non-informative dropouts process and censoring at Stage II 18
(assume there are no non-randomized patients at Stage II)

Figure 6: Informative and non-informative dropouts at Stage II 19

Figure 7: Naïve Estimator: censor both B2 and non-randomized 21
patients at Stage II

Figure 8: A naïve approach to censor B2 patients at Stage II and include 22
non-randomized patients together with B1 patients in the analytical
study cohort

Figure 9: Analytical Approach and IPW Estimator: assign various weights to 25
patients and generate analytical cohort based on weighing schema

Figure 10: Bootstrap Approach and Proposed Estimator for one bootstrap loop 28

Figure 11: Event-free survival plots by treatment combinations for high-risk 70
neuroblastoma study

Figure 12: Event-free survival plots by treatment combinations for B NHL 74
study

Figure 13: Power curves: difference between treatment A arms 82

Figure 14: Power curves: difference between treatment B arms 84

Figure 15: Power curves: interactive effects between treatment A and B 85

ix
Abstract

As two stage randomized study designs gain increased recognition and
popularity for oncology studies it remains a challenge to analyze and interpret
clinical outcomes due to lack of sufficient research. In this study we investigated
existing methodologies and explored novel means to estimate survival probabilities
using this study design. First a Naïve Approach was formulated and studied under
the extended notion of Intent-to-Treat (ITT) analysis pertinent to two stage design.
Secondly a bootstrap variance estimate was proposed for Inverse Probability
Weighted (IPW) Estimator to simplify and improve the variance estimate. Thirdly
we developed a Bootstrap Approach by creatively using a “hybrid” bootstrap
process to handle artificial “dropouts” due to late stage randomization. Finally we
conducted power analysis for a global test statistic based on log transformation.

Simulation results reveal that the Naïve Estimator is prone to bias for ITT
analysis. The IPW variance estimate underestimates the true variance of the
estimator by 20-50% where a bootstrap variance provides a nearly unbiased
estimate. Both the survival probability estimate and variance estimates using the
Bootstrap Approach are nearly unbiased with comparable Mean Square Error
(MSE) to IPW Estimator.

x
The application to two previously published Children’s Oncology Group
(COG) studies demonstrates that analytical results using proposed method are
consistent with clinical findings. Finally the proposed global test has sufficient
power for detecting heterogeneity due to late treatment or qualitative interaction.

KEYWORDS: Two stage design; Bootstrap process; Survival analysis;
Randomized clinical trial; Induction therapy; Maintenance therapy; Oncology;
Phase III; COG; IPW; Missing data

Chapter 1: Introduction

In recent years two stage design randomized clinical trial has gained
increased visibility and popularity among certain oncology research (Becton et al.,
2006; Cairo et al., 2007; Forstpointner et al., 2006; van Oers et al., 2006). A
typical oncology trial may involve two or more treatment stages in sequential order.
A two stage design allows a delayed randomization following early therapies or a
randomized study followed by a second randomization to late stage treatment.
Recent publications demonstrated considerable development of statistical
methodology and computerized application in response to needs for data analysis
from two stage design randomized clinical trials ( Lunceford, Davidian, & Tsiatis,
2002; Guo & Tsiatis, 2005; Lokhnygina & Helterbrand, 2006; Wahed & Tsiatis,
2006). In addition to the method based on a formal analytical framework there are
less studied methods of an exploratory nature using naïve methods or using
bootstrap processes (Matthay et al., 1999; Cairo et al., 2007).

The availability in analytical tools makes two stage design randomized
clinical trial more readily to be utilized in designing oncology studies. However
the complex nature of the analytical framework makes the derived statistical
models difficult to comprehend or program in application software, which as a
result leads to limited usage and low recognition among data analysts and
statisticians and thus even less accessibility to general clinical and medical research
2

teams. More new method specifically complicated mathematical formulations
masked the connection between s and well recognized statistical models in survival
analysis such as the Kaplan-Meier Method. Finally insufficient ground work and
lack of simulation studies give way to uncertainty in the behavior of those
methodologies in modeling data in practical settings.

In this study we study existing methods, propose improvement to these
methods, and propose our own methods for modeling data that arise from two stage
randomized studies. Specifically we will formulate a model framework for a Naïve
Method (Matthay et al., 1999); investigate the mathematical and behavioral
properties of the IPW Estimator (Lunceford, Davidian, & Tsiatis, 2002); formulate
a survival estimator based on Bootstrap Approach (Cairo et al., 2007), devise its
variance estimate, and examine its properties under specific model settings. In
addition we conduct a series of simulation studies in order to test and compare
reliability and efficiency of each of the above estimators. From the simulation
results the advantage and pitfalls of each estimator are addressed and the “optimal”
survival estimator is identified and also applied to two previous published COG
studies (Cairo et al., 2007; Matthay et al., 1999; Stone et al., 1995). Last a global
testing strategy comparing different treatment groups and/or combinations are also
developed and discussed.
3

Chapter 2: Background

2.1 Two stage design schema and stochastic processes

Figure 1 demonstrates a generic design schema for a 2 by 2 randomized
clinical trial with treatment A as early treatment and B as the late treatment. Figure
1 also shows several key concepts and processes involved in a two stage trial that
will be explained further later in this section. The feature of the randomization
process in a two stage design randomized trial is determined by the multi-phased
treatment cycles in treating cancer patients. During cancer treatment patients often
receive a regimen consisting of multiple treatment phases. Each treatment phase
can consist of one or more cycles and bears a specific clinical objective and plays a
particular role in fighting the disease which ranges from administratering a primary
and aggressive treatment to limit and prohibit cancer cell growth and targeting
residual diseases. For example commonly defined therapeutic phases in treatment
strategies for treating leukemia patients include induction phase, continuation or
consolidation phase, and maintenance phase. The term “two stage” in the phrase
“two stage design” will refers to the two different time points during the above
treatment phases when randomization to different treatment components may
occur.

4

Figure 1 2×2 two stage design study diagram with treatment A (A
1
A
2
) and treatment B (B
1
B
2
)
* Subjects not CR after Stage I treatment or not consenting are not randomized to Stage II B treatments.
Indicates the evaluation process not the actual follow-up time.
Indicates treatment arm A1B1 is chosen as the treatment arm of interest.
Non-randomized*
2
nd
Randomization
Non-randomized*

1
st
Randomization
2
nd
Randomization
Evaluation
Stage II Stage I
A
1

A
2

B
1

B
2

B
1

B
2

5
The type and dosage and intensity of cancer therapy vary from disease to
disease and from phase to phase. Treatment administered during induction phase is
often referred to as induction therapy. The induction therapy can be chemotherapy,
radiation therapy, or any types of therapy that aim at eliminating primary disease
and inducing remission. In some cancer trials, e.g. the B NHL trial (Cairo, et al.,
2007), patients may go through initial therapies prior to receiving the induction
therapy according to the stage of cancer. Initial therapies intend to stabilize a
patient’s physical condition and also treat other present diseases in order to enhance
the success rate of primary therapy. Consolidation therapies are normally given at
the consolidation phase following the induction stage, which goal is to sustain
achieved remission status among responding patients or to further induce remission
among patients with relatively poor initial responses.

The cancer targeting regimens administered during induction and
consolidation phases can be by and large aggressive in nature which is reflected
either in high dosage levels or in prolonged treatment cycles. The cancer
treatments are often difficult to tolerate and may potentially lead to high toxicity
and increased morbidity along with inducing desired outcome. The severe side
effects can cause secondary cancer, hospitalization, and is potentially detrimental to
long-term survival. Therefore for treatment that demonstrates sufficient benefit in

6
achieving survival a constant challenge lies in identifying an optimal dosage level
that can sustain survival and bear minimum side effects. Often following the
induction and consolidation phase patients are put on maintenance therapy which
aims to control residual diseases with minimal toxicity.

The key feature of the two stage design randomized clinical trial is the late
randomization process after early cycles of therapies. The late randomization may
occur at any phase or cycle along the treatment (i.e. induction, consolidation, or
maintenance phases). When the early treatment is assigned in a randomized
fashion there may be more than one randomization process occurred over the life
span of a two stage design clinical trial. When two randomization processes occur
in a two stage design we simply refer to them as Stage I randomization and Stage II
randomization, early randomization and late randomization, or the first
randomization and the second randomization. Figure 2 depicts the relationship
between treatment cycles and randomization processes in a two stage design
randomized clinical trial.

Prior to the late randomization at a two stage design trial the outcome from
early treatments needs to be assessed and evaluated to determine if a patient is
eligible for further randomized treatment. During clinical evaluation cancer related
primary outcomes are assessed and categorized by study physician based on the
study protocol. The commonly recognized outcome classification is contingent on

7
Figure 2 Cancer treatment cycles and candidacy for randomization

Newly Diagnosed
cancer patients
Initial Therapy

(Preparation)
Induction Therapy

(Treating cancer)
Consolidation

Therapy
(Optional)
Maintenance

Therapy
Treatment Start Treatment End
Candidates of
early randomization
(1
st
randomization)
Candidates of
late randomization
(2
nd
randomization)

8

disease remission status, i.e. the most desirable outcome being complete remission
(CR) while the less satisfactory outcomes may include partial remission (PR) or no
remission (NR). Based on the types of diseases some clinical trials may categorize
clinical outcomes according to disease progression status, i.e. whether disease has
progressed (DP) or not (NDP) since the beginning of therapy sessions. Without
losing generality the first type of classification (CR vs. PR vs. NR) is employed in
describing eligibility for late randomization in this research.

Among eligible patients only those who consent to a late randomization will
be randomized to late therapies. As a result the actual enrollment in the second
randomization is a combined vector of both remission and consent status. Neither
ineligible patients nor unwilling patients will participate in the late randomization.
One of the primary and strong assumptions for two stage design models is that the
non-randomized group of patients will remain the same when the late treatment is
given in non-randomized fashion. This implies that in a hypothetical trial if one of
the late treatment regimens is specified for the second phase all the previously
randomized patients would receive, yet those previously non-randomized patients
in the late stage study will still not participate. In statistical terms we assume that
the combined remission and consent process is independent of the randomization
process. The above assumption determines the very nature of the ITT (Intent-to-
Treat) analysis in such a trial which will be explained in the following sections.

9

2.2 Two stage design randomized COG trials

The proposed research is motivated by two previously published COG
(Children’s Oncology Group) studies. Both COG studies employed the design of
two stage randomization featuring a late randomization. They illustrate two stage
design schema in randomized oncology clinical trials and in addition address the
complexity in conducting of actual trials.

The first COG study is a two stage design randomized trial primarily
investigating bone marrow transplantation as a new treatment approach in
consolidation phase of therapy for treating high-risk neuroblastoma among children
and adolescents (Matthay et al., 1999). Figure 3 describes the treatment regimen
sessions as well as the randomization process involved in this trial. During the trial
patients went through a series of clinical phases including initial treatment (five
cycles of chemotherapy, surgery, radiotherapy, bone marrow havesting),
continuation treatment (continuation chemotherapy or autologous bone marrow
transplantation), and maintenance treatment (13-cis-retinoic acid, no further
therapy). This particular trial involved two randomization processes. The first
randomization occurred prior to the third cycle of combination chemotherapy
during initial therapy phase to one of the consolidation treatments, autologous bone
marrow transplantation (BMT), the experimental treatment under study, or standard
treatment, continuation chemotherapy (Stage I). The second randomization for this

10

Figure 3 Treatment regimens for high-risk neuroblastoma among children and adolescences
(Source: Matthay et al., 1999)

11
trial occurred prior to maintenance therapy phase where patients without disease
progression after clinical assessment were randomized to either 13-cis-retinoic acid
maintenance therapy or no further therapy (Stage II). In this trial, for example, one
of the interesting treatment paths would be the BMT arm during Stage I and the
experimental 13-cis-retinoic acid arm during Stage II. Another important fact to
notice is that there were 379 patients enrolled in the first randomization yet only
258 patients enrolled in the second randomization and not all the loss in study
population was due to disease progression during Stage I.

The second COG trial was an international study of central nervous system
B non-Hodgkin lymphoma (B-NHL) and B acute lymphoblastic leukemia (B-ALL)
in children and adolescents (Cairo et al., 2007). B-ALL is considered as a subtype
of B-NHL in that both the prognostic profile and treatment strategy of B-ALL is
very similar to that of B-NHL. The B-NHL trial was a collaboration among three
international pediatric cancer groups CCG (Children’s Cancer Group), SFOP
(Société Française d’Oncologie Pédiatrique), and UKCCSG (United Kingdom
Children’s Cancer Study Group). As the standard combination chemotherapy in
treating B-NHL patients are often very toxic the primary goal of this trial was to
evaluate a reduced intensity version of FABLMB (French-American-
British/Lymphoma Malignancy B) as compared to the standard intensity version.
Figure 4 illustrates the flow of treatment regimen as well as the stratification and
randomization processes. This particular trial only has one randomization process.

12

Figure 4 Treatment regimens for Non-Hodgkin lymphoma and Acute
Lymphoblastic Leukemia among children and adolescents
(Source: Cairo et al., 2007)

13
Enrolled eligible patients were first stratified according to presence of CNS
disease (CNS+ versus CNS-). Prior to the randomization patients went through
three courses of initial and induction therapies (COP, COPADM1, COPADM2)
and possibly additional therapies based on their disease status (Figure 3). After
those cycles of therapy eligible and consented patients were randomized to either
standard or reduced intensity therapy under study (FAB/LMB96). During this
phase patients randomized to standard therapy were given two courses of
consolidation therapy (CYVE1, CYVE2) and four courses of maintenance therapy
(M1, M2, M3, M4). Patients randomized to experimental reduced intensity therapy
were given two courses of reduced intensity version of the standard therapy (mini-
CYVE1, mini-CYVE2) and only one course of maintenance therapy (M1). The
mini version of the standard therapy had lower dosage level and possibly shortened
cycle time. In addition patients in each of the strata and randomization arms were
administered slightly different therapies on top of their study therapies in order to
treat central nervous system (CNS) disease. In the B-NHL trial there was no clear
first and second stages. However because there was a late randomization occurred
after initial and induction therapies there were also patients who were enrolled in
the study who dropped out from the late randomization, which raised similar
questions as in a typical two stage design clinical trial and therefore for this trial
statistical issues in estimating survival for one of the randomization arms can be
addressed in a similar manner.

14
2.3 Study endpoints and ITT analysis in two stage design

A primary interest in two stage design randomized clinical trials is to
evaluate various treatment strategies and combinations of treatment options in
order to identify potentially the most beneficial treatment policy and possibly the
interactive effects between early and late treatments. The statistical analysis of
such studies should allow an informed decision being made regarding
recommendations of treatment strategy to clinical practitioners and to lay down
groundwork for future research.

The primary outcomes from a two stage design randomized clinical trial are
determined by clinical endpoints. Several types of clinical endpoints can be
assessed to evaluate treatment effects on survival. The most commonly used
survival outcomes include event-free survival (EFS) and overall survival (OS).
The EFS time is defined as time to event which may include death, secondary
cancer, disease progression, hospitalization, etc, as is defined in the study protocol.
The OS is a comparatively more general measure of survival and OS time is
defined as time to death due to any. Some clinical trials are more concerned with
progression-free survival (PFS), which is similar to EFS except that the specific
event of interest is related to disease progression. Disease Free Survival (DFS) is
also commonly considered where the disease defined in the study protocol is the
event of interest.

15
There are potentially three treatment strategies under study for a 2×2 two
stage design randomization schema as in Figure 1 based on patients’ remission and
consent status. Considering a certain treatment strategy such as B
1
during Stage II
the first treatment strategy would be regimen B
1
for patients who are assigned to
the designated treatment under study protocol. On the other hand the direct
opposing treatment strategy would be regimen B
2
for patients who are randomized
to this treatment arm. Aside from B treatment arms there are non-randomized
patients who do not participate in randomization to Stage II investigative agents by
study protocol. However in practice this group of patients may receive protocol
treatment or treatment that differs from protocol. The therapies non-randomized
patients receive can reflect both their prognostic characteristics and their decision
on randomization process. As a result the array of the treatments non-randomized
patients may receive is considered as “alternative treatment strategy” to be
distinguished from the protocol specific treatment assigned to Stage II
randomization participants.

By the spirit of the ITT analysis all patients assigned to study therapy
should be included in the ITT analysis of that treatment regimen regardless of the
actual therapy they receive. Due to the complexity associated with the late
randomization the nature of the intent-to-treat (ITT) analysis is broadened to better
model the study population in a two stage design randomized clinical trial. The
ITT analysis in a two stage design demands that when considering a certain

16
treatment arm not only patients who are assigned the stated policy are included in
the ITT analysis but the non-randomized group of patients due to remission and
consent processes should also be considered as part of the ITT study population. In
order to explain this concept suppose we discover that treatment B
1
is the better
treatment strategy in a theoretical design model such as the one in Figure 1. Under
such consideration treatment B
1
will be recommended to all patients at their Stage
II treatment cycle. According to the basic assumption of two stage design stated in
Section 2.1 the group of non-randomized patients will still be left out of the Stage
II treatment cycle. This is because first their prognostic state is not changed by B
treatment while for those who deny further treatment their concerns maybe are
regarding safety issues associated with B treatment rather than the randomization
process. Thus the “natural” study population at the late stage of a two stage design
randomized trial will include not only the patients randomized to the treatment of
interest but also those non-randomized patients. Accordingly the survival quantity
of interest would be to estimate survival among a risk population with a group of
non-randomized patients and patients who received the treatment of interest.

2.4 Types of study dropouts in two stage design

The broadened scope of the ITT analysis for two stage designs can also be
viewed through dropout process due to the late randomization. In a clinical trial
study the potential “dropouts” can be considered either “informative” or “non-

17
informative”. In the context of ITT analysis random dropouts are automatically
included in the study cohort and not to be confused with the concept of “dropout”
due to late randomization. Hence the types of “dropouts” we discuss below are
derived from a relative sense. Suppose in a 2×2 two stage design randomized trial
we are interested in treatment policy A
1
B
1
. At the late randomization the study
cohort under treatment arm A
1
branches out into three groups of patients. Patients
on treatment policy A
1
B
1
remain to be the interest of study. Both patients assigned
to A
1
B
2
and patients not randomized are considered “dropping out” of the study
cohort, however the nature of the dropout process is quite different for these two
groups and so is the consideration for inclusion. Patients in A
1
B
2
arm are dropped
out as a result of a randomization process and independence relative to study cohort
in treatment arm A
1
B
1
. This means that they do not contribute additional
information to the evaluation of various policies relative to policy A
1
B
1
and in fact
this group of patients will disappear if treatment B
1
proves to be superior and is
recommended to patients at Stage II in a non-randomization setting. As a result
they are considered “non-informative”. In statistical analysis they can be censored
at the time of “dropout” without distorting survival curve under study. In contrast
the survival profile of non-randomized patients can bear information on their
prognostic profile from early treatments, their concerns for Stage II treatments, and
most importantly the “alternative treatment strategy” the patients undertake. Thus
those “dropouts” are considered informative dropouts. In light of the various types
of dropouts introduced by the late randomization the ITT analysis of two stage

18
design needs to address theoretical means to handle each type of dropouts, i.e.
dropouts due to “wrong” randomized treatment assignment (policy B
2
as we are
considering policy B
1
), and dropouts due to the fact of having a randomization at a
late treatment cycle (non-randomized patients). The answer to this question lies in
the very nature of the dropping out process while the statistical consideration of this
issue motivates several types of survival estimators. The process of non-
informative dropouts is shown in Figure 5 assuming there are no non-randomized
patients. Figure 6 demonstrates the informative dropout process.

