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Estimation of treatment effects in randomized clinical trials which involve non-trial departures

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Estimation of treatment effects in randomized clinical trials which involve non-trial departures

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ESTIMATION OF TREATMENT EFFECTS IN RANDOMIZED CLINICAL TRIALS
WHICH INVOLVE NON-TRIAL DEPARTURES

by
Tingting Ge
________________________________________________________________

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

May 2008

Copyright 2008 Tingting Ge

ii
Dedication
I dedicate my dissertation to my father Ge, Zengjie and my mother Qu, Shaolan.

iii
Acknowledgements
First and foremost, I would like to thank my Supervisor, Dr. Stanley P. Azen. He was
always willing to help on any problems I met. I could not have imagined having a better
advisor and mentor. He was the first person who made Statistics so fun to me and let me
finally decide to start my Ph.D. in Biostatistics. It has been an honor and privilege to
have him as my advisor. Dr. Mark D. Krailo has been like a second advisor to me. I am
deeply grateful for his invaluable support and guidance. Their serious and honest attitude
on research is the trait that I would like to learn from them. This dissertation project will
be impossible without their timeless tutoring.
Second I would also like to thank my committee members Drs. Carolee J. Winstein,
Anny H. Xiang and Larry M. Goldstein for their invaluable contribution, providing me
with the data and helpful discussions. Their personal kindness and scientific enthusiasm
are the best traits that I learn from them.
I would like to thank all my friends and fellow graduate students in the department
for the wonderful time we spent together. I am also indebt to Mary Trujillo and Valerie
Molina etc. for all the administrative help they provided during these years at USC.
Last but not the least, I thank my husband Peng Zhao and my parents for their
unconditional love and continuous support. Their help made a big difference in my life.
To them, I dedicate my dissertation.

iv
Table of Contents
Dedication
Acknowledgements
List of Tables
List of Figures
Abstract
Chapter 1. Introduction
1.1 Statement of the Problem
1.2 Purpose of the Dissertation
1.3 Overview of the Dissertation Topic

Chapter 2. Review of Methods of Estimating the Causal Effect of a Treatment in
RCTs Which Involve Within-trial Noncompliance
2.1. As-treated and Per-protocol Approaches
2.2 Instrumental Variable Approaches
2.3 Potential Outcomes and Latent Class Modeling Approaches
2.4 The Subtraction Method

Chapter 3. Compliance Matching Method for Non-trial Departures
3.1 Notation and Assumptions
3.2 Estimating Treatment Effect by Assuming Constant Relative Risk
3.3 Estimating Treatment Effect by Eliminating Some Latent
Noncompliance Categories
3.4 The Extension to More Than One Non-trial Treatment
3.5 The Likelihood and MLE of the CM Estimator
3.6 Asymptotic Performance of the CM Estimator

Chapter 4. Sensitivity Assessment of the CM Estimator to Assumptions
4.1 Violations of the Condition 3
4.2 Violations of the Condition 5
4.3 Violations of the Condition 4

Chapter 5. Simulation study
5.1 Notation and Estimators
5.2 Simulation Settings and Results for Case 1
5.3 Simulation Settings and Results for Case 2

ii
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vi
vii
viii
1
1
3
4

6

7
7
12
20

26
26
29
31

37
38
39

43
43
45
47

50
50
51
58

v
Chapter 6. Illustration: Two Examples
6.1 A Muscle-Specific Strength Training Study
6.2 A Study on Treatment of Ewing's Sarcoma or Primitive
Neuroectodermal Tumor of Bone

Chapter 7. Discussion
7.1 Summary of Results
7.2 Direction of Future Research

Bibliography

Appendix: Summary of ITT paper finding of the treatment effect on Oswestery
Outocmes

64
64
70

75
75
79

81

86

vi
List of Tables
Table 2.1 Classification of Compliance Behaviors

Table 2.2 The Observable Subgroups and the Mixture Structure of Compliance
Types in Each Subgroup

Table 2.3 Summary Results of the Sommer and Zegger’s Vitamin A trial

Table 3.1 Classification of Latent Compliance Behaviors

Table 3.2 Results of a Hypothetical Trial (notation)

Table 3.3 Classification of Latent Compliance Behaviors When There are Two
Non-trial Treatments

Table 5.1. Simulation Results of R
CM
: Case 1

Table 5.2. Simulation Results of R
CM,
R
ITT,
R
AT,
R
PP
and

R
IV
: Case 1

Table 5.3 Simulation Results of R
CM
: Case 2 under the Assumption of Constant
Relative Risk

Table 5.4 Simulation Results of R
CM,
R
ITT,
R
AT,
R
PP
and

R
IV
: Case 2 Under the
Assumption of Constant Relative Risk

Table 5.5 Simulation Results of R
CM
: Case 2 When Compliance Categories 2, 3
and 8 are Eliminated

Table 5.6 Simulation results of R
CM,
R
ITT,
R
AT,
R
PP
and

R
IV
: case 2 When Compliance
Categories 2, 3 and 8 Are Eliminated

Table 6.1 Classification of Compliance Behaviors for the MUSSEL Example

Table 6.2 Estimation of the Relative Recovery Rate for MUSSEL Study

Table 6.3. Estimation of the Relative Event Occurrence Rate for a Study on Treatment
of Ewing's sarcoma or Primitive Neuroectodermal Tumor of Bone
13

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27

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37

56

57

60

61

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68

70

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vii
List of Figures
Figure 1.1 Non-trial Departures, the Noncompliance Pattern Studied in this Paper

Figure 2.1 Directed Acyclic Graph Illustrating the Causal Connections Between
Randomization, Treatment Received and Outcome of an Imperfect RCT

Figure 2.2 Directed Acyclic Graph of a Clinical Trial With Noncompliance

Figure 3.1. Flowchart of the Compliance Matching Procedures

Figure 4.1 Flowchart of the Estimating Procedure When Condition 3 is Violated

Figure 4.2 Flowchart of the Estimating Procedure When Condition 5 is Violated

Figure 6.1 Flow Diagram of the MUSSEL Randomized Controlled Trial: Exclusion,
Enrollment, Randomization and Compliance

Figure 6.2: Flowchart of CM Method Application for a Study on Treatment of
Ewing's sarcoma or Primitive Neuroectodermal Tumor of Bone
2

8

10

36

44

46

66

73

viii
Abstract

Motivated by a real clinical trial, we consider the problem of estimating the causal
treatment effect of a two-arm randomized controlled trial in which some of the
participants selected a third treatment outside of the protocol. Following Rubin's potential
outcome model approach, we classified the study sample into nine subgroups according
to their potential compliance behaviors under each assignment. Under two alternative sets
of assumptions outlined, a relative risk estimator for a binary outcome is proposed and
estimated for the subgroups of participants identified as providing information to the
causal estimation. Asymptotic performance of the proposed estimator is evaluated both
theoretically and through simulation. Our approach is compared with traditional
approaches including intent-to-treat, per-protocol, as- treated and instrumental variable
analyses. Results show our proposed estimator is asymptotically unbiased and thus gives
a better estimate of the true treatment effect for the subpopulation than other estimators.
Illustration of application to a real dataset is also presented.

1
Chapter 1. Introduction
1.1 Statement of the Problem
In randomized clinical trials, a standard methodological procedure to determine the
sample of participants to be analyzed has been the “intention-to-treat (ITT)” principle,
that is, participants are analyzed according to the treatment they were assigned regardless
of what treatment they actually take. The advantage of ITT analysis is obvious: it retains
balance in prognostic factors arising from the original random treatment assignment and
therefore yields an unbiased estimate of treatment effect when compliance is perfect
1
.

However, almost always, randomized clinical trials (RCTs) are characterized by
imperfect compliance with the randomly allocated treatments. Examples noted by Dunn
8
include the cases that many patients may fail to take their prescribed medicine or only
take part of the prescribed dose; others may take the medicine or treatment that was
assigned to other participants in the trial; some others may even use medication or a
treatment package that is not offered by the trial.
ITT analysis estimates the effect of assigning treatment by comparing treatment
groups as randomized, but not the effect of receiving the assigned treatment, as it does
not consider whether or not participants take or complete the assigned treatment.
Consequently, estimating the effect of receiving treatment in randomized trials which
involve noncompliance is an active topic of research. Although there is an extensive
literature on methods of analysis for two-arm trials which involve the noncompliance
pattern that participants can be considered as switched to the other trial arm, there is little

2
literature on methods of analysis which can be applied to trials with the following non-
compliance pattern in which participants go for a third treatment outside of the trial
protocols. Such cases will be called “non-trial departures” in this dissertation and are
illustrated in Figure 1.1:
Treatment A
Treatment B
Treatment A
Treatment B
Treatment A
Treatment B
Treatment C
Treatment C
Assignment Receipt

Figure 1.1. Non-trial departures, the noncompliance pattern studied in this paper.

A randomized trial which involves non-trial departures as shown in Figure 1.1 is
common in practice. Participants are randomly allocated to treatment A and treatment B.
Treatment A is a newly developed intervention and the aim of the trial is to estimate its
effect. Treatment B is a placebo or standard treatment. Some participants in these
clinical trials refuse to or fail to take the assigned treatment. They either switch to the
other trial treatment or take a non-trial treatment C, which may be another existing
treatment such as standard care, or they simply drop out of the study and do not take any
treatment.

3
So for clinical trials which involve non-trial departures, what has been done to
estimate the effect of taking treatment? The mostly widely used method has been
covariate adjustment. However it is on the basis of assumption of overt selection bias,
that is, we can find all the covariates that distinguish one treatment group from the other.
This noncompliance pattern was studied by Sheng et al.
7
when they investigated the
impact of noncompliance on an ITT analysis of equivalence trials. However, their
research was based on the assumption that compliance status was independent of the
outcome and they did not consider the baseline differences across compliance groups.
Walter et al.
42
in 2006 proposed a preference-based instrumental variable method to
estimate the treatment effect when some participants had the special case of non-trial
departure-drop out. Similar to Sheng et al, they assumed equality of both baseline failure
rates and treatment effects (in relative risk terms) among different treatment subgroups.
In the famous paper of Nagelkerke et al.
3
building a causal framework in which to
estimate treatment effects in two-arm clinical trials where non-compliers switched to the
other trial arm, the authors mentioned that “…it is also difficult to develop a method to
evaluate treatment effects from a trial in which patients can become non-compliers by
taking an intervention that is not under study….Teasing out biological treatment effects in
these circumstances is extremely complex.”.
1.2 Purpose of the Dissertation
This study proposes a method that can be used to identify the effect of receiving an
assigned treatment in randomized clinical trials which involve non-trial departures. It

4
will focus on situations in which compliance is all or nothing (either the participant takes
the assigned treatment or does not). The specific objectives of the study are:
1. To develop a framework for estimating the treatment effect in trials which involve
non-trial departures. It proposes a “compliance matching (CM)” approach that
combines the latent class model approach
5
and the subtraction approach
6
.
2. To investigate the bias and efficiency of the asymptotic performance of the CM
estimator both theoretically and through simulation.
3. To compare the performance of the proposed CM estimator relative to standard
ITT, As-treated(AT), per-protocol(PP) and instrumental variable (IV) estimators
with regard to estimating the true treatment effect.
4. To demonstrate the applicability of the proposed CM approach to examples taken
from the real-world data.
5. To provide a discussion of the proposed method in terms of assumptions and ease
of use.
1.3 Overview of the Dissertation Topic
In Chapter 2, a background review of current methods of estimating the causal effect
of a treatment in randomized clinical trial studies which involve noncompliance is given.
Three standard approaches, AT, PP and IV are introduced in Sections 2.1 and 2.2. The
methods closely related to the proposed compliance matching method, latent class
modeling approach and the subtraction method are introduced in Section 2.3 and Section
2.4.

5
In Chapter 3, the proposed method of estimating the causal effect of the treatment in
two-arm trials which involve non-trial departures is presented. In Section 3.1, notations
and assumptions of this framework is introduced. Two possible alternative conditions are
proposed to generate the CM estimator, illustrated in Section 3.2 and Section 3.3
respectively. In Section 3.4, MLE of the CM estimator is described. In Section 3.5,
asymptotic properties of this estimator are evaluated and efficiency comparison with ITT
estimator is conducted.
A discussion of the assumptions in this framework is provided in Chapter 4. A
simulation design and results are presented in Chapter 5. Two different treatment
scenarios that typically occur in RCTs in practice are considered in Section 4.2 and
Section 4.3, where the accuracy of the large sample properties of the proposed CM
estimator is assessed and compared with ITT, AT, PP and IV estimators.
An application of the proposed method to the MUSSEL study is described in Chapter
6. Discussion of the results, conclusions, and suggestion for further research are
presented in Chapter 7.

6
Chapter 2. Review of Methods of Estimating the Causal Effect
of a Treatment in RCTs Which Involve Within-trial
Noncompliance
Since the 1980s, there has been a great deal of progress in the development of
techniques for estimating the causal effect of receiving treatment in the context of
randomized clinical trials with less than perfect adherence to the assigned treatments.
The methods vary in assumptions, type of statistical model, simplicity, and conditions
under which they can be used. A review of some of the most common methods is
presented here.
For the purpose of clarity and consistency, the following notations are used. The
letters Z, D and Y refer to observed variables: Z represents the treatment assignment, D
represents the treatment actually received, and Y represents the outcome. For participant
i, Y
i
is the outcome, Z
i
is the treatment that participant i is assigned and D
i
is the treatment
that participant i actually takes. The variable Z
i
is binary, taking the value 1 if the
participant i is randomized to treatment A, and taking the value 0 if the participant i is
randomized to the control, which is treatment B. The variable D
i
is also binary, taking
the value 1 if the participant i takes treatment A, and taking the value 0 if participant i
takes the control treatment. Neither of these two approaches respects the randomization
and therefore is subject to potential selection bias. Indeed there are many examples
demonstrating the possibility of arriving at incorrect conclusions when trials are analyzed
using either of these two approaches
16-18
.

7
2.1. As-treated and Per-protocol Approaches
The most common, straightforward approaches used are 1) as-treated (AT) and 2)
per-protocol (PP). In an AT approach, participants are analyzed according to the
treatment they actually received regardless of whether or not they actually complied with
the treatment regimen
15
. In a PP approach, only participants who comply fully with the
treatment are included in the analysis. Neither of these two approaches respects the
randomization and therefore is subject to potential selection bias. Indeed there are many
examples demonstrating the possibility of arriving at incorrect conclusions when trials
are analyzed using either of these two approaches
16-18
. As a result, they should only serve
as secondary analyses following an ITT analysis; they do not replace ITT analysis.
2.2 Instrumental Variable Approaches
In the 1920s, economists, who were typically interested in estimating causal effects
rather than association of variables, made causal inferences based primarily on structure
equation models (SEM). These models rely on the specification of systems of equations
with parameters and variables that attempt to capture behavioral relationships and to
specify causal links between variables
19
. Instrumental variable (IV) techniques were
exploited to assist in making inferences. Instrumental variables are variables that are
explicitly excluded from some equations and included in others and are therefore
correlated with some outcomes only through their effect on other variables
2
.
The instrumental variable techniques were adopted from econometrics and have been
aforementioned methodological pitfalls of AT and PP.

