an adaptive seamless phase ii/iii design for oncology trials with subpopulation selection using...

An adaptive seamless phase II/III design foroncology trials with subpopulation selectionusing correlated survival endpointsy

Martin Jenkins,a� Andrew Stone,a and Christopher Jennisonb

Although the statistical methods enabling efficient adaptive seamless designs are increasingly well established, it isimportant to continue to use the endpoints and specifications that best suit the therapy area and stage of developmentconcerned when conducting such a trial. Approaches exist that allow adaptive designs to continue seamlessly either in asubpopulation of patients or in the whole population on the basis of data obtained from the first stage of a phase II/IIIdesign: our proposed design adds extra flexibility by also allowing the trial to continue in all patients but with both thesubgroup and the full population as co-primary populations. Further, methodology is presented which controls the Type-Ierror rate at less than 2.5% when the phase II and III endpoints are different but correlated time-to-event endpoints. Theoperating characteristics of the design are described along with a discussion of the practical aspects in an oncology setting.Copyright r 2010 John Wiley & Sons, Ltd.

Keywords: seamless design; subpopulation selection; phase II/III; oncology; targeted therapy; time-to-event endpoints

1. INTRODUCTION

Adaptive, seamless, phase II/III designs provide an approachwhereby important new medicines may be made available topatients more rapidly and efficiently through the utilization ofrecently developed statistical methodologies. The periodbetween the analysis of phase II data and recruitment of phaseIII patients, sometimes termed ‘white space’, can be minimized,while the seamless approach also allows the flexibility toinvestigate other crucial issues, such as dose finding orsubpopulation selection [1], without the need for separatetrials. In these studies, there is no break between the learningphase II and the confirmatory phase III and subjects from bothphases are used in the final decision-making process. Patientnumbers can be used more efficiently as none of theinformation gained from the learning phase is ignored.

The papers by Schmidli et al. [1] and Bretz et al. [2] describe aframework for phase II/III clinical trials based on the p-valuecombination methods of Bauer and Kohne [3]. They demon-strate how the closure principle can be applied to test multiplehypotheses under consideration in a treatment selectionproblem. The testing procedure required to implement thedesign in any multi-hypothesis situation is now well understood.Brannath et al. [4] applied this work more specifically to the issueof adaptive population selection for the development of atargeted therapy and addressed the questions of decision rulesand the control of Type-I error.

In this paper, we consider the development of a targetedoncology therapy, where there is an a priori hypothesis thata prospectively defined subgroup could particularly benefit.This subgroup may be defined by a biomarker or any pre-defined clinical criteria and it is assumed that the subjects whoare members of this subpopulation can be successfully and

reliably identified. The methods of adaptive seamless phase II/IIIclinical trials will be applied to this setting and extended toallow the most appropriate survival endpoints and decisionrules to be employed. Crucially, the experience gained from anintermediate, time-to-event endpoint during the learning phaseof the trial can be used to ensure that the confirmatory sectionof the study includes the most appropriate patient cohorts whomay benefit from the treatment, whether this is the entirepopulation or the subpopulation, or whether we continue totest the hypothesis in both groups, here described as the co-primary case.

Broadly speaking, there are two distinct families of seamlessdesign methods in the literature: those based on the p-valuecombination techniques of Bauer and Kohne [3] and thosebased on the multivariate normal methods of Stallard andTodd [5], which use modified group sequential computations.The p-value based phase II/III designs, such as those of Schmidliet al. [1] and Brannath et al. [4], have been restricted to a singleendpoint as combining p-values based on differing endpointswould not relate to the test of a sensible hypothesis. Todd andStallard have extended their work to consider a change ofendpoint [6] and Royston et al. [7] have addressed relatedsurvival outcomes, but both approaches rely on assumptions

34

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MAIN PAPER

Published online 8 December 2010 in Wiley Online Library(wileyonlinelibrary.com) DOI: 10.1002/pst.472

Pharmaceut. Statist. 2011, 10 347–356 Copyright r 2010 John Wiley & Sons, Ltd.

ySupporting information may be found in the online version of this article.

aAstraZeneca Pharmaceuticals, Global Clinical Development, Parklands, AlderleyPark, Macclesfield, UK

bDepartment of Mathematical Sciences, University of Bath, Bath, UK

*Correspondence to: Martin Jenkins, AstraZeneca Pharmaceuticals, Global ClinicalDevelopment, Parklands, Alderley Park, Macclesfield SK10 4TG, UK.E-mail: [email protected]

about the joint distributions of test statistics between stagesand between subgroups. These methods quickly becomecomplicated when extended to a population selection problem.In this paper, we propose a hypothesis test based on combiningtest statistics for the final endpoint from each stage, eventhough the decision to proceed to phase III is based on theintermediate endpoint.

Including a co-primary option in this new design recognizesthat there may still be uncertainty after phase II concerning theoptimum population to study. Hypotheses relating to both theoverall population and pre-defined subpopulation can beinvestigated using patients from both phases, although someauthors have chosen to formulate designs where the subgroupis characterized on an initial stage of patients and examined in asecond stage [8]. Wrongly dropping a relevant group at theinterim analysis would be costly. Even when an overall effect isfound, there can still be interest in the enhanced performance ofthe subgroup. Furthermore, the trial can be discontinued at theinterim analysis if no promising results are seen. A similarsituation has been considered by Wang et al. [9], although witha single normally distributed endpoint.

The benefits of our proposed design would be lost if the usualintermediate endpoints of an oncology phase II trial could notbe incorporated. Although progression free survival (PFS) isbeginning to be accepted as a confirmatory endpoint in manycancer types, overall survival (OS) is commonly required inphase III by the regulatory agencies. PFS is frequently used inphase II both for expediency and as it is often the most sensitiveendpoint for targeted therapies. We shall extend existingseamless design methods by basing population selection inphase II on PFS but combining OS data from phases II and III inthe final analysis, which will support possible licensing claims.In doing this, it is clear that the dependence between PFS andOS must be accounted for. There are two major considerationsin the use of PFS alongside OS:

1. The combination of test statistics must test a sensible nullhypothesis.

2. The data from two different time-to-event endpointscollected during overlapping periods must be combinedwithout the introduction of bias.

