Improved efficiency for cross-arm comparisons via platform designs

Summary

Though platform trials have been touted for their flexibility and streamlined use of trial resources, their statistical efficiency is not well understood. We fill this gap by establishing their greater efficiency for comparing the relative efficacy of multiple interventions over using several separate, 2-arm trials, where the relative efficacy of an arbitrary pair of interventions is evaluated by contrasting their relative risks as compared to control. In theoretical and numerical studies, we demonstrate that the inference of such a contrast using data from a platform trial enjoys identical or better precision than using data from separate trials, even when the former enrolls substantially fewer participants. This benefit is attributed to the sharing of controls among interventions under contemporaneous randomization. We further provide a novel procedure for establishing the noninferiority of a given intervention relative to the most efficacious of the other interventions under evaluation, where this procedure is adaptive in the sense that it need not be a priori known which of these other interventions is most efficacious. Our numerical studies show that this testing procedure can attain substantially better power when the data arise from a platform trial rather than multiple separate trials. Our results are illustrated using data from two monoclonal antibody trials for the prevention of HIV.

1. Introduction

This work is motivated by the World Health Organization (WHO) Solidarity Trials for coronavirus disease 2019 (COVID-19) vaccines (Krause and others, 2020) and treatments (WHO Solidarity Trial Consortium, 2021), which seek to concurrently evaluate multiple candidate vaccines and treatments to contain the burden and spread of COVID-19. To achieve this aim, the investigators are using a platform design (Sridhara and others, 2015; Saville and Berry, 2016; Woodcock and LaVange, 2017), sometimes also known as a multiarm multistage design (Royston and others, 2003; Parmar and others, 2017). Such designs enable a simultaneous evaluation of several public health interventions within a single trial. In contrast to more traditional multiarm designs, platform trials allow for the evaluation of candidate interventions that may be available at different times and various international sites. Having this flexibility increases the chances of generating reliable evidence to determine which interventions work effectively. Owing to these advantages, platform designs have recently been advocated to evaluate candidate interventions for the treatment or prevention of COVID-19 (Dean and others, 2020), HIV (Choko and others, 2017), and cancer (Meyer and others, 2020).

Platform trials make more efficient use of resources than separate, independently conducted trials by reducing the number of participants enrolled on the control arm (Woodcock and LaVange, 2017). Consequently, trial resources can be redistributed to enroll participants in the active intervention arms. For sponsors, this redistribution has the benefit of potentially decreasing the total required sample size, while, for participants, it has the appeal of increasing the chance that they will receive an experimental intervention that they could not receive outside of the trial. Moreover, by using centralized governance, platform trials amortize the cost of establishing study sites across multiple active interventions and can ensure common eligibility criteria and study procedures across all intervention-control comparisons. In addition, as each candidate’s active intervention is monitored for early evidence of benefit or harm, employing a platform design makes it possible to target trial resources to the study of active interventions that are more likely to be successful (Saville and Berry, 2016).

Methods for analyzing platform trial data should be able to accommodate key features of the design, including that candidate active interventions can be added to the trial once they become available, and those that show a lack of efficacy can be eliminated. To this end, several authors have advocated that, for each active intervention, controls that are under contemporaneous randomization should be used as comparators (Lee and Wason, 2020; Kopp-Schneider and others, 2020; Lee and others, 2021). Methods that restrict to contemporaneous comparisons can avoid estimation bias and anticonservative confidence interval coverage that may arise due to a potential temporal trend in the outcome or baseline characteristics of the control arm. Moreover, during periods when multiple active interventions are under randomization simultaneously, the contemporaneous control comparators may be shared between these various arms.

Analysis methods should also be able to accommodate the fact that, once an active intervention has been found to be efficacious, it may serve as an active control in the evaluation of the other candidate interventions (Woodcock and LaVange, 2017; Kaizer and others, 2018). One approach to make this evaluation would involve directly comparing the outcomes of a candidate’s active intervention to those on the active control. Unfortunately, this approach would be susceptible to the same temporal-trend-induced biases as described above. A less direct, but more robust, the method involves comparing the two interventions by contrasting their efficacies relative to their respective contemporaneous control arms. This method relies on a constancy assumption that, conditional on baseline covariates, the efficacy of an active intervention is the same across enrollment windows. Under this constancy condition that underlies the validity of many methodologies developed for noninferiority trials (Everson-Stewart and Emerson, 2010), this strategy will yield unbiased comparisons of the efficacies of the two interventions.