8
To estimate the causal effect of actually receiving treatment, that is, the effect of D
i

on Y
i
, a standard SEM would have the form:
*
i 0 1 i di
Y = β +β D +ε (1)
*
i 0 1 i zi
D = α +α Z +ε (2)
In this model
1
β represents the causal effect of D* on Y . The normally used
Ordinary Least Square approach cannot apply to Equation (1) to estimate
1
β directly
because, as illustrated in Figure 2.1, there are confounding factors U (both observable and
unobservable, which cannot be adjusted by conditioning on U) that influence both the
receipt of treatment D
i
and the outcome Y
i
. That is, D
i
and the error term
i
ε are
correlated.
Z D Y
U
Δ

Figure 2.1. Directed acyclic graph illustrating the causal connections between
randomization, treatment received and outcome of an imperfect RCT
8
.

We can obtain an unbiased and consistent estimate of
1
β by using an instrument
variable or instrument. The instrument must meet the following three main
requirements
9, 22.

(1) The instrument must be correlated with the explanatory variable D
i
.
(2) The instrument cannot be correlated with the error term of its regression on D
i
.
The randomization Z
i
can play the role of instrumental variable in the context of an
RCT because the assumptions needed are usually plausible: Z
i
correlates with D
i
; after

9
conditioning on D
i
and U
i
, Y
i
and Z
i
are independent. Therefore, we can write the
effect of Z on Y as a product of the effect of Z on Dand the effect of D on Y
23
, that is,
Z-Y Z-D D-Y
effect = effect * effect
Note that if it is assumed that there is a linear relationship between each variable, it is
simple to show that
1
β can be estimated by the ratio of sample covariances:

Z-Y
D-Y
Z-D
effect Cov(Z,Y)
effect
effect Cov(Z,D)
= =

N N N N
i=1 i i i=1 i i=1 i=1
N N N N
i=1 i i i=1 i i=1 i=1
Y Z / Z - Yi(1-Zi)/ (1-Zi)
D Z / Z - Di(1-Zi)/ (1-Zi)
=
∑ ∑ ∑ ∑
∑ ∑ ∑ ∑

This is called Bloom’s IV estimator
24
. There are also regression programs written for
implementing the technique. These often use the computational method of two-stage
least squares (2SLS), which first regress D on Z, and then regress Y on the predicted
value of D obtained from the first regression
25
. Mathematically, the estimate will be
same as the single stage estimator presented in Equation (3). However, the advantage of
the 2SLS approach is that it can efficiently combine information from multiple
instruments of over-identified regressions. When the outcome variable is binary, two-
stage probit or logistic regression method is used, which is similar to the 2SLS, except at
the second step, probit or logistic regression is used instead.
An extension of this parametric instrumental variable method is the two-stage
procedure described by Nagelkerke et al.
3
:

10
Z D Y
Δ
E
U
N1
N2

Figure 2.2. Directed acyclic graph of a clinical trial
3
. Z denotes the assigned treatment
through randomization, D the treatment actually received, Y the outcome, U is
confounders that influence both D and Y. N1 and N2 are variables that influence D and
Y, respectively (but not the other), and E is the total of variables having an effect on D
other than Z.
Nagelkerke et al.
3
argue that variable E shown in Figure 2.2 blocks every indirect
path from D to Y. Under the conditions needed for the instrumental variable method, and
by applying Pearl’s back door criterion
10
,
it is enough to condition on E to make the
causal effect of D on Y identifiable, instead of adjusting by the unobserved confounding
factors U. Figure 2.3 is the simplified graph after conditioning on E. There is only one
edge connecting D with Y, implying absence of confounding factors.
Z D Y
Δ
U
N2

Figure 2.3. The simplified graph

At this stage the central issue is how to estimate E. Figure 2.2 shows how E and Z act
together to form D. As an example of how to estimate E, let us assume a multiplicative
effect of Z on D, that is, D = E (D|Z) * E. Then:

11
1) E=0 in the group of Z=1 and D=0. This group comprises a fraction of 1-E(D|Z)
of the Z=1 trial arms;
2) E=1/E(D/Z=1) in the group of Z=1 and D=1. This group comprises a fraction
E(D/Z=1) of the Z=1 trial arm;
3) E is unknown or undetermined in the Z=0 group.
In the case of (3), the values of E can be estimated from number of compliant participants
in the placebo group, or we could use multiple imputation of E in the Z=0 trial arm.
In addition to the assumptions required in the instrumental variable method,
Nagelkerke et al. make an additional assumption which is that the treatment effect does
not depend on the level of the true confounders U on a given scale (for example, a linear
scale or a logistic scale). That is, there is no interaction between confounders U and the
treatment received D. Under these conditions, E has absorbed all the effect of U on D,
thus, the treatment effect of D on Y can be estimated by adjusting for E. The advantage is
that this argument holds whether linear regression, logistic regression or Cox’s
proportional hazards model is used. In all cases, the instrument variable Z as a covariate
in conjunction with E can be used to correct for hidden confounders.
The method that Nagelkerke et al. developed agrees with the conventional
instrumental variable method used in the case of a linear model and is relatively easy to
generalize to more complex settings such as that in which there is a multiplicative effect
of Z on D. However, they make an additional assumption that the confounders caused by
noncompliance cannot act as an effect modifier on the outcome.

12
2.3 Potential Outcomes and Latent Class Modeling Approaches
2.3.1 Potential outcome model
Neymean’s 1923 study of a randomized agricultural experiment
26
later extended by
Rubin
14, 27, 28, 29
to observation studies provided a potential outcome framework called
Rubin Causal Model (RCM). RCM provides a useful basis for understanding the causal
effect of actually receiving treatment in randomized trials which involve noncompliance.
In RCM, each participant i has two potential outcomes, namely Y
i
(0) and Y
i
(1), which are
“potential” responses to receiving treatment A or treatment B, respectively. An outcome
is called potential in the sense that it can only be observed as one value of these two,
Y
i
(0) or Y
i
(1). Consequently, causal effect through the potential outcomes framework is
defined as the average difference between the two potential outcomes across all
participants.
Imbens and Angrist and Angrist
12
, and Imbens and Rubin
2
embedded the
instrumental variables method within the framework of RCM and thus nonparametrically
identified the causal effect of actually receiving a treatment for the subgroup of the
participants who would receive the treatment if assigned to the treatment group and
would receive the control if assigned to the control group (called Complier Average
Causal Effect, CACE), under certain assumptions. In the potential outcome framework,
the assumptions made for the parametric IV estimator are reformulated in a more
transparent manner and are more accessible to statisticians.
D
i
(Z
i
) denotes the potential treatment the participant i would receive if assigned to
treatment Z
i
. This notation reflects the dependence of the treatment received by

13
participant i on the treatment assigned, which is required by the IV assumption (1)
described in section 2.2. Based on a subject’s joint values of D
i
(1) and D
i
(0), that subject
in a two-arm trial can be classified into one of four compliance categories:
Table 2.1. Classification of compliance behaviors.
D
i
(1) D
i
(0) Compliance-category
0 0 Cat 1
1 1 Cat 2
0 1 Cat 3
1 0 Cat 4

Cat 1: Participants who never take treatment A, regardless of randomization
Cat 2: Participants who always take treatment A, regardless of randomization
Cat 3: Participants who always defy their assignment, that is, if randomized to
treatment A they take treatment B and vice versa.
Cat 4: Participants who receive the treatment to which they are assigned, this is the
subpopulation called “compliers”.
In the potential outcome framework, the treatment effect on category 4 subjects can
be expressed as
cat4 cat4 cat4
δ = ( | 1) - ( | 0)
i i i i
E Y Z E Y Z = =
where
cat4
( | 1)
i i
E Y Z = and
cat4
( | 0)
i i
E Y Z = are the mean responses when the category 4
subpopulation of compliers take treatment A and treatment B, respectively. This is the so
called CACE when the outcome of interest is the difference between the two treatments.

14
If we use δ to denote the overall treatment effect, and
cat4
p to denote the proportion
of compliers in the population, then
cat4 cat4 cat4
cat4
δ = p δ (1 p )δ + − . Assuming that there are
no participants who belong to category 3, and randomization does not correlate with
outcomes, Angrist et al.
2,5
would argue that the subjects in category 4, the compliers,
make up the only subgroup that provides information for estimating the causal effect of
receiving treatments. In the case of participants in category 1 and category 2, treatment
effect equals zero because the treatment they are assigned to has no effect on the
treatment they receive since they always take same treatment regardless of
randomization. Thus the CACE can be thought of as the causal effect of treatment
received by the category 4 subpopulation, since only for this population does the
treatment assignment agree with the treatment received. That is, δ =
cat4
p CACE .
where
cat4
p ( | 1) ( | 0)
i i i i
E D Z E D Z = = − = . Therefore, the CACE is
( | 1) ( | 0)
( | 1) ( | 0)
i i i i
i i i i
E Y Z E Y Z
E D Z E D Z
= − =
= − =

2.3.2 Latent class model
The CACE estimator derived in the RCM framework agrees with the standard IV
estimator as derived in section 2.1, and will be referred to as the IV_RCM estimator:

( | 1) ( | 0)
( | 1) ( | 0)
i i i i
i i i i
E Y Z E Y Z
E D Z E D Z
= − =
= − =

However, in Imbens and Rubin’s later work
5
, they developed a latent class
framework, and demonstrated that the IV_RCM estimator is not an efficient estimator of
the CACE because it only makes use of the outcomes of the observable subgroups by

15
cross classifying the assigned treatment and the treatment actually received, but does not
make full use of the underlying mixture structure of the latent compliance types in each
observable subgroup. Table 2.2 presents the observable subgroups and the mixture
structure of compliance types in each subgroup.
Table 2.2. The observable subgroups and the mixture structure of compliance types in
each subgroup .
Observable Subgroups Latent Compliance-category
Z
i
=1, D
i
=1 Cat2 or Cat 4
Z
i
=0, D
i
=1 Cat2 or Cat3
Z
i
=1, D
i
=0 Cat1 or Cat3
Z
i
=0, D
i
=0 Cat1 or Cat4

Let f
zd
(y) be the distribution of outcomes in the observable subgroup defined by Z =
z and D = d, g
i
(y) be the distribution of outcomes among participants whose compliance-
type is category i, and
i
π be the proportion of participants of category i in the population.
Then
1 4
00 1 4
1 4 1 4
( ) ( ) ( ) f y g y g y
π π
π π π π
= +
+ +

3 2
01 2 3
2 3 2 3
( ) ( ) ( ) f y g y g y
π π
π π π π
= +
+ +

3 1
10 1 3
1 3 1 3
( ) ( ) ( ) f y g y g y
π π
π π π π
= +
+ +

2 4
11 2 4
2 4 2 4
( ) ( ) ( ) f y g y g y
π π
π π π π
= +
+ +

16
Assuming that there are no participants from category 3 (those who will take treatment A
if assigned to B and will take A if assigned to B), then the difference of complier
outcomes under each treatment can be derived as follows:
i i i i i i
1 00 0 10 1 11 0 01
i i i i i i i i
i i i i
i i i i
E[Y |Z =1,D =1,i cat4] - E[Y |Z =0,D =0,i cat4]
E[1-D ]E[Y ]-E[1-D ]E[Y ] E[D ]E[Y ]-E[D ]E[Y ]
E(D |Z =1)-E(D |Z =0) E(D |Z =1)-E(D |Z =0)
E(Y |Z =1)-E(Y |Z =0)
E(D |Z =1)-E(D |Z =0)
∈ ∈
= −
=

Although the difference between the two terms
i i i
E[Y |Z =1,D =1,i cat4] ∈ and
i i i
E[Y |Z =0,D =0,i cat4] ∈ is equal to the IV-RCM estimator, the latent class estimator of
the CACE takes into account the underlying mixture structure that is implicitly indicated
in this model, that is, the two terms are required to be nonnegative because they represent
densities of outcome distribution in the latent classes. Therefore, the latent class
estimator has less variance and is more efficient than the IV-RCM estimator.
2.3.3 Inference methods
2.3.3.1 Maximum likelihood method
The maximum likelihood method for CACE estimation which takes account of the
mixture structure of the outcome distributions has been developed and implemented by
Imbens and Rubin
5
, Little and Yau
12
and others. Compared with the method-of-moments
and other traditional estimation methods, , but is flexible, making it relatively easy to
cope with situations in which the required assumptions are not met.
The following is an example of the MLE method for CACE estimation from
uncensored data by assuming normal distribution for the outcomes. Assume

17
2
iA
g (y) ( , )
iA
N μ σ for participants of category i who are assigned to treatment A; and
2
iB
g (y) ( , )
iB
N μ σ for participants of category i who are assigned to treatment B. Then
the likelihood based on the observed data takes the form
L ∝
2 2
2 2 4 4
{ 1, 1}
[ ( | , ) ( | , )]
i i
i A i A
i Z D
g y g y π μ σ π μ σ
∈ = =
+
∏

2 2
2 2 3 3
{ 0, 1}
[ ( | , ) ( | , )]
i i
i B i B
i Z D
g y g y π μ σ π μ σ
∈ = =
× +
∏

2 2
1 1 3 3
{ 1, 0}
[ ( | , ) ( | , )]
i i
i A i A
i Z D
g y g y π μ σ π μ σ
∈ = =
× +
∏

2 2
1 1 4 4
{ 0, 0}
[ ( | , ) ( | , )]
i i
i B i B
i Z D
g y g y π μ σ π μ σ
∈ = =
× +
∏

Little and Yau illustrated the MLE method by using a single consent design trial, in
which the control group cannot get the treatment, and some of the participants from
treatment group do not take the treatment, and hence the presence of participants of
categories 2 and 3 is ruled out. That is,
2
π = 0 and
3
π = 0. Assume
2
1 1
g (y) ( , ) N μ σ for participants who do not take any treatment (assuming the same
distribution between treatment and control groups), and assume
2
2A 2
g (y) ( , )
A
N μ σ for
participants of category 2 in the treatment group, and
2
2B 2
g (y) ( , )
B
N μ σ for
participants of category 2 in the control group. Then the likelihood simplifies to:
L∝
2
4 4
{ 1, 1}
[ ( | , )]
i i
i A
i Z D
g y π μ σ
∈ = =
∏

2
1 1
{ 1, 0}
[ ( | , )]
i i
i
i Z D
g y π μ σ
∈ = =
×
∏
2 2
1 1 4 4
{ 0, 0}
[ ( | , ) ( | , )]
i i
i i B
i Z D
g y g y π μ σ π μ σ
∈ = =
× +
∏

18
where
1 4
1 π π + = . The parameters to estimate are
4
π ,
1
μ ,
4 A
μ ,
4B
μ and
2
σ . The EM
algorithm can be used to compute the maximum likelihood estimates by treating the
unobservable compliance categories in the control group as missing data. EM is an
iterative algorithm consisting of an E step, which can be viewed as imputing the
probability of compliance for participants in the control group, and an M step, which can
be viewed here as an maximization step to maximizes an expected complete-data log
likelihood. The algorithm is applied using the following steps :
• Form initial estimates of the parameters
(0)
θ = (
(0)
4
π ,
(0)
1
μ ,
(0)
4 A
μ ,
(0)
4B
μ ,
(0)2
σ )
T
.
• E step: Compute { 4 | 0, 0, }
k
i i i i
W pr i cat D Z Y = ∈ = =
( ) ( ) 2
4 4 ( )2
( ) ( ) 2 ( ) ( ) 2
4 4 4 1 ( )2 ( )2
1
exp[ ( ) ]
2
1 1
exp[ ( ) ] (1 )exp[ ( ) ]
2 2
k k
i A k
k k k k
i B i k k
y
y y
π μ
σ
π μ π μ
σ σ
− −
=
− − + − − −

based on estimates of the parameters from k
th
step
• M step: Compute new estimates
( 1) k
θ
+
of θ as weighted estimates, with
participants assigned to the treatment group being classified according their actual
observed category of compliance type and participants in the control group
classified in the control group with weight equal to
k
i
W from the E-step. Then the
MLE estimates are :

( 1)
( )
4
{ 0, 0}
1
( )
i i
k
k
AA i
i Z D
N W
N
π
+
∈ = =
= +
∑

( 1)
4
{ 1, 1}
1
( )
i i
k
A i
i Z D
AA
y
N
μ
+
∈ = =
=
∑

19

( 1)
( )
4
( 1)
{ 0, 0}
4
1
( )
i i
k
k
B i i k
i Z D
B
W y
N
μ
+
+
∈ = =
=
∑

( 1)
( )
1
( 1)
{ 0}
4
1
(1 )
i
k
k
i i k
i D
AB BB B
W y
N N N
μ
+
+
∈ =
= −
+ +
∑

( 1)2 ( 1)
2
4
{ 1, 1}
1
[ ( )
i i
k k
A AA i
i Z D
N y
N
σ μ
+ +
∈ = =
= −
∑

+

( 1)
( ) ( ) 2
4 4
{ 0, 0}
( ) (
i i
k
k k
A B i i AB BB
i Z D
N W y N N μ
+
∈ = =
− + +
∑

−

( 1)
( ) ( ) 2
4 4
{ 0}
) (1 )( )
i
k
k k
A B i i
i D
N W y μ
+
∈ =
− −
∑
]
Where N is the total sample size of the study, N
AB
, N
BB
, and N
AA
are the sample
sizes of the four observed subgroups cross classified by the randomization and the
receipt of the treatment, and
( ) ( )
4
{ 0, 0}
i i
k t
B i
i Z D
N W
∈ = =
=
∑
is the estimated number of
participants of Cat 4 in the control group.
• Repeat E and M steps until changes in
( ) k
θ and
( 1) k
θ
+
are negligible.