Solutions to these issues and further practical considerationswill be presented.

We shall propose a form of seamless phase II/III trial designincluding population selection based on an intermediateendpoint. Section 2 will outline the trial design and Section 3will cover the methods for control of Type-I error rate in themultiple testing procedures that are utilized. In Section 4, thespecifics of oncology trials and appropriate decision rules for ablinded review are addressed. Section 5 will explain issues raisedby the use of associated time-to-event endpoints. The resultsof simulations of the trial design will be presented in Section 6.The suitability of the trial and the operational issues will beaddressed in the closing discussion.

2. THE PROPOSED DESIGN

We shall consider a randomized, parallel group clinical trial withtwo arms, experimental and control. There will be two distinctstages, an initial learning stage analogous to a randomizedphase II trial and a second confirmatory phase analogous to a

randomized phase III trial. An interim analysis takes place basedon the first stage subjects only, whereas the final analysis isbased on all subjects. Both the full population (F) and a knownsubgroup (S) are to be investigated for evidence of increasedefficacy with the new treatment. The subgroup S should beclearly defined and this definition cannot be altered at theinterim analysis.

At the interim analysis, which considers a short-termintermediate time-to-event endpoint, the trial can either:

� Continue in co-primary populations F and S� Continue in subgroup S only� Continue in the full population F without an analysis in S� Stop for futility

Each of the above options has a pre-specified, but potentiallydifferent, stage 2 sample size and length of follow-up associatedwith it. This allows for more subgroup patients to be recruitedin the subgroup only case than in scenarios where the fullpopulation is continued to be studied.

The stage 1 patients remain in the trial and continue to bemonitored for survival events, at the same time as thosesubjects newly recruited to stage 2, so that this information canbe used in the analysis of the long-term endpoint.

The final assessment is of OS for all patients from both stages.However, these are kept as two distinct groups for the purposeof analysis. The appropriate combination methods for inte-grating OS data from the two stages are described in Section 3.A flow-chart of the proposed design is given in Figure 1.

3. METHODS AND PRINCIPLES

In order to account for the levels of multiplicity involved in thetrial, several correction methods and testing procedures must beemployed. We shall present methods previously summarized inseveral papers [1–3,10,11] in the context of our problem.

By considering both the full population F and the subgroup S,multiple one-sided hypotheses about the investigational treat-ment are taken into account. Within each population, there is asingle null hypothesis of no difference in OS between arms. Thealternative hypothesis is that the new treatment demonstratesincreased efficacy over the comparator in terms of prolongingOS. These null hypotheses for the full population and subgroupwill be denoted HF

0 and HS0, respectively, and similarly we denote

the alternative hypotheses HF1 and HS

1. The decisions aboutwhich hypotheses to proceed to test will be made at the interimanalysis and we discuss rules for doing this in Section 4.

We wish to control at a nominal level a the family-wise errorrate, that is, the probability of rejecting at least one true nullhypothesis. To do this, we use the closure principle, whichinvolves considering all possible intersection hypotheses

THj

0,where the Hj

0 are in the set of original null hypotheses fHF0; HS

0g.This produces three hypotheses, HF

0, HS0, and also HFS

0 , whichspecifies that there is no survival difference in either F or S.A null hypothesis Hj

0 is only rejected overall if all intersectionhypotheses that imply Hj

0 are also rejected. Thus, for example, HF0

can only be rejected overall if individual tests reject both HF0 and

HFS0 at level a.For subjects recruited in stage iA{1,2} the p-values for testing

HF0 and HS

0 will be denoted pFi and pS

i , respectively. Specifically, pF1

and pS1 are based on the OS data for subjects recruited in stage 1

using their OS through stages 1 and 2, while pF2 and pS

2 are34

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M. Jenkins, A. Stone and C. Jennison

Copyright r 2010 John Wiley & Sons, Ltd. Pharmaceut. Statist. 2011, 10 347–356

calculated from OS data for stage 2 subjects only. The reasonsfor choosing these definitions and advantages over otherpossible choices are discussed further in Section 5. The stage ip-value corresponding to HFS

0 , pFSi is a function of pF

i and pSi

correcting for multiplicity. We shall use a Hochberg correction[12] with equal weighting of HF

0 and HS0, which gives

pFSi ¼ min ½2 min fpF

i ; pSi g; maxfpF

i ; pSi g�. Other methods such

as that of Dunnett and Tamhane [13] are also possible.We conduct the final analysis on all subjects using an inverse-

normal combination test, which will control the Type-I error rate,regardless of the decision at the interim analysis [14]. Weightsw1 and w2, with w2

11w22 ¼ 1, are specified to combine the

p-values from each stage and the null hypothesis is rejected ifC(p1,p2) = {w1F

�1(1-p1)1w2F�1(1-p2)}Xc. For a one-sided signi-

ficance level of 0.025, we set c = 1.96. The p-values are defined soas to be independent and uniformly distributed under theirrespective null hypotheses.

An important step in achieving this independence is to pre-specify the total length of follow-up of stage 1 subjects for theirOS in stages 1 and 2. This can be defined at the start of the trialby setting a calendar time for the end of follow-up or by fixingthe total number of failures to be observed among stage 1subjects. It is not permissible for stage 1 follow-up to be affectedby the stage 2 design as decisions about the population beingtested and length of follow-up of this population are based onPFS of stage 1 patients, which is liable to be correlated withthose subjects’ OS. The handling of correlated time-to-eventendpoints is discussed further in Section 5 and it is themaintenance of independent test statistics for each stage thatallows previous proofs of control of Type-I error via the closureprinciple [3,10,14] to be applied.