Figure 5 Non-informative dropouts process and censoring at Stage II
(assume there are no non-randomized patients at Stage II)
Non-informative dropout at Stage II
Stage I Stage II
B2 patients: censor at Stage II
A1
Event
Evaluation & 2
nd
randomization
B1 patients

19

Figure 6 Informative and non-informative dropouts at Stage II

2.5 Naïve Estimators

The Naïve Estimators are a direct implementation of the Kaplan-Meier
(KM) Estimator in two stage design studies. The first type of Naïve Estimator
(Naïve Estimator I) considers only the patient who are actually randomized to the
study arm of interest i.e. A
1
B
1
, to derive a survival estimate. According to this
approach both A
1
B
2
patients and non-randomized patients would be excluded from
study population after late randomization and in statistical terms they are censored
at Stage II. This consideration motivated the exploration in the neuroblastoma
Stage I Stage II
A1
Even Non-randomized
patients
Evaluation & 2
nd
randomization
B2 patients: censor at Stage II
B1
Non-informative dropout at Stage II
Potentially informative dropout at Stage II

20
COG trial (Matthay et al., 1999). The Naïve Estimator I assumes that the survival
among non-randomized patients is similar to that of patients under treatment B
1
and
it produces relatively reasonably sound estimate when this assumption holds true in
practical data. However as the clinical data deviates away from the model
assumption the Naïve Estimator is susceptible to potential biases. The Naïve
Estimator is shown in Figure 7.

In an effort to accommodate non-randomized patients at Stage II Naïve
Estimator II emerges as a quick “fix”. Due to the loss in study population at Stage
II once B
2
patients are censored the resulted study cohort during Stage II only
contains B
1
patients and non-randomized patients. Hence in this study cohort the
non-randomized patients are possibly over-represented while on the contrary the
information from B
1
patients is diluted due to crude inclusion of non-randomized
patients. Figure 8 demonstrate the censoring process in Naïve Estimator II.

21

Figure 7 Naïve Estimator: censor both B2 and non-randomized patients at Stage II

A1
Event
Evaluation & late randomization
Censored patients at Stage II
Stage I
Stage II
censor at Stage II
B1 patients Include in Stage II analysis
B2 patients
censor at Stage II
Non-randomized
patients

22

Figure 8 A naïve approach to censor B2 patients at Stage II and include non-randomized patients together
with B1 patients in the analytical study cohort
A1
Event
Censored patients at Stage
II
Stage
I
Stage II
Evaluation & late randomization

Include in Stage II
analysis
with 1:1 in proportion
censor at Stage II
B1 patients
B2 patients
Non-randomized
patients

23
2.6 Analytical Approach and IPW Estimator

Motivated by a two stage design randomized clinical trial on primary acute
myelogenous leukemia (AML) among elderly patients (Stone et al., 1995)
Lunceford et al. in 2002 paper (Lunceford, Davidian, & Tsiatis, 2002) proposed
adopting the inverse weight theory in the presence of “missing” data due to late
randomization (Robins, Rotnitzky, & Zhao, 1994). Based on this approach
(Analytical Approach) the weighting schema assigns a weight factor to each group
of patients at Stage II based on both their remission/consent status and Stage II
treatment assignment. The analysis led to a survival estimator that incorporates a
weight factor. We call this the IPW estimator. Given those weights the resulting
cohort would resemble the original study cohort as if there was no 2
nd

randomization. For example if the interest of the study is to estimate survival for
treatment policy A
1
B
1
this weighting schema weighs A
1
B
1
patients in reverse
proportion to their randomization probability so that they not only represent
themselves but also compensate for the loss of patients due to the “wrong”
treatment assignment, i.e. policy A
1
B
2
. Accordingly B
2
patients are given a weight
of zero which is equivalent to exclude them by censoring at the time of the second
randomization. In another look the loss due to excluding B
2
patients is thus
compensated by overweighing B
1
patients in the resulting cohort under the
weighting schema. In addition this approach assigns weight one to non-
randomized patients so that they only represent themselves in the analytical

24
survival cohort. Thus the inverse weighting schema generates a cohort that
contains the same number of patients with proper presentation of each group of
patients as in the ITT cohort. This weighting process of the IPW estimator is
shown in Figure 9.

From a first look the IPW Estimator bears little similarity to the Kaplan-
Meier Method. The implementation of the proposed variance estimate is extremely
complex in mathematical formulation and proves to be difficult to program in
application software. Therefore one of the secondary objectives in the proposed
research is to establish properties of IPW Estimator to allow better understanding.
Two properties are proposed for this estimator. Property I establishes connection
between IPW estimator and Kaplan-Meier estimator in a theoretical case when
there is no late randomization. A corollary derived from Property I is also given.
Property II establishes the relationship between IPW and Kaplan-Meier estimator
for a two stage design randomized clinical trial where there is no non-randomized
patients during Stage II randomization, i.e., everybody survives Stage I treatment is
eligible and consented to a late randomization. Collectively Property I and
Property II examine the relationship between IPW Estimator and Kaplan-Meier
Estimator. The detailed mathematical derivation can be found the in the Methods
Section.

25

Figure 9 Analytical Approach and IPW Estimator: assign various weights to patients and generate analytical
cohort based on weighing schema

Weight = 1
Weight = (1-π)
-1

Weight = 0
Include in Stage II
analysis
in proportion to weight
Stage II
Event
Evaluation & late randomization
B1 patients
B2 patients
Non-randomized
patients
π: observed B2 randomization probability
A1

26
2.7 Bootstrap Approach and the Proposed Estimator

Modern resampling methodology and technique provides a new angle to
examine the “missing data” problem present due to a late randomization in a two
stage design randomization setting (Efron, 1986). Similarly to the Analytical
Approach the Bootstrap Approach is geared to generate a “balanced” risk set as if
there was no “loss” of patients in study population after Stage II randomization.
The IPW Estimator relied upon the inverse weight theory and required
sophisticated mathematical framework to formulate the survival estimate and the
variance estimate. Comparable and improved results in handling distorted study
populations at Stage II can easily be achieved with the facilitation of the most
commonly used sampling methods in empirical research, i.e. the Bootstrap Process.
The bootstrap technique in handling two stage design analysis was briefly explored
in the advanced B-NHL COG trial (Cairo et al., 2007). The Bootstrap Approach is
intuitive in nature and is readily implemented in many statistical packages. The
potential drawback of using bootstrap process is that it typically involves intense
computer time and may drastically increase the run time. However the overall gain
from adopting an intuitive bootstrap based model may potentially outshine the
downside of consumption of computational resource. What’s more with drastic
improvement in computer processors the actual time involved in using bootstrap
may be negligible in most situations, which makes the method a desirable
alternative to the Analytical Approach.

27
The bootstrap process involves random sampling with replacement. This
process draws random subjects one by one from the original sample, and after each
drawing the subject selected is put back in the dataset to be available for next
drawing. The sampling process is repeated for a large number of iterations and
various statistical estimates can be drawn from the resulting bootstrap samples.
Grounded in this line of work we propose a type of survival estimator that utilizes
the bootstrap process as one of the key steps to achieving a “balanced” risk set for
estimating survival for treatment policy A
j
B
k
, j, k = 1,2. The Bootstrap Approach
incorporates information from non-randomized patients. Figure 10 illustrates using
the bootstrap process to replace the “missing” values after a late randomization.

2.8 Global Test

The ultimate goal of the ITT analysis is to compare the various treatment
combinations and identify the potentially most beneficial treatment strategy. For a
two stage design randomized clinical trial with two randomizations (early
randomization and late randomization) a global test based on a Wald test statistic
can be constructed given the proper estimation of the variance-covariance matrix.
The global test helps to identify any heterogeneity across all treatment arms. For
trials with only a late randomization but no early randomization such as the B-NHL
trial the comparisons of treatment strategies can be compared similarly using the
global test. Or for this particular case log-rank test can take place of global test.

28

Figure 10 Bootstrap Approach and Proposed Estimator for one bootstrap loop
Event
Evaluation & late randomization

Include in
Stage II
analysis
Non-randomized
patients
A1
Stage I
Stage II
Bootstrapped
sample to replace
B2 patients
B1
patients
B2
patients
Bootstrap
Process
Exclude from study
population
29

2.9 Summary

The proposed study formulates three types of survival estimators for a two
stage design randomized clinical trial. In addition the proposed study formulates the
variance estimate of each of the survival estimator. Chapter 3 presents the model
formulation as well as the properties of each of the survival estimators as well as the
variance estimate.

In order to compare the reliability and efficiency of each of the survival
estimates a series of simulation studies are conducted and the results are shown in
Chapter 4. The “best” survival estimate is identified and the recommendation is
applied to reanalyze the two COG trials in Chapter 5. Chapter 6 addresses statistical
modeling issues related to the Global Test Statistic. Chapter 7 summarizes the study
findings and discusses the strength and limitation of each of the methods. In addition
further research areas are identified and briefly discussed in the last chapter. All the
statistical analyses in this proposed research are conducted in SAS 9.1 (Cary, NC).

30

Chapter 3: Methods and Survival Estimators

In this chapter we formulate model frameworks for the three types of
survival estimators discussed in the previous chapter. First of all fundamental
concepts of the Kaplan-Meier method are briefly reviewed as it serves as the basis
and foundation for more sophisticated modeling. The Naïve Estimators are a direct
application of a modified version of the Kaplan-Meier Estimator, thus the model
formulation of the Naïve Estimators as well as a proposed variance estimate using
the Greenwood formula is presented following the theoretical review. Due to its
lack of consideration for the non-randomized patients in a two stage design the
Naïve Method can not be used for the ITT analysis in such design. The first
method that addresses the issues in the ITT analysis is the Analytical Approach,
i.e., the IPW Estimator. Given the complex nature of the IPW Estimator two
mathematical properties are derived that establish the connection between IPW
Estimator and the Kaplan-Meier Estimator. The second estimator suitable for ITT
analysis is given based on the proposed conceptual framework which uses the
bootstrap process to impute “missing” values due to late randomization. The
formulation of the variance estimate is also provided for the Bootstrap Estimator.
Finally a bootstrap variance is proposed to estimate variance for the IPW Estimator.

31

3.1 Basic assumptions and common notations

For the purpose of this study we consider a 2×2 two stage design with two
randomization processes involving treatment regimens A and B for Stage I and
Stage II respectively and each with two treatment levels under study, level 1 and 2
(as shown in Figure 1). Under this setting eligible and consented subjects are first
randomized to one of the A treatment levels, A
j
, j = 1, 2, followed by a late
randomization to B policies, B
k
, k = 1, 2, upon clinical evaluation and consent
status. Given the randomization process study population assigned to treatment A
j
,
j = 1, 2, are independent samples hence the process to estimate survival for the
study population under treatment assignment A
1
can be easily generalized to that
under treatment assignment A
2
and vice versa. Therefore for simplicity we restrict
our consideration for estimating survival to one of the A treatment policies A
1
while the formulation of the survival estimators can be derived similarly for policy
A
2
.

In practice the randomization to B treatment is usually blocked within each
A treatment level and the randomization schema for B assignment is typically the
same for each A treatment level. Given those considerations it is conceivable to
model survival under one of the four potential treatment polices A
j
B
k
, j = 1, 2, k =
1, 2, while the results can be generalized to the rest of the treatment policies in a
similar manner. Combined with our choice in A treatment our efforts in studying

32

survival distribution is restricted to treatment A
1
and more specifically using

A
1
B
1

as an example to formulate various types of survival estimates. Under treatment A
1

the derivation of model framework of policy A
1
B
1
can be expanded to treatment
combination A
1
B
2
in a parallel fashion.

There are several types of survival endpoints as that were introduced in the
previous chapter. In this study we intend to model either OS (overall survival) or
EFS (event-free survival) as study interest while the other study endpoints can be
modeled accordingly. Under such consideration the event of interest is death (or
occurrence of any events) due to disease under study. The death/event time is
denoted by T
i
for patient i and defined as time to death/event from enrollment. The
censoring time C
i
is defined as time to administrative censoring (end of study
without death) from enrollment.

The two stage design modeling assumes that the same group of patients will
remain in the non-participants group regardless of late stage randomization. This
also implies that the proportion of patients will remain the same in the study cohort
whether the late treatment is given by randomization or in non-randomized fashion.

Suppose treatment policy A
1
B
1
being the potentially beneficial treatment
option. Let T be overall time since the beginning of trial, T
I
be Stage I time and T
II

be Stage II time. In addition let S
1
(T
I
) be Stage I survival probability for treatment

33

A
1
, and let S
10
(T
II
) and S
11
(T
II
) be the conditional survival among non-randomized
patients and policy A
1
B
1
patients during Stage II. Also let θ represent the
proportion of patients who are not randomized for Stage II treatments among
patients who survive under Stage I treatment. Using the above definitions the
quantity of interest S under ITT framework could be expressed in the following:
) ( ) 1 ( ) ( [ ) ( ) (
11 10 1 II II I
T S T S T S T S × − + × × = θ θ (3.1.1)

3.2 Kaplan-Meier Estimator and Greenwood Formula

The Kaplan-Meier method is most commonly employed in the presence of
censored survival type of data. Consider treatment arm A
1
B
1
. Suppose we had
ordered event time t
0
, t
1
, …, t
i
, … for patients in this group. Let n
i
be the
corresponding number at risk at time t
i
and d
i
be the number of events occurred at
time t
i
. Given this notation the Kaplan-Meier survival estimate ( )
KM
S t
)
at time t for
treatment arm A
1
B
1
is given by:
( )
i
i i
KM
t t i
n d
S t
n
≤
−
=
∏
)
(3.2.1)

The Greenwood formula for the variance estimate of ( )
KM
S t
)
is given by:
C
) ) )
t t i i i
i
KM KM
i
d n n
d
t S t S ar V
≤
−
× =
) (
) ( )) ( (
2
(3.2.2)

34

3.3 Naïve Estimators

Using treatment policy A
1
B
1
as an example both Naïve Estimator I and II
first computes Stage I survival probabilities under treatment policy A
1.
The
conditional survival probability for a given B treatment arm during Stage II is
estimated conditional on previous treatment A
1
. Hence the overall survival
probabilities can be estimated by multiplying the conditional survival probability
and the corresponding prior survival probability during Stage I. This estimate can
be derived by censoring the patients not randomized to the B
1
arm at Stage II. The
difference between Naïve Estimator I and Naïve Estimator II is whether to censor
the non-randomized patients at the end of Stage I. Naïve Estimator I chooses to
exclude this group of patients by censoring them yet Naïve Estimator II chooses to
keep them in study population until event or actual censoring.

If we use this method to estimate the survival quantity in (3.1.1) the results
are biased in most cases unless the following assumption is valid. The additional
assumption states that given treatment A
1
the survival of non-randomized patients
is the same as that for B
1
patients.

Given the 2×2 model under treatment A
1
there are three groups of patients
with different protocol treatment assignments or no protocol treatment at the time
of Stage II randomization, namely, A
1
B
1
patients, A
1
B
2
patients, and non-

35

randomized patients. Let X
i
be A treatment assignment indicator where X
i
= j-1
corresponds to randomization to A
j
, j = 1,2 for the first randomization at Stage I.
Let R
i
denote the remission/consent status of subject i for the second randomization
with R
i
= 0 indicating no remission or consent and R
i
= 1 if remission and consent.
Furthermore let Z
i
be the B treatment indicator where Z
i
= k-1 corresponds to
randomization to B
k
, k = 1, 2, for the 2
nd
randomization at Stage II and Z
i
is only
defined for R
i
= 1. Let t
SI
be Stage I follow-up time from time of enrollment.

Given the above definitions the Stage I survival for all A
1
patients is
estimated by Kaplan-Meier method and denoted by ) 0 | (
ˆ
= X T S
I prior
. The
conditional survival probability for A
1
B
1
patients at time T
II
from the start of Stage
II is estimated among A
1
B
1
patients using Kaplan-Meier method and denoted by
) 0 , 0 | (
ˆ
= = Z X T S
II StageII
for Naïve Estimator I and ) 1 , 0 | (
ˆ
≠ = Z X T S
II StageII
for
Naïve Estimator II. Then the survival estimate using Naïve Estimator I &
II, ) (
ˆ
T S
NVI
and ) (
ˆ
T S
NVII
for treatment policy A
1
B
1
at time T is given by the
following:
) (
ˆ
T S
NVI
= ) 0 | (
ˆ
= X T S
I prior
× ) 0 , 0 | (
ˆ
= = Z X T S
II StageII
(3.3.1)
) (
ˆ
T S
NVII
= ) 0 | (
ˆ
= X T S
I prior
× ) 1 , 0 | (
ˆ
≠ = Z X T S
II StageII
(3.3.2)

Here time variables t, t
SI
, and t
SII
satisfied the following constraint:
II I
T T T + = (3.3.3)

36

In practice Stage I time T
I
needs to be estimated. Algorithm I shows an
alternative approach to implement Naïve Estimators, which gives more accurate
estimates compared to the survival probabilities estimated using formula (3.3.1)
and (3.3.2). In addition this approach provides a way to estimate variance using
Greenwood formula for the survival estimates.

Algorithm I:

1a). Censor A
1
B
2
patients at Stage II randomization time (Z
i
= 1);
1b). Censor non-randomized patients at the end of Stage I (R
i
= 0);
2a). Naïve Estimator I: Among A
1
patients use Kaplan-Meier method
(3.2.1) to estimate survival probability under policy A
1
B
1
and the
Greenwood formula (3.2.2) to estimate variance for the survival estimate;
2a). Naïve Estimator II: Skip Step 1b), among A
1
patients use Kaplan-Meier
method (3.2.1) to estimate survival probability under policy A
1
B
1
and the
Greenwood formula (3.2.2) to estimate variance for the survival estimate.

3.4 Analytical Approach and IPW Estimator

The IPW Estimator was proposed by Lunceford, Davidian, & Tsiatis
(2002). As discussed previously we have treatment policies A
j
and B
k
for Stage I
and Stage II randomizations respectively, where j, k = 1,2, indicating two levels for

37

each treatment under study. In addition we assume there are n subjects randomized
to treatment policy A
1
and all the notations as well as the entire model formulation
are developed solely for subject i under treatment A
1
where i = 1,2,…n. With slight
modification of the indices, the entire model framework for A
1
B
1
can be easily
transformed to estimate survival for treatment combinations under A
2
for that
matter. The randomization and remission/consent indicators X
i
, R
i
, and Z
i
are
similarly defined as for Naïve Estimator for each patient i, i = 1,2,…n.

The IPW Estimator requires the following model assumptions: 1) the
potential remission/consent status R
i
is a function of A treatment levels only and
not dependent upon the subsequent B treatment levels; 2) the potential survival
time T
i
for subjects who do not remit or consent, R
i
= 0, do not depend upon
subsequent B treatment assignment they would have if randomized; 3) time to
censoring C
i
is independent of remission/consent status R
i
, B treatment assignment
B
k
with indicating variable Z
i
= k-1, k = 1,2, or subject i’s potential survival time T
i

under A treatment assignment A
j
with indicator X
i
= j-1, j = 1,2; 4) conditional on
R
i
= 1 (subject remits and consents to Stage II randomization) and A treatment
assignment indicator X
i
= j-1, j = 1,2, B treatment randomization indicator Z
i
is
independent of potential survival time under B
k
, k = 1,2.

38

Given C
i
to represent time to censoring the censoring distribution is allowed
to differ by A treatment and is denoted by . 2 , 1 ), 1 | ( ) ( = − = > = j j X t C P t K
i i j

Use T
i
to represent the observed survival time for each patient i, i = 1,2,…n, then
the censoring indicator is denoted by ) (
i i i
C T I < = Δ , while the observed event or
censoring time is given by ). , min(
i i i
C T V = At the presence of censoring the
remission/consent status indicator R
i
is arbitrarily set to 0 if subject i is censored
prior to reaching the remission evaluation point. Treatment B randomization
probability is defined as ) 1 | 1 ( = = =
i i z
R Z P π . In practice the randomization
probability is based on an empirical value rather than a theoretical value.