2.3.3.2 Bayesian method
Imbens and Rubin
30
improved inferences for small sample sizes by combining
Bayesian analysis with the potential outcome model using Gibbs’ sampler. Later
Madigan
13
improved and generalized the approach by formulating the RCM as a
graphical model, which can be viewed as imputing the probability of compliance for
participants in the control group. The following is an example of the Bayesian approach
that Imbens and Rubin have developed.

20
Let Y
i
(D
i
) denote the potential response that participant i would have if treatment D
i

were taken. Because of the assumption of random assignment of Z, we can write the
joint probability function f (Z
i
, D
i
(0), D
i
(1), Y
i
(0), Y
i
(1)) as

i i i i i i i i i i i
f (D (0), D (1), Y (0), Y (1)|Z ) f (Z ) = f (D (0), D (1), Y (0), Y (1)) f (Z )
Bayesian inference for the causal estimands, functions of
i i i i
D (0), D (1), Y (0) and Y (1)
follows from their joint conditional distribution given observed values derived from
above equation, that is, their joint posterior distribution, and thence the posterior
distribution of the CACE.
A prior distribution is assumed on each parameter. Let θ denote the complete
parameter vector, which is (
1
π ,
2
π ,
3
π ,
4
π ,
1A
μ ,
1B
μ ,
2 A
μ ,
2B
μ ,
3A
μ ,
3B
μ ,
4 A
μ ,
4B
μ ,σ )
T
.

If
we assume normal distribution of the outcome with mean
it
μ and variance σ for each
compliance category i taking treatment t, the posterior distribution of θ can be written as

i i i i i
1
( | , , ) ( ) [ f (D (0), D (1), Y (0), Y (1)|Z )]
N
obs obs obs mis mis
i
p Z D Y p dY dD θ θ
=
∝
∏
∫∫

The essence of Imbens and Rubin’s approach is to alternately sample from the
conditional distribution of the missing data using values from the parameters and the
conditional distribution of the observed given values for the missing data.
2.4. The Subtraction Method
Sommer and Zeger developed a method applicable to the case of a binary response
variable and all-or-none compliance for estimating “biologic efficacy”
6
, which is defined
as the effect of treatment relative to a control in the ideal situation in which all

21
participants take the treatment to which they are assigned. Like the CACE, the biologic
efficacy is an index to estimate the causal effect of receiving a treatment. Here this
method is referred to as “the subtraction method”.
2.4.1 Sommer and Zeger’s subtraction method
The subtraction method developed in Sommer and Zeger’s work involved a study of
the use of vitamin A supplementation to reduce mortality among children in Indonesia.
In this clinical trial, half of the children were assigned to the treatment (Vitamin A) and
half were randomized to the control treatment (no Vitamin A). The binary outcome is the
mortality of the children after intervention. Because nearly twenty percent of the
treatment group failed to receive vitamin A as prescribed, Sommer and Zegger expected
that the intention-to-treat analysis understated the efficacy of Vitamin A. Therefore, in
addition to the intention-to-treat analysis, they developed the subtraction method as a
supplement to assess the efficacy of the treatment.
In implementing their method, they displayed the results for the vitamin A trial in a
2×2×2 table (Table 2.3). In the treatment sub table (right), they crossclassified the
participants by their compliance status and their mortality outcome. However in the
control group, the compliance status of each individual was not observable. Therefore, to
infer the missing element in the left sub table, two assumptions were made:
(a) The expected proportions of compliers in the two groups are the same;
(b) Those in the treatment group who did not take Vitamin A had the same mortality
rate as the noncompliers in the control group, since neither group received
treatment.

22
Table 2.3 Summary results of the Sommer and Zegger’s Vitamin A trial
Control
Compliance
Treatment
Compliance

Alive M
00
M
01
M
0.
=
11,514
Alive N
00
=
2385
N
01
=
9663
N
0.
=
12,048
Dead M
10
M
11
M
1.
= 74 Dead N
10
= 34 N
11
= 12 N
1.
= 46
Total M =
11,588
N =
12,094

Under this assumption, the compliant subgroups in the two treatment arms have
balanced potential confounding factors and are therefore comparable. Assumption (b)
appears to be a reasonable assumption for such no placebo controlled trials. Accordingly,
the efficacy is estimated by the relative mortality rate if they had full information for the
cells in table 3. This is expressed as

11 01 11
11 01 11
N /(N +N )
R =
M /(M +M )

where M
01
and M
11
are not observed but can be estimated by virtue of assumptions (a)
and (b) by
M

01 0. 00
M = M - (M/N) N ;

11 1. 10
M = M - (M/N) N .
Substituting equation (2) into equation (1), R is given by
11
1. 10
E(N )
R =
M (N/M) - E(N )

23
The method is called “the subtraction method” because of the following heuristic
derivation of R : Given the null model in which the treatment and control are equivalent,
the two groups should experience same mortality, that is, M
1.
/M = N
1.
/N. Then we can
obtain the total number of deaths expected in the treatment group by applying the
mortality rate of the control group to the treatment population, which is
1.
M (N/M) .
Subtracting the number of deaths that actually occurred among children in the treatment
group who did not receive vitamin A from this estimate of total mortality leaves the
number of deaths expected among vitamin A recipients, that is,
1.
M (N/M) -N
10
. R is the
ratio of the observed death rate in the compliant subgroups who take the treatment to the
expected death rate in the same subgroup who take the control treatment.
However, it should be noted that the Vitamin A study was a single controlled trial,
which eliminated the existence of subjects who are always treatment takers in the
potential outcome framework. Otherwise, the definition of compliant subgroup in the
Vitamin A study was different from the definition of compliant subgroup made in Section
2.2. The latter definition of compliant subgroup means that Sommer and Zeger’s
compliant subgroup was a mixture of real compliers and always takers. Therefore, the
estimator proposed here,

R would not be a CACE estimator unless assumptions such as
no always takers is made.
As described, R is derived by constructing a compliance-mortality table for controls
that uses the same compliance profile as the treatment table, under assumptions (a) and
(b). R estimates the combined biologic impact of treatment as well as any placebo effect
of capsule distribution. The placebo effect is thought ignorable in the vitamin A trial

24
study because the endpoint was mortality. Sommer and Zeger argued that in general the
placebo component and the biologic component of treatment effects based on a study
without placebos cannot be separated.
Sommer and Zegger estimated the efficacy estimator R using the MLE method.
They defined p as a 4×1 vector of mortality rates, that is, p = E (M
1.
/M, N
01
/N, N
10
/N,
N
11
/N) = (p
1
, p
2
, p
3
, p
4
). Then the distribution of mortality follows a multinomial
distribution.
The asymptotic distribution of log(R) is obtained by the usual delta method.
Assuming
$
p is asymptotically normal with mean p and covariance matrix
$
(p)
∑
, where
$
(p)
∑
equals
1 1
2 2 2 3 2 4
2 3 3 3 3 4
2 4 3 4 4 4
p (1-p )/M 0 0 0
0 p (1-p )/N - p p /N - p p /N
0 - p p /N p (1-p )/N - p p /N
0 - p p /N - p p /N p (1-p )/N
 
 
 
 
 
 

The biological efficacy γ is expressed in term of p by
11
1. 10
E(N )
γ =
E(M )(N/M) - E(N )
.
Accoring to the invariance principle for MLEs, R is the maximum likelihood estimate of
γ. The estimator log(R) , being a continuous function of
$
p , is asymptotically normal
with mean log(R) and variance
$ $ $
T
r'(p) (p) r'(p)
   
   
∑
, where
$
1 3 1 3 4
-1 1 1
r'(p) ,0, ,
p -p p -p p
 
=
 
 

25
2.4.2 Extension of the subtraction method to RCTs with two-arm noncompliance
Cuzick et al.
31
extended the subtraction method to the case when experimental
exposure also appears in the control arm, which is defined as “contamination”. They
divided the population into four groups according to their actual compliance behavior:
the intervention complier group in which participants are randomized to the intervention
and comply (with disease rate p
11
), the control complier group in which participants are
randomized to the control and comply(with disease rate p
00
), the non-complier group in
which participants are randomized to the intervention but take the control(with disease
rate p
10
), and the contaminated group in which participants are randomized to the control
but take the intervention (with disease rate p
01
).
The key assumption they made is that the treatment benefits in terms of the relative
risk reductions afforded by the intervention are the same for the participants who were
randomized to the intervention and complied and who were randomized to the control but
took the treatment. By virtue of this assumption, the treatment effect estimator β is
determined from the following equation:
11 01
10 00
αp γp
+(1-α)p = +(1-γ)p
β β

Where α and γ are the proportions of compliers and contaminators respectively. Then
they showed through simulation study that when the baseline outcome rates were the
same for the noncompliers and the contaminators, the estimated treatment effect is larger
than the ITT estimate, although its confidence interval is wider.

26
Chapter 3. Compliance Matching Method for Non-trial
Departures
A new method of analysis, the compliance matching method (CM), to evaluate the
benefit of treatment in two-arm trials which involves non-trial departures is presented. A
study sample is categorized according to the potential compliance behaviors of the
participants. Then, through matching the participants’ compliance categories, the
subtraction method is applied to generate the group of participants whose complete
information about disease risk in the current treatment group and their counterfactual
group is available. A relative risk estimator, called a compliance matching estimator, is
derived in order to estimate the causal effect of the treatment of interest. In Section 3.1,
notations are explained and assumptions behind the use of compliance matching are
introduced. Two possible alternative conditions are proposed to generate the CM
estimator and MLE of the CM method is described. Then asymptotic properties of this
estimator are evaluated and efficiency comparison with ITT estimator under the null is
conducted. Finally, a discussion of the assumptions behind the CM framework is
provided.
3.1 Notation and Assumptions
It is assumed that the outcome variable is binary and the status of a disease is denoted
as (1= disease; 0 = no disease). Randomization is to a novel treatment A and a standard
treatment B. The aim is to evaluate the relative treatment effect of A compared with B.

27
Noncompliers may not only switch to the other group, but also may select a non-study
treatment, denoted as treatment C subsequently. The following notation is used:

jk
p
= (probability of disease | randomized to intervention j, received intervention k)
Pr
jk

= proportion of participants randomized to j who take k.
Pr 1
jk
k
=
∑

R
CM
= relative disease density in people who take treatments A to B, the estimator of
effect of treatment A
j ∈ {A , B}
k ∈ {A , B, C}
Following Imbens and Rubin
5
, we suppose that each participant hypothetically could
be assigned to either treatment A or treatment B, and we make a table representing all
possible compliance behaviors:
Table 3.1. Classification of Latent Compliance Behaviors.
Randomized to A
Received A Received B Received C
Received A Cat1 Cat2 Cat3
Received B Cat4 Cat5 Cat6
Randomized
To B
Received C Cat7 Cat8 Cat9

Table 3.1 characterizes study participants into nine categories:
Cat 1: participants who always take treatment A regardless of the assigned group;
Cat 2: noncompliant participants who are assigned to treatment A but take treatment
B or vice versa;

28
Cat 3: noncompliant participants who take treatment C if assigned to treatment A and
take treatment A if assigned to treatment B;
Cat 4: compliers who take the assigned treatment;
Cat 5: participants who always take B regardless of their group assignments;
Cat 6: participants who take C if assigned to treatment A, but who are otherwise
compliers;
Cat 7: participants who take C if assigned to treatment B, but who are otherwise
compliers;
Cat 8: noncompliant participants

who take treatment B if assigned to treatment A and
take treatment C if assigned to treatment A;
Cat 9: participants who always take C regardless of the group assignment;
The following conditions are assumed to be in force throughout the study. Finally, a
discussion of the assumptions behind the CM framework is provided.
Condition 1: Randomization is carefully applied and data are fully recorded for all
participants.
Condition 2: Potential outcomes for each individual do not depend on the treatment
status of other individuals in the sample;
Condition 3: The treatment benefit in terms of risk reduction in treatment C relative to
risk reduction in treatment B is known for participants who take treatment C.
Under Condition 1, the same baseline characteristics of each category exist in the
two assigned treatment groups. Conditions 2 and 3 are included in most noncompliance
studies. By virtue of Condition 3, randomization has no effect on outcomes other than

29
those resulting from the treatment actually received. Condition 4 makes it possible to
quantify the causal effect of taking a third treatment.
3.2 Estimating Treatment Effect by Assuming Constant Relative Risk
In addition to Conditions 1, 2, 3 and 4 in Section 3.1, we assume the following
assumption:
Condition 5: The relative risk of disease incidence, denoted as r, is constant across
all nine compliance categories.
Condition 5 assumes the same treatment benefit in terms of relative risk reduction
across the compliance categories. This assumption has also been made by S. D. Walter
32

and other investigators
31
. It is plausible when the characteristics that are different across
the latent compliance categories are not effect modifiers of the treatment effect.
Under conditions 1-5, an analytical approach based on the latent classes model and
the potential outcome model is generated as follows:
Let p
im
be the disease incidence for participants from category m assigned to
treatment i after they take standard treatment B. Let n
im
be the number of participants
from class m assigned to treatment i. Under Condition 1, we assume that the compliance
category, as a baseline characteristic inherent for all the participants, has been perfectly
balanced between the two randomized groups. Also, without loss of generality, we
assume equal sample size of the two groups. Then,
∀ m: p
Am
= p
Bm
=

p
m
and n
Am
= n
Bm
= n
m

30
From Table A, we know that N
AA
consists of categories 1, 4 and 7, denoted by, n
AA
=
1 4 7
n n n + +
. Using the above notation, the disease probability of N
AA
participants had
they all

taken treatment

B would be
1 1 4 4 7 7
1 4 7
p n p n p n
n n n
+ +
+ +
. On the other hand, by virtue
of Condition 5, the relative risk reduction is constant across these categories. The disease
probability of the mixture of categories 1, 4 and 7 had they taken treatment B is given by
AA
p
r
. Therefore the following equation is derived:
1 1 4 4 7 7
1 4 7
AA
p n p n p n p
n n n r
+ +
=
+ +