Ideally, the weights w1 and w2 would be chosen to beproportional to the square roots of the numbers of OS eventsobserved during each stage. The combination test would thenhave the attractive property of yielding, approximately, theusual test statistic from a single combined analysis. One mighteven pre-define different weights in the different hypothesis

tests of HF0, HS

0, and HFS0 to match the likely proportions of events

in each stage. However, we are constrained in that weights w1

and w2 must be pre-specified and, since the decision at theinterim analysis can affect the number of subjects to berecruited in the full population F or subgroup S in stage 2, it isnot possible to match the weights to all eventualities.

As a simple compromise solution, we specify weights suitedto the important cases of continuing to test for a treatmenteffect in the full population alone or to test for effects in co-primary populations of the full population and subgroup. Let N1

and N2 denote the anticipated numbers of OS events fromstage 1 and stage 2 subjects, respectively, in these cases.(The trial design may define the length of follow-up in terms ofthese numbers or, if follow-up is specified in calendar time, it willbe necessary to estimate the numbers of events that will beobserved.) We set

w1 ¼ffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiN1=ðN11N2Þ

pand w2 ¼

ffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiN2=ðN11N2Þ

p

as the stage 1 and stage 2 weights for the testing of eachhypothesis HF

0, HS0, and HFS

0 .To make the final decision, the relevant p-values for HF

0, HS0,

and HFS0 are substituted into C(p1,p2) as displayed in Table I.

A worked example can be found in Appendix A. 34

9

Table I. The weights and p-values to be used in combina-tion tests.

Co-primary case – when considering both HF0 and HS

0

Testing HF0: w1 F�1 (1 - pF

1)1w2 F�1 (1 - pF2)

Testing HS0: w1 F�1 (1 - pS

1)1w2 F�1 (1 - pS2)

Testing HFS0 : w1 F�1 (1 - pFS

1 )1w2 F�1 (1 - pFS2 )

F only case – when considering HF0 only

Testing HF0: w1 F�1 (1 - pF

1)1w2 F�1 (1 - pF2)


1 )1w2 F�1 (1 - pF2)

S only case – when considering HS0 only

Testing HS0: w1 F�1 (1 - pS

1)1w2 F�1 (1 - pS2)


1 )1w2 F�1 (1 - pS2)

Figure 1. Flow chart of the adaptive seamless design.



4. INTERIM DECISION RULES

There are several features of oncology clinical trials that areimportant to incorporate into this design. We have alreadycommented that PFS (the minimum of time to death, time tothe growth of existing lesions by a pre-specified amount or timeto the occurrence of new lesions [15]) is not yet an acceptableendpoint for confirmatory phase III trials in all cancer types andso the use of a more traditional endpoint may be required forregulatory submissions. However, PFS is more rapidly observed,is often a more sensitive endpoint to drug effects, and in manysettings is regarded as either a marker of clinical benefit, a goodpredictor, or even a valid surrogate for OS. Our design takesadvantage of the early availability of PFS in using this endpointin decision-making at the interim analysis, while retaining OS asthe endpoint for final hypothesis testing.

The decision rule to be applied at the interim analysis should beclearly expressed so that the study can be conducted with thesponsor remaining completely blinded to all results at this stage.Possible decision rules could be based on group sequentialboundaries or Bayesian methods [4,16]. Whatever approach isused, a simple, unequivocal rule is desirable. In this study, wepropose to use a rule based on the estimated hazard ratios for PFSwithin the full population and the subgroup of interest. Targetvalues are set and the trial only continues in those groups forwhich the estimated hazard ratio exceeds the target. Simulationsof the clinical trial design can be used to choose the thresholds forthis decision rule so as to ensure the design has high power todetect an effect in the groups for which the treatment is effectivewhile stopping early for futility if this is appropriate. Table II showsan example where a hazard ratio less than 1 indicates increasedbenefit from the experimental treatment.

The possibility to stop for futility at the interim analysis isvaluable for sponsors and investigators to optimize theinvestment of resources. Futility stopping will decrease thetrial’s Type-I error rate since there is less chance of continuingpast the interim analysis and so a reduced probability ofrejecting a null hypothesis erroneously at the end of the trial.Similarly, power is also decreased, as there are two opportunitiesto stop without rejecting a null hypothesis.

We make no attempt in our design to ‘recover’ the reduction inType-I error probability due to stopping for futility. This would runthe risk of the error rate increasing if a decision were made tocontinue despite failing a futility rule. Such an approach is inkeeping with the increasing use of ‘non-binding’ futility bound-aries. In any case, an adjustment to recover Type-I error probabilitywould be hampered by the need to estimate the correlationbetween endpoints. Our approach guarantees that the Type-Ierror rate is fully controlled in the proposed design. Simulations ofthe effect of the chosen decision rule will be seen in Section 6.

5. TIME-TO-EVENT ENDPOINTS

As discussed in the previous section, it is important in practical termsthat separate short-term and long-term time-to-event endpoints canbe used in different aspects of a seamless design. However, Bauerand Posch [17] have identified a problem in using time-to-eventendpoints in a two-stage adaptive design. If the choice of stage 2population is affected by short-term responses of stage 1 subjectsand follow-up of the long-term response of these stage 1 subjectscontributes to the stage 2 log-rank statistic for this endpoint, thenthis statistic may not have the desired null distribution. Our solutionis to perform a trial with the following characteristics:

Option A: Our Solution.

� PFS from stage 1 subjects is used at the interim analysis indeciding which subgroups to follow, but does notcontribute to the final test statistics.

� p-Values for comparisons of OS based on log-rank tests areproduced separately for those subjects recruited to stage 1and those recruited to stage 2. In particular, the additionalfollow-up of stage 1 subjects during stage 2 contributes tostage 1 p-values. Also, the extent of total follow-up of stage1 subjects for OS is pre-specified and, hence, not affected bytheir PFS times observed at the interim analysis.

� The comparisons of OS are not carried out until the endof the trial, when a pre-specified number of events or lengthof follow-up is reached for each set of stage 1 and stage 2patients, respectively. At this point, the p-values from eachstage are combined.