Though standard analyses can be used to evaluate the efficacy of each active intervention compared to its contemporaneous control, more care is needed to quantify uncertainty when contrasting the efficacies of various active interventions. The main challenge is that the overlap in the contemporaneous control groups for different interventions induces a positive correlation between their corresponding efficacy estimates. This positive correlation has been used as a means to justify not doing multiplicity adjustments in multiarm trials (Howard and others, 2018). In particular, the positive correlation induces a reduction in the family-wise error rate compared to independent separate trials, suggesting that multiplicity adjustment should not be required solely due to sharing control data. Since multiple testing corrections would not have been employed had separate trials been conducted, platform trials (WHO Solidarity Trial Consortium, 2021; Howard and others, 2021) have often followed multiarmed trials (Freidlin and others, 2008) in not including them. In this work, we follow this precedent and do not consider multiple testing in the platform trial setting. In another line of research, recent works have provided Bayesian strategies to describe and accommodate this positive correlation in platform trials when the outcomes are binary (Saville and Berry, 2016; Hobbs and others, 2018; Kaizer and others, 2018). To the best of our knowledge, there is no available frequentist method that properly addresses this issue, nor is there any approach that is applicable when the outcomes may be right censored. In this work, we introduce a theoretically grounded framework to account for this correlation when making cross-intervention comparisons with time-to-event outcomes based on platform trial data.

Our contributions are as follows:

• 1) In Section 3, we establish the joint asymptotic normality of intervention-specific conditional relative risk estimators. The limiting covariance matrix quantifies the positive correlation induced from sharing control participants between the active interventions.

• 2) In Section 4, we show that natural estimators of the relative efficacy of two interventions are statistically more efficient when applied to platform trial data rather than on data from separate, intervention-specific trials. This enables a substantial reduction in the sample size of the platform trials relative to that of the pooled separate trials, without sacrificing precision for evaluating efficacy.

• 3) In Section 5, we develop a noninferiority test that evaluates the efficacy of a given intervention relative to the most efficacious of the remaining interventions. This test is adaptive in the sense that there is no need to know, in advance, which of the remaining interventions should serve as the benchmark.

As is evident from the above, in this work, our focus is on the specification and efficiency of analysis methods for platform trials, rather than on design elements such as determining when to remove interventions from randomization due to an apparent lack of efficacy.

The randomization scheme, data structure, and assumptions that shape the framework of our proposed methods are introduced in Section 2. Numerical studies that support our theoretical findings are presented in Section 6, and an illustration of the proposed methods on data from the Antibody Mediated Prevention (AMP) trials (Corey and others, 2021) can be found in Section 7. Section 8 concludes.

2. Preliminaries

2.1. Randomization scheme

We consider platform designs in which the availability of active interventions may vary over discrete windows defined by time and location. Within each location, windows are contiguous and may be of unequal widths: a window starts when an active intervention is placed under or removed from randomization and ends when the next window begins. To simplify the presentation, we focus on a particular randomization scheme where, within each window, equal numbers of participants are expected to be enrolled in each available active intervention arm and to the control arm. More concretely, within an arbitrary window in which active interventions are under simple randomization, each active intervention is assigned with probability , and control is also assigned with probability . In settings where the different active interventions require different administration schedules or modalities, blinding may be maintained via the use of matched controls. To do this, -matched total control arms are used, where each matched control is designed to be as indistinguishable as possible from a particular active intervention. Each active intervention is assigned with probability and each matched control is assigned with probability , where all of these random assignments are made independently of participant covariates. The control arm is then taken to be the union of the -matched control arms. Matched controls were used in the WHO Solidarity Trial Vaccines (World Health Organization, 2020).