For simplicity, let
1 1
Pn

=
1
x where { 1 9, l categories observable groups ∈ −
, , , , , } AA AB AC BA BB BC . Then the above equation can be rewritten as
1 4 7
( )
AA
r x x x x + + = (1)
The above equation is derived by using information about the subgroup N
AA
. Similarily,
equations can be derived for the other observable subgroups:
2 5 8

AB
x x x x + + = (2)
3 6 9

A AC
x x x a x + + = (3)
1 2 3
( )
BA
r x x x x + + = (4)
In equation (3),
A
a denotes the relative disease risk for the sample N
AC
who take
treatment C to treatment B. That is,
A
a
*
AC
AB
p
p
= , where
* AB
p is the probability of

31
disease for the same sample N
AC
had

they taken standard treatment B. Similarly, in
Equation (6)
B
a is the disease rate ratio of the sample N
BC
taking treatment C relative to
taking treatment B, so
B
a
*
BC
BB
p
p
= , where
* BB
p denotes the probability of disease in the
sample N
BC
had

they taken standard treatment B.
By (4) + (5) + (6) - (2) - (3), we get
-1
1 4 7
- -
BA BB B BC A AC AB
x x x r x x a x a x x + + = + + (7)
Combining (1) and (7) gives
-1

- -
AA
BA BB B BC A AC AB
x
r
r x x a x a x x
=
+ +

Solving the equation for r , and substituting
l
x for
l l
p N ,

we get

Pr Pr
Pr Pr Pr Pr
AA AA BA BA
CM
BB BB BC B BC AB AB AC A AC
p p
R r
p a p p a p
−
= =
+ − −
(8)
3.3 Estimating Treatment Effect by Eliminating Noncompliance
Categories
In Section 3.1, we established that there are nine possible categories of compliance
behaviors. In Section 3.2, in order to estimate the effect of treatment A, we assumed that
the relative risk reduction is the same across the compliance categories. Here we propose
an alternative assumption to relax this constraint. In the presence of noncompliance, the
relative risk in the two complier subgroups S
A4
and

S
B4,
is an estimator of the biological
efficacy. In this section, Sommer and Zeger’s idea is adapted. Their idea was to exclude

32
as many noncompliant subgroups as possible to eliminate the potential selection bias
resulting from the noncompliance and then derive the rate of disease in the rest of the
relatively comparable complier subgroups in each treatment arm.
Condition 5*: There are no participants who were from categories 2, 3 and 8. Those
participants always refused their randomized treatment assignment. This assumption is
made by in most studies of noncompliance.
Table 3.2 shows the data structure design and what is actually observed using the
notation and conditions described thus far.
Table 3.2. Results of a hypothetical trial (notation)
C1 C2 C3 C4 C5 C6 C7 C8 C9
Data structure
Randomized to A S
A1
S
A2
S
A3
S
A4
S
A5
S
A6
S
A7
S
A8
S
A9

Randomized to B S
B1
S
B2
S
B3
S
B4
S
B5
S
B6
S
B7
S
B8
S
B9

What we observe
Randomized to A
N
AA
= S
A1
+ S
A4
+ S
A7

N
AB
= S
A5
+

S
A2
+ S
A8

N
AC
= S
A6
+S
A3

+S
A9

Randomized to B
N
BA
= S
B1
+ S
B2
+ S
B3

N
BB
= S
B4
+ S
B5
+

S
B6

N
BC
= S
B7
+ S
B8
+S
B9

Step 1:
N
AB
and N
AC
are pooled

together, replacing the disease probability
AC
p in N
AC
with
* AB
p , yielding the disease probability of participants from Categories 5 and 6 who

33
were assigned to treatment A, had they taken treatment B. This probability is expressed
as
Pr Pr
Pr Pr
AB AB AC B AC
AB
AB AC
p a p
p
+
+
=
+

Step 2:
Table 2 shows N
BB
= S
B4
+ S
B5
+

S
B6
, which indicates that the observable B takers in
randomization group B are not only members of the complier group (Category 4), but
also are members of categories 5 and 6. In step 1, we estimated the disease probability of
participants from Categories 5 and 6 assigned to treatment A, had they received treatment
B. Under condition 1, the same number and baseline characteristics of participants from
Categories 5 and 6 should potentially exist in randomization group B. Since participants
in Categories 5 and 6 take treatment B, their disease probability is
AB
p
+
and the
proportion is Pr
AB
and Pr
AC
respectively. This makes it possible to calculate the number
of subjects from Categories 5 and 6 in N
BB
who get the disease, (Pr Pr )
AB AC AB
p
+
+ . The
remaining disease occurrence from N
BB
would have occurred among the true compliers
(Category 4) randomized in treatment B. Therefore, the probability of disease among the
participants from Category 4 in treatment B assignment group is
*
Pr (Pr Pr )
Pr Pr Pr
BB BB AB AC BA
BB
BB AB AC
p p
p
+
− +
=
− −

It is worth noting that to making this formula work implicitly requires
Pr Pr Pr
BB AB AC
> + , that is, the proportion of participants who were assigned to A but

34
take other treatments should not exceed the number of participants who were assigned to
B and take B.
Similarly, disease occurrence density of participants in category 1 can be separated
from the mixture of categories 1, 4 and 7 in the N
AA
group. The disease occurrence
density of category 1 in treatment B assignment group is observable, because, by virtue
of condition 5, the observable N
BA
group consists only of Category 1 participants, which
is
. BA B
p N . Under Condition 1 that there are no baseline characteristic differences
between category 1 participant enrolled in treatment A and those enrolled in treatment B
and Condition 3 that the treatment assignment is unrelated to the potential outcomes
given the treatment received, it is safe to say that participants from category 1 in the two
assignment groups have the same disease occurrence as they all take treatment A.
Therefore the number of participants who have the disease in category 1 in treatment A is
.
Pr
BA BA B
p N . Accordingly, the disease probability for the mixture of categories 4 and 7
in the randomization group B is
Pr Pr
Pr Pr
AA AA BA BA
AA
AA BA
p p
p
+
−
=
−

Step 3:
Next, we pool N
BC
, the participants from category 7

and the true compliers, the
participants from category 4 in the randomization group B together, replacing
BC
p
with
* BB
p , to get the disease occurrence density across categories 4 and 7 had they all
taken treatment B, which is

35
*
*
(Pr Pr Pr ) Pr
Pr Pr Pr Pr
BB AB AC BB B BC BB
BB
BB AB AC BC
p a p
p
+
− − +
=
− − +

Step 2 yields the disease occurrence density for the mixture of participants from
Categories 4 and 7 in the randomization group A, had they all received treatment A,
AA
p
+
.
Accordingly, the relative risk of disease in participants from categories 4 and 7 of
randomization group A to group B is:
Pr Pr
Pr Pr Pr Pr
AA AA AA BA BA
CM
BB BB BB BC B BC AB AB AC A AC
p p p
R
p p a p p a p
+
+
−
= =
+ − −

If we can assume same relative risk reduction by treatment A in participants from the
two categories 4 and 7, or we can assume that there are no participants from category 7 in
the study, then the derived relative risk estimator R
CM
is equal to the relative risk rate R
4

for true compliers from categories 4, which is an estimator of CACE, using Imbens and
Rubin’s definitions.

36
Figure 3.1. The flow chart of the modeling procedures.
Pr
AA
Pr
BA
P
AB
+
P
AA
Pr
AB
Pr
AC
Pr
BB
Pr
AB
Pr
AC
Pr
AA Treatment A
Pr
BB
Pr
BC
Pr
BA
Treatment B
P
AB
P
AC
P
AA
P
BB
P
BC
P
BA
Pr
BA
Pr
BA
P
AA**
Pr
AB
+
Pr
AB
+
P
BA
Step 1
Step 2
Pr
BA
Pr
BA
P
AA**
Pr
AB*
P
BA
Pr
AB*
P
BB**
P
BA
Step 3
P
BB*
Pr
BC
Pr
BC
P
AB
+
P
AB
+
P
AB
+
P
AB
+
C
4,5,6
C
1
C
7,9
C
5,6,9
C
4
C
7
C
1
P
BB
P
BA
P
BC
P
BC
P
BA
C
5
C
6,9
C
1,4,7
C
5,6,9
C
1,4,7
C
4,5,6
C
7,9
C
1
C
5,6,9
C
1,4,7
C
5,6,9
C
4,7
C
1
C
5,6,9
C
4,7
C
1

37
3.4 The Extension to More Than One Non-trial Treatment
When there are non-compliant participants who go to two non-trial treatments C and
D, the noncompliance types can be classified into sixteen categories as shown in Table
3.3.
Table 3.3. Classification of latent compliance behaviors when there are two
non-trial treatments.
Randomized to A
Receive A Receive B Receive C Receive D
Receive A Cat1 Cat2 Cat3 Cat10
Receive B Cat4 Cat5 Cat6 Cat11
Receive C Cat7 Cat8 Cat9 Cat12
Randomized
to B
Receive D Cat13 Cat14 Cat15 Cat16

Then under Condition 5*, there are no participants who are against both assignments,
categories 2, 3 10, 8, 14 and 15 are eliminated. By using similar three steps illustrated in
section 3.3, a subset of participants, from categories 4, 7, 13 can be drawn after
compliance classes matching. For these participants, we are able to compute their
potential outcomes of taking treatment A and treatment B, therefore, we can estimate the
relative risk by using similar three steps illustrated in sections 3.3 and 3.4, which takes
the form:
Pr Pr
Pr Pr Pr Pr
AA AA AA BA BA
CM
BB
BB BB i i i AB AB j j j
i j
p p p
R
p
p a p p a p
+
+
−
= =
+ − −
∑ ∑

38
This is the relative risk estimated from all the categories that provide information for
estimating the causal effect of receiving treatment A.
3.5 The Likelihood and MLE of the CM estimator
Let
k
m and
k
n be the observed number of disease occurrences and the sample size
in the k
th
observable subgroup, { , , , , , } k AA AB AC BB BA BC ∈ . Then for each subgroup,
k
m follows a binomial distribution with mean
k k
n p and variance (1 )
k k k
n p p − . Let P
u r

be a 6×1 vector of disease rates of the six observable subgroups, that is,
( )
AA AB AC BA BB BC
P = p , p , p , p , p , p
u r
. Overall the binomial likelihood function is
expressed as
} { , , , , ,
( ) (1 )
k k k
m n m
k k
k AA AB AC BA BB BC
l P p p
−
∈
= −
∏
ur

Standard likelihood estimation methods show that
k
p can be estimated by
k
k
m
n
.
Accordingly, given the invariance property of MLEs, the relative risk
CM
R expressed by
equation (8) leads to the maximum likelihood estimator of the treatment effect:

Pr Pr
Pr Pr Pr Pr
AA BA AA BA
CM
BB BC AB AC BB BC B AB AC A
p p
R
p a p p a p
−
=
+ − −

Where { , ,....} i BC BD ∈ , { , ,....} j AC AD ∈ and
*
i
i
B
p
a
p
=

39
3.6 Asymptotic Performance of the CM Estimator
3.6.1 Consistency, unbiasness and asymptotic normality of

CM R .
First, we calculate the asymptotic mean of

CM R . A multivariable Taylor series
expansion of

CM R around P
u r
gives

{ }

{ }
2
2
2
, , , ,
,
, , , ,
1 1
( ) ( ) ( ) ( ) ( )
2
CM CM
CM
i j CM i i p
AA AB AC AA AB AC
i i j i i j
BA BB BC BA BB BC
R R
R P R P p p p p O
p p p N
∈ ∈
∂ ∂
= + − + − +
∂ ∂
∑ ∑
u r u r

Thus,

{ }

{ }
2 2
2
, , , ,
,
, , , ,
1 1
( ) ( ) ( ( ) ) ( )
2 2
CM CM
CM
j CM i CM
AA AB AC AA AB AC
i j k i j k k
BA BB BC BA BB BC
R R
aE R R P E p p R P
p p p p
∈ ∈
∂ ∂
= + − = +
∂ ∂
∑ ∑ ∑
ur
where
0
CM
AA AA
R
p p
∂
=
∂

[ ]
2
2
2Pr
(1 Pr Pr ) Pr Pr Pr
CM AB CM
AB AB
BC BA BB BC B BC AB AB AC A AC
R R
p p
p a p p a P
∂
=
∂
− − + − −

[ ]
2 2
2
2Pr
(1 Pr Pr ) Pr Pr Pr
CM AC A CM
AC AC
BC BA BB BC B BC AB AB AC A AC
R a R
p p
p a p p a P
∂
=
∂
− − + − −

0
CM
BA BA
R
p p
∂
=
∂

( )
[ ]
2
2
1 Pr Pr
(1 Pr Pr ) Pr Pr Pr
BC BA CM CM
BB BB
BC BA BB BC B BC AB AB AC A AC
R R
p p
p a p p a p
− − ∂
=
∂
− − + − −

[ ]
2 2
2
Pr
(1 Pr Pr ) Pr Pr Pr
CM BC B CM
BC BC
BC BA BB BC B BC AB AB AC A AC
R a R
p p
p a p p a p
∂
=
∂
− − + − −

40
Hence, substituting all these derivatives we get

2 2 2
2
2 2 2
2
1 (1 ) (1 )
( ) (2Pr 2Pr
2
(1 ) (1 ) 1
Pr Pr ) ( )
CM AB AB AC AC
CM
CM AB AC A
AB AC
BB BB BC BC
BB BC B p
BB BC
R p p p p
aE R R a
D n n
p p p p
a O
n n N
− −
= − +
− −
+ + +

where
[ ]
2
(1 Pr Pr ) Pr Pr Pr
BC BA BB BC B BC AB AB AC A AC
D p a p p a p = − − + − −
Let the total sample size be N=N
A
+N
B
, then the above yields,

2
2
1 1
( ) 2Pr (1 ) 2Pr (1 )
2
CM
CM
CM AB AB AB AC A AC AC
R
aE R R p p a p p
N D

= − − + − 




}
2
2
1
Pr (1 ) Pr (1 ) ( )
BB BB BB BC B BC BC p
p p a p p O
N
+ − + − + 

(1)
The derivation implies that the bias term vanishes as the sample size N goes to infinity.
Therefore the MLE of
CM
R is consistent and unbiased.
Now that

lim Pr{ } 1 CM
n CM
R R ε
→∞
− < = , the multivariate delta method gives the
asymptotic distribution of
CM
R :

1
2
( ( )) (0, ( ))
d
CM CM
CM
N R E R N V R −  →
in which the asymptotic variance of

CM R is given by

' '
( ) ( ) ( ) ( ) (1)
T
CM
CM CM p
V R R P p R P o
   
= +
   
∑
ur u r ur

41
Then the limiting variance is

( )

{
2
2
2 2 2
2
( ) Pr ( ) Pr ( ) [Pr ( )
Pr Pr
CM
CM
AA BA AB AA BA CM AB
AA BA AA BA
R
aV R V p V p R V p
p p
= + +
−

