Download 4 Examples of Adaptive Seamless Phase II/III Designs

Adaptive Seamless Phase II / III Designs – Background, Operational
Aspects, and Examples
1
Introduction
One challenge in the development of new and innovative medicines is the amount of time
which it takes to discover, develop, and then demonstrate the benefits of a new drug. For
this reason, much thought has been given to find ways in which drug development could
be expedited and be made more efficient without compromising integrity and validity of
the development process. One intriguing possibility involves addressing within a single
trial objectives which have traditionally been addressed in separate trials.
We define an adaptive design as a clinical trial design which incorporates the possibility
of modifying some aspect of the trial while it is still ongoing based upon data collected in
the trial. A seamless design combines into a single trial objectives traditionally
addressed in separate trials. This type of design eliminates the time that would have
occurred between the trials had they been conducted separately, and may provide
additional efficiencies in terms of the total number of patients or long-term follow up. In
an adaptive seamless design as we describe in this paper, we combine trials in this sense,
and we will further view that the analysis is inferentially seamless, i.e., the final analysis
will use data from patients enrolled before and after the adaptation.
Combining studies into a seamless design is possible within or across development
phases. There are important opportunities for seamless designs in early development, but
they are not the focus of this paper: we will concentrate on the seamless transition
between Phase IIb (“learning”) and III (“confirming”). We are envisioning that at an
interim analysis following the learning stage, a selection decision will be made governing
patient cohorts which will continue into the confirmatory stage. Selection of treatment
arms which will, along with a control group, continue into the confirmatory phase, may
be considered the most typical example, though other types of selection are possible as
well. Section 4 will illustrate two cases studies involving adaptive seamless dose
selection trials, and one involving patient population selection.
1.1
Opportunities and challenges in seamless development
Benefits and drawbacks of implementing an adaptive seamless Phase II/III designs must
be carefully weighed against each other. Not all clinical development programs may be
candidates for such a design. We will outline some criteria to help in determining the
feasibility of such a design for a clinical development program. None of these factors can
be considered as strict rules governing when an adaptive seamless design can or cannot
be used. Rather, it should be a combination of these types of considerations which will
lead to a final conclusion as to whether or not an adaptive seamless approach should be
used. These factors should also not be considered as an exhaustive list, but rather as
some important considerations to begin the discussion.
A main motivation behind adaptive seamless designs is the possibility of saving time in
the development of a new and needed medication. However, besides the reduction in
development time, there is also added efficiency in the use of data collected from
patients; most efficiently using patient data should be the goal of any clinical
development program. Allowing the data from the learning phase to be combined with
data from the confirmation phase suggests that such a design would be able to draw
stronger conclusions with the same number of exposed patients. Alternatively, fewer
patients may be needed to provide the same strength of conclusions as in the standard
paradigm. Also, if patients in the learning phase remain in the study and continue to be
monitored, more long term safety data could be captured in such a design, and long term
safety effects could thus be better understood.
1.1.1
Endpoints and enrollment
The most important feasibility consideration for an adaptive seamless design is the
amount of time a patient needs to be followed to reach the endpoint which will be used
for the selection decision. Using a dose selection example, just prior to the interim
analysis which will be used to select the dose that will continue, there will generally be a
period of the study during which some patients have been randomized but have not yet
been followed long enough to have been evaluated for the endpoint being used for the
selection. Thus, if the time needed to reach this endpoint is short relative to the total
enrollment time of the study, then enrollment can continue uninterrupted with relatively
few patients enrolled during this ‘transition’ period. Although patients enrolled during
this period and randomized to doses which will not be continued can be used to better
understand the dose response and safety profile, they will not be part of the final
confirmatory analysis of the selected dose. If the endpoint duration is too long, then too
many patients would be randomized during this period, which could result in
unacceptable inefficiencies. In such a case, it could be considered whether enrollment
should be temporarily paused during the transition period, causing disruption to the trial
and eroding some of the time savings of an adaptive seamless design. Alternatively, a
surrogate marker might be used for the selection.