The critical variable in the IPW Estimator formulation is the “weight” for
each group of patients after the second randomization, which is defined for each B
treatment level and given by ) 1 ( ) 1 ( 1
1
i i z i ki
Z R R Q − − + − =
−
π for k = 1, 2.
Considering Q
1i
for treatment policy A
1
B
1
for subjects randomized to A
1
B
2
, i.e., R
i
= 1, k = 2 implying Z
i
= 1, according to the definition, Q
1i
reduces to 0 in this case.
Subjects who do not remit or consent, i.e., R
i
= 0, represents themselves and thus
Q
1i
= 1. Subjects whose randomization is consistent with A
1
B
1
, i.e., R
i
= 1 and k=1
equivalent to Z
i
= 0, are over represented in the resulting risk set in order to
compensate for the loss of population due to randomization to B
2
and thus their
weight is inversely proportional to their randomization probability and given
by
1
1
) 1 (
−
− =
z i
Q π .

39

Finally let ( )
IPW
S t
)
denote the survival estimate under policy A
1
B
1
. Then
the survival probability satisfies ( ) 1 ( ) 1 ( )
IPW i IPW
S t P T t F t = − ≤ = −
) )
. The above
considerations motivate the estimator (Lunceford, Davidian, & Tsiatis, 2002):
1 1
1
( ) 1 ( ) 1 ( )
ˆ
( )
n
i i
IPW IPW i
i
Q
S t F t n I V t
K V
−
Δ
= − = − ∑ ≤
) )
(3.4.1)

for k = 1, 2, where
∏
≤
− =
t u
c
i
u Y u dN V K )} ( / ) ( 1 { ) (
ˆ
is the Kaplan-Meier estimate
of the censoring survivor function. Here
∑
=
= Δ ≤ =
n
i
i i
c
u V I u N
1
) 0 , ( ) ( and
the survivor indicator at time u is denoted by ) ( ) ( u V I u Y
i
≥ = .
The variance estimator for the IPW survival probability is given by:
1 1 2 2 1
4 11
1
0
( )
ˆ ˆ ˆ ˆ
( ( )) ( ) ( ) { ( , )}
ˆ ˆ
( ) ( ) ( )
L c
n
i i
IPW i i
i
Q dN u
Var S t n n I V t F t E L t u
K V K u Y u
− −
 
Δ
= ∑ ≤ − +
 
 
∫

(3.4.2)

where
∑
=
−
≥
× − ≤ Δ =
n
i
i
i
i i i i
V K
t V I
u t G t V I Q n u t L E
1
2
11 1
1 2
11
) (
ˆ
) (
)} , (
ˆ
) ( { )} , ( {
ˆ
, and
∑
=
−
≥
× ≤ Δ =
n
i
i
i
i i i
V K
t V I
t V I Q u S n u t G
1
^ 1
1
11
) (
) (
) ( )} (
ˆ
{ ) , (
ˆ
in which ) (
ˆ
u S is the Kaplan-
Meier estimator for P(T > u).

40

3.5 Properties of IPW Estimator

Property I: In a single stage randomized clinical trial as in a regular
clinical trial design where the randomization is upfront and all eligible and
consented patients are randomized to one of the trial policies IPW Estimator
provides equivalent survival estimate for each treatment arm compared to that by
the Kaplan-Meier estimator.

Proof: For simplicity we assume there are only two treatment polices
under study in such a trial (denoted by A
1
or A
2
). Given the stochastic nature of the
randomization process the proof for each of the treatment arms is the same for each
of the treatment arms thus in following proof we use policy A
1
as an.

First we suppose there are a total of n subjects randomized to treatment
policy A
1.
In such a trial all eligible and consented patients are randomized and
there are no informative dropouts associated with the randomization process.
Under such setting the weighting factor Q
1i
is reduces to 1 for all n subjects
randomized to treatment policy A
1
and becomes 0 for all subjects randomized to
the “wrong” treatment arm A
2
. Substituting value 1 for Q
1i
in the IPW Estimator
for treatment arm A
1
we have the following:

41

1 1
1
1
1
1
1
( ) 1 ( )
1 ( )
ˆ
( )
1 ( )
1
ˆ
( )
( )
1
ˆ
( )
IPW IPW
n
i i
i
i
n
i i
i
n
i i
i
S t F t
Q
n I V t
K V
I V t
n
K V
I V t
n
K V
−
−
−
= −
Δ
= − ∑ ≤
Δ × × ≤
= − ∑
Δ ≤
= − ∑
) )
(3.5.1)

In order to prove that the IPW Estimator is equivalent to Kaplan Meier
Estimator under assumptions of Property I we consider the following two
theoretical : 1) consider an ideal situation with no censoring process; and 2)
consider an artificial situation with only censoring process and no events. For a
regular survival curve can be easily dissected into small time intervals of either one
of the above scenarios thus combining findings from above scenarios and using the
multiplicity of the conditional survivals we can prove the Property holds true for
the entire survival curve.

Theoretical scenario 1) assumes a survival distribution with no censoring.
Under such conditions both the censoring indicator
i
Δ and the censoring survivor
estimate ) (
ˆ
i
V K becomes 1 by definition. In addition the variable minimum time to
event or censoring
i
V becomes purely event time
i
T . Hence the survival described
in (3.5.1) further simplifies to:

42

1
1
1
1
1
1
( )
( ) 1
ˆ
( )
1 ( )
1
1
1 ( )
n
i i
IPW
i
n
i
n
i
I V t
S t n
K V
I T t
n
n I T t
−
−
−
Δ ≤
= − ∑
× ≤
= − ∑
= − ∑ ≤
)
(3.5.2)

Here the summation term ) (
1
t T I
i
n
≤ ∑ is summing across subjects with
events up to time t and essentially summing number of events occurred up to time t.
Let t
i
be the i
th
event time and d
i
be number of events occurred at this time point.
The summation term in equation (3.5.2) can be expressed using the ordered time
notation as below:
1
1
1
ˆ
( ) 1 ( )
1
i
n
IPW i
i
t t
S t n I T t
n d
−
−
≤
= − ∑ ≤
= − ×
∑
(3.5.3)

Define
t
d be the total number of the events up to time t, i.e.
i
i
t t
d
≤
∑
.
Substitute in
t
d in equation (3.5.3) and we have the following:
1
1
ˆ
( ) 1
1
1
i
IPW i
t t
t
t
t
S t n d
n d
d
n
n d
n
−
≤
−
= − ×
= − ×
= −
−
=
∑
(3.5.4)

43

The derived survival in (3.5.4) is evidently the same as the survival estimate
using Kaplan-Meier estimator for a survival curve with no censoring. Through
equations (3.5.1) to (3.5.4) we show that Property I holds true for a survival curve
with no censoring over time interval [0, t]. In survival analysis we assume that the
conditioning on survival at time t the conditional survival probability is
independent of the survival prior to time t. Thus if any time interval [t, t + Δt]
satisfies scenario 1) then the above proof can be extended for the conditional
survival.

In order to prove scenario 2) we consider a survival time interval (t
c
, t
c
+ Δt]
during which are no events but only censoring. In addition from time 0 up to time
t
c
, the survival meets scenario 1). For this situation given that the Kaplan-Meier
Estimator only concerns event times the survival probability estimate using the
Kaplan-Meier method at time t
c
would remain unchanged through time t
c
+ Δt.
This also implies that the conditional survival probability given survival up to time
t
c
over (t
c
, t
c
+ Δt] is 1.

In the IPW Estimator the censoring indicator
i
Δ is 0 for the censored
subjects, which implies that censored subjects do not contribute to the summation
term in (3.5.1). Thus the IPW survival probability estimator at time t
c
remains the

44

same throughout time t
c
+ Δt. This in addition implies that the conditional
probability over (t
c
, t
c
+ Δt] given survival up to time t
c
is 1 under the IPW
Estimator. The mathematical proof is given in the following sections.

Using the ordered time notation the Kaplan-Meier survival estimate from
time 0 till t + Δt can be expressed as a product of the survival estimate up to time t
c

and the conditional survival over time period (t
c
, t
c
+ Δt]. Combining our previous
arguments and substitute in 1 for the conditional survival over censored time we
thus have the following equation:

0
( )
1 1 ( )
i c c c i c c c
i c c c i c i c
i i i i i i
KM c
t t t t t t t t t t t t i i i i
i i i i i i
KM c
t t t t t t t t t t i i i
n d n n d n
S t t
n n n n
n d n d n d
S t
n n n
≤ ≤ < +Δ ≤ ≤ < +Δ
≤ ≤ < +Δ ≤ ≤
− − −
+Δ = × = ×
− − −
= × = × = =
∏ ∏ ∏ ∏
∏ ∏ ∏ ∏
)
)

(3.5.5)

Similarly the IPW survival estimate will also remain the same over this
particular time interval as shown below using the ordered survival time notation:

45

1 1
1
1 1
1 1 1
1 1 1
1 1
( ) 1 ( )
ˆ
( )
1
ˆ
( )
1
ˆ ˆ
( ) ( )
0
1
ˆ ˆ
( ) ( )
1 0
ˆ
( )
c
c c c
c c c
c
n
i i
IPW c i c
i
i i
t t t
i
i i i i
t t t t t t
i i
i i i
t t t t t t
i i
i i
t t
i
Q
S t t n I V t t
K V
Q
n
K V
Q Q
n
K V K V
Q Q
n
K V K V
Q
n
K V
−
−
≤ +Δ
−
≤ ≤ ≤ +Δ
−
≤ ≤ ≤ +Δ
−
≤
Δ
+Δ = − ∑ ≤ +Δ
Δ
= − ∑
 
Δ Δ
= − ∑ + ∑
 
 
 
Δ ×
= − ∑ + ∑
 
 
 
Δ
= − ∑ +
 
 
)
1 1
1 ( )
ˆ
( ) c
i i
IPW c
t t
i
Q
n S t
K V
−
≤
Δ
= − ∑ =
)
(3.5.6)

So far we have shown that the IPW and the Kaplan-Meier Estimators
produce the same results for scenario 1) type time interval with only events and no
censoring. Here we have also shown that the conclusion remains true to a scenario
2) time period following a scenario 1) time interval. In summary the two
estimators yield the same estimate for time interval with events followed by
censoring.

Given the conditional independence of the survival distribution we can
break down the entire survival curve into many intervals as described above and the
overall survival probability can be estimated by the product of the conditional
survival estimate over those intervals. As we proved that the IPW estimator gives
the same results as Kaplan-Meier estimator does on each of the described intervals
we can infer that overall the two estimators give the same estimates for the entire

46

survival distribution. A natural extension of Property I leads to Corollary I as
summarized below.

Corollary I: Property I is not only true for the survival estimates for a
regular randomized clinical trial but also holds true for the conditional survival
estimates for a late randomization.

Property II: In an ideal two stage design randomized clinical trial there are
no informative dropouts during clinical evaluation and Stage II randomization
processes. This implies that all patients survived Stage I are both eligible and
randomized to one of the Stage II treatment policies. In this ideal setting the IPW
Estimator for a specific treatment policy produces the same survival estimate as the
Kaplan-Meier Estimator.

Proof: Based on similar argument it suffices to limit the considerations to
one of the treatment combinations A
1
B
1
. Let S
1
denote the survival estimate for
Stage I and S
11
be the conditional survival estimate for treatment policy A
1
B
1

during Stage II given S
1
. Thus the survival estimate over both stages denoted by
S(t) is given by the following:
11 1
) ( S S t S × = (3.5.7)
This formula hints that to prove that Property II holds true for S(t) we
merely need to prove IPW and Kaplan-Meier Estimator are equivalent for both S
1

47

and S
11
respectively. It is obvious that Stage I randomization process satisfies the
ideal setting as described in Property I. According to that the resulting survival
estimate S
1
during Stage I is the same from either IPW Estimator or Kaplan-Meier
Estimator.

Given that there is no randomization dropout associated with Stage II
randomization there are only two valid values for weight Q
1i
in the IPW Estimator,
either 1/(1-
z
π ) for the subjects randomized to study treatment policy A
1
B
1
or 0 for
subjects randomized to “worng” policy A
1
B
2
.

It is evident that conditional on Stage I survival S
1
Stage II randomization
process meets the ideal setting as described by Property I. Therefore we can apply
Property I to the survival estimate resulting from Stage II randomization (Corollary
I). This suggests that the conditional probability S
11
estimated by IPW Estimator
conforms to that by Kaplan-Meier Estimator.

Combining the conclusion for S
1
and S
11
we conclude that Property II holds
true for the overall survival S.

48

3.6 Bootstrap Approach and Proposed Estimator

A late randomization at Stage II in a two stage design randomized clinical
trial causes distortion of data proportion in each of the treatment arms due to the
loss of patients assigned to the “wrong” treatment policy. If we analyze a certain
treatment arm from the late randomization and include all patients then patients
assigned to the “wrong” arm would have missing values for the given treatment
policy. Thus the major issue to face when estimating survival is to handle the
“missing” data problem such that in the analytical risk set all patients will be
properly represented. The essential question is to make up for the number of
patients lost due to “wrong” treatment assignment. In order to achieve a balanced
dataset we resort to the resampling technique and propose using a “hybrid”
bootstrap to sample from “valid” non-missing data to replace the “missing” values.

The hybrid bootstrap process is demonstrated using treatment policy A
1
B
1

as an example. In order to estimate survival for policy A
1
B
1
patients assigned to
policy A
1
B
2
are excluded from study cohort and considered “missing”. Thus to
make up for the missing data and generate a cohort resembling the original sample
space with a balanced proportion we select bootstrapped sample from patients
assigned A
1
B
1
to replace A
1
B
2
patients. The bootstrapped dataset is combined with
the dataset excluding patients assigned to policy A
1
B
2
.

49

The bootstrap process in the proposed method can be better explained with
a numeric example. Suppose there are m (
1 2 ntx
m m m m = + + ) patients under
treatment A
1
reached Stage II and this risk set is denoted by R
1
. At the second
randomization let
1
m be number of patients randomized to A
1
B
1
and name this risk
set R
11
. Let
2
m be the number of patients randomized to A
1
B
2
and denote this risk
set by R
12
. Last but not least let
ntx
m be the number of patients who do not
participate in the second randomization and name this risk set R
1ntx
.

At Stage II the
2
m patients randomized to A
1
B
2
in risk set R
12
are excluded
from the analytical cohort. As a result there are
2
m patients with missing values.
The bootstrap process samples from the
1
m patients in risk set R
11
to replace
2
m missing values. Thus a total number of
2
m patients are drawn one at a time with
replacement from the risk set R
11
. The bootstrapped risk set with
2
m patients is
represented by R
12boot
. The analytical cohort after the bootstrap comprises risk sets
R
11
, R
1ntx
, and R
12boot
. The total number of patients in this analytical risk set
remains
1 2 ntx
m m m m = + + as in the original risk set R
1
. The resulting analytical
risk set includes the A
1
B
1
patients, the non-randomized patients at Stage II and the
bootstrapped patients replacing the A
1
B
2
patients.

50

To increase precision in estimation the single bootstrap process is repeated
for a total of B = 300 times. For each replicate a Kaplan-Meier survival estimate
and its Greenwood variance estimate can be calculated using formulas (3.2.1) and
(3.2.2). For replicate i, i = 1,2, …, B, denote the Kaplan-Meier and Greenwood
variance estimates by
_ _
( ) ( ( ))
km i km i
S t and V S t
) ) )
respectively. Hence the propose
survival estimate using the Bootstrap Approach can be expressed as following:
_
1
1
( ) ( )
B
boot km i
i
S t S t
B
=
=
∑
) )
(3.6.1)

The variance estimate of the Proposed Estimator is derived in similar
fashion as the variance for multiple imputation. Basically the variation roots from
two major sources: first the within bootstrap variation, and secondly the between
bootstrap variation (Rubin, 1996). In the case of survival data the within bootstrap
variation can be estimated using the Greenwood formula for each bootstrap
iteration denoted by )) ( (
_
t S V
i km GW
) )
. Following that the overall within bootstrap
variation is shown below:
∑
=
=
B
i
i km GW WI
t S V
B
V
1
_
)) ( (
1
) ) )
(3.6.2)

The between bootstrap variation is considered across the B bootstrap
replicates and is essentially the bootstrap variance as the following:
2
_
1
)) ( ) ( (
1
1
t S t S
B
V
boot i km
B
i
BI
) ) )
−
−
=
∑
=
(3.6.3)

51

The formula in (3.6.2) would suffice as an estimate for within bootstrap
variation if the dataset comprises of independent data points. However due to the
hybrid nature of the bootstrap used in this particular situation after each bootstrap
loop the resulting survival cohort is somewhat correlated with many ties. In this
situation the Greenwood variance tends to underestimate (Eriksson & Adell 1994).
Accordingly the Greenwood variance needs to be adjusted to account for extra
dispersion. The adjusted Greenwood variance is given in below for each loop i:






+
−
=










−
=
∑
∑
∑
)
2
1 (
) (
) (
) (
) ( )) ( (
2
_
2
2
_ _ _
l
ol
t l l l
l
i km
l
o
ol
t l l l
l
i km i km ADJ GW
n
n
d n n
d
t S
n
n
d n n
d
t S t S V
l
l
)
) ) )
(3.6.4)

Here let n
lo
represent number of ties in cluster o at time l, while o = 1,…,O
be the indices for clusters of ties due to combining bootstrapped sample from A
1
B
1

patients with data containing original A
1
B
1
patients. Thus the within bootstrap
variance is captured in expression (3.6.5):
∑
=
=
B
i
i km ADJ GW WI
t S V
B
V
1
_ _
)) ( (
1
) ) )
(3.6.5)

52

Combining all the above considerations the variance estimate associated
with the survival estimate ) (t S
boot
)
is the total variance:
BI WI boot
V
B
V V
) ) )
)
1
1 ( + + = (3.6.6)
The described method and estimator is summarized in the Algorithm II.

Algorithm II:

1. Exclude A
1
B
2
(n = m
2
) patients from analytical cohort;

2. Randomly draw a sample of m
2
patients with replacement (bootstrap
process) from m
1
A
1
B
1
patients;
3. Combine patients drawn from Step 2 and analytical cohort from Step 1;
4a. Estimate survival probability for cohort formed in Step 3 using Kaplan-
Meier Estimator (3.2.1);
4b. Estimate within bootstrap variance for the survival estimate in 4a by
using adjusted Greenwood formula (3.6.4);
5. Repeat the process stated in Step 1 – Step 4b by a total of B (e.g. B =
300) times;
6. Estimate between bootstrap variance across the B iterations (i.e. bootstrap
variance) (3.6.3);
7. Estimate survival estimate and its variance estimate using formula (3.6.1)
and (3.6.6).

53

3.7 Modified IPW Estimator

The Analytical Approach provides a variance estimate for the IPW
Estimator (3.4.2). However the mathematical nature of the formula makes it
difficult to implement and realize in application software. In addition simulation
studies suggest that this variance estimate can be biased when informative dropouts
are abundant at Stage II. The situation calls for the development of a more reliable
and unbiased variance estimate for the IPW Estimator. Given the simplistic nature
here we propose using the bootstrap process to derive a variance estimate.