An example of this randomization scheme is illustrated in Table 1, which represents a modification of a figure from the protocol for the WHO Solidarity Trial Vaccines. Three candidate active interventions are considered in this example, labeled as , , and , and corresponding matched controls are under concurrent randomization. Intervention and its matched control are under randomization in Windows 1–3 and 5; intervention and its matched control are under randomization in Windows 2–4; and intervention and its matched control are under randomization in Windows 3–5. As the availability of active interventions may vary across enrollment windows, especially when windows represent geographic locations, it is possible for active interventions such as to go under randomization in nonconsecutive windows. For instance, some COVID-19 vaccines may not be administered in certain countries or at certain time points due to supply chain constraints. When assessing the efficacy of a given active intervention, the control group used for comparison consists of all participants who were enrolled in a matched or unmatched control arm during a period in which the active intervention was under randomization. This union of the matched and unmatched controls is referred to as the shared control arm. For example, for intervention , the shared control arm consists of for Window 2, for Window 3, and for Window 4.

Table 1.

Allocation ratios of each active intervention versus its matched control and versus shared control in a platform trial. Within each window, each arm label and , , denotes an equal number of participants who are expected to enroll in the trial during that window and be randomized to the corresponding arm. However, the arm labels may denote different numbers of participants across different windows. For example, in Window 1, each arm label might denote 500 participants so that a total of 500 participants would be expected to be enrolled and randomized to each of  and , whereas in Window 2 each arm label might denote 100 participants, so that a total of 200 participants would be expected enrolled and randomized to and 100 to 

2.2. Data structure, assumptions, and estimands

We now describe the variables that are measured for each participant in the considered platform trial. The window in which a participant enrolls is denoted by and their baseline covariates are denoted by . We suppose that these covariates are discrete with finite support—it is possible that arises by combining multiple discrete covariates or by discretizing one or more continuous covariates into categorial subgroups. The randomization arm is indicated via a categorical variable , which takes the value for control and the value for intervention . To ease presentation, hereafter, we denote the active interventions by , , etc., rather than by , , etc., as was done in Table 1. The observed time is defined as the minimum of a continuous event time (e.g., time to virologically confirmed symptomatic COVID-19 infection) and a censoring time , and is a corresponding indicator of having observed the event. Enrollment is treated as time zero, so that indicates that the participant experienced the event exactly at the time of enrollment. Uncensored binary outcomes emerge as a special case of this right-censoring setup by setting equal to the indicator that the binary outcome was observed to be equal to 1 and equal to 1 so that all outcomes are treated as uncensored. Interventions and windows are labeled sequentially so that the first active intervention (window) is labeled “intervention (window) 1,” the second is labeled “intervention (window) 2,” and so on. We use to denote the total number of active interventions, to denote the set of all active interventions, and to denote the number of windows over the course of the trial. For an active intervention , we let denote the set containing the windows in which intervention is under randomization. We observe independent and identically distributed (iid) copies , , drawn from a distribution .

We will make use of the following condition, which often holds in randomized trial settings:

• (C1) Randomized arm assignment: The baseline covariate is independent of conditional on .

We will also make use of a constancy condition that the efficacy of an active intervention, defined in terms of a relative risk, should be stable across windows within specified strata. These strata are defined via the value of a coarsening of . More concretely, for a known, possibly many-to-one, function ; we similarly let . By taking to be the identity or a constant function, we could make correspond to the original baseline covariate or a degenerate random variable, respectively. Alternatively, if results from a combination of several discrete covariates (such as age group and sex), then could be chosen as a coordinate projection that returns a particular one of those covariates (such as age group). Henceforth, we will take to be a generic realization of corresponding to a generic realization of , that is, .

As the event rate may vary across windows, so does the survival function conditionally on being randomized to intervention , enrolled in window , and belonging to the stratum . The corresponding conditional relative risk is

(2.1)

To avoid dividing by zero or considering degenerate cases where it is all but obvious that an intervention is efficacious or not, we suppose throughout that for all possible values of , namely when is control or any active intervention. In the context of vaccine trials, the vaccine efficacy is often defined as one minus the relative risk. The constancy condition at a specified time can be stated as follows.