We recommend using well established and well understood endpoints or surrogate
markers when implementing adaptive seamless designs. If a goal of a Phase II program
in a novel disease area was to determine a primary endpoint to be carried forward into
Phase III, an adaptive seamless design would likely not be feasible.
1.1.2
Clinical development time
As a primary rationale behind seamless development is to get effective medications to
patients sooner, it must be considered whether a seamless development program would
accomplish a reduction in development time. This reduction is clear if the seamless trial
is the only pivotal trial that will be required for registration. However, if the seamless
trial is one of two required pivotal trials, the second pivotal trial should be completed in a
timeframe which shortens the overall development time. Ideally, the second, more
traditionally designed, pivotal trial could begin immediately after the interim analysis and
selection in the seamless study, and would be completed near the time the seamless study
is completed. There will also be more time needed for the planning, development, and
health authority review for such a design. This additional time must be included in the
evaluation of the overall clinical development time.
1.1.3
Logistical considerations
Drug supply and drug packaging could be more challenging in this setting, since the
number of treatment groups would change during the trial. Therefore, development
programs which do not have costly or complicated drug regimens would be better suited
to such designs. It is also advantageous to have the final formulation of the drug
available by the start of the seamless trial, otherwise a bioequivalence study might be
required prior to registration. Procedural considerations relative to decision processes
and dissemination of information are discussed in Section 3.
2
Methodology
2.1
General overview
Traditionally, selection of the most promising treatment is made in Phase II of drug
development, and comparison of this treatment for superiority versus a control is done in
a Phase III confirmatory trial. It is highly desirable to avoid a delay between the end of a
Phase II trial and the start of the subsequent Phase III trial. One way to streamline the
process is to conduct both treatment selection and confirmation of treatment efficacy over
control under a single protocol where all the data are appropriately used in the analysis.
Treatment selection may be based on a short-term endpoint (e.g. surrogate or clinical
endpoint measured in a short-term interval), while the confirmation stage uses a longterm (clinical) endpoint. Examples are: pain-free at two weeks versus pain-free at 12
weeks, tumor shrinkage response versus survival, fasting plasma glucose versus HbA1c,
change in bone mineral density one year after the start of treatment versus occurrence of
fractures within five years, etc.
Selection of the best treatment after the first stage can be a complex decision process that
involves not only the primary endpoint but also the secondary endpoints, safety data, and
possibly external information. Enough information should be obtained during the
“learning” stage to enable adequate risk-benefit assessments in the confirmatory stage.
Such decision making should be done by a group of experts with a wide range of
scientific knowledge about the disease, the compound, the therapeutic area, and should be
based on well-reasoned considerations of all aspects of the data.
The second stage data and the relevant data from the first stage are combined in a way
that guarantees the Type I error rate for the comparison with control and produces
efficient unbiased estimates and confidence intervals with correct coverage probability.
2.2
Descriptions of common methods
The methodology of seamless Phase II/III design represents a fusion of treatment
selection techniques and hypothesis testing for integration, both operationally and
inferentially, of Phase II and Phase III into a single trial.
2.2.1
Selection and testing against control
Early work on treatment selection includes that of Bechhofer et al (1968) on fully
sequential identification and ranking and Paulson (1964) elimination procedures based on
continuous sequential comparisons of two populations at a time. The goal is to select the
“best” treatment (defined as the treatment with the largest mean, rate, etc) with a
requirement on the probability of correct selection under certain sets of means (outside
the “indifference zone”). Methods allow early elimination of weak treatments and use
response adaptive treatment allocation to reduce the number of patients on inferior
treatments as well as the total sample size of the study.
In order to avoid continuous monitoring, Thall et al (1989) proposed a two-stage design
for trials with binary outcomes, in which the first is used to select the “best” treatment
and the second includes just the selected treatment together with the control. Inclusion of
the control in the first stage is crucial: it allows results from that stage to be pooled with
the data in the second stage. Schaid et al (1990) considered a time to event endpoint and
allowed also possibilities of stopping early for efficacy after the first stage, or allowing
more than one treatment to continue into the second stage.
Stallard and Todd (2003) generalized these designs by using error spending functions to
allow for the possibility of more than two stages. The test statistic is based on efficient
score, so the design is applicable for general endpoint, including normal, binary, ordinal,
or survival time.