The bootstrap variance estimate of the survival estimate of treatment policy
A
1
B
1
using the IPW Estimator can be computed through the following algorithm:

Algorithm III:

1. Estimate survival probability ) (t S
IPW
)
for policy A
1
B
1
using the IPW
Estimator on the original study cohort;
2. Generate B (e.g. 300) bootstrap samples from study cohort under A
1
;
3. Use IPW Estimator to estimate survival for each of bootstrapped
samples, denote the estimate for the l
th
sample by ) (
_
t S
l IPW
)
, l = 1, …, B;
4. Estimate variance of survival estimate (bootstrap variance) ) (
1 _
t S
IPW
)
,
… ) (
_
t S
l IPW
)
, … ) (
_
t S
B IPW
)
and obtain variance estimate )) ( ( t S ar V
IPW
) )
.

54

Chapter 4: Simulation Studies

To effectively assess and compare the performance of the existing and
proposed survival estimators a series of Monte Carlo simulation studies are
designed and have been carried out. In this chapter we describe the parameter
settings for various simulation studies. In addition we present the results and
findings from each simulation. To keep in line with model framework for survival
estimators we assume a 2×2 design using the same notations as in previous
chapters. The simulated data is generated for treatment policy A
1
and the survival
probabilities are estimated using each estimator for treatment arm A
1
B
1
as an
example while the simulation can be easily repeated for other treatment arms and
the results can also be generalized.

The objectives of the simulation study are threefold for survival estimators.
First we compare four survival estimators for a common clinical setting to
investigate their performance and bias. Then considerations regarding different
randomization schema and heavy tail model are incorporated to test the behavior of
the estimators under more extreme situations and for different survival models.
Additional simulations are also conducted to look into the proposed bootstrap
variance estimate for the IPW Estimator.

55

4.1 Simulation considerations for comparing survival estimators

The simulated data mimics a trial with a 5-year recruiting period and a 2-
year follow-up time, which is a typical setting in a two stage design oncology trial.
Let T
SI
be the time from enrollment to the end of Stage I. In reality this parameter
would vary from patient to patient, i.e. a random variance. For simplicity and
without compromising the rigidity of the simulation design we force this variable to
be a constant for all patients, i.e. T
SI
= 4 months. To further tighten and simplify
the simulation process we assume that there is no time lag between the end of Stage
I and Stage II randomization while in reality there is normally a time span between
these two time points for clinical assessment, informed consent, patients contact,
etc. Based on the time frame the censoring process C
i
(t) is drawn from a Uniform
distribution, i.e. Uniform [2, 7]. For the failure process we use the most commonly
studied exponential distribution for event time for both Stages and for all clinical
groups despite of their varied prognostic profile and treatment strategies. The
choice of using exponential survival time distribution would not compromise the
interpretability of the simulation studies.

The simulation studies are conducted for both large and small sample sizes,
where the latter one has not been studied thoroughly in previous simulation studies.
For this purpose we conduct all simulations with a sample size of 100 as well as a
sample size of 500 for each of the A treatment arms. A sample size with a total of

56

1000 patients is more representative for a common two stage design randomized
clinical trial. Furthermore for additional simulations we take into consideration
more extreme cases with roughly 50 patients per A treatment arms.

Another determinant variable is the randomization probability for the late
randomization process. The 1:1 randomization schema for both randomization
processes in two stage design is most commonly adopted in clinical and research
atmosphere. Therefore for most simulation studies a balanced randomization
schema is assumed for both the 1
st
randomization and the 2
nd
randomization.
However to test and demonstrate the modeling capabilities of the survival
estimators simulations are also carried out with imbalanced randomization schema
(i.e. 1:3 and 3:1) for the second randomization to B treatment levels.

The most crucial parameter to our knowledge in a two stage design would
be the proportion of non-randomized patients (“informative” dropouts) during
Stage II randomization. The value of this parameter would have direct impact on
the survival estimators. It is likely to detect any potential bias when there is sizable
percentage of non-randomized patients at Stage II. Therefore in the simulation
configuration the remission/consent status R
i
is sampled from a Bernoulli
distribution Bernoulli(π
R
) where π
R
= 75% yielding a 25% non-randomization rate
among Stage II patients. This parameter is assumed to resume the same value for
both A treatment arms.

57

Using the exponential survival model the survival time during Stage I for
treatment A
1
denoted by T
1
was sampled from exponential (α) with a mean 1/α
over time [0, T
SI
]. For patients who do not participate in the 2
nd
randomization, i.e.,
R = 0, their post-remission survival time is draw from exponential distribution with
mean 1/λ = 5 years. For subjects randomized to B
1
treatment policy, i.e., R = 1 and
Z = 0, their post-remission survival time is sampled from exponential (β
1
) with
mean 1/β
1
= 8 years. For subjects randomized to B
2
treatment policy, i.e., R = 1
and Z = 0, their post-remission survival time is sampled from exponential (β
2
) with
mean 1/β
2
= 5 years. As treatment policy A
1
B
1
is considered the interest of the
study we assume treatment strategy B
1
is superior to treatment B
2
. For the non-
randomized patients we suppose they have inferior outcome compared to patients
under policy B
1
in the second stage, which is quite likely in practice. Since
survival under policy B
2
is not factored in the estimating process of survival under
policy B
1
the choice of β
2
is merely arbitrary and will not affect the desirable
comparisons. Thus for simplicity we force the mean survival of policy B
2
is the
same as that of the dropout patients.

Additional considerations are given in order to achieve a realistic survival
rate roughly around 50-70% by the end of a 3-year period. Given the clinical as
well as statistical constraints in the simulation we assumed Stage I exponential
distribution mean survival: 1/α = 4 years.

58

In addition to the basic parameter settings it is also of the study interest to
test the variance estimate suggested by both previous studies and the proposed
study. In particular the secondary goal of the simulations studies is to further
examining the variance estimate proposed by the Analytical Approach. Thus
additional simulations are conducted taking into consideration of small samples to
show if using complex computing method such as bootstrap process would
effectively improve the variance estimate for the IPW Estimator.

The overall evaluation of the survival and variance estimates is threefold.
The estimated mean survival is judged by the closeness to the “true” mean, which
is measured by bias. Secondly the variance estimate is first compared to the “true”
variance, which is estimated for the simulated samples by taking the simulation
variance of the mean survival estimate. Then magnitude of variance is compared
across various survival estimators and the estimator with the minimal variance with
similar bias is considered “better”. In addition the standard error of the variance
estimate is also taken into account when comparing variance estimates. Last the
overall performance of the survival estimator is manifested in the Mean Standard
Error (MSE), which can be compared between different estimators.

59

4.2 Simulation Studies I - IV

In order to fulfill the stated investigative objectives four basic simulation
studies (Basic Simulation I to Basic Simulation IV) are carried out with the
following parameter setting (Table 1). For each simulation 1,000 simulated
dataset are generated under the specific parameter setting.

Table 1 Parameters for basic simulation studies comparing survival estimators

Source Parameter Description Simulation Values
Simulation # of simulation = 1,000
Timeline # of years of recruitment = 5 years
Censoring Administrative censoring Ci ~Uniform [2, 7]
# randomized to A1 arm = {100, 500}
Duration (arbitrary) = 4 months
Stage I

Survival distribution for A1 ~ exponential, mean = 4 years
Clinical Evaluation Remission/Consent probability θR ~Bernoulli (0.75)
Randomization probability πR ~Bernoulli (1:1, 1:3, 3:1)
Conditional survival for B1 ~ exponential, mean = 8 years
Conditional survival for B2 ~ exponential, mean = 5 years
Stage II

Conditional survival for no RX ~ exponential, mean = 5 years
Outcome Endpoint estimate = 3 year survival for A1B1

Considering various combinations of the simulation parameters plus the
“heavy tail” model there are a total of four simulation studies, while each is
conducted with a sample size of 100 and 500. The first three simulation studies are

60

conducted with varied randomization probability during Stage II randomization
while the “heavy tail” model is achieved by randomly selecting 10% of the study
subjects and inflating the survival time by 10 fold. The results of the four basic
simulation studies are displayed in Table 2 to Table 5 in the following pages.

The simulation results suggest that both IPW Estimator and Bootstrap
Estimator produce unbiased survival estimate. However when there is a sizable
proportion in “dropouts” at Stage II with different survival profile the Naïve
Methods gives biased survival estimate while the direction and magnitude of bias
dependent upon the relative relationship between the survival from the “dropouts”
and that of policy A
1
B
1
. As we examine the variance estimate of each method both
the Naïve Methods and Bootstrap Approach generate unbiased variance compared
to the simulation variance. On the other hand the variance estimates from the IPW
Estimator tend to underestimate and the “underestimating” is mostly observable in
the third simulation study when the second stage randomization probability is 1:3
(Table 4). The MSE is the biggest for the Naïve Estimators across all simulations
while the MSE is mostly comparable between the IPW Estimator and the proposed
Bootstrap Estimator. The above findings suggest that additional simulation is
required to further investigate the variance estimate of the IPW Estimator.

61
Table 2 Basic simulation I: compare survival estimators for 1:1 randomization

Survival Estimator: 1:1 randomization
Simulation
Setting
Parameter of
Interest
Expected
3-year
Survival
Estimate
Naïve
Estimator I
Naïve
Estimator II
IPW
Estimator
Proposed
Estimator
S
11
Est.
0.6294 0.6609 0.5608 0.6298 0.6302
Var(S
11
) Est.
(SE)
--- 0.005523
(0.000038)
0.001277
(1.0E-6)
0.003330
(0.000020)
0.004119
(0.000022)
Simul. Var
---
0.005522 0.001260 0.003811 0.003932
N=100
MSE
---
0.0065 0.0060 0.0038 0.0039
S
11
Est.
0.6294
0.6601 0.5613 0.6302 0.6292
Var(S
11
) Est.
(SE)
--- 0.001116
(3.4 E-6)
0.000256
(9.3E-8)
0.000712
(2.1 E-6)
0.000815
(2.0 E-6)
Simul. Var
---
0.001046
0.000267
0.000786 0.000803
N=500
MSE
---
0.0020
0.0049
0.0008 0.0008

62
Table 3 Basic simulation II: compare survival estimators for 3:1 randomization

Survival Estimator: 3:1 randomization
Simulation
Setting
Parameter of
Interest
Expected
3-year
Survival
Estimate
Naïve
Estimator I
Naïve
Estimator II
IPW
Estimator
Proposed
Estimator
S
11
Est.
0.6294
0.6586
0.5388
0.6283 0.6282
Var(S
11
) Est.
(SE)
--- 0.003831
(0.000020)
0.001290
(8.5E-7)
0.003122
(0.000013)
0.003183
(0.000012)
Simul. Var
---
0.004076 0.001249 0.002947 0.003189
N=100
MSE
---
0.0049 0.0095 0.0029 0.0032
S
11
Est.
0.6294
0.6599
0.5395

0.6306 0.6300
Var(S
11
) Est.
(SE)
--- 0.000773
(1.7 E-6)
0.000259
(7.7E-8)
0.000654
(1.3 E -6)
0.000649
(1.6 E-6)
Simul. Var
---
0.000749 0.000270 0.000614 0.000639
N=500
MSE
---
0.0017 0.0084 0.0006 0.0006

63
Table 4 Basic simulation III: compare survival estimators for 1:3 randomization

Survival Estimator: 1:3 randomization
Simulation
Setting
Parameter of
Interest
Expected
3-year
Survival
Estimate
Naïve
Estimator I
Naïve
Estimator II
IPW
Estimator
Proposed
Estimator
S
11
Est.
0.6294
0.6637
0.5597
0.6248 0.6309
Var(S
11
) Est.
(SE)
--- 0.010610
(0.000128)
0.001278
(1.1E-6)
0.003965
(0.000044)
0.007597
(0.000140)
Simul. Var
---
0.011550 0.001325 0.007245 0.007651
N=100
MSE
---
0.0127 0.0062 0.0073 0.0077
S
11
Est.
0.6294
0.6616
0.5605

0.6302 0.6309
Var(S
11
) Est.
(SE)
--- 0.002167
(0.000001)
0.000256
(9.3E-8)
0.000891
(6.4 E-6)
0.001603
(0.000020)
Simul. Var
---
0.002022
0.000277
0.001332 0.001404
N=500
MSE
---
0.0031
0.0050
0.0013 0.0014

64
Table 5 Basic simulation IV: compare survival estimators for heavy tail model

Survival Estimator: heavy tail model
Simulation
Setting
Parameter of
Interest
Expected
3-year
Survival
Estimate
Naïve
Estimator I
Naïve
Estimator II
IPW
Estimator
Proposed
Estimator
S
11
Est. 0.6517 0.6768
0.5875
0.6548 0.6551
Var(S
11
) Est.
(SE)
---
0.005347
(0.000037)
0.001255
(1.3E-6)
0.003059
(0.000020)
0.004028
(0.000027)
Simul. Var --- 0.005303 0.001209 0.003593 0.003805
N=100
MSE --- 0.0059 0.0053 0.0036 0.0038
S
11
Est. 0.6517 0.6757 0.5893 0.6577 0.6554
Var(S
11
) Est.
(SE)
---
0.001078
(3.4 E-6)
0.000252
(1.1E-7)
0.000650
(1.8 E-6)
0.000796
(3.3 E-6)
Simul. Var --- 0.001074 0.000246 0.000809 0.000770
N=500
MSE --- 0.0017 0.0041 0.0008 0.0008

65

4.3 Simulation studies V and VI

In order to further investigate the property of the variance estimate proposed
by the Analytical Approach (IPW Estimator) additional simulation studies are
carried out in this section. Simulation study V examine the potential bias
associated with the variance estimate for IPW Estimator under the exact setting
stated in Table 1 except for using more extreme sample size choices N = {50, 100}
compared to the original N = {100, 500}. In addition instead of 1,000 simulations
each simulated data contains 10,000 datasets to better capture the variation. The
results of this simulation study can be found in Table 6. What’s more due to the
presence of bias in the variance estimate of the IPW Estimator we propose using
the bootstrap process as in Algorithm III to estimate variance. The simulation
studies of the proposed variance with 1,000 datasets can be found in Table 7.

Based on the simulation results in Table 6 it appears that the variance
estimate for IPW Estimator underestimates variance by roughly somewhere
between 15% and 25% for most situations while the bias is mostly pronounced in
the third simulation setting with as much as 50% underestimation. The bias
embedded in the variance estimate seems to disappear as we switch to bootstrap
process to estimate variance (Table 7). The unbiased variance estimate using
bootstrap process also demonstrate robustness for extreme small sample (N = 50),
different randomization ratios (3:1 or 1:3), or even heavy tail model (Table 7).

66
Table 6 Simulation study V: 10,000 simulations for variance estimate of IPW Estimator

Sample
Size N
Parameter of
Interest
Simulation I
(RX ratio =1:1)
Simulation II
(RX ratio =1:3)
Simulation III
(RX ratio =3:1)
Simulation IV
(Heavy tail model)
S
11
Est. 0.6301 0.6248 0.6298 0.6425
Var(S
11
) Est. 0.006114 0.004343 0.007008 0.005884
Simul. Var 0.007945 0.005859 0.015114 0.007694
N = 50
Var(S
11
) Est.
Bias %
-23% -26% -54% -24%
S
11
Est. 0.6295 0.6304 0.6301 0.6575
Var(S
11
) Est. 0.003309 0.002276 0.003941 0.003006
Simul. Var 0.003936 0.002907 0.007347 0.003678
N = 100
Var(S
11
) Est.
Bias %
-16% -22% -46% -18%

Table 7 Simulation study VI: bootstrap variance estimate of IPW Estimator
Sample
Size N
Parameter of
Interest
Simulation I
(RX ratio =1:1)
Simulation II
(RX ratio =1:3)
Simulation III
(RX ratio =3:1)
Simulation IV
(Heavy tail model)
S
11
Est. 0.6301 0.6298 0.6248 0.6425
Var(S
11
) Est. 0.004253 0.003294 0.007016 0.004011
N = 50
Simul. Var 0.003811 0.002947 0.007245 0.003805
S
11
Est. 0.6295 0.6301 0.6302 0.6575
Var(S
11
) Est. 0.000786 0.000614 0.001332 0.000770
N = 100
Simul. Var 0.00793 0.000581 0.001411 0.000786

67

4.4 Summary of simulation studies

Based on the simulation studies we conclude that both IPW Estimator and
Bootstrap Estimator provide sufficiently good survival estimates with comparable
MSE (Table 2 – Table 5). The variance of the Bootstrap Estimator is unbiased
while there is evidence suggesting bias in the direction of potentially
underestimating for the IPW Estimator (Table 6). The bootstrap process provides
an alternative to generate an unbiased variance estimate to the IPW Estimator
(Table 7). As a result the IPW Estimator for survival estimate combined with its
bootstrap variance estimate (Modified IPW Estimator) is comparable to using the
Bootstrap Estimator in survival analysis for two stage design randomized clinical
trials. Despite that the implementation of Bootstrap Approach is straightforward,
less time-consuming, and much more simplified compared to the IPW Estimator
while the modified IPW Estimator basically demands additional computation.
Therefore we recommend using the Bootstrap Estimator to estimate survival
probabilities as well as variance estimate for two stage design randomized clinical
trials.

68

Chapter 5: Data Analysis of COG Trials

In this chapter we conduct statistical analysis for two previously published
COG studies, i.e. a high-risk neuroblastoma trial CCG3891 (Matthay et al., 1999)
and a B NHL and B ALL trial CCG5961 (Cairo et al., 2007). The details of both
studies can by found in Chapter 2 Section 2.2. The study design and treatment
assignments are given by Figure 3 and Figure 4.

According to simulation findings the Bootstrap Approach is implemented to
estimate survival as well as variance estimate (Formula 3.6.1 and 3.6.6). In
addition analysis is also conducted using Naïve Estimator I & II (Section 3.3) and
Modified IPW Estimator with bootstrap variance estimate (Formula 3.4.1,
Algorithm III). The survival curve is plotted for event-free survival (EFS) by
treatment groups using Kaplan-Meier Method for data pooled across bootstrap
loops. The analysis provides event-free survival estimates at year 3 for CCG3891
two stage trial and 4-year survival estimates for CCG5961 trial. The results are
compared to findings based on Naïve Method and Analytical Approach at
comparable time points. Section 5.1 presents survival analysis for high-risk
neuroblastoma two stage trial while Section 5.2 demonstrates results and
comparisons for B NHL and B ALL study.

69

5.1 Statistical analysis for high-risk neuroblastoma trial

Among 539 study participants a total of 379 patients were randomized to
either autologous bone marrow transplantation (BMT) (N = 189) or continuation
chemotherapy (CC) (N = 190). For patients undertaken BMT 98 patients (51.9%)
continued to randomization to either maintenance therapy (N = 50) (13-cis-retinoic
acid) or observation (N = 48). In comparison among CC patients 105 patients
(55.2%) were randomized in maintenance phase with 52 assigned to 13-cis-retinoic
acid and 53 to observation only. The estimated “dropout” rates are comparable
between BMT (28.6%) arm and CC arm (27.9%).

The survival curves for EFS are given in Figure 11. According to the plot
patients assigned to autologous BMT therapy have better survival outcomes and the
beneficial effects are more evident after the 2
nd
year of randomization. For both
BMT and CC treatment groups patients assigned 13-cis-retinoic acid during
maintenance phase have better long-term event-free survival and the protective
effect seems to be of larger magnitude among CC patients. In addition the
protective effect of 13-cis-retinoic acid therapy among BMT patients appears to
decrease after 7 or 8 years. The last patient on CC and maintenance therapy died at
about 11.8 years since randomization.

70

Figure 11 Event-free survival plots by treatment combinations for high-risk neuroblastoma study

71

Table 8 showed 3-year event-free survival estimate and its standard error
estimates for each of the treatment arms. For patients assigned to BMT group the
3-year EFS is 37.5% (4.4%) for those given maintenance therapy compared to
31.1% (4.2%) with observation only. Similar patterns are observed for patients in
CC treatment group with 26.1% (4.0%) EFS under maintenance therapy compared
to a low 20.4% (3.7%) without further therapy.