This method ensures that a selected hypothesis can be testedwith proper protection of the family-wise Type-I error rate. Ourconstruction avoids the problem noted by Bauer and Posch [17]because we allocate stage 2 follow-up of stage 1 recruits to thestage 1 p-values, pF

1, pS1 and pFS

1 , rather than their stage 2equivalents. This guarantee of independent test statisticsensures that existing theory regarding control of Type-I error[2,3,10,14] continues to hold under the selection of subpopula-tions, as has been previously described in similar designswithout an intermediate endpoint [1,4].

The potential dangers in defining a procedure for our situationare subtle and we shall illustrate them by describing, in additionto our proposed approach, option A, a series of design options Bto D which are unsuitable for reasons of ambiguity, inefficiency orbias. Figure 2 illustrates how the different phases of follow-up onPFS and OS for stage 1 and stage 2 recruits are used in eachoption. As a point of reference, in our proposed method, PFSoutcomes of stage 1 subjects are used to make the interimdecision on which populations to follow. Then, the p-values pF

1, pS1

and pFS1 are calculated from OS results for stage 1 subjects using

the information about these subjects available at the end of thestudy. The p-values pF

2, pS2 and pFS

2 are calculated using the OSdata accruing in stage 2 for the new stage 2 recruits.

Option B: PFS results from stage 1 subjects are used to definethe p-values pF

1, pS1and pFS

1 at the interim analysis. OS of stage 2recruits provides the second set of p-values, pF

2, pS2and pFS

2 . The p-values from the two stages are then combined in an inverse-normal combination test.

There is ambiguity here as it is questionable what hypothesisis finally tested in the combination test. Combining stage 1p-values based on PFS and stage 2 p-values from OS will notprovide a clear and sensible conclusion.3

50

Table II. Example decision rule.

PFS hazard ratioestimates at theinterim analysis HRFo0:8 HRF

X0:8

HRSo 0:6 Continue withco-primary analysis

Continue insubgroup S only

HRSX0:6 Continue in full

population F onlyStop for futility



Option C: PFS outcomes of stage 1 subjects are used to makethe interim decision on which populations to follow. The p-valuespF

1,pS1and pFS

1 are calculated from OS results on stage 1 subjects atthe time of the interim analysis, while pF

2, pS2and pFS

2 are producedfrom OS results at end of stage 2 solely for the new subjectsrecruited in stage 2.

Although this solution is mathematically sound (as no bias isintroduced) it suffers from practical problems. Of the stage 1subjects, only those deaths observed by the time of interimanalysis contribute to the final hypothesis test. Very few events

can be expected by this time and hence overall power will belower than it could be.

Option D: PFS outcomes of stage 1 subjects are used to makethe interim decision on which populations to follow and p-valuespF

1, pS1and pFS

1 are calculated from OS results on stage 1 subjects atthe time of the interim analysis. The stage 2 p-values pF

2, pS2and

pFS2 are calculated using all additional OS data accruing in stage 2,

both from the new stage 2 recruits and from continued follow-upof the OS of stage 1 subjects.

The intention behind this option is to make efficient use ofthe stage 1 subjects by including their OS events that did notcontribute to pF

1,pS1and pFS

1 in the stage 2 p-values instead.Wassmer [18] describes how independent increments arise inlog-rank statistics based on increasing follow-up of a given time-to-event endpoint. Applying this independence property, thestage 2 p-values are calculated from the weighted increment ofthe log-rank statistics based on the total follow-up of all subjectsminus that based only on events prior to the interim analysis.

However for this approach to be valid when multipleendpoints are used, the future increment in the OS log-rankstatistic for stage 2 follow-up must be independent of the PFSdata used to select hypotheses for testing in stage 2. This maynot be the case as there is a set of subjects who have progressedby the interim analysis, but not yet died. These subjectscontribute to both the interim decision and to p2 and sointroduce bias as they have a bearing on both which group ischosen and the final result derived from that group.

Suppose, for example, there is a positive correlation betweenoutcomes PFS and OS, so patients with better than average PFScan also expect good OS. Then, under the null hypothesis HS

0,the decision to follow subgroup S will be taken when thosemembers of S on the experimental treatment show better PFSthan the controls, and so follow-up of OS for these stage 1subjects is also likely to produce better outcomes for theexperimental group. Deciding to test HS

0 when rejection of HS0 is

more likely will bias the test of this hypothesis. This bias and theresulting contamination of the stage 2 p-values is seen veryclearly in the example we present in Appendix B. Thus, option Dis not viable, in keeping with the warnings of Bauer and Posch[17] on adaptations based on time-to-event endpoints andcorrelated surrogates.

Returning to our proposed design (Figure 2, image 1), sincethere are clearly separate sets of subjects involved in stage 1 and2 p-values, there is no chance of bias being carried across stages.This solution is based on two pieces of insight. First, a seamlessdesign does not have to divide data on OS into deaths occurringbefore and after the interim analysis: rather, the subdivision canbe into the survival results of any two well-defined, non-intersecting patient groups. Second, as an intermediate end-point is used during the interim analysis, the calculation ofp-values based on OS for stage 1 subjects can be deferred untilthe end of the trial, allowing long-term follow-up of all stage 1subjects to contribute to the log-rank statistic for OS.

In the interests of operational effectiveness, it is recom-mended that recruitment should be allowed to continuewithout cessation at the interim analysis. The sample sizes andnumber of events required to trigger OS analysis can be pre-specified for each group, allowing appropriate weights to be setfor each stage. Once the required number of subjects has beenentered into stage 1 recruitment can switch immediately tostage 2 while possible additional follow-up for PFS of stage 1subjects and data cleaning for the interim analysis takes place. 3

51

Figure 2. Options for the combination of stage 1 and 2 survival data.Diagrammatic representation of design options. N = patient numbers, t = time.The horizontal reference line is at the number recruited to stage 1. The verticalreference line is at the time of the interim analysis. The shaded box indicates theset of subjects and associated OS or PFS data used to calculate each p-value.