These proposals can be used for seamless Phase II/III design with the first, selection stage
taking the place of a Phase II trial, and the second, testing stage the ensuing Phase III
trial. Various ingredients of these methods can be combined to allow sequential
monitoring, response-adaptive treatment allocation and elimination of inferior treatments
throughout the seamless trial.
2.2.2
Pairwise comparisons with group sequential designs
Comparison of several treatments and a control can be considered as a testing problem of
the global null hypothesis that all treatments are equal in the framework of group
sequential tests.
Follmann et al. (1994) (see also Hellmich (2001)) proposed such group sequential tests
with Pocock and O’Brien-Fleming type boundaries. These boundaries are chosen to
guarantee the Type I error rate. They note that a simple Bonferroni approximation is only
slightly conservative. Treatments may be dropped in the course of the trial if they are
significantly inferior to others. Step-down type procedures allow critical values for
remaining comparisons to be reduced after some treatments have been eliminated. The
focus of this approach is on controlling the Type I error rate rather than on power.
For treatment selection based on means of normal distribution, Bischoff and Miller
(2005) developed a two-stage adaptive design with minimal number of patients that
controls the Type I error rate, achieves a required power to detect a given clinically
relevant difference in means, and also controls the probability of wrong selection (i.e., an
inferior treatment is chosen after the first stage). An early stopping either for efficacy or
for futility is available, and the information received about the variance is used to
determine the number of patients on the selected treatment and control for the second
stage.
In contrast to all methods considered above, in which the selection and confirmation are
based on the same primary endpoint, Todd and Stallard (2005) considered a group
sequential design that incorporates treatment selection based upon a short-term endpoint,
followed by a confirmation stage comparing the selected treatment with control in terms
of a longer-term primary endpoint.
2.2.3
P-value combination tests
The methodology of adaptive combination tests (see e.g. Bauer and Kohne (1994), Bauer
and Kieser (1999), Brannath et al. (2002), Muller and Schafer (2001), Liu and Pledger
(2005)) allows information from earlier stages to be combined with that of later stages,
although treatments (doses) are selected at adaptive interim analyses based upon all
previous information from inside or outside the seamless trial. Many mid-trial design
modifications (which need not necessarily be pre-specified a priori) are possible without
compromising the familywise Type I error rate. A general formulation of the adaptive pvalue combination test in the context of treatment selection is recently given in Posch et
al. (2005).
Assume that we plan the seamless trial as a two-stage design. For the first stage, we fix
in the protocol the treatments (doses), primary outcome measure(s), the sample sizes for
the two stages, the allocation rule, the test statistics, the p-value combination function,
and so on. We conduct the first stage and get our first stage p-value for testing the global
null hypothesis that all treatments are equal to placebo (this may be a p-value from a
trend test, from a pairwise comparison with control using a closed testing principle, a
Dunnett’s test, etc).
All data collected thus far in the trial or available from sources outside of the trial are
used in making the interim decision. This may lead to dropping some treatments because
of lack of efficacy or safety concerns, or adding new treatments because they seem to be
sufficiently safe and more effective. The allocation rule for the second stage may be
changed, for example, assigning a greater sample size to a particular treatment arm to get
more safety information. The total sample sizes may be modified based upon observed
nuisance parameters such as the variability of the primary outcome or the event rate in
the control arm.
If after the first stage the trial is not stopped for lack of efficacy, we proceed into the
second stage. After the second stage, we calculate the second stage p-value based upon
the disjoint sample of the second stage only. The final analysis is conducted by
combining the two p-values into a single test statistic using a predefined combination
function. Note that this combination rule cannot be chosen in a data-dependent way after
the first stage, it must be laid down a priori in the planning phase.
This formulation in terms of combination of p-values provides an enormous generality
with regard to hypotheses and statistical models. The adaptive combination test controls
the familywise Type I error in the strong sense (i.e., the probability that one treatment is
erroneously declared superior to the control) under all types of adaptations which
preserve the simple properties of the distribution of the stage-wise p-values under the
overall no effect hypothesis. It is important to note that if the treatment continuation
criterion used during the trial differs from that which was planned, then this may have an
impact on the power, but will not affect the Type I error rate.