Compared to Bootstrap Approach Naïve Estimator I produced slightly
different survival estimates with roughly 5% to 2% overestimation for most
treatment groups except for the CC + observation group (Table 8). On the other
hand Naïve Estimator II underestimated survival probability by roughly 30% for
BMT arm yet went the opposite direction compared to Bootstrap Estimator for CC
arm by roughly 40%. This is reasonable because this group did not involve any
investigative new agents and would be a normal line of treatments given to patients
at the time. This implies that non-participated patients may very well have similar
survival compared to patients assigned to this group. However the results for BMT
group suggested that survival among non-participants was relatively poor compared
to patients randomized to maintenance therapy and as a result by excluding those
patients Naïve Estimator inflated the survival estimates. The IPW Estimator
produced relatively comparable EFS as to Bootstrap Approach.

72

Table 8 High-risk neuroblastoma trial (CCG3891): compare 3-year event-free
survival estimates

3-year EFS: EFS Est. (Std. Err. Est.)
Treatment
Group
Bootstrap
Approach
Naïve
Estimator I
Naïve
Estimator II
Modified
IPW
Estimator
13-cis
37.5%
(4.4%)
42.6%
(5.6%)
25.5%
(3.9%)
36.8%
(4.8%)
BMT
Obs.
31.1%
(4.2%)
33.7%
(5.7%)
21.1%
(3.6%)
32.5%
(3.5%)
13-cis
26.1%
(4.0%)
28.4%
(5.4%)
35.8%
(4.1%)
26.7%
(5.2%)
CC
Obs.
20.4%
(3.7%)
20.4%
(4.9%)
30.8%
(4.1%)
20.0%
(5.4%)

5.2 Statistical analysis for B NHL and B ALL trial

A total of 233 patients are included in the survival analysis of B NHL and B
ALL trial. Among all evaluable patients 121 patients (51.9%) are classified as
CNS
-
and 112 patients (48.1%) as CNS
+
. The percentage of randomized patients is
85.1% (N = 103) among CNS
-
patients with 52 randomized to standard
combination chemotherapy and 51 patients to reduced chemotherapy
(FAB/LMB96). Similarly for CNS
+
stratum a total of 85 patients (75.9%) are
randomized with 42 patients compared to 43 patients for standard combination
chemotherapy versus reduced chemotherapy respectively. The randomization
“dropout” rate is 13.6% (N = 16) among CNS- patients compared to 18.1% (N =
19) among CNS
+
patients.

73

The event-free survival curves are plotted for each of the four treatment
groups (CNS
-
/Standard, CNS
-
/Reduced, CNS
+
/Standard, and CNS
+
/Reduced)
shown in Figure 12. According to the survival curves patients without CNS
involvement (CNS
-
) had better event-free survival outcomes compared to CNS
+

patients. For both CNS groups standard therapy demonstrated protective effects in
terms of EFS compared to reduced therapy. As a result standard therapy was most
beneficial for patients without CNS disease involvement while reduced therapy
produces the worst EFS among CNS
+
patients. Event-free survival remained flat
after roughly 2 years of therapy for all four treatment groups.

The four-year survival estimate for EFS using Bootstrap Approach and
other methods is displayed in Table 9. The findings are consistent with
observations from Figure 12. Overall the CNS
-
patients had better 4-year EFS
outcomes while CNS
-
patients under standard therapy had 91.4% EFS compared to
84.2% EFS among CNS
-
patients assigned to reduced therapy. Among CNS
+

patients standard treatment also demonstrated better 4-year EFS outcome, 73.9%
versus 64.5% for CNS
+
patients treated with reduced therapy.

Naïve Estimators generated similar survival estimates for both treatment
groups among CNS
-
patients (Table 9). However the Naïve I estimate for CNS
+

patients appeared to be relatively biased in the upward direction. This is most

74

Figure 12 Event-free survival plots by treatment combinations for B NHL study

75

evident for standard therapy (81.3% versus 73.9%). For CNS
-
group Naïve
Estimator II appeared to produce slightly downward results compared to Bootstrap
Estimator. This finding suggests that the “dropouts” among CNS
+
patients might
have relatively poor survival outcomes and as a result by excluding them Naïve
Estimator I artificially inflated survival while Naïve Estimator II went the opposite
direction. The survival estimates using Modified IPW Estimator are almost
identical to that using Bootstrap Estimator (Table 9).

Table 9 B NHL (B ALL) trial (CCG 5961): compare 4-year event-free survival
estimates

4-year EFS: EFS Est. (Std Err Est.)
Treatment Group
Bootstrap
Approach
Naïve
Estimator I
Naïve
Estimator II
Modified
IPW
Estimator
Standard
91.4%
(3.3%)
91.3%
(3.6%)
88.6%
(3.7%)
90.9%
(3.2%)
CNS
-

Reduced
84.2%
(4.5%)
85.4%
(4.7%)
84.9%
(4.3%)
84.2%
(5.1%)
Standard
73.9%
(5.3%)
81.3%
(5.2%)
70.8%
(5.4%)
74.0%
(7.2%)
CNS
+

Reduced
64.5%
(6.1%)
67.4%
(6.6%)
61.2%
(6.0%)
64.7%
(6.9%)

76

Chapter 6: Hypothesis Test

One of the primary goals of the two stage design study is to compare
treatment policies and policy combinations in order to identify potentially most
beneficial treatment strategy. Considering a 2×2 two stage design randomized
clinical trial with two randomization processes the most basic comparison would be
to compare the four treatment arms to detect any heterogeneity across all treatment
combinations. For test of heterogeneity a global test is introduced and discussed in
this chapter.

6.1 Global Test Statistic

Given mean survival vector µ = (µ
11
, µ
12
, µ
21
, µ
22
)
T
the null hypothesis for
the global test is H
0
: µ
11
= µ
12
= µ
21
= µ
22
. In another word the null hypothesis is
expressed as Dµ = 0, where D (d×4), d < 4. Let v
jk
, j, k = 1, 2, be the variance
estimate for the mean survival estimate µ
jk
. According to the study design the
covariance of the mean survival estimates from different A treatment arms would
be naturally zero because of independence. Therefore let w
jk’
be the covariance
between µ
jk
and µ
jk’
, j = 1, 2, k ≠ j, k ≠ k’. By default property of the covariance
we have w
jk’
= w
k’j
. Following the above notation the variance covariance matrix Λ
is expressed as below:

77















= Λ
22 21
21 21
12 12
12 11
0 0
0 0
0 0
0 0
v w
w v
v w
w v

The above consideration allows us to construct a Wald test statistic:
) ( ) ( ) (
1
μ μ
)
)
)
D D D D
T T −
Λ (6.1.1)

Under the null hypothesis this test statistic asymptotically follows χ
2

distribution with 3 degrees of freedom.

6.2 Global test based on log transformation

The global test stated above can be easily constructed for the Naïve
Estimator. However the variance covariance matrix proves to be difficult to
estimate for the survival estimates using Naïve Method (3.3.1). In order to
overcome this challenge we consider the natural log transformation of the null
hypothesis. Under the log transformation the new null hypothesis is given by H
0
:
ln (µ
11
) = ln (µ
12
) = ln (µ
21
) = ln (µ
22
). The survival estimate for treatment policy
A
1
B
1
in (3.3.1) can be expressed as following by taking the logarithm:
ln (S
11
(t)) = ln ( S
1
(t
SI
) × S
11
(t
SII
) ) = ln (S
1
(t
SI
)) + ln (S
11
(t
SII
)) (6.2.1)

The above relationship is very important for estimating covariance between
the log transformed survival quantities.

78

Using (6.2.1) the covariance can be estimated for the log transformation of
survival estimates S
11
(t) and S
12
(t) as shown below:
Cov ( ln (S
11
(t)), ln (S
12
(t)) )
= Cov ( ln (S
1
(t
SI
)) + ln (S
11
(t
SII
)), ln (S
1
(t
SI
)) + ln (S
12
(t
SII
)) )
= Cov ( ln (S
1
(t
SI
)), ln (S
1
(t
SI
)) ) + Cov ( ln (S
1
(t
SI
)), ln (S
12
(t
SII
)) )
+ Cov ( ln (S
1
(t
SI
)), ln (S
11
(t
SII
)) ) + Cov (ln (S
11
(t
SII
)), ln (S
12
(t
SII
)) )
(6.2.2)

Due to the nature of the randomization process the survival probability from
early stage is independent of the conditional survival at the later stage. Similarly
the survival probabilities are independent under treatment B
1
and B
2
. Hence the
quantity in (4.2.2) can be simplified to the following:
Cov ( ln (S
11
(t)), ln (S
12
(t)) ) = Cov ( ln (S
1
(t
SI
)), ln (S
1
(t
SI
)) )
= Var ( ln (S
1
(t
SI
)) ) (6.2.3)

The variance of the survival estimate can be estimated by the Greenwood
formula in (3.2.2). In order to estimate the variance for the log transformation we
need to expand the quantity by Taylor series. As a result the variance of ln (S
1
(t
SI
))
takes the following format:
Var ( ln (P) ) ≅ Var (P) / P
2
(6.2.4)

79

As we already know that the covariance between survival estimates under
different A treatment arms is zero due to independent sampling. In addition from
the method section we learn that the survival probability in (3.2.1) can be directly
estimated by properly censoring the unwanted subjects at Stage II. Similarly the
Greenwood variance of the survival estimate can be estimated by censoring.
Therefore through (6.2.3) and (6.2.4) together with both the variance estimates and
the covariance estimates for the log transformed survival estimates can be obtained.
Hence the variance covariance matrix for log transformed survival quantities is also
known.

Let µ’ = ( ln (µ
11
), ln (µ
12
), ln (µ
21
), ln (µ
22
))
T
. Thus the null hypothesis
under the log transformed data is given by Dµ’ = 0, where D (d×4), d < 4. Let Λ’
be the variance covariance matrix for the log transformed survival then a Wald test
statistic for the above null hypothesis is given below:
) ( ) ( ) (
1
μ μ
)
)
)
′ Λ′ ′
−
D D D D
T T
(6.2.5)

Similarly to the test statistic in (6.1.2) this test statistic follows χ
2

distribution asymptotically under the null hypothesis with 3 degrees of freedom.

80

6.3 Simulation studies and results

In order to evaluate the performance of the proposed global test based on
the natural log transformed data a series of simulations are conducted to examine
Type I Error rate and power performance of the test statistic. The parameter setting
follows that utilized by Simulation I (Table 1) in Chapter 4. In addition to the
choice of using sample sizes N = {200, 1,000} this round of simulation extends the
consideration to very small sample size N = 50. The power of the test statistic is
compared across various hazard ratios (HR) between treatment policies under
investigation. Further more the hazard ratio of one represents the “null” situation
when there is no difference between treatment arms. Thus the actual Type I Error
can be estimated from the simulation results with HR = 1.

To better understand the power of the global test three types of difference
among treatment policies are distinguished and studied separately. First we
consider simple difference between early treatment policies or late treatment
policies but no interactive effects. Naturally the second category of difference
involves interaction between early and late treatment regimens. There are two
types of interaction, quantitative interaction versus qualitative interaction. In this
section we refrain our efforts to the latter type of interaction, i.e. qualitative where
the difference between B treatment arms goes in opposite direction between the two
A treatment arms. In addition we consider an α = 0.05 nominal significance level

81

(Type I Error). The power (%) is calculated across hazard ratios for samples of
sizes N = {100, 200, 1,000} and also for each of the three scenarios described
above. The power curves are fitted over hazard ratios to depict the power of the
test statistic for each of the simulation scenarios (Figure 13 – Figure 15).

The power curves in Figure 13 shows the gradual increase in power of the
test statistic in (6.2.5) in detecting difference in A treatment arms for a hazard ratio
from 1 to 5 comparing policy A
1
and A
2
. The simulation results demonstrate that
all power curves cross Y-axis (power in %) through roughly 5% under the null
hypothesis i.e. HR = 1, which coincides with nominal Type I Error rate (α). The
power increases with increased difference in A treatment arms. However the test
statistic seems to be much more powerful for a large sample (N =1,000) compared
to that for smaller samples (N = 100 or 200). As there is a roughly 1.7 fold
difference in hazards for treatment A the power is roughly 40% for large sample yet
to achieve roughly the same power the difference has to be higher than 5 fold for
small sample of 200. The test severely lacks of power for smaller sample (N =
100) with the power lingering around 20% to detect a 5 fold difference. Despite
that the test proves to be sufficiently powerful for large samples. The power is
roughly 80% to detect a 2.5 fold difference in hazards for sample of 1,000.

82

Figure 13 Power curves: difference between treatment A arms

83

The power curves displayed in Figure 14 show that the Type I Error rate α
for the log-based global test is roughly around 0.05 for all sample size N = (100.
200, or 1,000). The power of the test is positively associated with sample size
where sample size of 1,000 has the highest power and sample size of 100 has the
lowest power to detect a difference given a specific hazard ratio. In addition the
test statistic has greater than 80% of power to detect a 1.75 fold difference in
hazards between B treatment arms with sample size of 1,000. And the power of the
test statistic breaks through 80% as the HR is as large as 3.0 for a sample of size
200. The increase in power is much more gradual for a relatively small sample
with a size of 100 with power of 40% for a 3 fold difference in B arms.

The study of power curves for testing potential interactive effects between
early and late treatments yields consistent findings (Figure 15). The hazard ratios
are comparing difference between treatment B
1
and B
2
for treatment A
1
with the
opposite relationship between B treatment policies for treatment A
2
. For
interactive effect the power reaches 80% for a roughly 1.5 (or 1/1.5) fold difference
in hazards for sample size of 1,000 and a roughly 2.5 (or 1/2.5) fold difference for
sample size of 200. The test is adequately powerful for even small samples (N =
100). When the difference is 3 fold the power reaches roughly 60%.

84

Figure 14 Power curves: difference between treatment B arms

85

Figure 15 Power curves: interactive effects between treatment A and B

86

In summary the log-based global test is not recommended to detect
difference in A treatment arms for small samples (N = 100 or 200) but is sufficient
for large samples (N = 1,000) to detect a difference of at least 2 fold. However
compared to the power of the test for other types of difference the test is less
powerful to detect a difference of similar scale in B treatment arms. To detect
difference in B treatment arms the test is sufficient for samples of sizes 200 or
1,000 and could be potentially useful only if the difference is fairly large (>> 3.0
fold) for smaller samples (N = 100). The test is quite powerful to detect qualitative
interactive effects for an HR greater than 1.5 among medium or large samples and
maybe be useful for relatively small samples (N = 100) for large HRs (>> 2.5).

87

Chapter 7: Conclusion and Discussion

Two stage design randomized clinical trial is a novel design strategy in
oncology clinical research as well as in studies in other areas involving multi-phase
treatments. Many features of this type of study still requires further exploration
and perfection for the particular study design to become a more accessible
investigators to use for design of preliminary studies, recommendation on early
stage duration, improving participation in late stage, etc. Regardless the design
proves to be cost-effective and flexible in testing innovative treatment regimens at
different clinical phases simultaneously. In addition this design could be the sole
tool to test the hypothesis on interactive effects between an early stage treatment
and late stage treatment.

One of the major challenges facing by promoting this study design roots in
the lack of feasible analytical strategy and methodology. Therefore the statistical
analysis of data from such trial remains a major roadblock up to date, which further
discourages wider acceptance and implementation. Despite some of the early
exploration of the statistical methods, most of the studies did not provide adequate
information or details to address many statistical questions and data issues common
to study design. Another common problem of existing methods is insufficient
technical support or difficulty in realization.

88

One of the primary assumptions underlying all statistical methods
incorporating “informative” dropouts states that this particular group would remain
the same even if the “desired” late stage treatment is administered through non-
randomized fashion. This assumption holds reasonably well for patients whose
refusal/non-participation reasons are not treatment or randomization related such as
due to ineligibility or external factors (i.e. insurance, financial situation, etc).
However if there exists circumstances that may suggest deviation from this
fundamental assumption the statistical methods using proportional based adjusting
factors or sampling techniques to impute “missing” data may not be applicable.
The violation of assumption may challenge the design itself even though the
affected population may be a limited proportion of the entire study population.

In this study our primary goal is to resolve some of the fundamental
statistical and data questions encountered by two stage design, more importantly to
develop reasonable and reliable statistical methodologies to facilitate analysis of
data collected from two stage design randomized clinical trials. In this chapter we
summarize study findings from the proposed study and discuss the strength and
limitations of various aspects of our research. Finally the findings and conclusions
from the proposed study inspire further work, which is also discussed among the
findings in this chapter.

89

7.1 Strength and limitation of proposed methods

First of all we intend to answer the core question as to estimate overall
survival across therapeutic phases, which can be used for Intent-to-Treat (ITT)
analysis of two stage design randomized clinical trial with a late stage
randomization. For that purpose two types of survival estimators are developed
based on the Naïve Approach and the Bootstrap Approach respectively. In addition
to the survival estimators the variance estimate is also formulated for each of the
proposed methods. The model framework of each of the above methods is more or
less derived and relied upon the conventional survival methods such as Kaplan-
Meier Method. Similarly the variance estimate of the proposed methods is closely
related to the existing Greenwood Formula to estimate variance for Kaplan-Meier
Estimator. The association between the novel models and traditional model allows
the new methods to borrow many elements from traditional theoretical models and
as a result only a few additional modifications are required to put forth the new
model framework. Therefore the new estimators are easily accessible and ready to
be implemented with minimal modifications of existing coding in application
software. More specifically the Naïve Approach can be implemented using
statistical modules developed for Kaplan-Meier method on study cohort with
arbitrary censoring while the Bootstrap Approach largely depends upon the
resampling technique, the bootstrap process, and thus bypasses the complicated
mathematical modeling. With the bootstrap process sitting at its core the Bootstrap

90

Estimator is intuitive and affordable given advancement in computational
technology. The formulation of the variance of the Bootstrap Estimator also
surrounds the existing statistical module for the Greenwood formula. This largely
decreases the demand to introduce additional computation and the coding process
during implementation.

The Naïve Estimators I & II can be implemented in two ways. The direct
and more intuitive implementation requires the estimation of a prior probability
during Stage I and a conditional survival during Stage II at the expense of
precision. The overall survival hence is estimated using the Bayesian formula. In
order to derive the estimation of the prior probability we need to know the average
Stage I time, which has to be estimated across study cohort. This demands
additional work. On the other hand the proposed implementation is quite
straightforward. It only requires censoring all subjects not assigned to the study
treatment under study at Stage II and then the overall survival can be estimated
together with its Greenwood variance on this censored cohort. Thus this approach
improves the precision of the estimate.

The bootstrap process used in the Bootstrap Approach differs from its more
recognized utility manifested in three aspects. The most distinguishing factor is
that the novice utilization only draws bootstrap samples from a subset of the overall
study cohort. The other difference lies in the objective of using the bootstrap.

91

While normally the bootstrap is used directly to estimate certain statistical
properties the primary objective of using bootstrap in the proposed method is to
“impute” the “missing” values due to loss in sample size after a late randomization.
The other deviation lies in that the statistical estimates are not directly computed on
the bootstrapped sample instead all the estimates are computed on a combined
sample comprising of both the bootstrapped sample and a subset of original cohort.