}
2 2 2 2 2
Pr ( ) Pr ( ) Pr ( )]
BB AC BC BB AC A BC B
V p a V p a V p + + + (2)
3.6.2 Efficiency comparison with the intent to treat analysis assuming constant
relative risk
In the null situation, both ITT and CM estimators are unbiased; therefore it is
possible to compute the relative efficiency of these two estimators to test the same
hypotheses that treatments A and B are equally effective. Let
i
p
•
denote probability of
disease for participants who were randomized to treatment i , where i = A or B. The
treatment effect estimator
ITT
R in intent-to-treat analysis is given by
.
.
Pr Pr Pr
Pr Pr Pr
A AA AA AB AB AC A AC
ITT
B BA BA BB BB BC B BC
p p p a p
R
p p p a p
+ +
= =
+ +

Using the same approach to estimate the asymptotic mean and variance of

CM R
yields:

1 Pr Pr Pr
( ) ( )
Pr Pr Pr
AA AA AB AB AC A AC
ITT
ITT p
BA BA BB BB BC B BC
p p a p
aE R R O
N p p a p
+ +
= + ≈
+ +

{
2 2 2 2 2 2
2
1
( ) Pr ( ) Pr ( ) Pr ( ) [Pr ( ) ITT
AA AA AB AB AC A AC ITT BA BA
B
aV R V p V p a V p R V p
p
•
= + + +
}
2 2 2
Pr ( ) Pr ( )]
BB BB BC B BC
V p a V p + +

42
According to Lemma 9.14
33
, the efficacies of testing equivalence by these two
approaches are:

( )
2 2
1
Pr Pr /
| [Pr ( ) Pr ( )
( )
CM
CM
AA AA BA BA CM
CM R AA AA BA BA
CM CM
p p ER R
c V p V p
N R
NaV R
=
− ∂ ∂
= = = +
2 2 2 2 2 2 2 1/ 2
(Pr ( ) Pr ( ) Pr ( ) Pr ( ))]
CM AB AB BB BB AC A AC BC B BC
R V p V p a V p a V p
−
+ + + +

2 2
1
/ (Pr Pr )
| [Pr ( ) Pr
( )
( )
ITT CM
ITT
CM BA BA AA ITT AA
ITT R R AA AA AB
B CM ITT
ER R p R p
c V p
p N R
NaV R
= =
•
∂ ∂ −
= = +
2 2 2 2 2 2 1/ 2
Pr ( ) Pr ( ) Pr ( ) Pr ( )]
AC A AC BA BA BB BB BC B BC
a V p V p V p a V p
−
+ + + +
Hence, the asymptotic relative efficiency of the proposed analysis and the ITT analysis is
2
( : ) ( ) 1
CM
ITT
c
ARE CM ITT
c
= =
This demonstrates that the proposed estimator has an equal power of testing equivalence
of two treatments as the ITT estimator.

43
Chapter 4. Sensitivity Assessment of the CM Estimator to
Critical Assumptions
In Chapter 3 a series of assumptions are laid out to identify the causal effect of the
new treatment. In this chapter the sensitivity of the proposed CM analysis to deviations
from these assumptions will be discussed. We focus on Assumptions 3, 4 and 5 because
they form the core of our framework.
4.1 Violations of the Condition 3
Condition 3: the treatment assignment is unrelated to the outcomes given the
treatment received;
First, violations of the Condition 3 are considered. We maintain other assumptions in
this case. If participant i is not from categories 4 or 7, then the causal effect of Z on Y is
defined as ( 1, ) - ( 0, )
i i i
H Y z d Y z d = = = . Accordingly, the effect for participants from
category m is defined as E [ ( 1, ) - ( 0, )]
i i
i cat m i cat m
H Y z d Y z d
∈ ∈
= = = .
Proposition 1. Give all the conditions outlined in the framework except condition 3, the
causal treatment effect is given by
1
5 6,9
(Pr Pr ) [ ](Pr Pr )
(Pr Pr Pr Pr ) Pr [ ] Pr [ ]
AA AA BA BA AA BA
CM
BB BB BC B BC AB AB AC A AC AB AC
p p E H
R
p a p p a p E H E H
− − −
=
+ − − + +

The bias due to violations of condition 3 is composed of two factors. The first factor
1
(Pr Pr ) [ ]
AA BA
E H − in the numerator is related to the proportion of participants from
category 1 and is equal to zero under condition 3. The second factor

44
5 6,9
Pr [ ] Pr [ ]
AB AC
E H E H + in the denominator is related to the proportion of participants
from category 5, 6 and 9.
As we see from the flowchart (Figure 4.1) below, the estimator can be written as:
4,7
4,7
[ ( 1, 1)]
[ ( 0, 0)]
i cat
CM
i cat
E Y Z D
R
E Y Z D
∈
∈
= =
=
= =
.
Pr
AB
Pr
AC
Pr
AA Treatment A
Pr
BB
Pr
BC
Pr
BA
Treatment B
P
AB
P
AC
P
AA
P
BB
P
BC
P
BA
C
4,5,6
C
1
C
7,9
C
5
C
6,9
C
1,4,7
Treatment A
Treatment B
H
5,6
, H
9 H
1
Pr
BA
Pr
BA
PAA**
Pr
AB
+
PBA
Pr
AB
+
PBB** PBA
PAB
+
C5,6,9 C4,7 C1
C5,6,9 C4,7 C1
PAB
+

Figure 4.1 Flowchart of the estimating procedure when condition 3 is violated.
Under Condition 3, basing on the subtraction method, we have
4,7 1,4,7 1
[ ( 1, 1)] [ ( 1, 1)] [ ( 1, 1)]
i cat i cat i cat
E Y Z D E Y Z D E Y Z D
∈ ∈ ∈
= = = = = − = = .

45
However, when there is a direct effect of assignment on the outcome,
1
[ ( 1, 1)]
i cat
E Y Z D
∈
= = equals
1 1
[ ( 0, 1)]
i cat
E H Y Z D
∈
+ = = . Similarly, without
condition 3,
4,7
[ ( 0, 0)]
i cat
E Y Z D
∈
= = equals
4,5,6,7,9 5,6,9
[ ( 0, 1)] [ ( 1, 1)]
i cat i cat
E Y Z D E Y Z D
∈ ∈
= = − = = with a bias term resulted
from categories 5, 6 and 9.
4.2 Violations of the Condition 5
Condition 5: there are no participants who are against both assignments.
Next, violations of the condition 5 are considered. Because all other conditions
proposed in the CM method are maintained, so the effect of taking treatment for
participant i is still uniquely defined, and equal to Y
i
(1) – Y
i
(0).
Proposition 2. Given all the conditions outlined in the framework except condition 5, the
causal treatment effect is given by
2,3 2,3
2,3 2,3
(Pr Pr ) Pr (1)
(Pr Pr Pr Pr ) Pr (0)
AA AA BA BA i cat i cat
CM
BB BB BC B BC AB AB AC A AC i cat i cat
p p E Y
R
p a p p a p E Y
∈ ∈
∈ ∈
  − +
 
=
  + − − +
 

When Condition 4 is violated, the observable subgroup N
BA
is a mixture of participants
from categories 1, 2 and 3, instead of category 1 only. That is, the number of disease
occurrence in the subgroup N
BA
equals
[ ]
1 1 2,3 2,3
Pr Pr (1) Pr (1)
BA BA i cat i cat i cat i cat
p E Y E Y
∈ ∈ ∈ ∈
= +  
 
and
1 2,3
Pr Pr Pr
i cat i cat BA ∈ ∈
+ = .
Then the subtraction method we used to derive
4,7
[ ( 1, 1)]
i cat
E Y Z D
∈
= = equals
(Pr Pr )
AA AA BA BA
p p − +
2,3 2,3
Pr (1)
i cat i cat
E Y
∈ ∈
 
 
. Similarly, the denominator of the rate

46
ratio estimator has a bias term of the treatment B outcome from categories 2 and 3.
The bias term
2,3 2,3
Pr (1)
i cat i cat
E Y
∈ ∈
 
 
and
2,3 2,3
Pr (0)
i cat i cat
E Y
∈ ∈
 
 
resulted from
violations of Condition 4 are related to the proportion of noncompliers from categories 2
and 3. The smaller the proportion, the smaller the bias well be.
Pr
AB
Pr
AC
Pr
AA Treatment A
Pr
BB
Pr
BC
Pr
BA
Treatment B
P
AB
P
AC
P
AA
P
BB
P
BC
P
BA
C
4,5,6
C
1,2,3
C
7,8,9
C
2,5,8
C
3,6,9
C
1,4,7
Treatment A
Treatment B
Pr
BA
Pr
BA
PAA**
Pr
AB*
PBA
Pr
AB*
PBB** PBA
PAB
+
C
2,3,5,6,8,9
C4,7 C1
C5,6,8,9 C4,7 C
1,2,3
PAB
+

Figure 4.2 Flowchart of the estimating procedure when condition 5 is violated.

47
4.3 Violations of the Condition 4
Condition 4: the treatment benefit in terms of risk reduction in treatment C relative
to risk reduction in treatment B is known for participants who take treatment C.
When effect of treatment C relative to B for those who take treatment C

is unknown,
the proposed framework does not work and it is not possible to quantify treatment effect
of A relative to B without bias. However, when using the standard ITT analysis to
compare the equivalence of the effect of treatments A and B, our framework can be
helpful to investigate the impact of non-trial departures on ITT analysis.
The null and alternative hypotheses of ITT test are specified as H
o
: 1
AA
ITT
B B
p
R
p
= =
and H
a
: 1
AA
ITT
BB
p
R
p
= ≠ , where
AA
p =
ITT
R (
1 4 7 5 6
x x x x x + + + + ) and
BB
p =
1 4 7 5 6
x x x x x + + + + .
In the absence of non-compliance, the appropriate statistics for testing H
o
is
log
AA
BB
rr
p
p
Z
SE
=
Where the standard error (SE) is approximately
1 1
2 2
1 1
2 ( )
AA BB
AA BB
p p
N
p p
−
− −
+ and
rr
Z
follows a standard normal distribution
33
.
In the presence of non-compliance, we observe
A
p
•
and
B
p
•
instead of
AA
p and
B B
p , where

48
1 4 7 5 5 6 6
Pr Pr Pr ( ) Pr Pr
A AA AA AB AB AC AC ITT c c c A c
p p p p R x x x p a p
•
= + + = + + + +
and
B
p
•
=
4 5 6 1 1 7 7
Pr Pr
c ITT c c B c
x x x R p a p + + + + . Under the null hypothesis
that
ITT
R =1,
1 4 7 5 5 6 6
5 4 6 1 1 7 7
Pr Pr Pr (1 ) Pr (1 )
1
Pr Pr
A c c c A c BC B BC AC A AC
B c c c B c B
p x x x p a p a p a p
p x x x p a p p
•
• •
+ + + + − − −
= = +
+ + + +

Then instead of
rr
Z , the test statistics becomes
.
*
.
*
log
A
B
rr
p
p
Z
SE
=
Where
*
SE is approximately equal to
1 1
2 2
1 1
2 ( )
A B
A B
p p
N
p p
−
• •
• •
− −
+ .
The type I error rate here is the probability of erroneously concluding relative risk is
unity when a true clinically important risk difference exists. Now assume the type I error
rate is α , then the probability of a type I error in the presence of non-compliance is
equal to
0 *
log
Pr(type I error) Pr[ | : 1]
A
AA B
BB
p
p p
Z H
SE p
α
•
•
= < =
0 *
| : 1]
Pr (1 ) Pr (1 )
log log[1 ]
Pr{ }
AA
BB
A BC B BC AC A AC
B B
p
Z H
p
p a p a p
p p
SE
α
•
• •
< =
− − −
− +
=
*
(1 )(Pr Pr )
2
log[1 ]
[ ]
A B
BC BC AC AC
B
a a
p p
p
Z
SE
α
•
+
− −
+
≈ Φ −

49
Where Z
α
is the lower 100 × αth percentile of a standard normal distribution. It indicates
that the direction of the change in the type I error rate depends on the sign of the term
(1 )(Pr Pr )
2
A B
BC BC AC AC
B
a a
p p
p
•
+
− −
. If this term is positive then the type I error rate
will be decreased relative to the nominal α level; if it is negative the type I error rate will
be increased when the sample size of the study is big enough. Therefore, contrary to the
usual concern that ITT approach increases the chance of erroneously concluding
equivalence, the effect of non-trial departures can result the bias of ITT estimator in
either direction. Treatment effectiveness comparison between B and C is a key factor to
determine the direction of the bias. For example, under these two conditions:
(1)
1
A
a <
and
1
B
a <
, that is, treatment C is less effective than treatment B for those who
take treatment C;
(2) Pr Pr
BC BC AC AC
p p > , that is, more participants from N
AC
get disease than from N
BC;

the type I error rate will be decreased relative to the nominal α level

50
Chapter 5. Simulation Study
The main purposes for this simulation study are 1) to assess the accuracy of the large
sample properties of the proposed CM estimator with moderate sample size; 2) to
compare the relative performance of the CM estimator with ITT, AT, PP and IV
estimators under different settings; 3) to assess the sensitivity of the estimator to critical
assumptions.
Two different treatment scenarios that typically occur in randomized clinical trials in
practice are considered.
Case 1: Trials such as single consent design trials in which noncompliance only
occurs in the active treatment group, but not in the control treatment group
35, 37
. The
scenario is discussed in Section 4.2.
Case 2: More general trials in which noncompliance occur in both treatment groups.
The scenario is discussed in Section 4.3.
5.1. Notation and Estimators
Let π
c
denote

the proportion of compliance category c in the sample. Let B
c
be the
baseline disease probability for participants i from category c, that is, B
c
= E(Y
i
| i∈c,
D=0 ). Let R
c
denote the relative protection provided by treatment A for participants
from category c, that is,
i i
c
i i
E(Y | i c, D =1 )
R =
E(Y | i c, D =0 )
∈
∈

. Then the three standard
estimators ITT, AT and IV that we intend to evaluate are defined respectively as follows:

51

i i
ITT
i i
E(Y | Z =1 )
R =
E(Y | Z =0 )

i i
AT
i i
E(Y | D =1 )
R =
E(Y | D =0 )

i i i
PP
i i i
E(Y | Z =D =1 )
R =
E(Y | Z =D =0 )

The instrumental variable estimator R
IV
is calculated based on the method developed
by Johnston et al.
34
for binary outcomes. It is done in two steps: First a grouped-
treatment

variable (GT) is determined as the proportion of participants treated

by the new
treatment A for each randomization group. Then the logistic model is built to calculate
the odds ratio of treatment A to treatment B:
Logit [Pr(Yi=1)] = ß ×GT + K
Where K is a constant and ß represents an unconfounded estimate of the

treatment effect
because there is no association between GT

and the outcome Y independent of treatment
assignment Z. Accordingly, the relative risk estimator is given by

K+β (GT|Z=0)
β (GT|Z=1)
IV
K+β (GT|Z=1)
1+e
R = e
1+e

5.2 Simulation Study for Case 1
In this section, we formulate a simple setting for a RCT where noncompliance only
occurs in one of the treatments, the active treatment A. Therefore, this setting eliminates
the existence of subgroups N
BA
and N
BC
and our estimator is simplified as