Any patients recruited after this switch would be considered aspart of stage 2 and would not be included in the PFS interimanalysis. This approach gives the maximal time savings, but mayrisk additional costs if subjects are recruited who are not thenrequired for stage 2, e.g. when recruitment continues in the fullpopulation, but it is decided at the interim analysis to restrictattention to the subpopulation.

One could alternatively define stage 1 to include all thesubjects recruited up until the interim analysis. This wouldinclude subjects with immature PFS data at the time of theinterim analysis and, as it is not uncommon for survival curves totake time to separate, these late recruits would contribute littleto the PFS comparison and they may even dilute the magnitudeof any treatment effects on PFS. Consequently, our preference isfor recruitment to switch to stage 2 some time before theinterim analysis.

The final analyses for each stage can be triggered by theoccurrence of a pre-set number of OS events or, alternatively, byreaching a specified calendar time. Although it might seemmore natural for the follow-up of OS for stage 1 and stage 2patients to conclude at the same time, the validity of thestatistical test relies on the length of follow-up of stage 1subjects being pre-set at the beginning of the study. It shouldbe noted that this difference in cut-off points means that theremay be events occurring in one of the two cohorts (of stage 1 orstage 2 patients) which must be disregarded from the finalanalysis if they occur in the first cohort to reach this cut-off, butin the period in between this time and the second cohortcompleting. Hence, for example, if the stage 1 patients reachtheir cut-off first, additional events in this cohort, which occurwhile follow-up of stage 2 patients is completed, will not beused in the final analysis and vice versa.

6. SIMULATION RESULTS

The effectiveness of a seamless design depends on manyparameters, including event rates, recruitment rates, the size ofthe subgroup, and the hazard ratios for PFS and OS in eachgroup. It is therefore necessary to simulate possible designs

under a variety of conditions in order to evaluate their operatingcharacteristics. The simulation results presented in Tables III, IVand V demonstrate good performance of our proposedmethods in a range of situations. In these examples, correlatedOS and PFS times with marginal exponential distributions weredefined using a mixture approach [19]. Study entry wasmodeled with a univariate distribution for arrival times.

Table III demonstrates that, in agreement with theory, theType-I error rate is controlled at less than 2.5%. This is true bothfor testing of the intersection hypothesis, and also for the globalfamily-wise error rate. This overall error rate is lower than theintersection hypothesis rejection rate as on some occasions HFS

0

will be rejected, but not HF0, or HS

0. These results cover a widerange of values for the correlation between endpoints in thecase where there is no futility stopping and the trial alwayscontinues to the co-primary scenario. The absence of earlystopping for futility means that the conservatism seen here isdue to the corrections for multiplicity. If futility stopping hadbeen included here then this would have reduced the Type-Ierror rate. The independence between first and second stagep-values is also demonstrated with the magnitude of allcorrelations being less than 0.05.

Table IV gives estimated probabilities of the various interimand final decisions for our procedure under three differentdecision rules. The interim analysis occurs after 200 PFS eventsfrom the 300 patients recruited to stage 1. A further 800 patientsare then recruited to stage 2 if we continue in the fullpopulation or co-primary case, with 400 recruited if only thesubgroup is used in stage 2. The final analysis of OS is performedwhen 250 deaths have occurred in stage 1 and stage 2 subjectshave produced 500 deaths in the full or co-primary case or 250deaths in the subgroup only case. The subgroup is one fourth ofthe population and there is a correlation of 0.7 between PFS andOS. The results show that if the trial continues to stage 2, HFS

0 isalmost always rejected for the two cases considered. However,stopping for futility at the end of stage 1 occurs in 5–25% ofcases and this rate is highly dependent on the decision rulechosen, as would be expected. As the conditions on estimatedhazard ratios for PFS become more stringent from decision rule

35

2

Table III. Control of type-I error under H0.

Correlationbetween OSand PFS

Family-wise Type-Ierror (rejection of HF

0

or HS0)

Probability ofrejection of

HFS0

Correlationbetween pF

1 and pF2

Correlationbetween pS

1 and pS2

Correlationbetween pFS

1 and pFS2

0.1 0.018 0.020 0.009 �0.020 �0.0180.2 0.019 0.021 �0.019 �0.013 �0.0080.3 0.022 0.024 0.005 �0.031 �0.0370.4 0.024 0.026 0.020 �0.010 0.0130.5 0.020 0.023 �0.011 0.016 0.0080.6 0.019 0.021 �0.019 �0.027 �0.0140.7 0.021 0.023 0.012 0.005 0.0090.8 0.020 0.023 0.025 0.045 0.0520.9 0.021 0.023 0.000 0.006 0.017

Each row is based on 3000 simulations of a trial under the global null hypothesis where all hazard ratios are equal to one.A family-wise error is defined as rejecting at least one of the true hypotheses HF

0 and HS0 in the closed testing procedure. Three

hundred patients were simulated to be recruited to stage 1 and 800 to stage 2. The interim analysis occurs after 200 progressions.The final analysis occurs after 250 deaths in stage 1 subjects and 500 deaths in stage 2 subjects. The full correction methods areused, with the exception of stopping for futility. The standard error for estimated type-I error rates is approximately 0.003 basedon the normal approximation to the binomial.



1 through to decision rule 3 the likelihood of stopping for futilityincreases. This illustrates how the choice of decision rule iscritical and how simulation can aid in the design process.

Table V examines our procedure’s operating characteristicsfor various alternative hypotheses in a trial with the samesample size as in Table IV. Criteria HRFo 0:9 and HRSo 0:7 areapplied for continuing in stage 2 with the full population andthe subgroup respectively, as in decision rule 1 of Table IV.The simulations demonstrate that correct conclusions arereached sufficiently often in the various scenarios. As one wouldexpect, the relative size of the subgroup has a bearing on theoutcomes.