As explained previously the variance estimate of the Naïve Estimators is a
direct adoption of Greenwood formula on an arbitrarily censored study cohort.
From the simulation studies such implementation gives unbiased variance estimate
under various simulation settings. However the variance estimate is larger
compared to the variance estimates from other methods. A variance estimate based
on Greenwood formula is also a key component for the variance estimate using
Bootstrap Approach. Given the nature of utilizing bootstrap in an unconventional
sense the variance estimate of the Bootstrap Estimator can not be computed using
bootstrap variance along. Instead we analyze sources of variation and formulate a
variance combining both within-sample variation and between-sample variation
(3.6.6). The within-sample variation is an adjusted Greenwood-based variance
with an inflation component due to the correlation from combining bootstrap
sample and subset of original cohort while the between-sample variation is the

92

conventional bootstrap variance. According to simulation studies the within-
sample variation contributes to the majority of data variation (data not shown). The
simulation studies also demonstrate the unbiased property of this estimate.

There are two common schools of thoughts regarding the appropriate
statistical analysis for two stage design randomized clinical trials. The first one
simply ignores the non-randomized patients at the late randomization and believes
that only those assigned to the treatment under study should be included in the
study cohort. On the contrary the other way of thinking focuses on answering the
question “what is the true study population” and they believe that the “true” cohort
that represents the population under study is the one from the very beginning of the
study and accordingly every patient including the non-randomized patients due to
late randomization or patients randomized to different study regimen at this
randomization should be represented proportionally in the “true” study cohort. The
Intent-to-Treat analysis in this proposed study follows the rational of this latter
belief. Even though there are two sources for “dropout” to occur, i.e. either
determined by eligibility status or by consent status, they are both part of the “true”
study population and thus no distinction is given to treat them differently. From the
model framework it can be seen that the Naïve Estimator I falls in the former line
of thinking and Naïve Estimator II does not address the question properly. On the
other hand the Bootstrap Approach and the Analytical Approach belongs to the
latter. Hence we argue that the Naïve Method is not suitable to use for the ITT

93

analysis. According to simulation studies the survival estimate is biased for the
ITT analysis using the Naïve Method while the direction and magnitude of the bias
is more or less depends upon both the percentage of “dropouts” and the difference
in survival between “dropouts” and patients under study regimen. Considering the
relative magnitude of the variance estimate Naïve Method produces the largest
MSE among all three methods. On the other hand the Bootstrap Approach
provides unbiased survival estimate for the ITT analysis.

7.2 Limitation of Analytical Approach

Compared to the intention of using novice statistical modeling to deduce
relatively simple survival estimators the Analytical Approach resorted to rigid
mathematical deduction and reasoning (Lunceford et al. 2002). As a result the IPW
Estimator based on Analytical Approach has an intricate model formulation and
complicated variance estimate. While the simulation results suggest that the IPW
Estimator is unbiased under various study settings from a theoretical point of view
the estimator is susceptible to bias if the observed randomization probability
deviates largely away from the planned randomization schema. Thus in the actual
realization the theoretical randomization probability is replaced by its empirical
value to avoid introducing unnecessary bias. Despite of the fact that the survival is
unbiased with relatively small variance using this method one of the critical
findings about this estimator is the underestimation of the variance estimate. Given

94

the unknown distribution of the IPW Estimator a bootstrap variance is proposed to
improve the variance estimate. Based on Simulation Study IV the bootstrap
variance is unbiased for various simulation settings (Table 7). However compared
to the Bootstrap Estimator such an algorithm consumes almost double amount of
computational resources for a 1:1 randomization schema given that the bootstrap
for the modified approach is conducted on the entire study population while similar
process is limited to a subset of the study cohort (< 50% with dropouts present in
data) using Bootstrap Estimator. The additional computing time may vary
dependent upon the nature of study data. Regardless the number of bootstrap
iterations is always larger for the modified IPW Estimator compared to the
Bootstrap Estimator for any dataset.

7.3 Strength and limitation of simulation studies

The simulation studies carried out in this chapter investigate various
properties of the existing and proposed survival estimators as well as their variance
estimates. The parameter setting considered captures both realistic situation and
theoretical models. The choice of using a relative high percentage of “dropouts” at
the late stage allows for testing the effectiveness of methods that intend to
incorporate “informative” dropouts using various techniques (IPW Estimator and
Bootstrap Estimator). A 1:1 randomization schema is most commonly observed in
practice. Besides considering a 1:1 randomization ratio examining survival

95

estimators under more extreme scenarios such as using 3:1 and 1:3 randomization
ratios enables the study of robustness of each method as the fraction of patients in
each therapy group breaks apart further. In addition all methods are also examined
for a heavy tail model that somewhat resembles a cure model common to pediatric
oncology trials.

Most simulation studies are conducted with 1,000 simulated datasets. In
order to closely examine the bias embedded in the variance estimate of the IPW
Estimator simulation study with 10,000 datasets is carried out which provides more
power to detect potential bias.

One of the variables that have not be considered to vary in simulations is
the Stage I duration, which instead is chosen based on realistic values. The actual
duration of Stage I normally varies patient to patient yet based on the theoretical
framework it does not have direct impact on the overall simulation results. The
other parameter that could potentially vary is the blocked Stage II randomization
probability within each Stage I arm. However in reality this is rarely the case.
Also all the estimating methods are formulated within a certain treatment arm.
Therefore even though such a scenario happened it would not necessarily have any

96

impact on the simulation findings. Finally the percentage of dropouts should not
impact the survival estimate of either IPW Estimator or Bootstrap Estimator only
that it may influence the amount of computation involved in Bootstrap Estimator in
an obvious manner.

The proposed methods are mostly considered under a non-parametric
setting. Simulation studies suggest that those methods are also appropriate under
exponential model or cure model (heavy tail model). Additional parameterization
may potentially simply or improve the estimators for parametric modeling.
However this topic is beyond the scope of this study.

7.4 Strength and limitations of proposed global test

A log-based global test is proposed for Naïve Estimator in this study to test
heterogeneity across treatment combinations. The main reason to conduct the
global test on the logarithm scale is due to the difficulty in estimating covariance
between mean survival estimates. The log transformation allows using the Taylor
expansion (Delta Method) to estimate with certain loss in the precision of the
covariance estimate. The extent of such compromise is beyond the investigative
objectives of the study. The test statistic is a Wald test which follows χ
2

distribution with 3 degree of freedom. The asymptotic nature of the test statistic
makes it less powerful when used for small samples (Figure 13 – Figure 15). The

97

log-based global test is not as powerful when the only heterogeneity in data rises
from early treatment. This is because the magnitude of the difference is not only
determined by the hazard ratio between A treatment arms but also affected by the
magnitude of conditional survival from late treatment. An alternative testing
strategy to detect difference in early treatment is simply conduct a log rank test for
early stage without taking into account late follow-up data.

The test is reasonably powerful (> 40%) for a large sample (N = 1,000) to
detect a difference as small as 1.5 fold in hazards between late treatment arms
(Figure 14) or even smaller as 1.25 or 1/1.25 fold difference for qualitative
interaction between early and late treatment arms (Figure 15). However the test is
not powered enough (< 40%) to detect a hazard ratio less than 2 between late
treatment arms or hazard ratios less than 1.75 (or > 1/1.75) for interactive effect for
a sample of 200 patients. The increase in power is quite steep for large samples (N
= 1,000) in comparison to that for small samples (N = 200) (Figure 13 – Figure 15).
Given the linearity relationship between sample size and power the power will
increase with sample size for 200 < N < 1,000 for each specific HR between B
treatment arms. Overall the test statistic needs to be used with caution for small
samples (N < 200) and is not recommended to use in testing hypothesis states that
there is only difference among early treatment arms.

98

The simulation studies are conducted at Type I Error α = 0.05 level. Further
studies may investigate the powerful in relationship to varied α level to provide
more insight into the behavior of test statistic. In addition the test of interaction
considers only strict opposite hazard ratios between late randomization arms
stratified by early randomization arms. Other forms of qualitative interaction may
also be worth looking at given clinical interaction may not be exact opposite in
magnitude.

While the global test answers the question whether there is any sort of
heterogeneity among treatment combinations it does not point to the origination of
the heterogeneity to a specific treatment. Another type of tests can be constructed
within each A treatment stratum to compare B treatment regimens. This test can
use logrank test statistic. Due to the “dropouts” the expected cell values as well as
the “observed” cell values at a specific time points may also incorporate “dropouts”
with certain adjustment for proportion. This test statistic may be based on survival
estimation based on Bootstrap Estimator. Further research is needed to develop
such a test statistic.

99

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101

Appendix A

SAS MACRO for Bootstrap Estimator:
*******************************************************************

BOOTSTRAP APPROACH:
BOOTSTARP AjBk PATIENTS TO COMPENSATE FOR AjBk’ PATIENTS

******************************************************************;

****************************************************
MACRO:KAPLAN-MEIER SURVIVAL ESTIMATE
& GREENWOOD FORMULA FOR VARIANCE
****************************************************;

%MACRO LIFTST(INDAT,OUTDAT,SRVTM,CENS);

PROC LIFETEST DATA=&INDAT METHOD=KM NOPRINT;
TIME &SRVTM*&CENS(0);
SURVIVAL OUT=&OUTDAT (KEEP=&SRVTM _CENSOR_ SURVIVAL SDF_STDERR)
STDERR;
RUN;

%MEND;

****************************************************
MACRO:SINGLE BOOTSTRAP TO REPLACE B2/1 PATIENTS
WITH B1/2 PATIENTS FOR EACH SET
WKIN = INPUT DATA EXCLUDING B2/1 PATIENTS
BTIN = INPUT DATA WITH B1/2 PATIENTS ONLY

BTOUT = OUTPUT DATASET FOR EACH BOOTSTRAP LOOP
BTYROUT = OUTPUT POINT ESTIMATES FOR EACH LOOP
****************************************************;

%MACRO BOOTSTRP(WKIN,BTIN,RSEED,BTOUT);

**********************************************
BOOTSTRAP # OF B2/1 PATIENTS FROM B1/2 PATIENTS
**********************************************;
DATA BTSMP1;
DO I = 1 TO &A1B2N;
X=ROUND(RANUNI(I+&RSEED)*&A1B2N);
SET &BTIN POINT=X;
OUTPUT;
END;
STOP;
RUN;

102

***************************************************
MERGE BOOTSTRAPPED DATA BACK TO ORIGINAL DATA
***************************************************;
DATA TMP1;
SET &WKIN BTSMP1(DROP=I);
PROC SORT DATA=TMP1; BY BTS_DAYS; RUN;

***************************************************
COMPUTE MODIFIED GREENWOOD VARIANCE COMPONENTS
***************************************************;

****# OF TIES AT EACH TIME POINT;
PROC FREQ DATA = BTSMP1 NOPRINT;
TABLES BTS_DAYS/OUT=TSET(DROP=PERCENT CUM_PCT) OUTCUM;
RUN;

DATA TSET2; SET TSET;
RENAME COUNT = REPNUM; DROP CUM_FREQ;
TIEYN = 1; RUN;

****# AT RISK AT EACH TIME POINT;
PROC FREQ DATA = TMP1 NOPRINT;
TABLES BTS_DAYS/OUT=RSET(DROP=PERCENT CUM_PCT) OUTCUM;
RUN;

DATA RSET2 (KEEP=BTS_DAYS RSNUM); SET RSET;
RSNUM = &A1N - CUM_FREQ + COUNT; RUN;

****# OF EVENTS DURING TIME T-dT TO T;
PROC FREQ DATA = TMP1 NOPRINT;
TABLES BTS_DAYS/OUT=ESET(DROP=PERCENT CUM_PCT) OUTCUM;
WHERE BTS_EVNT EQ 1; RUN;

DATA ESET2; SET ESET;
RENAME COUNT=EVNUM; DROP CUM_FREQ; RUN;

*****MERGE ALL THE DATASET;
DATA COMSET; MERGE TMP1 TSET2 RSET2 ESET2; BY BTS_DAYS; RUN;

****COUNT # OF TIES IN RISK SET;

PROC SORT DATA=COMSET NODUPKEY; BY BTS_DAYS; RUN;

*****COUNT TOTAL # OF TIES;
PROC SQL NOPRINT;
SELECT COUNT(TIEYN) INTO :TOTTIE FROM COMSET;QUIT;

*****COUNT # OF TIES UP TO T;
DATA COMSET2; SET COMSET;
BY BTS_DAYS;
IF TIEYN EQ . THEN TIEYN =0;
IF FIRST.BTS_DAYS;
TIENT+TIEYN;

103

IF LAST.BTS_DAYS THEN OUTPUT;
RUN;

*****# OF TIES IN RISK SET AT TIME T;
DATA COMSET3; SET COMSET2;
TIENUM = &TOTTIE - TIENT;
RUN;

*****COMPUTE THE SUMMATION PART OF MODIFIED GW VAR;
DATA MGWSET; SET COMSET3;
BY BTS_DAYS;
IF FIRST.BTS_DAYS;
MGWSUM + EVNUM/(RSNUM*(RSNUM-EVNUM))*(1+2*TIENUM/RSNUM);
IF LAST.BTS_DAYS THEN OUTPUT;
RUN;

****************************************************
KM ESTIMATE+GW FORMULA
****************************************************;
%LIFTST(TMP1,KM1,BTS_DAYS,BTS_EVNT);

DATA KM2(DROP=_CENSOR_ SDF_STDERR);
SET KM1;
WHERE _CENSOR_ EQ 0;
RENAME SURVIVAL=BTS_SRV;
BTS_GWVR=(SDF_STDERR)**2;
BTS_GWVRCR=BTS_GWVR*(1+&A1B2N/&A1N);
RUN;

***************************************************
COMPUTE MODIFIED GREENWOOD VARIANCE COMPONENTS
***************************************************;

DATA MGWSET2; MERGE KM2(IN=A) MGWSET; BY BTS_DAYS;
IF A;
BTS_MDGWVR=(BTS_SRV)**2*MGWSUM;
RUN;

*****************************************************
3 YR SURVIVAL
*****************************************************;
%LET YEARD=%SYSEVALF(365.25);
%LET SRVT3Y=3*&YEARD;

*****KEEP ONLY EVENT TIME;
DATA OUT1;
SET MGWSET2;
DIF3=ROUND(&SRVT3Y-BTS_DAYS,.0001);
RUN;

*****SEARCH FOR LAST EVENT TILL YEAR 3;
PROC SQL NOPRINT;
SELECT MIN(DIF3) INTO :D3EST1 FROM OUT1
WHERE (DIF3 GE 0);

104

QUIT;

********************************************
OUTPUT ONLY 3YR SURVIVAL
********************************************;
DATA &BTOUT1;SET OUT1;
IF (DIF3 EQ &D3EST1) THEN OUTPUT; RUN;

%MEND BOOTSTRP;

****************************************************
MACRO:REPLICATE BOOTSTRAP PROCESS
PARAMETER:
TRLDAT = INPUT DATASET
RXA = EARLY TREATMENT ASSIGNMENT
RXB = LATE TREATMENT ASSIGNMENT
BTDAT = OUTPUT DATA WITH ALL BOOTSTRAP LOOPS
BTEST = ESTIMATES FOR GIVEN TIME POINT

****************************************************;

%MACRO BOOTEST(TRLDAT,RXA,RXB,BTDAT,BTEST);

PROC PRINTTO LOG='C:\BOOTAPP.LOG' NEW;RUN;

%LET BTSTRPN=500;

****************************************************
PREPARE AB1 & AB2 DATA FOR BOOTSTRAP
VARIABLES IN TRLDAT:
STGIIYN = 0/1, SURVIVE STAGE I
STGIIRX = 0/1/., STAGE II RANDOMIZATION
STGIIDRP = 1-STGIIRX, STAGE II DROPOUT
X_I = 1/2, STAGE I TREATMENT
Z_I = 1/2, STAGE II TREATMENT
DAYSL = DAYS ON STUDY
STATUS = 0/1, EVENT OR CENSORING

****************************************************;

PROC SQL;
CREATE TABLE WK0 AS
SELECT STGIIYN,STGIIRX,STGIIDRP,X_I,Z_I,
DAYSL AS BTS_DAYS, STATUS AS BTS_EVNT
FROM &TRLDAT
WHERE (X_I EQ &RXA);
***SELECT RXB PATIENTS+DROPOUTS;
CREATE TABLE WK1 AS
SELECT * FROM WK0 WHERE Z_I NE (3-&RXB);
****OUTPUT RXB SUBSET;
CREATE TABLE BTWK1 AS
SELECT * FROM WK1 WHERE Z_I EQ &RXB;
***OUTPUT PATIENTS RANDOMIZED TO OTHER ARM;
CREATE TABLE BTWK2 AS

105

SELECT * FROM WK0 WHERE Z_I EQ (3-&RXB);
QUIT;

******COUNT # IN DATABSET;
PROC SQL NOPRINT;
SELECT COUNT(X_I) INTO :ASZ FROM WK0 WHERE (X_I EQ
&RXA);
SELECT COUNT(STGIIYN) INTO :STGIIN FROM WK0 WHERE
(STGIIYN EQ 1);
****NUMBER OF RXB PATIENTS;
SELECT COUNT(Z_I) INTO :ABSZ FROM BTWK1;
SELECT COUNT(Z_I) INTO :ABOSZ FROM BTWK2;
QUIT;

***************************************************
RUN FIRST BOOTSTRAP
***************************************************;
%BOOTSTRP(WK1,BTWK1,0,&BTDAT,BTYR);

***************************************************
RUN BOOTSTRAP REPLICATES & APPEND RESULTS
***************************************************;
%DO G=2 %TO &BTSTRPN;

%LET BTSD=(&G-1)*&ABOSZ;

%BOOTSTRP(WK1, BTWK1,&BTSD,BOOT&G,BYR&G);

PROC APPEND BASE=&BTDAT DATA=BOOT&G;
PROC APPEND BASE=BTYR DATA=BYR&G;
PROC SQL;DROP TABLE BOOT&G;DROP TABLE BYR&G;QUIT;

%END;

******ESTIMATE SURVIVAL & VARIANCE ACROSS ALL LOOPS;

PROC SQL;

CREATE TABLE &BTEST AS
SELECT "BOOTSTRAP" AS ESTYP,MEAN(BTS_SRV) AS
BTSRVMN,STDERR(BTS_SRV) AS BTSRVSE,VAR(BTS_SRV) AS
BTSRVVR,
MEAN(BTS_GWVR) AS BTGWMN,MEAN(BTS_GWVRCR) AS BTGWCRMN,
(1+1/&BTSTRPN)*VAR(BTS_SRV) AS BTBTVR,
MEAN(BTS_GWVR)+(1+1/&BTSTRPN)*VAR(BTS_SRV) AS BTSVEST,
MEAN(BTS_GWVRCR)+(1+1/&BTSTRPN)*VAR(BTS_SRV) AS
BTSVESTCR
FROM BTYR;

QUIT;
%MEND BOOTEST;

106

Appendix B

SAS MACRO for Modified IPW Estimator:
*******************************************************************

MODIFIED IPW ESTIMATOR USING BOOTSTRAP VARIANCE

*******************************************************************;

/*******SAS MACRO ESTIMATING CENSORING SURVIVAL CURVE******/;
%MACRO CSEST(INDAT,OUTDAT,SRVTM,CENS);

PROC LIFETEST DATA=&INDAT METHOD=KM NOPRINT;
TIME &SRVTM*&CENS(1);
SURVIVAL OUT=&OUTDAT (KEEP=&SRVTM _CENSOR_ SURVIVAL);
RUN;

%MEND;

/*******SAS MACRO ESTIMATING KAPLAN-MEIER SURVIVAL CURVE******/;
%MACRO KMEST2(INDAT,OUTDAT,SRVTM,CENS);

PROC LIFETEST DATA=&INDAT METHOD=KM NOPRINT;
TIME &SRVTM*&CENS(0);
SURVIVAL OUT=&OUTDAT (KEEP=&SRVTM _CENSOR_ SURVIVAL);
RUN;