• (C2) Constancy condition at time : For each active intervention and stratum , there exists a such that, for all windows for which , .

The above condition states that the conditional relative risks of the active interventions are invariant across windows and is plausible in many settings, for example, in vaccine trials (e.g., Fleming and others, 2021; Tsiatis and Davidian, 2021). When windows encode spatial information, this condition requires generalizability over space—the efficacy of an active intervention is the same across different locations where it is under randomization. In fact, the plausibility of this condition has been systematically evaluated across many disease areas, due to its importance to noninferiority analyses (D’Agostino and others, 2003; Fleming, 2008; Mauri and D’Agostino, 2017; Zhang and others, 2019; May and others, 2020). In Figure S1 of Appendix F of the Supplementary material available at Biostatistics online, we provide an illustration of the implications of C2 in a particular example. The above is distinct from proportional hazards assumptions that are often employed in analyses based on the Cox model. Indeed, unlike proportional hazards assumptions that require a constant hazard ratio between an intervention and the control, C2 allows for the efficacy of each active intervention, quantified in terms of relative risk, to vary over time since enrollment. This flexibility is important, for example, in vaccine studies, where vaccine efficacy is often low shortly after inoculation, ramps as the immune response builds and booster shots are administered, and subsequently wanes over time. The results in this work do not rely on a proportional hazards assumption.

Under C2 at time , the relative risk estimand further writes as

(2.2)

where the first equality simply multiplies the left-hand side by one, the second holds by C2, and the third holds by the law of total expectation. We require that for all and of interest, which guarantees that each considered relative risk estimand is well-defined. In this work, we will have three primary interests regarding the relative risk estimands defined above: (i) estimating the relative risk for one or more given interventions and strata of , (ii) contrasting and for two interventions and , and (iii) in a noninferiority analysis, contrasting against .

The constancy condition C2 only applies to active interventions , covariate strata , and windows for which . This requirement is natural given that, when it fails, the conditional relative risk in (2.1) is not even well-defined. Indeed, if individuals from covariate stratum are never enrolled in window —say, because individuals from this stratum do not live near the location to which window pertains—then it is not even clear how to define the relative risk of an intervention among those individuals in stratum who enroll in window . Even if we restrict attention to windows in which covariate stratum is enrolled with positive probability, a given intervention will likely not be under randomization in some of these windows, rendering the conditional relative risk in (2.1) ill-defined. To define the effect of intervention in such windows, counterfactual reasoning can be applied (e.g., Hernán and Robins, 2020). For each participant, this involves conceptualizing a counterfactual event time that would have occurred if, possibly contrary to fact, intervention had been under randomization at their time of enrollment and they had been randomized to that intervention. Under standard causal assumptions (pp. 5–6 of Hernán and Robins, 2020), the counterfactual relative risk is equal to the relative risk in (2.1) whenever that quantity is well-defined, that is, whenever . Hence, under the natural counterfactual extension of the constancy condition that says that for all that are such that , the relative risk estimand of interest can be interpreted as defining the effect of intervention in all windows in which participants with are under enrollment, rather than just in those windows in which participants with are under enrollment and is under randomization. We leave further consideration of this counterfactual constancy condition to future work, and instead focus in the remainder on making inference about the quantity defined in C2, which is well-defined even in the absence of causal assumptions.

Though the relative risk of interest does not depend on the full collection of baseline covariates , the conditionally independent censoring condition C3 below generally makes it necessary to make use of when estimating the relative risk, where is used to denote (conditional) independence:

• (C3) Conditionally independent censoring: For each active intervention and covariate stratum with , it holds that and .