In scenario 1, where all null hypotheses hold, the Type-I erroris maintained below 2.5%, at around 1%. The decrease relativeto the Type-I error rates seen in Table III is due to stopping forfutility on 70–80% of occasions, so the trial would not continuewith the costly second phase too frequently. Making stage 1larger while retaining the same criteria for HRF and HRS wouldincrease this probability of stopping still further.

In scenario 2, where there is a difference in survival in thesubgroup only, the relative size of the group has a clear impact.

As the size of the subgroup increases, this increases the overalltreatment effect and so increases the rate of rejection of HF

0 aswell as HS

0. Rates of stopping for futility or continuing in thesubgroup only also drop as a larger proportion of patientsbenefit. In order to have a chance of finding a treatment effectin S only, there must be a large survival difference compared toF and a reasonably small subgroup. For larger subgroups,efficacy is likely to be demonstrated in both S and F, as a higherproportion of patients benefit from the treatment.

In scenario 3, where all subgroup and non-subgroup patientsshow a difference in survival between the experimentaltreatment and control, there is a high power to reject HFS

0 . Theeffect in F is reliably detected, while it is rare for only HS

0 to berejected without also rejecting HF

0. When the trial does continueto a second stage it is in F alone on around half of theseoccasions, although when the co-primary option is taken HS

0 isalso generally rejected unless the subgroup is small. The resultsin scenario 4 are similar to those in scenario 3, with a moderatetreatment effect for the non-subgroup patients, but a largereffect in the subgroup patients. Although there is little chanceof rejecting HS

0 in the subgroup only, in contrast to scenario 3 35

3

Table IV. Expected proportions of trial outcomes for three decision rules.Three rules based on estimated hazard ratios for PFS were applied at the end of the first stage:Decision rule 1: Continue in the full population if HRFo 0:9 and continue in the subgroup if HRSo 0:7; if both apply continuewith co-primary populations; if neither apply stop for futility.Decision rule 2: Continue in the full population if HRFo 0:8 and continue in the subgroup if HRSo 0:8; if both apply continuewith co-primary populations; if neither apply stop for futility.

Decision rule 3: Continue in only the full population if HRFo 0:8 and continue in the subgroup if HRSo 0:6; if both applycontinue with co-primary populations; if neither apply stop for futility.

Stop forfutility

Continued in co-primary population Continued in F Continued in S Totalpower

Don’t rejectany H0

Don’t rejectany H0

RejectHF

0& HS0

Reject HF0

onlyReject HS

0

onlyDon’treject H0

Reject HF0

onlyDon’treject H0

Reject HS0

onlyRejecteither H0

Decision rule 1Case 1) Hazard ratios: HRSc = 0.8, HRS = 0.6, for both PFS and OS5.5% 0.9% 64.6% 2.8% 0.5% 0.7% 22.2% 0.1% 2.8% 92.9%Case 2) Hazard ratios: HRSc = 0.9, HRS = 0.5, for both PFS and OS

10.5% 0.3% 59.4% 0.3% 4.5% 0.7% 10.6% 0.0% 13.8% 88.5%

Decision rule 2Case 1) Hazard ratios: HRSc = 0.8, HRS = 0.6, for both PFS and OS10.2% 0.4% 58.4% 3.3% 0.4% 0.1% 5.9% 0.1% 21.3% 89.2%Case 2) Hazard ratios: HRSc = 0.9, HRS = 0.5, for both PFS and OS

11.2% 0.2% 46.9% 0.2% 2.6% 0.1% 2.9% 0.0% 35.9% 88.4%

Decision rule 3Case 1) Hazard ratios: HRSc = 0.8, HRS = 0.6, for both PFS and OS25.1% 0.4% 37.0% 2.2% 0.5% 0.6% 24.0% 0.1% 10.1% 73.8%Case 2) Hazard ratios: HRSc = 0.9, HRS = 0.5, for both PFS and OS23.8% 0.1% 39.6% 0.1% 1.8% 1.0% 9.1% 0.0% 24.4% 75.1%

The table shows the proportion of simulations in which each continuation decision and final conclusion were reached. These areestimates of overall, rather than conditional, probabilities. Where rows do not sum to 100%, this is due to rounding errors. Eachcase is based upon 3000 simulations of a trial with a subgroup of one-fourth of the total population, 300 subjects recruited instage 1, 800 in stage 2 in the full and co-primary cases, and 400 in the subgroup only case. The interim analysis occurs after 200progressions. The final analysis occurs after 250 deaths in stage 1, 500 deaths in stage 2 for the full or co-primary cases, and 250deaths in stage 2 for the subgroup only case. The median PFS is 4 months, the median OS is 12 months, and the correlationbetween these is 0.7. Stage 1 recruitment was modelled uniformly over 12 months and stage 2 uniformly over 18 months. Wedenote the hazard ratio in the subgroup by HRS and that in the complement of this group by HRSc.



the most common result is to continue to the co-primary caseand to reject both HS

0 and HF0, and this is the desirable outcome.

The final situation considered is scenario 5, where thetreatment effects on the subgroup and non-subgroup patientsare in opposing directions, with a greater effect on PFS than OS.One would hope in this case to reject HS

0, but HF0 should not be

rejected. Table V shows that, indeed, when the subgroup issmall the trial virtually never continues to test HF

0 in the secondstage and HS

0 is often rejected. As the size of this subgroupincreases, the treatment effect for the full population isenhanced and there is a tendency to continue to stage 2 withco-primary populations. As the subgroup increases further, firstHS

0 alone is rejected and then, when this group dominates, bothHS

0 and HF0 are rejected regularly.

It is of interest to draw comparisons with more conventionaldevelopment programs, with a separate phase II and III.Suppose conventionally 250 subjects are observed in phase IIand, on the basis of their PFS and OS outcomes, it is decidedwhether to proceed with phase III. If so, 500 subjects arerecruited to phase III and followed until 331 OS events areobserved. Conditional on proceeding to the phase III trial, thisdesign has 90% power to detect a hazard ratio of 0.7 in the fullpopulation when applying a one-sided test of 2.5% significance.