52
Pr
Pr Pr Pr
AA AA AA
CM
BB BB BB AB AB AC A AC
p p
R
p p p a p
+
+
= =
− −

and Σπ
i
= 1, where i∈{1, 4, 5, 6, 7} in this single consent trial setting.
5.2.1 Simulation setting when compliance categories 2, 3 and 8 are eliminated
Under the assumption made in section 3.2 that certain noncompliance categories
(categories 2, 3, 8) would not exist, to apply the CM method, N
AB
(participants from
category 5), N
AC
(participants from category 5) are subtracted from participants who were
assigned to treatment A, and participants who have same compliance categories as those
in N
AB
and N
AC
are subtracted from participants assigned to treatment B. Then the rest of
the sample is a mixture of participants from categories 1, 4 and 7. Therefore, the
compliance-matching estimator R
CM
estimates the treatment effect for the mixture, which
is not exactly equals to the CACE, the treatment effect estimation for participants from
category 4 only, unless some additional assumptions such as equal treatment effect on
participants in categories 1, 4 and 7 are made.
Five settings are considered to assess the accuracy of the large sample properties of
the CM estimator. First it is set that ten percent of participants assigned to treatment A
take treatment B and fifteen percent of participants assigned to treatment A take treatment
C, that is, π
5
= 0.1

and π
6
= 0.15, along with baseline rate of B
5
= 0.3,

B
6
= 0.2. For the
mixture of participants from categories 1, 4 and 7, R is set to equal 1 along with the
baseline rate of B
1,4,7
= 0.25 for a null situation. In the second setting, everything is same
except twenty percent protection of treatment A is assumed for categories 1, 4 and 7 as an
alternative to the null situation. In the third setting, the proportion of participants who

53
are randomized to treatment A and take treatment C increased to 30 percent and the
proportion of participants who are randomized to treatment A and take treatment B
increased to 20 percent. In the fourth setting, the baseline rate of category 5 is increased
to 0.9 and the baseline rate of category 6 is raised to 0.6 so that they are different from the
baseline rate of category 1, 4 and 7. In the fifth setting, the treatment effects are set as
R
5
=1.2, R
6
=0.9, R
1,4,7
=0.6 to make the difference of the effects across the categories
significant. The total trial population is fixed at 3000, 5000 or 10000 in each set.
Z
i
is randomized to assign value of 1 or 0 with an equal probability of 0.5 for
balanced allocation. I derive the treatment D
i
that participant i take based on the
compliance category i is from and the treatment Z
i
that i is assigned to. For each
compliance category c, I generate potential outcomes Y
i
from a binomial distribution with
baseline probability B
c
and probability after treatment Bc*R
c
, respectively. Each study is
based on 500 replications.
5.2.2 Simulation results
Simulation results are summarized in Table 5.1 and Table 5.2. The coverage
percentage (CP) was calculated as a percentage of the number of times the true rate ratio
value was included in the 95% confidence interval estimated in each iteration of the
simulation study.
Table 5.1 illustrates that:
1) The CM estimator is unbiased with accurate coverage probability under both the
null and alternative situations, the difference of estimated value and the true value is in
either direction.

54
2) When the noncompliance rates increase, the CM estimator maintains its
unbiasness, but the variance of the estimator increases.
3) When treatment effects change in some subgroups, the CM estimator remains
unbiased; the variance does not change significantly.
4) When baseline rates of compliance categories vary, then the non-compliance is
non-ignorable or non-random, the variance is relatively bigger but the estimator remains
unbiased.
Table 5.2 illustrates that:
1) Under the first null effect and the second alternative effect, when the baseline
rate of each category doesn’t differ much, so that the noncompliance is noninformative,
ITT estimators are biased with very low coverage probability. Different from the
situation of within trial compliance, when ITT estimator usually is conservative, ITT
estimator in this case may overestimate the treatment effect. Both R
CM
are unbiased with
slightly bigger variances than the rest of the estimators.
2) The above pattern holds when the noncompliance rates increase, however each
estimator gives a wider CI.
3) When the noncompliance is informative in setting 4, the IV estimator is biased
by overestimating the treatment effect, giving a message that IV approach can be
misleading as other AT and PP approaches. The R
CM
estimator remains unbiased.
4) The results from the fifth setting show that when noncompliance only occurs in
the active treatment arm, whether treatment effect is different or not across compliance
categories does not have much effect on the estimators.

55
As anticipated, the CM estimator gives a relatively wider CI than the rest estimators
in most of the cases. However, it is the only estimator that remains unbiased no matter
the compliance is random or informative.

56
Table 5.1. Simulation results of R
CM
: case 1.
Parameters

N Median Mean Empirical
variance
Variance CP
1. Null
α
AB
= 0.1; p
AB
= 0.3;
α
AC
= 0.15; p
AC
= 0.1;
α
AA
= 0.75; p
AA
=
0.25;
α
BB
= 1; p
BB
= 0.25;
π
5
= 0.1; B
5
= 0.3; r
5
= 0.9;
π
6+9
= 0.15; B
6+9
= 0.2;
a
6+9
= 0.6;
π
1+4+7
= 0.75; B
1+4+7
= 0.25;
R
CM
= 1;
3000
5000
10000
1.013
0.998
1.000
1.014
1.001
1.004
0.0081
0.0065
0.0038
0.0076
0.0060
0.0032
0.95
0.94
0.94
2. Alternative: R = 0.6
α
AB
= 0.1; p
AB
= 0.3;
α
AC
= 0.15; p
AC
= 0.1;
α
AA
= 0.75; p
AA
=
0.15;
α
BB
= 1; p
BB
= 0.25;
π
5
= 0.1; B
5
=0.3; r
5
= 0.9;
π
6+9
= 0.15; B
6+9
= 0.2;
a
6+9
= 0.6; π
1+4+7
=
0.75; B
1+4+7
= 0.25;
R
CM
= 0.6;
3000
5000
10000
0.597
0.601
0.601
0.603
0.603
0.600
0.0043
0.0026
0.0014
0.0036
0.0021
0.0010
0.94
0.95
0.95
3. Noncompliance rates increase
α
AB
= 0.2; p
AB
= 0.3;
α
AC
= 0.3; p
AC
= 0.1;
α
AA
= 0.5; p
AA
= 0.2;
α
BB
= 1; p
BB
= 0.24;
π
5
= 0.2; B
5
= 0.3; r
5
= 0.9;
π
6
= 0.3; B
6
= 0.2; a
6+9
=
0.6; π
1+4+7
= 0.5;
B
1+4+7
= 0.25;
R
CM
= 0.8;
3000
5000
10000
0.796
0.797
0.801
0.812
0.809
0.809
0.0086
0.0066
0.0034
0.0091
0.0065
0.0051
0.95
0.94
0.94
4. Different baseline rates (Informative
noncompliance)

α
AB
= 0.2; p
AB
= 0.6;
α
AC
= 0.3; p
AC
= 0.3;
α
AA
= 0.5; p
AA
= 0.2;
α
BB
= 1; p
BB
= 0.43;
π
5
= 0.2; B
5
= 0.6; r
5
= 0.9;
π
6+9
= 0.3; B
6+9
= 0.6; a

6+9
= 0.6; π
1+4+7
=
0.5; B
1+4+7
= 0.25;
R
CM
= 0.8;
3000
5000
10000
0.797
0.797
0.797
0.821
0.813
0.804
0.0146
0.0083
0.0046
0.0148
0.0085
0.0043
0.95
0.95
0.95

57
Table 5.2. Simulation results of R
CM,
R
ITT,
R
AT,
R
PP
and

R
IV
: case 1.
Parameters Estimator Median Mean Variance CP
1. Null
α
AB
= 0.1; p
AB
= 0.3;
α
AC
= 0.15; p
AC
= 0.1;
α
AA
= 0.75; p
AA
= 0.25;
α
BB
= 1; p
BB
= 0.25;
π
5
= 0.1; B
5
= 0.3; r
5
= 0.9;
π
6+9
= 0.15; B
6+9
= 0.2; a
6+9
= 0.6;
π
1+4+7
= 0.75; B
1+4+7
= 0.25;
R
CM
= 1;
R
CM

R
ITT

R
AT

R
PP

R
IV

0.998
0.939
0.988
1.010
0.988
1.001
0.939
0.991
1.010
0.989
0.0060
0.0029
0.0027
0.0029
0.0003
0.95
0.83
0.81
0.83
0.35
2. Alternative: R = 0.6
α
AB
= 0.1; p
AB
= 0.3;
α
AC
= 0.15; p
AC
= 0.1;
α
AA
= 0.75; p
AA
= 0.15;
α
BB
= 1; p
BB
= 0.24;
π
5
= 0.1; B
5
=0.3; r
5
= 0.9;
π
6+9
= 0.15; B
6+9
= 0.2; a
6+9
= 0.6;
π
1+4+7
= 0.75; B
1+4+7
= 0.25;
R
CM
= 0.6;
R
CM

R
ITT

R
AT

R
PP

R
IV

0.601
0.636
0.595
0.608
0.679
0.603
0.638
0.597
0.609
0.679
0.0021
0.0016
0.0014
0.0015
0.0015
0.95
0.87
0.86
0.86
0.87
3. Noncompliance rates increase
α
AB
= 0.3; p
AB
= 0.3;
α
AC
= 0.2; p
AC
= 0.1;
α
AA
= 0.5; p
AA
= 0.2;
α
BB
= 1; p
BB
= 0.26;
π
5
= 0.2; B
5
= 0.3; r
5
= 0.9;
π
6+9
= 0.3; B
6+9
= 0.2; a
6+9
= 0.6;
π
1+4+7
= 0.5; B
1+4+7
= 0.25;
R
CM
= 0.8;
R
CM

R
ITT

R
AT

R
PP

R
IV

0.797
0.777
0.784
0.817
0.934
0.809
0.777
0.786
0.816
0.935
0.0065
0.0023
0.0026
0.0031
0.0030
0.94
0.68
0.72
0.75
0.75
4. Different baseline rates (Informative noncompliance)
α
AB
= 0.3; p
AB
= 0.6;
α
AC
= 0.2; p
AC
= 0.3;
α
AA
= 0.5; p
AA
= 0.2;
α
BB
= 1; p
BB
= 0.43;
π
5
= 0.2; B
5
= 0.6; r
5
= 0.9;
π
6+9
= 0.3; B
6+9
= 0.6; a
6+9
= 0.6;
π
1+4+7
= 0.5; B
1+4+7
= 0.25;
R
CM
= 0.8;
R
CM

R
ITT

R
AT

R
PP

R
IV

0.790
0.727
0.439
0.469
0.739
0.813
0.728
0.439
0.469
0.738
0.0085
0.0012
0.0007
0.0008
0.0009
0.95
0.38
0.30
0.31
0.34

58
5.3 Simulation Study for Case 2
In this section, we formulate a more generous setting for a two-armed RCT in which
noncompliance occur in both treatment arms.
5.3.1 Simulation setting under the assumption of constant relative risk
The same scheme used in case 1 is employed for generating the simulation data
except that noncompliance behaviors are also allowed in the control treatment group B.
To apply the constraint of equal relative risk reduction afforded by treatment A, the
fifth setting in Section 4.2 of different treatment effect across the compliance categories
is removed; for the other four settings except treatment effect in terms of the relative rate
ratios are modified to be constant across each category in each setting, the rest parameters
remain the same.
5.3.2 Simulation setting when compliance categories 2, 3 and 8 are eliminated
The same scheme used in case 1 is employed for generating the simulation data
except that noncompliance behaviors are also allowed in the control treatment group B.
5.3.3 Simulation results
The simulation results for case 2 under the assumption of constant relative risk
are summarized in Table 5.3 and Table 5.4. The results for case 2 when compliance
categories 2, 3 and 8 are eliminated are summarized in Table 5.5 and Table 5.6.
Table 5.3 shows that the asymptotic performance of the CM estimator under the
constant relative risk model is similar to the performance of the estimator under condition

59
5 shown in table 5.1, with a relatively bigger variance. The reason may be because more
compliance categories are included in the sample and bring more uncertainly when
generating the simulation data.
Table 5.4 illustrates that the CM estimator gives a relatively wider CI than the rest
estimators in most of the cases. However, similar to what is shown in Table 5.2, it is the
only estimator that remains unbiased with accurate coverage probability no matter the
compliance is random or informative. The limitations of ITT, AT and PP estimators are
obvious under this model. The IV estimator is not consistently behaved despite its
merited performance overall
36
.
The results produced by eliminating categories 2,3 and 8 shown in Table 5.5 and
Table 5.6 are consistent with previous results under case 1 scenario (Table 5.1 and Table
5.2).

60
Table 5.3 Simulation results of R
CM
: case 2 under the assumption of constant relative risk
Parameters N Median Mean Empirical variance Variance CP
(500 runs)
1. Null
α
AB
= 0.1; p
AB
= 0.4;
α
AC
= 0.15; p
AC
= 0.6;
α
AA
= 0.75; p
AA
= 0.4;
α
BA
= 0.15; p
BA
= 0.6;
α
BC
= 0.1; p
BC
= 0.3;
α
BB
= 0.75; p
BB
= 0.5;
R
CM
=1
3000
5000
10000
0.993
0.995
1.001
1.029
1.035
1.011
0.0095
0.0053
0.0027
0.0085
0.0053
0.0026
417
473
478
2. Alternative: R = 0.8
α
AB
= 0.1; p
AB
= 0.3;
α
AC
= 0.15; p
AC
= 0.5;
α
AA
= 0.75; p
AA
= 0.2;
α
BA
= 0.15; p
AC
=
0.35;
α
BC
= 0.1; p
BB
= 0.3;
α
BB
= 0.75; p
BB
= 0.2;
R
CM
=0.8
3000
5000
10000
0.799
0.799
0.800
0.804
0.806
0.801
0.0145
0.0089
0.0046
0.0141
0.0086
0.0041
454
473
485
3. Noncompliance rate
increases

α
AB
= 0.2; p
AB
= 0.5;
α
AC
= 0.3; p
AC
= 0.25;
α
AA
= 0.5; p
AA
= 0.3;
α
BA
= 0.3; p
BA
= 0.3;
α
BB
= 0.5; p
BB
= 0.4;
α
BC
= 0.2; p
BC
= 0.25;
R
CM
=0.8
3000
5000
10000

0.801
0.789
0.799
0.808
0.804
0.810

0.0173
0.0099
0.0062
0.0175
0.0102
0.0061
450
479
426

61
Table 5.4. Simulation results of R
CM,
R
ITT,
R
AT,
R
PP
and

R
IV
: case 2 under the assumption of constant relative risk.