Recently, Kelly et al. (2005) developed a very flexible design that uses adaptive group
sequential methodology to monitor the largest efficient score statistic over multiple stages
of a trial. The design allows the trial to begin with any number of treatments, to have any
number of stages, and permits any number of treatments to continue at any stage.
2.2.4
Bayesian model-based designs
Inoue et al. (2002) envisage a Phase II trial in which a single treatment is compared with
a control based on both survival time and short-term events that may be related to
survival through a parametric mixture model. The main comparison is based on the
survival endpoint, and the utility of short-term events must be demonstrated by the results
actually observed in the trial. Initially, patients are enrolled only in one main center and
are randomized between treatment and control throughout. Interim decisions of whether
to stop early, continue Phase II, or proceed to confirmatory Phase III are made repeatedly
during a time interval, and are based on predictive probabilities of concluding superiority
of the new treatment. If the data suggest that the new treatment may have a positive
impact on the short-term events and that this impact translates into a survival benefit,
then the trial is seamlessly expanded to include other centers, increasing the accrual rate.
Randomizing from the start allows the conventional sharp division between Phase II and
Phase III to be replaced by a process of repeatedly deciding whether to stop the trial or
expand it by adding new centers without wasting the Phase II data. If it is decided to
proceed with Phase III, then Phase II is continued and data are accumulated while Phase
III is being organized. There is no interim suspension of patient accrual. This allows a
staggered investment requiring additional cost of expanding only when needed.
Berry et al. (2002) consider whether to shift from model-based dose finding in Phase II to
a confirmatory Phase III trial on the basis of a decision analysis, with the goal to
maximize the expected profit. Each new cohort of patients is allocated to the doses that
maximize the information about the dose-response, given the current interim data. The
dose-ranging stage continues until a decision is made that the drug is not sufficiently
effective to pursue future development, or that the optimal dose for the confirmatory
stage (Phase III) is sufficiently well known.
Although the Bayesian approach is used as a tool for deriving the design, its parameters
are tuned and frequentist properties are shown by simulation to satisfy regulatory
constraints on both Type I and Type II error rates.
2.2.5
Point estimates and confidence intervals
The analysis of data from seamless trials may be problematic because of the treatment
selection and the possibility of early stopping after the first stage. These aspects lead to
statistical bias of the maximum likelihood estimate of the effect of the selected treatment
over the control, and in inaccurate coverage for the associated confidence interval. In the
same way that the test comparing the selected treatment with the control must be adjusted
to give a correct Type I error rate, estimates of treatment effect must also be adjusted to
avoid statistical bias and produce confidence intervals with correct coverage probability.
A confidence set can be derived by exploiting the duality of hypothesis tests and
confidence intervals (Brannath et al. (2003)). This approach leads to the so called
repeated confidence interval which is strictly conservative if the trial stops at the interim
analysis. A more general approach is to use for each null hypothesis a different
combination test (Posch et al. (2005)).
Assuming a normal distribution for the endpoint, Sampson and Sill (2005) invert a
conditional (on the order of the mean outcomes of the treatments after the first stage) test
to produce a confidence interval for the effect of the “best” treatment over control with a
correct confidence level. No early stopping and no sample size reassessment is
considered.
Stallard and Todd (2005) evaluated the bias of the maximum likelihood estimate and
proposed a bias adjusted estimate. Using a stage-wise ordering of the sample space, they
also construct a confidence region for the selected treatment effect. The statistical
properties of point estimates and simultaneous confidence intervals are also investigated
in Posch et al. (2005).
3
Decision Processes in Seamless Phase II/III Trials
3.1
Introduction
Seamless Phase II/III trials raise particular challenges with regard to the data review
performed at the end of the learning phase. For most types of conventional interim
monitoring of ongoing trials, procedural conventions are well-established and generally
involve a Data Monitoring Committee (DMC) composed of experts in the relevant
disciplines who are not otherwise involved in the trial; in trials with registration potential
the DMC is usually external to the sponsor to maximize objectivity and protect the
integrity of the trial. Of course, by definition, seamless Phase II/III trials aim to produce
results which could be part of a regulatory submission, so ensuring the credibility of the
trial is a critical concern.