%MEND;

*******************************************************************

ESTIMATE IPW SURVIVAL & VARIANCE
FOR EACH BOOTSTRAP LOOP
PARAMETERS:
BTIN = INPUT DATASET
RSEED = RANDOM NUMBER FOR BOOTSTRAP
ANAOUT = OUTPUT DATASET CONTAINING ESTIMATES

*******************************************************************;

%MACRO IPWBT_REP(BTIN,RSEED,ANAOUT);

%LET YEARD=%SYSEVALF(365.25);

107

*************************************
BOOTSTRAP DATA TO GET ONE REPLICATE
*************************************;

DATA TMP1;
DO I = 1 TO &ASZ;
X=ROUND(RANUNI(I+&RSEED)*&ASZ);
SET &BTIN POINT=X;
OUTPUT;
END;
STOP;
RUN;

*************************************
COMPUTE RANDOMIZATION PROBABILITY
*************************************;

PROC SQL NOPRINT;
SELECT COUNT(Z_I) INTO :ABSZ FROM TMP1 WHERE (Z_I EQ &BRX);
SELECT COUNT(Z_I) INTO :ABSZO FROM TMP1 WHERE (Z_I EQ 3-&BRX);
QUIT;

%LET STGIIPI=&ABSZO/(&ABSZ+&ABSZO);

*******************************************************
COMPUTE # OF EVENTS/CENSORING/AT RISK PER TIME POINT
FOR AjRMS
*******************************************************;

PROC FREQ DATA=TMP1 NOPRINT;
TABLE IPW_DAYS/OUT=WK21(DROP=PERCENT CUM_PCT) OUTCUM;
RUN;

DATA WK21F;
SET WK21;
YU_T=&ASZ-CUM_FREQ+1;
RUN;

*****************************************************
CENSORING SURVIVAL ESTIMATE 4 Aj
*****************************************************;

%CSEST(TMP1,WK31,IPW_DAYS,IPW_EVNT);

*****FIX SURVIVAL AFTER LAST EVENT;

PROC SQL NOPRINT;
SELECT MAX(IPW_DAYS) INTO :CSTMX1 FROM WK31 WHERE (_CENSOR_ EQ 0);
SELECT MIN(SURVIVAL) INTO :CSSRVMN1 FROM WK31 WHERE (_CENSOR_ EQ 0);
QUIT;

108

DATA WK31F;
SET WK31;
WHERE IPW_DAYS NE 0;
IF IPW_DAYS GT &CSTMX1 AND SURVIVAL EQ . THEN DO;
SURVIVAL=&CSSRVMN1;
END;
RUN;

*******************************************************
KAPLAN-MEIER ESTIMATE
*******************************************************;

%KMEST2(TMP1,WK41,IPW_DAYS,IPW_EVNT);

*****FIX SURVIVAL AFTER LAST EVENT;
PROC SQL NOPRINT;
SELECT MAX(IPW_DAYS) INTO :KMTMX1 FROM WK41 WHERE (_CENSOR_ EQ 0);
SELECT MIN(SURVIVAL) INTO :KMSRVMN1 FROM WK41 WHERE (_CENSOR_ EQ 0);
QUIT;

DATA WK41F;
SET WK41;
WHERE IPW_DAYS NE 0;
IF IPW_DAYS GT &KMTMX1 AND SURVIVAL EQ . THEN DO;
SURVIVAL=&KMSRVMN1;
END;
RUN;

********************************
MERGE ALL DATA SETS
********************************;

PROC SQL;

CREATE TABLE IPWA1 AS
SELECT A.*,B.COUNT AS CNTCE,B.YU_T,
C.SURVIVAL AS CS_SRV,D.SURVIVAL AS KM_SRV
FROM TMP1 AS A,WK21F AS B,WK31F AS C,WK41F AS D
WHERE (A.IPW_DAYS=B.IPW_DAYS) AND (B.IPW_DAYS=C.IPW_DAYS) AND
(C.IPW_DAYS=D.IPW_DAYS)
ORDER BY A.IPW_DAYS;

QUIT;

109

****************************************
ESTIMATE SURVIVAL USING IPW ESTIMATOR
****************************************;

*****A1 ARM;
****SET UP NOTATION;
DATA IPWA11;
SET IPWA1;
*****DELTA;
DELTA_I=IPW_EVNT;
*****V(t);
VT_I=IPW_DAYS;
******CENSORING SURVIVOR CURVE;
KVT_I=CS_SRV;
******KAPLAN-MEIER SURVIVING CURVE;
SVT_I=KM_SRV;
*****QX_I;
IF (Z_I EQ &BRX) THEN QX_I=1/(1-&STGIIPI);
IF (Z_I EQ 3-&BRX) THEN QX_I=0;
IF (Z_I NOT IN (1,2)) THEN QX_I=1;

*****SUMMATION FOR F(T) ESTIMATE;
IF (KVT_I NE 0) THEN DO;
FPRDCT_I=(1/&ASZ)*DELTA_I*QX_I/KVT_I*CNTCE;
END;
RUN;

****COMPUTE FAILURE;
DATA IPWA12;
SET IPWA11;
BY VT_I;
IF FIRST.VT_I;
IPW_FAI+FPRDCT_I;
IF LAST.VT_I THEN OUTPUT;
RUN;

**********FIX FAILURE RATE FOR EVENTS FOLLOWING LAST CENSORING;
DATA IPWA12F;
SET IPWA12;
IPW_SRV=1-IPW_FAI;
*****WIPE OUT ESTIMATE FOR "WRONG" PATIENTS;
IF (QX_I EQ 0) THEN DO;
IPW_FAI=.;IPW_SRV=.;
END;
RUN;

110

**************************************************************
ESTIMATE VARIANCE USING IPW ESTIMATOR
**************************************************************;

******************************************************
BINOMIAL VARIANCE
******************************************************;
DATA IPWVA1;
SET IPWA12F;
*****VARIANCE NON-INTGL PART;
VAR_BIN=IPW_FAI-IPW_FAI**2;
RUN;

***EVENTS;
DATA B1TMP(KEEP=VT_I DELTA_I QX_I KVT_I);
SET IPWVA1;
WHERE DELTA_I EQ 1;
RUN;

****CENSORING(ALL);
DATA CENSTMP(KEEP=VT_I DELTA_I KVT_I YU_T KM_SRV);
SET IPWVA1;
WHERE DELTA_I EQ 0;
RUN;

***************************************
SAS IML PROCESURE
**************************************;

PROC IML;

***************************************
READ IN DATA INTO MATRIX
**************************************;
USE B1TMP;
READ ALL VAR {VT_I DELTA_I QX_I KVT_I} INTO B1M;
USE CENSTMP;
READ ALL VAR {VT_I DELTA_I KVT_I YU_T KM_SRV} INTO CENSM;

NB1IN=NROW(B1M);NCEN=NROW(CENSM);

***********************************************************
B1 VARIANCE INTEGRAL PART
**********************************************************;
****MATRIX FOR COMPUTING PROCESS;
INTSM1A=J(NB1IN,NCEN,0);
INTSM1B=J(NB1IN,NCEN,0);
INTSM1C=J(NB1IN,NCEN,0);
INTSM1D=J(NB1IN,NCEN,0);

***********INNER SUMMATION;
DO I=1 TO NCEN;
DO J=1 TO NB1IN;

111

T=B1M[J,1];U=CENSM[I,1];
DO K=1 TO NB1IN;
T2=B1M[K,1];
***ASSIGN INNER SUMMATION COMPONENT OVER EVENTS
FROM TIME U UP;
IF (T>=U) & (B1M[K,4] ^= 0) & (CENSM[I,5] ^= 0)
THEN DO;
INTSM1A[K,I]=(B1M[K,2]*B1M[K,3]/B1M[K,4]);
END;
***EVENT BTWEEN TIME U & T;
IF T2>=U & T2<=T THEN DO;
****INNER SUMMATION;

INTSM1B[J,I]=INTSM1B[J,I]+(&ASZ*CENSM[I,5])**(-
1)*INTSM1A[K,I];
END;
END;
END;
END;

QxI=J(NB1IN,NCEN,0);

***********OUTER SUMMATION;
DO I=1 TO NCEN;
DO J=1 TO NB1IN;
T=B1M[J,1];U=CENSM[I,1];
DO K=1 TO NB1IN;
T2=B1M[K,1];
IF T2<=T THEN DO;
QxI[K,I]=B1M[K,3];
END;
IF (T>=U) & (B1M[J,4] ^= 0) THEN DO;
INTSM1C[K,I]=B1M[K,2]*((QXI[K,I]-
INTSM1B[J,I])**2)/B1M[K,4];
END;
****OUTER SUMMATION;
INTSM1D[J,I]=INTSM1D[J,I]+(1/&ASZ)*INTSM1C[K,I];
END;
END;
END;

*******INTEGRAL COMPONENT;
DO I=1 TO NCEN;
DO J=1 TO NB1IN;
IF (CENSM[I,3] ^= 0) & (CENSM[I,4] ^= 0) THEN DO;

INTSM1D[J,I]=(1/(CENSM[I,3]*CENSM[I,4]))*INTSM1D[J,I];
END;
END;
END;

VAR_INTG=J(NB1IN,1,0);

******SUMMER OVER ALL CENSORED;

112

DO I=1 TO NB1IN;
DO J=1 TO NCEN;
VAR_INTG[I,1]=VAR_INTG[I,1]+INTSM1D[I,J];
END;
END;

VT_I=B1M[,1];
CREATE B1INTG VAR {VT_I VAR_INTG};
APPEND;

QUIT;

********************************************
VARIANCE FOR EVENT ONLY
********************************************;
DATA IPWVA2;
MERGE IPWVA1 B1INTG;
BY VT_I;
IPW_BVR=.;
IF Z_I NE 2 THEN DO;
IPW_BVRA=(1/&ASZ)*VAR_BIN;
IPW_BVRB=(1/&ASZ)*VAR_INTG;
IPW_BVR=IPW_BVRA+IPW_BVRB;
END;
RUN;

****************************************!!!!!!!!!!!!!!!!!!!!!!!!!!!
IPW ESTIMATING RESULTS
****************************************!!!!!!!!!!!!!!!!!!!!!!!!!!!;

DATA TMP0;
SET IPWVA2(KEEP=IPW_DAYS IPW_EVNT Z_I
IPW_SRV IPW_BVR IPW_BVRA IPW_BVRB);
RUN;

****************************************
ESTIMATE 4 YR SURVIVAL
****************************************;
%LET SRVT4Y=4*&YEARD;

*****DEFINE THE DIFFERENCE VARIABLE FOR EVENT TIME ONLY;
DATA TMP01;
SET TMP0;
WHERE (Z_I NE 3-&BRX) & (IPW_EVNT EQ 1);
DIF4=ROUND(&SRVT4Y-IPW_DAYS,.0001);
IF DIF4 GE 0;
RUN;

*****SEARCH FOR LAST EVENT TILL YEAR 3/5;
PROC SQL NOPRINT;
SELECT MIN(DIF4) INTO :D4EST FROM TMP01;
QUIT;

113

DATA &ANAOUT;
SET TMP01;
IF (DIF4 EQ &D4EST) THEN OUTPUT;
RUN;

%MEND IPWBT_REP;

**************************************************
BOOTSTRAP DATA TO GET 500 SAMPLES
FOR EACH SAMPLE USING IPW ESTIMATOR
TO GET SURVIVAL ESTIMATE & FROM
THE BOOTSTRAP DISTRIBUTION
OBTAIN THE VARIANCE ESTIMATE
OF THE IPW SURVIVAL ESTIMATE
**************************************************;

%MACRO IPWBT_SET(INDAT,ARX,BRX,BTEST);

PROC PRINTTO NEW LOG='C\IPWBTAPP.LOG’; RUN;

%LET BTSTRPN=300;

*****IMPORT SIMULATED DATASET;
PROC SQL;
CREATE TABLE WK1 AS
SELECT STGIIYN, STGIIRX,STGIIDRP,
X_I,Z_I, DAYSL, STATUS,
DAYSL AS IPW_DAYS, STATUS AS IPW_EVNT
FROM &INDAT
WHERE (X_I EQ &ARX)
ORDER BY IPW_DAYS;
QUIT;

PROC SQL NOPRINT;
SELECT COUNT(X_I) INTO :ASZ FROM WK1;
QUIT;

******BOOTSTRAP PROCESS;
%IPWBT_REP(WK1,0,BT1);

****RUN BOOTSTRAP REPLICATES & APPEND RESULTS;
%DO G=2 %TO &BTSTRPN;

%LET BTSD=(&G-1)*&ASZ;

%IPWBT_REP(WK1,&BTSD,BT&G);

PROC APPEND BASE=BT1 DATA=BT&G;RUN;
PROC SQL;DROP TABLE BT&G;QUIT;

%END;

114

******ESTIMATE 3YR SURVIVAL & VARIANCE;
PROC SQL;
CREATE TABLE &BTEST AS
SELECT "IPW-BOOT" AS ESTYP,"4-YEAR" AS SRVTIME,
MEAN(IPW_SRV) AS IPWSRMN,
VAR(IPW_SRV) AS IPWBTVR,
MEAN(IPW_BVR) AS IPWVRMN
FROM BT1;
QUIT;

%MEND IPWBT_SET;

115

Appendix C

SAS MACRO for Global Test:
/***************************************************

NAIVE ESTIMATOR + STRAM GLOBAL TEST
COMPUTE TEST STATISTIC FOR SIMULATION

****************************************************/;

************************************************
MACRO:KM ESTIMATE--DAYS,CENSORING STATUS
************************************************;

%MACRO KMESTLG(INDAT,OUTDAT,SRVTM,CENS,KMVR,GWVR);

PROC LIFETEST DATA=&INDAT METHOD=KM NOPRINT;
TIME &SRVTM*&CENS(0);
SURVIVAL OUT=KMDAT (KEEP=&SRVTM _CENSOR_ SURVIVAL SDF_STDERR)
STDERR;
RUN;

PROC SQL;
CREATE TABLE &OUTDAT AS
SELECT &SRVTM,(1-_CENSOR_) AS &CENS,
SURVIVAL AS &KMVR,(SDF_STDERR)**2 AS &GWVR
FROM KMDAT
WHERE &SRVTM NE 0;
QUIT;

%MEND KMESTLG;

%MACRO KMEST3YR(INDAT,OUTDAT,SRVTM,CENS,KMVR,GWVR);

PROC LIFETEST DATA=&INDAT METHOD=KM NOPRINT;
TIME &SRVTM*&CENS(0);
SURVIVAL OUT=KMDAT (KEEP=&SRVTM _CENSOR_ SURVIVAL SDF_STDERR)
STDERR;
RUN;

PROC SQL;
CREATE TABLE TMP1 AS
SELECT &SRVTM,(1-_CENSOR_) AS &CENS,
SURVIVAL AS &KMVR,(SDF_STDERR)**2 AS &GWVR
FROM KMDAT
WHERE &SRVTM NE 0;
QUIT;

116

DATA TMP2;
SET TMP1;
WHERE &CENS EQ 1;
TDIFF=ROUND(&SRVT3Y-&SRVTM,.0001);
IF TDIFF GE 0;
RUN;

PROC SQL NOPRINT;
SELECT DISTINCT MIN(TDIFF) INTO :TDIFMIN FROM TMP2;
CREATE TABLE &OUTDAT AS
SELECT &KMVR,&GWVR FROM TMP2
WHERE TDIFF EQ &TDIFMIN;
QUIT;

%MEND KMEST3YR;

***********************************************
MACRO:
NAIVE ESTIMATE
FOR DATA
PARAMETERS:
INDAT INPUT DATASET
SETNUM:SETID 1-1000
OUTDAT:OUTPUT DATASET I

VARIABLES:
SURVIVAL&VARIANCE:
S11-S22 SV11-SV22
************************************************;

%MACRO NVI_SET(INDAT,SETNUM,OUTDAT);

%LET YEARD=%SYSEVALF(365.25);
%LET STGITM=%SYSEVALF(4);
%LET YEARM=%SYSEVALF(12);
%LET STGITD=%SYSEVALF(&YEARD*&STGITM/&YEARM);
%LET SRVT3Y=3*&YEARD;

PROC SQL;
CREATE TABLE WK1 AS
SELECT SIMID,SETID,SUBID,STGIIYN,
STGIIRX,STGIIDRP,X_I,Z_I,DAYSL,STATUS
FROM &INDAT
WHERE (SETID EQ &SETNUM);
QUIT;

117

*********************************
SURVIVAL ESTIMATES
*********************************;

DATA WK2;
SET WK1;
****A1 BRANCH;
IF (X_I EQ 1) THEN DO;
T11=DAYSL;EV11=STATUS;
IF (STGIIDRP EQ 1) OR (Z_I EQ 2) THEN DO;
T11=&STGITD;EV11=0;
END;
T12=DAYSL;EV12=STATUS;
IF (STGIIDRP EQ 1) OR (Z_I EQ 1) THEN DO;
T12=&STGITD;EV12=0;
END;
END;
IF (X_I EQ 2) THEN DO;
T21=DAYSL;EV21=STATUS;
IF (STGIIDRP EQ 1) OR (Z_I EQ 2) THEN DO;
T21=&STGITD;EV21=0;
END;
T22=DAYSL;EV22=STATUS;
IF (STGIIDRP EQ 1) OR (Z_I EQ 1) THEN DO;
T22=&STGITD;EV22=0;
END;
END;
RUN;

%KMEST3YR(WK2,WK21,T11,EV11,S11,SV11);
%KMEST3YR(WK2,WK22,T12,EV12,S12,SV12);

%KMEST3YR(WK2,WK23,T21,EV21,S21,SV21);
%KMEST3YR(WK2,WK24,T22,EV22,S22,SV22);

DATA WK3;
MERGE WK21 WK22 WK23 WK24;RUN;

*****************************
PRIORS:P1 V1 P2 V2
***************************;

****TIME/EVENT FOR A1;
DATA PRR1(KEEP=A1_T A1_EV);
SET WK1;
WHERE X_I=1;
***PRIOR;
A1_T=DAYSL;
A1_EV=STATUS;
IF (STGIIYN EQ 1) THEN DO;
A1_T=&STGITD;
A1_EV=0;
END;
RUN;

118

%KMESTLG(PRR1,PRR2,A1_T,A1_EV,PROB_A1,VAR_A1);

DATA PRR2; SET PRR2;
PROB_A1=ROUND(PROB_A1,.00001);
VAR_A1=ROUND(VAR_A1,.0000001);
RUN;

****PRIORS:P1 & V1;
PROC SQL NOPRINT;
SELECT DISTINCT MIN(PROB_A1) INTO :P1 FROM PRR2 WHERE (A1_EV EQ 1);
SELECT VAR_A1 INTO :V1 FROM PRR2 WHERE (A1_EV EQ 1) &(0 LT PROB_A1
LE &P1);
QUIT;

****TIME/EVENT FOR A2;
DATA PRR3(KEEP=A2_T A2_EV);
SET WK1;
WHERE X_I=2;
***PRIOR;
A2_T=DAYSL;
A2_EV=STATUS;
IF (STGIIYN EQ 1) THEN DO;
A2_T=&STGITD;
A2_EV=0;
END;
RUN;

%KMESTLG(PRR3,PRR4,A2_T,A2_EV,PROB_A2,VAR_A2);

DATA PRR4; SET PRR4;
PROB_A2=ROUND(PROB_A2,.00001);
VAR_A2 = ROUND(VAR_A2,.0000001); RUN;