Parameters Estimator Median Mean Variance CP
(500 runs)
1. Null
α
AB
= 0.1; p
AB
= 0.4;
α
AC
= 0.15; p
AC
= 0.6;
α
AA
= 0.75; p
AA
= 0.4;
α
BA
= 0.15; p
BA
= 0.6;
α
BC
= 0.1; p
BC
= 0.3;
α
BB
= 0.75; p
BB
= 0.5;
R
CM
=1
R
CM

R
ITT

R
AT

R
PP

R
IV

0.9949
1.0295
0.7538
0.7757
1.1043
1.0351
1.0288
0.7538
0.7755
1.1067
0.0053
0.0010
0.0004
0.0008
0.0096
473
418
0
0
404
2. Alternative: R = 0.8
α
AB
= 0.1; p
AB
= 0.3;
α
AC
= 0.15; p
AC
= 0.5;
α
AA
= 0.75; p
AA
= 0.2;
α
BA
= 0.15; p
AC
= 0.35;
α
BC
= 0.1; p
BB
= 0.3;
α
BB
= 0.75; p
BB
= 0.2;
R
CM
=0.8
R
CM

R
ITT

R
AT

R
PP

R
IV

0.7993
1.0050
0.6294
0.6619
0.9148
0.8061
1.0068
0.6284
0.6618
0.9228
0.0086
0.0011
0.0004
0.0008
0.0073
473
0
0
0
129
3. Noncompliance rates
increase

α
AB
= 0.2; p
AB
= 0.5;
α
AC
= 0.3; p
AC
= 0.25;
α
AA
= 0.5; p
AA
= 0.3;
α
BA
= 0.3; p
BA
= 0.3;
α
BB
= 0.5; p
BB
= 0.4;
α
BC
= 0.2; p
BC
= 0.25;
R
CM
=0.8
R
CM

R
ITT

R
AT

R
PP

R
IV

0.7895
1.0026
0.6024
0.6183
1.0172
0.8040
1.0023
0.6030
0.6186
1.0043
0.0102
0.0012
0.0008
0.0016
0.0086
479
0
0
0
15

62
Table 5.5. Simulation results of R
CM
: case 2 when compliance categories 2, 3 and 8 are eliminated.
Parameters

N Median Empirical
variance
Variance CP

1. Null
α
AB
= 0.1; p
AB
= 0.3;
α
AC
= 0.15; p
AC
= 0.1;
α
AA
= 0.75; p
AA
= 0.25;
α
BA
= 0.09; p
BA
= 0.25;
α
BB
= 0.70; p
BB
= 0.25;
α
BC
= 0.21; p
BC
= 0.12;
π
5
= 0.1; B
5
= 0.3;
π
6+9
= 0.15; B
6+9
= 0.2; a
6+9
= 0.5;
π
1+4+7
= 0.75; B
1+4+7
= 0.25;
R
CM
= 1;
3000
5000
10000
1.002
1.006
1.005
0.0078
0.0057
0.0035

0.0080
0.0056
0.0031
0.95
0.95
0.95
2. Alternative: R = 0.6
α
AB
= 0.1; p
AB
= 0.3;
α
AC
= 0.15; p
AC
= 0.1;
α
AA
= 0.75; p
AA
= 0.15;
α
BA
= 0.22; p
BA
= 0.15;
α
BB
= 0.51; p
BB
= 0.26;
α
BC
= 0.27; p
BC
= 0.11;
π
5
= 0.1; B
5
=0.3; r
5
= 0.9;
π
6+9
= 0.15; B
6+9
= 0.2; a
6+9
= 0.5;
π
1+4+7
= 0.75; B
1+4+7
= 0.25;
R
CM
= 0.6;
3000
5000
10000
0.600
0.602
0.601
0.0081
0.0051
0.0030
0.0068
0.0047
0.0034
0.96
0.96
0.96
3. Noncompliance rates increase
α
AB
= 0.2; p
AB
= 0.3;
α
AC
= 0.3; p
AC
= 0.1;
α
AA
= 0.5; p
AA
= 0.15;
α
BA
= 0.10; p
BA
= 0.15;
α
BB
= 0.57; p
BB
= 0.27;
α
BC
= 0.33; p
BC
= 0.10
π
5
= 0.2; B
5
= 0.3; r
5
= 0.9;
π
6
= 0.3; B
6
= 0.2; a
6+9
= 0.5;
π
1+4+7
= 0.5; B
1+4+7
= 0.25;
R
CM
= 0.6;
3000
5000
10000
0.601
0.601
0.599
0.0094
0.0063
0.0038
0.0076
0.0068
0.0034
0.96
0.95
0.94
4. Different baseline rates (Informative noncompliance)
α
AB
= 0.2; p
AB
= 0.6;
α
AC
= 0.3; p
AC
= 0.3;
α
AA
= 0.5; p
AA
= 0.15;
α
BA
= 0.1; p
BA
= 0.15;
α
BB
= 0.53; p
BB
= 0.47;
α
BC
= 0.37; p
BC
= 0.2;
π
5
= 0.2; B
5
= 0.6;
π
6+9
= 0.3; B
6+9
= 0.6; a
6+9
= 0.5;
π
1+4+7
= 0.5; B
1+4+7
= 0.25;
R
CM
= 0.6;
3000
5000
10000
0.602
0.604
0.598
0.0093
0.0067
0.0040
0.0087
0.0062
0.0046
0.95
0.95
0.96

63
Table 5.6. Simulation results of R
CM,
R
ITT,
R
AT,
R
PP
and

R
IV
: case 2 when compliance categories 2, 3 and 8 are eliminated.
Parameters Estimat
or
Median Variance CP
1. Null
α
AB
= 0.1; p
AB
= 0.3;
α
AC
= 0.15; p
AC
= 0.1;
α
AA
= 0.75; p
AA
= 0.25;
α
BB
= 1; p
BB
= 0.25;
π
5
= 0.1; B
5
= 0.3; r
5
= 0.9;
π
6+9
= 0.15; B
6+9
= 0.2; a
6+9
= 0.6;
π
1+4+7
= 0.75; B
1+4+7
= 0.25;
R
CM
= 1;
R
CM

R
ITT

R
AT

R
PP

R
IV

1.006
1.137
0.881
0.912
1.030
0.0057
0.0039
0.0025
0.0032
0.0043
0.95
0.18
0.22
0.69
0.95
2. Alternative: R = 0.6
α
AB
= 0.1; p
AB
= 0.3;
α
AC
= 0.15; p
AC
= 0.1;
α
AA
= 0.75; p
AA
= 0.15;
α
BB
= 1; p
BB
= 0.24;
π
5
= 0.1; B
5
=0.3; r
5
= 0.9;
π
6+9
= 0.15; B
6+9
= 0.2; a
6+9
= 0.6;
π
1+4+7
= 0.75; B
1+4+7
= 0.25;
R
CM
= 0.6;
R
CM

R
ITT

R
AT

R
PP

R
IV

0.602
0.813
0.566
0.582
0.619
0.0051
0.0030
0.0013
0.0018
0.0043
0.96
0.02
0.86
0.93
0.94
3. Noncompliance rates increase
α
AB
= 0.3; p
AB
= 0.3;
α
AC
= 0.2; p
AC
= 0.1;
α
AA
= 0.5; p
AA
= 0.2;
α
BB
= 1; p
BB
= 0.26;
π
5
= 0.3; B
5
= 0.3; r
5
= 0.9;
π
6+9
=

0.2; B
6+9
= 0.2;a
6+9
= 0.6;
π
1+4+7
= 0.5; B
1+4+7
= 0.25;
R
CM
= 0.8;
R
CM

R
ITT

R
AT

R
PP

R
IV

0.601
0.817
0.543
0.560
0.704
0.0063
0.0029
0.0015
0.0020
0.0036
0.95
0.01
0.70
0.86
0.59
4. Different baseline rates (Informative noncompliance)
α
AB
= 0.2; p
AB
= 0.6;
α
AC
= 0.3; p
AC
= 0.3;
α
AA
= 0.5; p
AA
= 0.15;
α
BA
= 0.1; p
BA
= 0.15;
α
BB
= 0.53; p
BB
= 0.47;
α
BC
= 0.37; p
BC
= 0.2;
π
5
= 0.3; B
5
= 0.6; r
5
= 0.9;
π
6+9
= 0.2; B
6+9
= 0.6;a
6+9
= 0.6;
π
1+4+7
= 0.5; B
1+4+7
= 0.25;
R
CM
= 0.8;
R
CM

R
ITT

R
AT

R
PP

R
IV

0.604
0.836
0.296
0.318
0.632
0.0067
0.0012
0.0005
0.0006
0.0009
0.95
0.00
0.00
0.01
0.81

64
Chapter 6 Illustration: Two Examples

6.1 A Muscle-Specific Strength Training Study

6.1.1 Study Rationale and Description
To further illustrate the proposed analytic method with real data, the Muscle-Specific
Strengthening Effectiveness Post Lumbar Microdisectomy (MUSSEL) project is
considered. It is one of the randomized clinical trials supported by the Physical Therapy
Clinical Research Network (PTClinResNet, Winstein et al., 2007), a clinical research
network for the evaluation of the efficacy of physical therapist interventions to enhance
muscle performance in patients with physical disabilities.
In the U.S., 12-33% of the adult work force is affected by low back pain each year.
The MUSSEL study is a Phase I/II investigation for assessing the effects of muscle
specific strength and endurance training on short term and long term disablement in
participants with chronic back pain post lumbar microdiscectomy surgery. In this
particular clinical trial, there were two treatment arms. One was the Education Only
(EO) arm receiving one session of back care education and the other was the Exercise
and Education (EE) arm receiving a back care education followed by the 12-week USC
Spine Exercise Program. The outcome examiners as well as the data managers were
blinded to group allocation.
The MUSSEL study started in June 2003 and met accrual goals and was closed to
patient entry in Dec, 2006. A total of 176 individuals (100 males, 76 females) between
the ages of 18 and 60 were informed about this study through participating surgeons’

65
offices. Among the 178 patients screened, a total of 98 participants (50 EE, 48 EO) were
eligible for randomization and signed the informed consent.
The primary outcome measurement for this study is disability assessment using the
Oswestry questionnaire. The Oswestry Disability Questionnaire (OD) was used to assess
the extent to which each subject participated in activities of daily living.
6.1.2 Data Description
A total of 176 patients were screened for randomization (Figure 1). Eighty of these
were excluded for the following reasons: 52 declined to enroll and 26 failed to meet the
inclusion criteria. Ninety-eight participants were originally assigned using blocked
randomization to receive EE (n=51) or EO (n= 47). However, some participants did not
take their assigned treatment, for reasons related to decisions made by themselves or their
clinicians, or through protocol violations. Four participants in the EE group did not
comply with the group assignment; subsequently 3 received EO and 1 sought the usual
care (UC). Furthermore, in the EO group, 22 participants did not comply with group
assignment; subsequently 3 received EE and 19 received UC. The participants who
remained in the study provided the basis for the evaluable data in three groups: EE
(n=44), EO (n=14) and UC (n=20) (Figure 6.1).
Overall, 53 (55%) of the patients were males and the mean age was 40±10 years
across both genders. The majority of the patients were employed, income of >$50,000,
and attended at least some college. No statistically significant baseline differences were
found between the two treatment groups (P>.05), nor were significant differences found
across the three actual treatment groups (P>.05).

66
47 Assigned to Receive
Education Only
51 Assigned to Receive
Exercise & Education
Education & Exercise
n=44
6 Withdrew
Education Only
n=14
12 Withdrew
Usual Care
n=20
2 Withdrew
n=19 n=1 n=47 n=3 n=25 n=3
Intent-to-Treat
Actual
Treatment
Groups
176 Patients Screened
78 Ineligible
52 Personal Reasons
26 Inclusion Criteria
Not Met
98 Randomized

Figure 6.1. Flow diagram of the MUSSEL randomized controlled trial: exclusion,
enrollment, randomization, and compliance.

6.1.3 Design of Data Analysis
6.1.3.1 Assessment of assumptions and Potential Outcome Model
In this example, the “treatment” (i.e., EE, EO or UC) is denoted by D and the binary
“assignment” is denoted by Z. If compliance with the treatment assignment had been
perfect, then all those randomized to the EE group (Z=1) would have taken EE (D=1) and
those randomized to the EO group would have taken EO (D=0). According to Lauridsen
et al
49-51
, a change score of 11% of the Oswestry Disability Index may be used as the
minimal clinical important difference cut-off score for health care providers to consider

67
the treatment as effective in an uncomplicated Low Back Pain case. Therefore, in our
example, the potential outcome Yi (z,d), is an indicator variable, equal to one if post
treatment change score is greater than 11%, that is participant i would have significant
disability recovery given physical intervention assignment Z=z and the treatment receipt
D=d.
For a valid causal interpretation of the treatment effect, we require:
Condition 1: The treatment assignment of any participant was not affected by the
treatment assignment of others, and, similarly, that the disability of any such participant
was not affected by the treatment assignment of others.
Condition 2: The relative treatment effect in terms of relative rate of recovery from
disability in UC to EO is known for participants who take treatment UC. In this example,
based on the prior knowledge, we think that individual education appeared to be just as
effective as usual care interventions.
Condition 3: Assignment of the physical interventions was random and data are fully
recorded for all participants.
Condition 4: Patients’ disability recovery rate (Oswestry change score) was not affected
by the treatment assignment once the treatment receipt is taken into account. That is, the
treatment assignment is unrelated to the outcome given the treatment received.
Condition 5: There are no participants who are from categories 2, 3 and 8. Table 1
presents the observable subgroups and the mixture structure of compliance types in each
subgroup. That is, the treatment assignment is unrelated to the outcome given the
treatment received.

68
After eliminating noncompliant participants from categories 2, 3 and 8, we use the
CM method to identify the comparable subgroups under each assignment. The subgroup
that provides information to the causal derivation of the recovery rate is the mixture of
subjects from categories 4 and 7, as illustrated in the flowchart (Figure 6.2). Then the
participants taking UC and those who take EO are pooled together. After pair matching
compliance categories of the two assignment groups, we got four observable subgroups,
each of which is a mixture of latent compliance categories as presented in Table 6.1.
Table 6.1. Classification of compliance behaviors for the MUSSEL example.
Observable Subgroups Latent Compliance-category
Z
i
=0, D
i
=0 or D
i
=2 Cat{4,7}+Cat{5,6,9}
Z
i
=1, D
i
=0 or D
i
=2 Cat{5,6,9}
Z
i
=1, D
i
=1 Cat{1}
Z
i
=0, D
i
=1 Cat{1}+Cat{4,7}

Under condition 4 that the treatment assignment is unrelated to the outcome given
the treatment received, we have
Pr( 1| { 1 }, 1, 1) Pr( 1| { 1 }, 0, 1)
i i i i i i
Y i Cat Z D Y i Cat Z D = ∈ = = = = ∈ = =
and Pr( 1| {5,6,9}, 1, 0) Pr( 1| {5,6,9}, 0, 0)
i i i i i i
Y i Cat Z D Y i Cat Z D = ∈ = = = = ∈ = = .
Therefore, there are four probabilities for the outcome distributions to estimate (Using the
notations introduced in Chapter 3, P
AA
* = Pr( 1| {4,7}, 1, 1)
i i i
Y i Cat Z D = ∈ = = , P
BB
* =
Pr( 1| {4,7}, 0, 0)
i i i
Y i Cat Z D = ∈ = = , P
BA
= Pr( 1| { 1 }, 1)
i i
Y i Cat D = ∈ = , P
AB+
=
Pr( 1| {5,6,9}, 0)
i i
Y i Cat D = ∈ = ).

69
Applying the estimation procedure introduced in Section 3.5, the likelihood of each
subgroup can be expressed by

(1,1) (1 (1,1))
* * *
{4,7}, 1
( ) (1 )
i
Yi Yi
AA AA AA
i Cat z
l P p p
−
∈ =
= −
∏

(0,0) (1 (0,0))
* * *
{4,7}, 0
( ) (1 )
i
Yi Yi
BB BB BB
i Cat z
l P p p
−
∈ =
= −
∏

( ,0) (1 ( ,0))
{5,6,9}
( ) (1 )
Yi Zi Yi Zi
AB AB AB
i Cat
l P p p
−
+ + +
∈
= −
∏

( ,0) (1 ( ,0))
{1}
( ) (1 )
Yi Zi Yi Zi
BA BA BA
i Cat
l P p p
−
∈
= −
∏

The estimand of primary interest is casual treatment effect of the subpopulation from
categories 4 and 7 in terms of relative disability recovery rate of EE vs. EO, that is,
* AA
RR P = /
* BB
P .
6.1.4 Results
Table 6.2 shows the means and the confidence intervals of the estimated relative
recovery rate of EE vs EO. The point estimate is 1.55. Results obtained using traditional
approaches including ITT, AT, PP and IV analyses (SAS, Genmod procedure) are also
summarized in Table 6.2. ITT effect is marginally significant at the significant level of
0.05. Other effects are non-significant. Our approach produces results relatively
consistent with those of other standard approaches. The likelihood of each subgroup is
expressed. The methodology was motivated by and is illustrated in the analysis of a
randomized community trial of the impact of vitamin A supplementation on children’s
mortality.