While current monitoring conventions are a sensible starting point for consideration of
processes for reviewing the learning phase results in a seamless Phase II/III trial, there
are two particular aspects of seamless designs which differ from most conventional
monitoring and warrant special consideration:

The decision process may require additional expertise or perspective not usually
represented on DMCs, and may potentially require sponsor input into the decision
process, or at least sponsor ratification of the DMC recommendation.

Unlike much conventional monitoring, in which the basic decision involves
continuation or termination, the primary motivation for review of the learning
phase data in a seamless design is to make a selection decision which will govern
the remainder of the trial. The specific decision may well be apparent to
observers, and this may convey some information about the interim results.
Below, we consider several aspects of these issues relevant to the decision process in
seamless Phase II/III designs.
3.2
Composition of the decision board
Many seamless Phase II/III trials would already have a DMC constituted for the more
usual purposes, most typically safety monitoring, and possibly also to make judgments
about interim results relative to a group sequential plan allowing termination for strong
indication of efficacy, or for lack of effect. Such a committee might well meet multiple
times during the study, not simply at the decision point before the confirmatory phase of
the seamless trial.
One decision to be made for a seamless trial is whether the learning phase decision and
the other monitoring objectives should be addressed by the same board or by separate
boards. There seems to be no uniformly correct approach, and the decision will depend
on trial specifics such as the nature of the selection, the motivation for the other
monitoring occurring in the trial, and the expertises that would be required for making the
relevant decisions of both types. If it is decided that a single board would suffice, then at
a minimum, it should be strongly considered whether the composition of the board should
be broadened to include individuals not normally represented on a DMC who have proper
perspective and experience in making the selection decision; for example, individuals
with safety monitoring expertise may not have relevant experience in dose selection. If
separate boards are used, then the members of the board making the selection decision
should in general only review unblinded data at the selection point and should only see
results relevant to the decision they are charged to make (i.e., unlike a safety monitoring
board, which would generally have a broader and ongoing role).
3.3
Process for producing analysis results
As in any confirmatory trial, it is in the interest of enhancing the credibility of the trial
results and minimizing potential for bias that access to treatment codes, unblinded data,
and interim analysis results be strictly withheld from trial participants, including (but not
limited to) the trial team managing the study, the Steering Committee, and investigators.
As in other types of monitoring, results should be produced by a statistician and
programmer without other roles in the trial, who would then provide the results directly
to the appropriate DMC for review.
3.4
Sponsor representation
In most monitoring situations in registration trials, sponsor representatives are not
members of the DMC and (perhaps apart from an independent statistician and
programmer) are not allowed access to the interim results. In adaptive seamless designs
there can be more motivation for sponsor participation in the decision process at the end
of the learning phase:

Sponsor perspective may be relevant to the selection decision being made, and it
might not be the case that a board totally external to the sponsor can provide full
perspective needed for the decision.

Especially in trials with long-term confirmation phases, the sponsor may be at
substantial commercial risk if the recommendation is made by an external board,
with no sponsor representative at least having opportunity to discuss the
recommendation with the DMC or ratify the decision.
If sponsors are to be part of the decision process, or be permitted access to the results on
which a recommendation is based in order to ratify a decision, then in the interest of the
integrity of the trial, as reflected in regulatory guidance documents (e.g., FDA (2005)),
the following principles should be adhered to:

Sponsor representatives who will participate in the recommendation, or be
allowed to ratify the recommendation, are adequately distanced from trial
activities, i.e., they do not have other trial responsibilities, and should have
limited direct contact with people who are involved in the day-to-day
management of the trial

Sponsor representation is “minimal” to meet the needs, i.e., the smallest number
of sponsor representatives which can provide the necessary perspective is
involved, these individuals see the minimum amount of unblinded information
needed to participate in the decision process, and only at the decision point.

Appropriate protections and firewalls are in place to ensure that knowledge is
appropriately limited; e.g., procedures and responsibilities are clearly documented
and understood by all parties involved, confidentiality agreements reflecting these
are produced, secure data access and transfer processes are in place, etc.