****PRIORS:P2 & V2;
PROC SQL NOPRINT;
SELECT DISTINCT MIN(PROB_A2) INTO :P2 FROM PRR4 WHERE (A2_EV EQ 1);
SELECT VAR_A2 INTO :V2 FROM PRR4 WHERE (A2_EV EQ 1) & (0 LT PROB_A2
LE &P2);
QUIT;

*********************************
GLOBAL TEST
*********************************;

DATA WK4;
SET WK3;
LENGTH VLNS11 VLNS12 VLNS21 VLNS22
LNS11 LNS12 LNS21 LNS22 8.;
P1=INPUT(SYMGET('P1'),8.);P2=INPUT(SYMGET('P2'),8.);
V1=INPUT(SYMGET('V1'),8.);V2=INPUT(SYMGET('V2'),8.);
VLNP1=V1/P1**2;VLNP2=V2/P2**2;
ARRAY VAR[4] SV11 SV12 SV21 SV22;

119

ARRAY PVR[4] S11 S12 S21 S22;
ARRAY LNP[4] LNS11 LNS12 LNS21 LNS22;
ARRAY LNV[4] VLNS11 VLNS12 VLNS21 VLNS22;
DO I = 1 TO 4;
LNP[I]=LOG(PVR[I]);
LNV[I]=VAR[I]/PVR[I]**2;
END;
DROP I;
CALL SYMPUT('LNS11',LNS11);CALL SYMPUT('LNS12',LNS12);
CALL SYMPUT('LNS21',LNS21);CALL SYMPUT('LNS22',LNS22);
CALL SYMPUT('VLNP1',VLNP1);CALL SYMPUT('VLNP2',VLNP2);
CALL SYMPUT('VLNS11',VLNS11);CALL SYMPUT('VLNS12',VLNS12);
CALL SYMPUT('VLNS21',VLNS21);CALL SYMPUT('VLNS22',VLNS22);
RUN;

PROC IML;

BETA_HAT={&LNS11,&LNS12,&LNS21,&LNS22};
K={1 -1 0 0,0 1 -1 0,0 0 1 -1};
V_HAT={&VLNS11 &VLNP1 0 0,
&VLNP1 &VLNS12 0 0,
0 0 &VLNS21 &VLNP2,
0 0 &VLNP2 &VLNS22};
***NULL HYPOTHESIS:K*BETA_HAT=0;
V_SAND=(T(K*BETA_HAT))*INV(K*V_HAT*T(K))*(K*BETA_HAT);
P_CHI=1-PROBCHI(V_SAND,3);

CREATE TST VAR {V_SAND P_CHI};APPEND;

QUIT;

*********************************
OUTPUT RESULT
*********************************;

DATA &OUTDAT;
MERGE WK4 TST;
SETID=&SETNUM;
RUN;

%MEND NVI_SET;

***********************************************
MACRO:
NAIVE ESTIMATE I
FOR ALL SIMULATED SET
PARAMETERS:
INDAT INPUT DATASET
SETNUM:SETID 1-1000
OUTDAT:OUTPUT DATASET I
************************************************;

%LET SIMTOT=1000;

120

%MACRO NVI_SET_RUN(SMDAT,RSLTDAT);

*PROC PRINTTO NEW
LOG="E:\Users\wang2\Global Test\Stram Test & Result\B arm result
data\POWERB.LOG";
PROC PRINTTO NEW
LOG="E:\Users\wang2\Global Test\Stram Test & Result\AxB result
data\POWERAB.LOG";
RUN;

*****NAIVE ESTIMATE I FOR DATASET 1;
%NVI_SET(&SMDAT,1,&RSLTDAT);

*****NAIVE ESTIAMTE FOR DATASET 2-&SIMTOT;
%DO G = 2 %TO &SIMTOT;

%NVI_SET(&SMDAT,&G,TMP&G);

****APPEND EACH ESTIMATE TO DATA;
PROC APPEND BASE=&RSLTDAT DATA=TMP&G;RUN;

PROC SQL;DROP TABLE TMP&G;QUIT;

%END;

%MEND NVI_SET_RUN;

/******EXAMPLE OF RUNNING GLOBAL TEST FOR SIMULATED DATA******/;

LIBNAME TST 'E:\B Arm raw data';
LIBNAME RLT 'E:\B arm result data';

%NVI_SET_RUN(TST.PWDB101,RLT.PRB101);
%NVI_SET_RUN(TST.PWDB201,RLT.PRB201);
%NVI_SET_RUN(TST.PWDB301,RLT.PRB301);

PROC PRINTTO;RUN;

/***********************************************
ESTIMATE POWER AND TYPE I ERROR
************************************************;

%MACRO TYPII(INDAT);

DATA ANA1;
SET &INDAT(KEEP=P_CHI);
IF (P_CHI NE .) THEN ALPHA=0;
IF (P_CHI NE .) AND (P_CHI LT 0.05) THEN ALPHA=1;
RUN;

PROC FREQ DATA=ANA1;TABLES ALPHA;
TITLE "POWER OF &INDAT"; RUN;

%MEND;

121

Appendix D

SAS MACRO for generating simulation data for Global Test (interaction):
/******************************************************************

Simulation setting:

2 randomization:late (2nd) randomization
administrative censoring
5 year enrollment,
2 year follow till death/censor,
treatment A1 vs A2
modeling A1&A2 branches

sample size n=50x2/100x2/500x2 ---A1SZ
censor time~uniform[2,7] ---C_I
remission/consent 75% ---STGIIRX/STGIIDRP
RX 1 1:1 ---X_I(1/2)
RX 2 1:1 ---Z_I(,1,2)

Stage I:
participants randomized to maintenance therapy at month 4
(days=4*365.25/12)
T_A1:exponential survival with mean 4 years
T_A2:exponential survival with mean 4 years

Stage II:
STAGE I SURVIVOR ---STGIIYN
T_A1B1:EXPONENTIAL WITH MEAN (6,7.5,9,10.5,12,15,18) YEARS
T_drp:exponential survival with mean 6 years
T_A2B1:EXPONENTIAL WITH MEAN (6,4.8,4,3.4,3,2.4,2) YEARS

lamda1/lamda2=1,2/3,1/2,2/5,1/3

******************************************************************/;

*******************************************************************
1).GENERATE RANDOM SAMPLES
*******************************************************************;

****TIME CONSTANTS;
%LET YEARD=%SYSEVALF(365.25);
%LET STGITM=%SYSEVALF(4);
%LET YEARM=%SYSEVALF(12);
%LET STGITD=%SYSEVALF(&STGITM*&YEARD/&YEARM);
****SURVIVAL PARAMETERS;
****MEAN SURVIVAL;
***A TREATMENT;

122

%LET SRVMS2=4;
%LET LMDA2=1/(&SRVMS2*&YEARD);
***B2 TREATMENT;
%LET SRVMS3=8;
%LET LMDA3=1/(&SRVMS3*&YEARD);

*********************************************
SMPSD IS THE ADJUSTING FACTOR FOR THE SEED
OF THE RANDOM SAMPLE,
CHTSZ IS THE TOTAL RANDOMIZED TO A1 BRANCH
SMX IS THE ID FOR SIMULATED SET
*********************************************;

%MACRO RNSMPGEN(SIMSD,CHTSZ,SRVMS,OUTDAT,SMX);

************************************
GENERATE RANDOM VARIABLES
TIME TO CENSORING C_I
A1/2 SURVIVAL TA_I,
B1 SURVIVAL TA1B1_I/TA2B1_I,
B2/DROPOUT SURVIVAL TB2D_I,
************************************;

****LAMDA;
**A1B1;
%LET SRVMS11=(&SRVMS*&SRVMS3);
%LET LMDA=1/(&SRVMS11*&YEARD);
***A2B1;
%LET SRVMS21=(&SRVMS3/&SRVMS);
%LET LMDAS=1/(&SRVMS21*&YEARD);

DATA RANSMP1;
DO I = 1 TO &CHTSZ;
SUBID=I;
C_I=(5*RANUNI(&SEED+2*I+2*&SIMSD)+2)*&YEARD;
TA_I=RANEXP(&SEED+2*I+2*&SIMSD)/(&LMDA2);
TA1B1_I=RANEXP(&SEED+2*I+4*&SIMSD)/(&LMDA);
TB2D_I=RANEXP(&SEED+2*I+6*&SIMSD)/(&LMDA3);
TA2B1_I=RANEXP(&SEED+2*I+8*&SIMSD)/(&LMDAS);
OUTPUT;
END;
DROP I;
RUN;

*************************************
STAGE I RANDOMIZATION
X_I=(1/2)
IDENTIFY STAGE II COHORT
SURVIVOR STGIIYN=0/1
TMP VAR:CHTSZ
*************************************;

123

DATA RANSMP2(DROP=SINUM);
SET RANSMP1;
*****STAGE I RANDOMIZATION;
DO I = 1 TO &CHTSZ;
SINUM=RANUNI(&SEED+2*I+4*&SIMSD);
END;
DROP I;
IF (SINUM LE 0.5) THEN X_I = 1;
ELSE X_I = 2;
****STAGE II INDICATOR;
STGIIYN=1;
*****STAGE I EVENTS;
IF (TA_I LE &STGITD) THEN STGIIYN=0;
RUN;

*****IDENTIFY TOTAL# OF SUBJECTS IN STAGE II
FOR EACH A TREATMENT ARM:
A1STGIIN,A2STGIIN;
PROC SQL NOPRINT;
SELECT DISTINCT COUNT(SUBID) INTO :A1STGIIN
FROM RANSMP2 WHERE (X_I EQ 1) & (STGIIYN EQ 1);
SELECT DISTINCT COUNT(SUBID) INTO :A2STGIIN
FROM RANSMP2 WHERE (X_I EQ 2) & (STGIIYN EQ 1);
QUIT;

**************************************
STAGE II REMISSION/CONSENT
STGIIRX=(.,0,1)
STGIIDRP=(.,0,1)
*************************************;

DATA RANSMP3(DROP=SIINUM1 SIINUM2);
SET RANSMP2;
*********A1 ARM STAGE II DROPOUTS;
IF (X_I EQ 1) & (STGIIYN EQ 1) THEN DO;
DO I = 1 TO &A1STGIIN;
SIINUM1=RANUNI(&SEED+2*I+6*&SIMSD);
END;
END;
DROP I;
IF (0 LE SIINUM1 LE 0.75) THEN DO;
STGIIRX=1;STGIIDRP=0;
END;
IF (0.75 LT SIINUM1 LE 1) THEN DO;
STGIIRX=0;STGIIDRP=1;
END;
*********A2 ARM STAGE II DROPOUTS;
IF (X_I EQ 2) & (STGIIYN EQ 1) THEN DO;
DO I = 1 TO &A2STGIIN;
SIINUM2=RANUNI(&SEED+2*I+8*&SIMSD);
END;
END;
DROP I;
IF (0 LE SIINUM2 LE 0.75) THEN DO;

124

STGIIRX=1;STGIIDRP=0;
END;
IF (0.75 LT SIINUM2 LE 1) THEN DO;
STGIIRX=0;STGIIDRP=1;
END;
RUN;

******STAGE II # OF SUBJECTS IN EACH A ARM
A1STGIIRXN,A2STGIIRXN;
PROC SQL NOPRINT;
SELECT DISTINCT COUNT(SUBID) INTO :A1STGIIRXN
FROM RANSMP3 WHERE (X_I EQ 1) & (STGIIRX EQ 1);
SELECT DISTINCT COUNT(SUBID) INTO :A2STGIIRXN
FROM RANSMP3 WHERE (X_I EQ 2) & (STGIIRX EQ 1);
QUIT;

***************************************
STAGE II RANDOMIZATION
Z_I=.,0,1
***************************************;

DATA RANSMP4(DROP=SIIRXNUM1 SIIRXNUM2);
SET RANSMP3;
*****A1 ARM B RANDOMIZATION;
IF (X_I EQ 1) & (STGIIRX EQ 1) THEN DO;
DO I = 1 TO &A1STGIIRXN;
SIIRXNUM1=RANUNI(&SEED+2*I+10*&SIMSD);
END;
DROP I;
END;
IF (0 LE SIIRXNUM1 LE 0.5) THEN Z_I=1;
IF (0.5 LT SIIRXNUM1 LE 1) THEN Z_I=2;
*****A2 ARM B RANDOMIZATION;
IF (X_I EQ 2) & (STGIIRX EQ 1) THEN DO;
DO I = 1 TO &A2STGIIRXN;
SIIRXNUM2=RANUNI(&SEED+2*I+12*&SIMSD);
END;
DROP I;
END;
IF (0 LE SIIRXNUM2 LE 0.5) THEN Z_I=1;
IF (0.5 LT SIIRXNUM2 LE 1) THEN Z_I=2;
RUN;

****************************************
TIME & STATUS VARIABLE
--DAYSL,STATUS
***************************************;

DATA RANSMP5;
SET RANSMP4;
*****STAGE I EVENT;
IF (STGIIYN EQ 0) THEN DO;
STATUS=1;
DAYSL=TA_I;

125

END;
*****STAGE II;
IF (STGIIYN EQ 1) THEN DO;
*****B2 & DROPOUT SUBJECTS;
IF (Z_I EQ 2) OR (STGIIDRP EQ 1) THEN DO;
TB2D_TOT=TB2D_I+&STGITD;
DAYSL=MIN(TB2D_TOT,C_I);
STATUS=1;
****CENSORING SUBJECTS;
IF (TB2D_TOT GT C_I) THEN STATUS=0;
END;
***A1B1 SUBJECTS;
IF (X_I EQ 1) AND (Z_I EQ 1) THEN DO;
TA1B1_TOT=TA1B1_I+&STGITD;
DAYSL=MIN(TA1B1_TOT,C_I);
STATUS=1;
****CENSORING SUBJECTS;
IF (TA1B1_TOT GT C_I) THEN STATUS=0;
END;
***A2B1 SUBJECTS;
IF (X_I EQ 2) AND (Z_I EQ 1) THEN DO;
TA2B1_TOT=TA2B1_I+&STGITD;
DAYSL=MIN(TA2B1_TOT,C_I);
STATUS=1;
****CENSORING SUBJECTS;
IF (TA2B1_TOT GT C_I) THEN STATUS=0;
END;
END;
RUN;

DATA &OUTDAT;
SET RANSMP5;
SIMID=&SMX;
SETID=&SIMSD;
A1B1MN=&SRVMS;
RUN;

%MEND RNSMPGEN;

/********************************************
RUN SIMULATIONS PER SETTING
*********************************************/;

LIBNAME TST 'C: \AxB raw data';

****MACRO VARIABLES FOR ALL SIMULATIONS;
%LET SIMTOT=1000;

*****FIRST SIMULATION;

%MACRO SMPGENRUN1(SIMSET1,SIMSET2,SIMSET3,A1SRVM);

PROC PRINTTO NEW LOG='C:\AxB raw data\PWDAxB.LOG'; RUN;

126

*****MACRO VARIABLES;
%LET SEED=101711;

*****RUN SIMULATION FOR 1ST DATASET;
%RNSMPGEN(1,100,&A1SRVM,&SIMSET1,1);

*****SIMULATE REST OF THE DATA AND APPEND;
%DO G = 2 %TO &SIMTOT;

%RNSMPGEN(&G,100,&A1SRVM,SMOUT&G,1);

PROC APPEND BASE=&SIMSET1 DATA=SMOUT&G;RUN;
PROC SQL;DROP TABLE SMOUT&G;QUIT;

%END;

*****MACRO VARIABLES;
%LET SEED=151711;

*****RUN SIMULATION FOR 1ST DATASET;
%RNSMPGEN(1,200,&A1SRVM,&SIMSET2,2);

*****SIMULATE REST OF THE DATA AND APPEND;
%DO G = 2 %TO &SIMTOT;

%RNSMPGEN(&G,200,&A1SRVM,SMOUT&G,2);

PROC APPEND BASE=&SIMSET2 DATA=SMOUT&G;RUN;
PROC SQL;DROP TABLE SMOUT&G;QUIT;

%END;

*****MACRO VARIABLES;
%LET SEED=191711;

*****RUN SIMULATION FOR 1ST DATASET;
%RNSMPGEN(1,1000,&A1SRVM,&SIMSET3,3);

*****SIMULATE REST OF THE DATA AND APPEND;
%DO G = 2 %TO &SIMTOT;

%RNSMPGEN(&G,1000,&A1SRVM,SMOUT&G,3);

PROC APPEND BASE=&SIMSET3 DATA=SMOUT&G;RUN;
PROC SQL;DROP TABLE SMOUT&G;QUIT;

%END;

%MEND;

127

/*****EXAMPLES OF USING MACRO TO CREATE SIMULATION DATASETS******/;

%SMPGENRUN1(TST.PWDAB10,TST.PWDAB20,TST.PWDAB30,1);
%SMPGENRUN1(TST.PWDAB1A,TST.PWDAB2A,TST.PWDAB3A,1.25);
%SMPGENRUN1(TST.PWDAB1b,TST.PWDAB2b,TST.PWDAB3b,1.5);
%SMPGENRUN1(TST.PWDAB1c,TST.PWDAB2c,TST.PWDAB3c,1.75);
%SMPGENRUN1(TST.PWDAB1d,TST.PWDAB2d,TST.PWDAB3d,2);
%SMPGENRUN1(TST.PWDAB1E,TST.PWDAB2E,TST.PWDAB3E,2.5);
%SMPGENRUN1(TST.PWDAB1F,TST.PWDAB2F,TST.PWDAB3F,3);

PROC PRINTTO;RUN;

Abstract (if available)

Abstract As two stage randomized study designs gain increased recognition and popularity for oncology studies it remains a challenge to analyze and interpret clinical outcomes due to lack of sufficient research. In this study we investigated existing methodologies and explored novel means to estimate survival probabilities using this study design. First a Naïve Approach was formulated and studied under the extended notion of Intent-to-Treat (ITT) analysis pertinent to two stage design. Secondly a bootstrap variance estimate was proposed for Inverse Probability Weighted (IPW) Estimator to simplify and improve the variance estimate. Thirdly we developed a Bootstrap Approach by creatively using a "hybrid" bootstrap process to handle artificial "dropouts" due to late stage randomization. Finally we conducted power analysis for a global test statistic based on log transformation.

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Asset Metadata

Creator Wang, Ying (author)

Core Title A comparison of methods for estimating survival probabilities in two stage phase III randomized clinical trials

School Keck School of Medicine

Degree Doctor of Philosophy

Degree Program Biostatistics

Publication Date 03/10/2009

Defense Date 01/08/2009

Publisher University of Southern California (original), University of Southern California. Libraries (digital)

Tag bootstrap process,COG,induction therapy,IPW,maintenance therapy,missing data,OAI-PMH Harvest,oncology,phase III,randomized clinical trial,survival analysis,two stage design

Language English

Contributor Electronically uploaded by the author (provenance)

Advisor Azen, Stanley Paul (committee chair), Sposto, Richard (committee chair), Stram, Daniel O. (committee member), Wilcox, Rand R. (committee member), Xiang, Anny (committee member)

Creator Email wang2@usc.edu,ywuscpm@gmail.com

Permanent Link (DOI) https://doi.org/10.25549/usctheses-m2013

Unique identifier UC1492223

Identifier etd-WANG-2623 (filename),usctheses-m40 (legacy collection record id),usctheses-c127-214403 (legacy record id),usctheses-m2013 (legacy record id)

Legacy Identifier etd-WANG-2623.pdf

Dmrecord 214403

Document Type Dissertation

Rights Wang, Ying

Type texts

Source University of Southern California (contributing entity), University of Southern California Dissertations and Theses (collection)

Repository Name Libraries, University of Southern California

Repository Location Los Angeles, California

Repository Email cisadmin@lib.usc.edu