We can contrast this with our proposed design wheresubgroup and non-subgroup patients benefit similarly fromthe compound, with hazard ratios of 0.7 in both groups. With nofutility stopping, an interim PFS analysis of the 250 stage 1patients could be made after 200 progressions with the eventual3

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Table V. Expected proportions of trial outcomes in various scenarios using decision rule 1.

Subgroupincidence

Stop forfutility

Continued in co-primary population Continued in F Continued in STotal

power

Proportionof patientsin S

Don’treject any

H0 (%)Don’t rejectany H0 (%)

RejectHF

0&HS

0 (%)

Reject HF0

only(%)

RejectHS

0 only(%)

Don’trejectH0 (%)

RejectHF

0 only(%)

Don’trejectH0 (%)

RejectHS

0 only(%)

RejecteitherH0 (%)

Scenario 1) Hazard ratios: HRSc = 1, HRS = 1 for both PFS and OS0.2 70.0 6.3 0.1 0.2 0.3 15.5 0.4 6.9 0.3 1.30.4 75.9 3.8 0.1 0.1 0.1 17.9 0.8 1.3 0.1 1.10.6 75.6 2.7 0.2 0.0 0.1 20.4 0.8 0.3 0.0 1.0

0.8 76.6 1.3 0.2 0.0 0.0 21.0 0.9 0.0 0.0 1.1

Scenario 2) Hazard ratios: HRSc = 1, HRS = 0.6 for both PFS and OS0.2 23.1 7.1 14.3 0.4 18.3 6.5 3.0 0.6 26.7 62.70.4 13.7 0.9 53.3 0.0 9.9 2.4 8.7 0.0 10.9 82.90.6 6.3 0.0 78.0 0.0 0.7 0.3 13.7 0.0 0.9 93.3

0.8 2.2 0.0 81.9 0.0 0.0 0.0 15.9 0.0 0.0 97.8

Scenario 3) Hazard ratios: HRSc = 0.7, HRS = 0.7 for both PFS and OS0.2 3.0 0.1 35.2 15.9 0.0 0.2 45.0 0.1 0.4 96.60.4 3.7 0.1 44.4 4.0 0.0 0.2 47.5 0.0 0.2 96.00.6 3.3 0.2 48.7 0.6 0.0 0.2 46.8 0.0 0.0 96.20.8 4.0 0.0 49.0 0.2 0.0 0.4 46.5 0.0 0.0 95.6

Scenario 4) Hazard ratios: HRSc = 0.7, HRS = 0.5 for PFS, HRSc = 0.8, HRS = 0.6 for OS,

0.2 0.7 1.9 72.8 7.6 1.1 1.0 14.5 0.0 0.5 96.40.4 0.3 0.3 91.7 0.6 0.2 0.1 6.7 0.0 0.1 99.30.6 0.1 0.0 96.1 0.0 0.0 0.0 3.8 0.0 0.0 99.90.8 0.0 0.0 98.3 0.0 0.0 0.0 1.7 0.0 0.0 100.0

Scenario 5) Hazard ratios: HRSc = 2, HRS = 0.5 for PFS, HRSc = 1.7, HRS = 0.6 for OS,

0.2 18.3 0.0 0.0 0.0 0.0 0.0 0.0 3.0 78.7 78.70.4 9.1 0.2 0.0 0.0 3.7 0.0 0.0 0.6 86.4 90.10.6 4.5 0.0 21.0 0.0 40.7 0.0 0.0 0.0 33.8 95.50.8 0.7 0.0 97.1 0.0 0.9 0.0 1.0 0.0 0.2 99.3

The table shows the proportion of simulations in which each continuation decision and final conclusion were reached. These areestimates of overall, rather than conditional, probabilities. Each row of results is based upon 3000 simulations of a trial with asubgroup of one fourth of the total population, 300 subjects recruited in stage 1, 800 in stage 2 in the full and co-primary casesand 400 in the subgroup only case. The interim analysis occurs after 200 progressions. The final analysis occurs after 250 deaths instage 1, 500 deaths in stage 2 for the full or co-primary cases and 250 deaths in stage 2 for the subgroup only case. The medianPFS is 4 months, the median OS is 12 months and the correlation between these is 0.7. Decision rule 1 from table 4 is used withcriteria HRFo 0:9 and HRSo 0:7 for continuing with the full population and the subgroup. Stage 1 recruitment was modelleduniformly over 12 months and stage 2 uniformly over 18 months. We denote the hazard ratio in the subgroup by HRS and that inthe complement of this group by HRSc.



survival analysis occurring after 227 deaths if the trial continuedinto stage 2. This stage 2 would be similar to the conventionalphase III trial, with 500 subjects and a survival analysis after 331events. This design has 97% power of rejecting at least one nullhypothesis; (55% of the time we reject HF

0 and HS0 and 42% of the

time we reject HF0 only). Therefore the re-use of the stage 1

patients in the OS analysis has increased the power, which inboth cases is stated conditionally on proceeding to stage 2.

If we had run a similar population selection process in stage 1,but only used the stage 2 survival events in the final analysis, soa more analogous approach to separate phase II and III trials,then the program would have had just 85% power; (35% of thistime we reject HF

0 and HS0 and 50% of the time reject HF

0 only).The drop in power from 90% is due in part to conservatism inthe multiple testing procedure, but the overall loss of powerdemonstrates the benefit of utilizing the stage 1 patients. In fact,without futility stopping, a sample size of 400 events for ourproposed design (for example, split 175 and 225 between stages1 and 2) would be sufficient to give 90% power of detecting ahazard ratio of 0.7 in our proposed new design, using a one-sided test of 2.5% significance.

If futility stopping is introduced, then the unconditionalpower of each development program across phases II and III canbe compared. In this study, identical decision rules, with hazardratio boundaries for PFS at 0.9 for F and 0.75 for S, could beintroduced to both our proposed design and to the end ofphase II decision in the conventional case. We now find that theunconditional power drops to 95% for our proposed design butto 84% for the conventional program.