3.5
Information inferable from the selection decision
As described previously, the decision made based upon the learning phase of a seamless
adaptive trial will govern an important aspect of the continuation of the trial into its
confirmation phase, namely selection of group(s) which continue. Usually it will not be
feasible to mask which group(s) of patients are continuing. It can thus be argued that
knowledge of the selection decision can provide to observers some information about the
interim results.
In general, knowledge of which treatment groups continue into the confirmation phase of
a seamless design should be perceived to provide only minimal information to observers,
without potential for biasing the conduct of the trial, as long as the numerical results on
which decisions were based remains strictly protected. In one sense, the seamless design
can be interpreted to be superior to the conventional separate-phase paradigm, in which
Phase II results will often be broadly known and in much detail prior to the Phase III trial.
One of the arguments cited in support of confidentiality conventions involves
“equipoise”, the desire for trial participants such as investigators to have reasonably
neutral predisposition regarding the comparative merits of treatments in the study; by
limitation of knowledge of learning phase results (which, for example, may be highly
suggestive of advantage for an experimental treatment), seamless designs may often offer
advantages over traditional separate-phase programs in this regard.
Additional precautions should also be considered and implemented as feasible to limit the
information which observers can infer from a particular selection decision. As an
example, while the trial protocol should provide some rationale for the selection decision
to be made, full statistical details may be withheld from the protocol and described in a
document of much more limited availability. In many circumstances, selection may be a
complex process involving a number of factors, and not simply results on key efficacy
endpoints (safety, compliance, marketing considerations, etc.), and this will further limit
what observers are able to specifically infer from knowledge of the selection decision.
4
Examples of Adaptive Seamless Phase II/III Designs
4.1
Example 1: Adaptive treatment selection
This example involves a study with two objectives, treatment selection and efficacy
confirmation (see Fig. 1), using the clinical endpoint American College of Rheumatology
(ACR) 20 score at month six; the ACR 20 score at month three will be considered an
early clinical endpoint. This is a randomized, blinded, placebo-controlled, multi-center,
dose-exploration and confirmatory study to evaluate the efficacy and safety of an
experimental treatment when given in combination with methotrexate to subjects with
active Rheumatoid Arthritis who have had two or more inadequate responses to anti-TNF
therapy. The study uses a seamless Phase II/III two-stage adaptive design similar to
Bauer & Kieser (1999), with dose selection made after the first stage. Second stage data
and the relevant data from the first stage will be combined based on Fisher’s combination
test, described in Section 2.2.3. The overall significance level is 0.025. Early stopping is
allowed for futility, but not for efficacy.
Subjects will be assigned in equal ratio to 5 treatment arms (4 active and 1 placebo) in
equal ratio. After the first stage of the trial, an interim analysis is planned. The ‘best’
active treatment arm and the placebo arm will be advanced to the second stage for
efficacy confirmation. The best treatment arm will be selected based on a set of predefined efficacy, safety, and immunogenicity criteria. It is estimated that at the time of
interim analysis we will have approximately 50% of the subjects with the clinical
endpoint information available, and 65% will have the early clinical endpoint information
available. During the interim analysis the following decisions will be made:
1. the best treatment group (safe and efficacious) will be promoted to the second
stage;
2. the least efficacious and / or unsafe treatment groups will be dropped;
3. the futility requirement will be evaluated.
All these decisions will be made based upon the clinical endpoint, and early endpoint
information will be used as supportive evidence. Subjects in arms discontinued from the
study at the end of the first stage will be given an option either to continue with the
second stage treatment arm, or drop out of the study, with their information used for
safety reporting only. There will be two committees involved, an external independent
Data Monitoring Committee and an internal Executive Decision Committee. The
decision making process during the interim analysis will be similar to that described in
Section 3.4.