70
Table 6.2. Estimation of the relative recovery rate for MUSSEL study.
Estimator Mean 5
th
percentile 95
th

percentile
P
value
CM 1.55 0.45 2.65 0.21
ITT 1.47 0.99 2.18 0.06
AT 1.23 0.75 2.02 0.40
PP 1.15 0.71 1.87 0.57
IV 1.34 0.67 2.66 0.40

6.2 A Study on Treatment of Ewing's Sarcoma or Primitive
Neuroectodermal Tumor of Bone
6.2.1 Study Rationale and Description
The Children’s Cancer Group and the Pediatric Oncology Group initiated a
randomized, controlled trial to investigate whether the combination of ifosfamide and
etoposide when added to a standard regimen would improve the outcome in Ewing’s
sarcoma. In this trial, there were two treatment arms. One was the 49 weeks of standard
chemotherapy with doxorubicin, the other was the experimental therapy.
The study started in December 1988 and was closed to patient entry in November
1992. It was initially designed to enroll about 400 patients and it actually enrolled
approximately 50 percent greater than expected.
The primary end point for the estimation of relative efficacy was event-free survival.
It was defined as the time from entry into the study until the occurrence of an adverse
event or until the last contact with the patient, whichever came first.

71
6.2.2 Data Description
A total of 530 patients who signed the informed consent were screened and enrolled.
One hundred twenty (120) patients with initially metastatic disease were excluded from
this illustrative analysis. Two hundred and sixty five patients with initially non-
metastatic disease successfully completed the first 14 weeks of therapy and after being
put into remission were followed for disease progression. Among them, one hundred and
eighteen patients were assigned to the standard therapy. One of them switched to the
experimental therapy and four of them did not take any treatment. One hundred and forty
seven patents were assigned to the experimental therapy, four of whom did not take the
assignment but chose the standard therapy and five of whom did not take any treatment.
Individuals who were not followed for the full five years, but had not yet experienced an
event were excluded from the dataset.
6.2.3 Design of Data Analysis
In this example, the “treatment” (i.e., standard, experimental, or no treatment) is
denoted by D and the binary “assignment” (i.e., standard or experimental) is denoted by
Z. If compliance with the treatment assignment had been perfect, then all those
randomized to the experimental group (Z=1) would have taken the experimental regimen
(D=1) and those randomized to the standard group would have taken the standard
regimen (D=0). For those people who did not get any further treatment after local
control, their treatment receipt D equals 2. These four drugs in alternation with course of
ifosfamide and etoposide. In our example, the potential outcome Yi (z,d), is an indicator
variable, equal to one if post treatment change score is greater than 11%, that is

72
participant i would have significant disability recovery given physical intervention
assignment Z=z and the treatment receipt D=d.
For a valid causal interpretation of the treatment effect, we require:
Condition 1: The treatment assignment of any participant was not affected by the
treatment assignment of others, and, similarly, whether one participant experienced an
adverse analytic event or not within the five years following local control was not
affected by the treatment assignment of others.
Condition 2: The relative rate of analytic event occurrence of the standard treatment vs.
no treatment after local control for the subpopulation who did not get any further
treatment after local control is known. In this example, based on the prior knowledge, we
think that the relative rate is between 0.25 and 0.7. Here for the illustration purpose, we
choose the point estimate of this rate as 0.5.
Condition 3: Assignment of these treatments was random and data are fully recorded for
all participants. In other words, we assume that we observe values of Z, D, and the health
outcome Y for each person.
Condition 4: Patients’ rate of event occurrence was not affected by the treatment
assignment once the treatment receipt is taken into account. That is, the treatment
assignment is unrelated to the outcome given the treatment received.
After eliminating noncompliant participants from categories 2, 3 and 8, we use the
CM method to identify the comparable subgroups under each assignment. The subgroup
that provides information to the causal derivation of the recovery rate is the mixture of
subjects from categories 4 and 7, as illustrated in the flowchart (Figure 6.2).

73
Y(1,2) Y(1,1)
Standard Therapy
C
5
C
6,9
C
1,4,7
Y(1,0)
Y(0,0) Y(0,2) Y(0,1)
C
4,5,6
C
1
C
7,9
Experimental Therapy
α α α α
BA
α α α α
BA
P
AA*
α α α α
AB*
α α α α
AB*
P
BB*
C
5,6,9
C
4,7
C
1
C
5,6,9
C
4,7
C
1
Standard Therapy
Experimental Therapy

Figure 6.2: Flowchart of CM method application for a study on treatment of Ewing's
sarcoma or primitive neuroectodermal tumor of bone.

6.2.4 Results
Table 6.3 shows the means and the confidence intervals of the estimated relative
event occurrence rate of experimental therapy vs standard therapy. The point estimate
using the CM method is 0.96. Results obtained using traditional approaches including
ITT, AT, PP and IV analyses (SAS, Genmod procedure) are also summarized in Table 6.3.
Our approach produces results relatively consistent with those of other standard

74
approaches. Due to the limitation of the sample size for the subgroups of noncompliers,
the confidence interval of the CM method was relatively wider.
Table 6.3. Estimation of the relative event occurrence rate for a study on treatment of
Ewing's sarcoma or primitive neuroectodermal tumor of bone.
Estimator Mean 5
th
percentile 95
th

percentile
P
value
CM 0.96 0.42 1.50 0.21
ITT 0.99 0.89 1.09 0.83
AT 1.01 0.91 1.11 0.87
PP 1.01 0.91 1.11 0.91

75
Chapter 7. Discussion
Neyman and Fisher pointed out that randomization is a cornerstone of scientific
experimentation. However, noncompliance is almost unavoidable in studies involving
human subjects, and the compliance patterns very likely differ between treatment arms.
In this paper, we have outlined a framework for estimating the causal effects of
treatments in settings where random treatment assignment has taken place, but the
compliance is less than perfect. We have considered several scenarios of non-trial
noncompliance data patterns in the context all-or-non compliance and binary outcomes
and studied the main concerns that arise when noncompliance occurs such as bias and
complication in data analysis.
7.1 Summary of Results
When noncompliance exists, both treatment effectiveness and treatment biological
efficacy are important but address different scientific questions. Treatment effectiveness
depends on biological efficacy and noncompliance. As the number of noncompliers
increases, treatment effectiveness can be decreased but biological efficacy remains the
same. Therefore, biological efficacy, the causal effect of the active treatment is more
likely to be reproducible in different populations or subgroups and is of our interest in
this paper.
7.1.1 Approaches used for within-trial noncompliance
The intention-to-treat analysis is a straightforward and acceptable approach for
estimating effectiveness. However, when estimating efficacy, it has to assume that

76
noncompliance is completely at random or at least the noncompliance patterns are the
same between treatment arms. In reality, it is very possible that the treatment protocol
presents a distinct (often tougher) challenge for compliers than the control protocol,
especially when there are non-trial departures. This results in serious potential selection
bias by using ITT approach. Normally, for within-trial departure, in superior trials with
noncompliance, an ITT approach gives more conservative estimation while in
equivalence or non-inferiority trials increases the chance of erroneously concluding
equivalence.
Similarly, when noncompliance presents, as-treated and per-protocol approaches
produce unbiased estimation of efficacy for the compliers only when we assume that all
prognostic effect of the noncompliers are the same as the prognostic effect of the
compliers who take the treatment. If the assumption is not true, which is very likely in
reality, and then severe bias can result both for estimation and testing the null hypothesis.
The bias from the true value can be in either direction depending on prognostic factors
that modify the treatment effect and also influence compliance.
In the randomized clinical trial setting, the instrumental variable method can be
used to estimate biological efficacy when we can identify an instrument, which correlates
with the treatment receipt exclusively and is independent to the outcome when
conditioning on the treatment receipt. This approach has been most used in the context of
regression models and the assumption of constant treatment effects. Under these
assumptions, the IV concept can be used to control noncompliance. As indicated by our
simulation results, when the amount of noncompliance increase, the sensitivity of the IV

77
corrections to the assumptions increases. Moreover, the IV estimation is large-sample
procedures. Even all assumptions are met, the estimation may be still biased due to
limitation of sample sizes.
The instrumental variables estimation can be embedded within Rubin Causal Model
to estimate the treatment efficacy under some assumptions. Models are specified in terms
of potential outcomes and potential receipt to the treatment assignment. The efficacy so
estimated pertains to the subgroup of compliers. The core assumptions of this framework
include that 1) the treatment assignment is unrelated to potential outcomes once treatment
received is taken into account; 2) there is no one who does the opposite of his
assignment, no matter what the assignment. To extrapolate to the full population of the
efficacy estimation requires additional model assumption.
The subtraction method is another extension of the instrumental variable method
with special focus on binary outcomes. It assumes constant treatment effect across
treatment receipt groups as the IV approach. It also implicitly assumes the existence of
potential noncompliers subgroup by subtracting the number of disease occurrence of the
subgroup from that of the whole population. It is more straightforward and requires less
computation compared with potential outcome model approach. However the
assumption of constant treatment effect is not testable and unlikely to be true in reality.
7.1.2 Approaches used for non-trial noncompliance
It is desirable to find a statistical framework that can apply to as many different
patterns of noncompliance behaviors as possible. The mostly widely used method for
clinical trials which involves non-trial departures has been covariate adjustment. It is

78
based on the basis of assumption overt selection bias, that is, all the covariates that
distinguish one treatment group from the other can be identified.
In this paper, we extended the subtraction method used for within-trial departures by
explicitly adopting the potential outcome model to consider all patterns of compliance
behaviors including non-trial departures. Two sets of assumptions are generated to
identify the subgroup of participants whose treatment efficacy is estimable. The core
assumptions of the first set are purely based on the subtraction method, include assuming
constant treatment effect across observable subgroups and no direct effect of treatment
assignment to the outcomes once treatment receipt is conditioned on. The second set of
assumptions is more logical and less strict: it replaces the constant treatment effect
assumption by assuming some compliance categories do not exist. Specifically, it
assumes that for a two treatment (A and B) trial, there are no such contradictory
noncompliers: they refused the assignment of A but chose to take B; however, if they
were assigned to B, they refused to take. Although untestable, it is very likely that
participants from these compliance categories do not exist in reality. Therefore, the
second set of assumptions and the framework based on it are highly recommended to be
used for solving the non-trial departures problem in this paper. Furthermore, as non-trial
departure involves a third treatment out of protocols, so the assumption of available prior
knowledge of the relative treatment efficacy of the third treatment to the control treatment
is required. Two sets of assumptions are generated to identify the subgroup of
participants whose treatment efficacy is estimable. This assumption is plausible when the
non-trial noncompliers take a standard treatment or simply do not take any treatment.

79
In a straightforward manner, we showed that the sensitivity of results to deviations
from the core assumptions outlined can be analyzed in this framework. Violations of
these assumptions need not be catastrophic; in general the bias is affected by two factors.
One is the proportion of noncompliers whose recovery rate after intervention is
significantly different from the compliers. The other factor is the availability of prior
knowledge of relative efficacy of the non-trial treatment to the control treatment for the
subpopulation who takes the non-trial treatment.
Although theoretically and trough simulation we conclude that the proposed
estimator is asymptotically normal and unbiased. It is possible that in practice, due to the
limit of sample size, the estimation might be biased. As shown in our real data example,
Bayesian approach can be used to improve the small sample size inference.
7.2 Direction of Future Research.
In our research, we dichotomize our compliance type as all or nothing. It is desirable
to extend the argument to ordered categorical compliance. For within trial departures,
Goetghebeur and Molenberghs
52
presented efficacy estimates for partial dose in the
subgroup of partial treatment compliers and for full dose in the subgroup of full treatment
compliers. Their approach is based on the subtraction method that deals with
dichotomous compliance. It suggests a model in which the two treatment efficacy
estimation (partial compliance vs. none, full compliance vs. none) are kept distinct, and a
set of complex second-order parametric restrictions are put on the association between
the treatment compliance and the outcome.

80
When data on compliance with treatments are more detailed, for example, when
exposure is measured continuously, it raises the problem of estimating the treatment
effect over very detailed exposure levels. It is interesting to know in such case how the
non-trial noncompliance affects the efficacy estimation. One possible solution is to use a
parametric structural model. It links the compliance information to the potential
outcomes data. One advantage of the structural model is that it also flexible to include
compliance-covariate interaction terms, which describe differential efficacy in subgroups
determined by covariates. It is especially useful for subgroups of participants who take
non-trial treatments. Examples include that Lapp assessed the treatment effect for 300
hypertensive patients’ blood pressure reduction. The blood pressure was measured
continuously and compliance to treatment was assessed by a medical monitoring system
that produced continuous relative dose information. The structural mean models were
used to handle responses measured on a continuous level and the structural failure time
models were used to handle response measured on a time-to-event scale
53-55
. Therefore,
structural estimators are highly recommended for future research on non-trial departures
problem when the noncompliance is measured on continuous scale and there are
covariates information available to distinguish different compliance subgroups.

81
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86
Appendix. Summary of ITT paper finding of the treatment effect on
Oswestery Outocmes
Pre- and post-intervention scores stratified by the intent-to-treat assignment and
the actual treatment received as well as their respective analyses are summarized in
Tables A.1 and A.2 below.
Table A.1 The ITT analysis of the Oswestry scores
Outcome
variables
Exercise and Education
(n=51)
Education Only
(n= 47)
P
Pre Post Pre Post
Oswestry
score (%)
31.4
(14.4)
13.0
(13.6)
31.4
(17.6)
22.2
(16.0)
.16
<.0001

Table A.2. The As-treated analysis of the Oswestry scores
Outcome
variables
Exercise and
Education
(n=44)
Education Only
(n=14)
Usual Care
(n=20)
P

Pre Post Pre Post Pre Post
Oswestry
score(%)
32.8
(15.6)
13.6
(13.8)
30.8
(15.8)
21.6
(16.8)
28.6
(16.6)
20.8
(16.4)
.78
<.0001

In the ITT analysis of the Oswestry scores (Table A.1), the ANOVA results
revealed a significant main effect for time (P<.0001). When averaged across both

87
treatment groups, Oswestry scores were lower post-intervention when compared to the
pre-intervention scores. A significant group by time interaction was observed (P=.002).
Post hoc comparisons demonstrated a significantly greater decrease in Oswestry scores in
the Exercise and Education group. When a repeated measures ANOVA was performed on
the Oswestry scores of the three actual treatment groups (Table A.2), a group by time
interaction was observed (P=.001). Post hoc comparisons showed most improvement in
the Exercise and Education group.

Abstract (if available)

Abstract Motivated by a real clinical trial, we consider the problem of estimating the causal treatment effect of a two-arm randomized controlled trial in which some of the participants selected a third treatment outside of the protocol. Following Rubin's potential outcome model approach, we classified the study sample into nine subgroups according to their potential compliance behaviors under each assignment. Under two alternative sets of assumptions outlined, a relative risk estimator for a binary outcome is proposed and estimated for the subgroups of participants identified as providing information to the causal estimation. Asymptotic performance of the proposed estimator is evaluated both theoretically and through simulation. Our approach is compared with traditional approaches including intent-to-treat, per-protocol, as- treated and instrumental variable analyses. Results show our proposed estimator is asymptotically unbiased and thus gives a better estimate of the true treatment effect for the subpopulation than other estimators. Illustration of application to a real dataset is also presented.

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