However, the adaptive design’s main potential benefits arethe savings in time and money that will be achieved in othersituations where there is a substantial subgroup difference. Theoverall number of subjects used in the development programcould well be lower under an adaptive approach as the need fora prior phase II trial or concurrent subpopulation trial isremoved.

7. DISCUSSION

The statistical methodology for adaptive seamless phase II/IIIdesigns allows one to conduct efficient trials that cansimultaneously investigate several vital questions for drugdevelopment, including the identification of the most beneficialsubgroup for a new treatment. We have extended the previouswork on the subject to show how the trial design can bemodified to suit the particular needs of oncology studies. Wehave developed the flexible use of a co-primary populationbased on intermediate time-to-event endpoints and havedemonstrated that these modifications do not inflate Type-Ierror. The most important aspect of these designs is that theyperform capably in realistic situations, as confirmed by thesimulations in Table V. Such simulations help to identifysituations where the design is most suitable, for example wherethe difference in treatment effects between the subgroup andnon-subgroup subjects is considerable and where this groupaccounts for a relatively small proportion of the total population.

Any novel adaptive design for subgroup selection, for exampleFreidlin and Simon’s alternative designs [8,20], must address thesevital issues of the control of Type-I error and the exclusion of bias.The ‘adaptive signature design’ [8] uses an exploratory phase toidentify molecular classifiers and hence stage 1 data cannot beused in the primary analysis of the subgroup hypothesis. Our

design is applicable when a possible predictive biomarker isalready identified and this allows it to incorporate data from bothstages in the primary hypothesis test. Hung et al. [21] are critical ofthe combination of an exploratory stage based on surrogateendpoints with a confirmatory stage, but in our design allhypotheses are fixed and pre-defined and so in the first stage welearn about proposed hypotheses rather than generate them.Our planned use of multiple endpoints is in contrast to a mid-trialadaptation that would change the hypotheses under investiga-tion, as has been discussed by Jennison and Turnbull [11] andHung et al. [22].

Adaptive designs have the potential to make drug develop-ment more efficient, although this can be at a price of increasedcomplexity, logistical challenges for drug supply and otheroperational issues. The large amount of intensive planning thatmust be undertaken to define go/no-go criteria is likely to delaythe start of the trial. The sponsor must also have identified thenecessary resources should the trial continue to the completionof the phase III portion. Should the trial terminate at the interimanalysis then there is likely to have been a larger investmentcompared with a conventional phase II study. This is due to theadvance recruitment of some of the phase III subjects and theearlier phasing of costs required for commercial formulationdevelopment and manufacture.

One of the first questions that should be addressed whenconsidering a seamless phase II/III design is the need for short-term responses of stage 1 patients to be observed, validatedand analyzed quickly in comparison with the recruitment ratefor stage 2 so that a timely decision can be made before largephase III costs begin to be accrued. Unless a rapid endpoint isavailable, this may preclude the use of the design.

An important consideration is whether the sponsor shouldremain blind to the stage 1 results. Some authors argue this maybe achieved by a firewall [23], although it is a generally acceptedprinciple that access to interim analyses from pivotal trialsshould be restricted to the Independent Data MonitoringCommittee. We believe that if the sponsor pre-defines and fullydescribes the criteria to be applied at the end of phase II, then itshould be possible to remain blind to accumulating results.Passing the threshold for continuation to phase III implies thedata are promising, but the sponsor has no need to know justhow good they are.

Our proposed design should only be applied if there is ana priori hypothesis about increased efficacy in a defined sub-population of patients. Further, this subgroup must be wellcharacterized, e.g. by a biomarker, and any quantitative thresh-olds classifying membership of the subgroup must be fully pre-specified. This definition must be made prior to the phase IIanalysis, and would ideally be specified prior to the trialcommencing. In addition, a reliable and reproducible assaymust have been developed in order to avoid any dilution ofthe benefits of the design. Any additional knowledge on theproportion of subjects who belong to the subgroup and therelative effects expected in each population could further aid inthe planning of the trial through simulations such as thosereported in this paper.

This approach could easily be applied in other therapy areasand to endpoints other than time-to-event. The closure principleand multiplicity correction procedures extend to larger numbersof subgroups and so it is feasible to study more than the singlesubgroup that was investigated in this study. However, if morethan one group were taken forward to the second stage or if 3

55



there were complicated relationships and interdependenciesbetween groups then this would introduce further levels ofcomplexity. The inclusion of new hypotheses after the interimanalysis, in this case corresponding to new subgroups, was alsoraised as an extension to seamless designs by Hommel [24].These are topics for possible future investigation.

Exact bivariate methods [13] could also be investigated toreplace the multiplicity correction methods for deriving p-valuesfor the intersection hypothesis HFS

0 of no treatment effect on OSin either the full population or the subgroup. The Hochbergprocedure can introduce some slight conservatism by nottaking account of the correlation between the populationsbeing tested under each hypothesis, although this could beaccounted for by using Dunnett’s method [13]. Further,the formula presented to calculate an adjusted p-value fromthe Hochberg method could be adapted to incorporate anuneven split of the Type-I error probability. Posch et al. [25]consider various combination tests and multiplicity correctionprocedures, as well as introducing confidence intervals.The Hochberg procedure was shown to perform well whencompared with ‘splitting the alpha’ type methods [9].

8. CONCLUSIONS

We have shown how practical design aspects for oncologytrials can be applied to allow adaptive seamless methods to beused in a subpopulation selection problem. Novel features suchas the co-primary population, the use of an intermediateendpoint for earlier decision-making, clearly defined decisionrules and the recruitment of larger numbers of subgrouppatients, if required, have been added. Simulations show that, inagreement with theory, these modifications have not inflatedthe Type-I error rate and that the design performs well in termsof the final conclusions that would be reached in varioussituations.

If a pre-defined hypothesis for a predictive biomarker exists,this approach could enable effective medicines to be madeavailable more rapidly to the most appropriate patientpopulation.

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