Phase II
Stage 1 (Exploratory)
4 Active Treatments Vs Placebo
Phase III
Stage 2 (Confirmatory)
1 Active Treatment Vs Placebo
Interim Analysis
1. Futility
2. Dose response
3. Dose Selection
File
Continuous Recruitment
Fig 1: Trial Design for Example 4.1
4.2
Example 2: Confirming sustained treatment effect of a dose
selected based on a short-term endpoint
The objective of this trial in patients with neuropathic pain is to confirm sustained
treatment effect, measured as PI-NRS score change from baseline to the 8th week of
treatment. Initially, patients are randomized equally to three doses of the new compound
and placebo. Two interim analyses are planned before the end of enrollment period. At
the first interim, all available data on patients in the trial will be used to change the
allocation rule. A longitudinal model for the primary endpoint in time (2, 4, 6 and 8
weeks) is used to improve the estimate of the sustained treatment effect. At the second
interim, one dose will be selected to continue for the confirmation part of the study. Final
analysis will use a p-value combination test to confirm the superiority of the selected
dose over placebo. In contrast to a conventional design of a Phase IIb trial with three
doses and placebo on a short-term endpoint (2 week change from baseline) followed by a
confirmatory Phase III trial with a long-term (8 week) endpoint, this adaptive design
combines the two trials in one study with a single protocol, and uses information on the
long-term endpoint from patients in the first and the second parts of the study.
4.3
Example 3: Confirming efficacy in an adaptively specified
subpopulation
In this two-stage adaptive design trial (see Fig.2) for patients with metastatic breast
cancer, we have two objectives: population selection at stage 1, and efficacy confirmation
based upon the hazard ratio for mortality between treatment and control at stage 2. A
genomic biomarker, expression level, will be available for all subjects. Initially patients
are to be randomized into 3 treatment arms (2 actives and 1 control) in equal ratio. One
interim analysis is planned for this study after occurrence of approximately 60% of the
targeted events, during which two subpopulations A and B will be defined based on
whether the biomarker expression level of each subject of that population exceeds or fails
to exceed a pre-defined cutoff value. Subsequently, efficacy and safety data will be
analyzed for both populations, and a decision will be made on which population will
advance to the second stage. Moreover, a futility requirement will also be checked at this
interim analysis. The final analysis will use the inverse normal p-value combination test
for the selected population to confirm the superiority of the doses under investigation
versus control. In contrast to a conventional design with a Phase IIb study for population
selection followed by a confirmatory Phase III study, here we will be able to achieve the
same objectives in a seamless manner via one study, saving considerable time and costs
while maintaining trial integrity.
Identification of subpopulation based on
predictive biomarkers
Randomization
Full population
I
N
T
E
R
I
M
D
E
C
I
S
I
O
N
Sub-Population A
OR
Sub-Population B
Stage 1
Stage 2
Continuous Recruitment
Fig 2: Trial Design for Example 4.3
5
Conclusion
The
FDA’s
“Critical
Path”
document
(ref.:
www.fda.gov/oc/initiatives/criticalpath/whitepaper.html) calls for “…new tools to get
fundamentally better answers about how the safety and effectiveness of new products can
be demonstrated, in faster time frames, with more certainty, and at lower costs.” For
reasons as we have described above, we feel that Seamless Phase II/III designs offer great
potential for achieving these objectives. When selected for use in appropriate programs,
and carefully and properly implemented to maintain integrity of the experimental process,
we feel that these designs can provide better answers to important questions with greater
certainty, and with a higher degree of efficiency with regard to patient exposure and the
time required to make effective treatments available to patients. Actual experiences with
successfully conducted seamless Phase II/III programs may go a long way towards
building acceptability of this approach. We encourage continued constructive debate and
discussion among the relevant parties in industry, the regulatory arena, and academia, to
hopefully pave the way for increased implementation of such advantageous clinical trial
designs.
6
Acknowledgement
The PhRMA working group on adaptive designs provided a platform for discussing the
topics described in this paper. The authors are members of a workstream on seamless
Phase II/III trials within this PhRMA working group. We would like to thank all our
colleagues, consultants, and informal members who provided feedback, including Keaven
Anderson, Don Berry, Mark Chang, David DeBrota, Jonathan Denne, Brenda Gaydos,
Andy Grieve, Gary Littman, Marc Walton. This paper is linked to an Executive
Summary our working group has previously published (Gallo et al., 2006, in press).
7
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