This condition will often be more plausible than the usual independent censoring assumption made in clinical trial analyses, which states that is independent of conditionally on . Indeed, the random variable can contain baseline factors that are predictive of both the event and censoring times. For example, in an infectious disease outbreak setting, these factors may include behavioral risk information and the calendar time of enrollment. The key insight is that, under C3, the conditional survival function is identifiable as a functional of the distribution of the observed data. Consequently, to estimate , it suffices to write this quantity as a function of this conditional survival function and the distribution of . Lemma B.1 of the Supplementary material available at Biostatistics online shows that this is indeed possible. In particular, under the randomization of arm assignment C1, the numerator and denominator on the right-hand side of (2.2) can be rewritten to show that

(2.3)

Even if C2 were to fail to hold, can be defined as above (see Appendix G of the Supplementary material available at Biostatistics online). In this case, represents a particular summary of the efficacy of intervention across windows. Nevertheless, C2 is advantageous since, when it holds, contrasts of the relative risks of different interventions can be interpreted as being independent of the particular windows under consideration. In Section 3.1, we will present so-called plug-in estimators that estimate each survival function and conditional probability above, and then insert them into the right-hand side of (2.3) to estimate the relative risk of interest.

We conclude by introducing some other notation that will appear throughout in this article. We denote a -variate column vector by and a set by . Let . We also let denote the collection of windows where the control is under randomization—by design, . Moreover, let be the end of follow-up relative to enrollment, denote the range of possible observed times, denote the set of all arms, and and be the support of and , respectively. We will write to denote the expectation operator under . We write to denote a generic realization of .

3. Inference and asymptotic properties

3.1. Estimated conditional relative risk

Our estimators of the conditional survival function in (2.3) will be based on the identity , where denotes the cumulative hazard function (CHF) at time conditional on a randomization arm , enrollment windows belonging to a specified window set , and a baseline covariate stratum such that . Specifically, this function is defined as , which we refer to as the conditional CHF.

Though we will be most interested in estimating and for one or more given interventions , it will simplify presentation to define an estimator of for a generic arm , set of windows , and covariate stratum for which . We will estimate this conditional CHF using the conditional Nelson–Aalen estimator. To introduce this estimator, we define the stratified basic counting process in the stratum and the average size of the risk set at time as and , respectively. The conditional Nelson–Aalen estimator at time is given by , and the conditional survival function can be estimated by . For and , let be estimated by . Inserting these estimators into (2.3) naturally suggests a plug-in estimator of , namely .

3.2. Asymptotic normality

To study the large-sample behavior of our proposed estimator of , it will be helpful to have characterized the joint asymptotic behavior of the estimators of the conditional survival functions and across different interventions . This characterization is simplified by the fact that participants on different randomization arms are mutually exclusive—as a consequence of this fact, is independent of for every intervention and of for every intervention arm . The joint distribution of the conditional survival functions for the shared control arms within window sets in is more involved. Owing to the control-sharing between interventions and , is not independent of unless and are never under contemporaneous randomization—that is, unless . Except in degenerate cases, the dependence is otherwise inevitable due to the mutual inclusion of participants who are under contemporaneous randomization in the estimation of and . To characterize this dependence, we derive the asymptotic behavior of the estimated stratified control-arm survival functions across all the intervention-specific window sets, namely —see Lemma B.4 of the Supplementary material available at Biostatistics online for details. In the same lemma, we also establish the asymptotic normality of the estimated stratified intervention-arm survival functions across their designated window sets, .

To derive the aforementioned distributional results, we establish that the estimators of the conditional survival functions are asymptotically linear. We recall that an estimator of an estimand is called asymptotically linear if there exists a mean-zero, finite-variance function such that , where we write to denote a term that converges to zero in probability as even once divided by . The function is known as the influence function of . The joint limiting distribution of several asymptotically linear estimators can be derived using Slutsky’s lemma and the central limit theorem: indeed, letting denote the influence functions of , we have that , where . A delta method is also available for asymptotically linear estimators, which makes it possible to compute the influence function of a real-valued function of one or more asymptotically linear estimators via the dot product of the gradient of the function and the influence functions of .

We use such a delta-method argument to translate the asymptotic linearity of , , and over into an asymptotic linearity result for the estimator of the log-relative risk . In particular, the following theorem shows that is an asymptotically linear with influence function , where the form of is given in Appendix B.1 of the Supplementary material available at Biostatistics online. As the proof is an immediate consequence of Lemmas B.2–B.5 of the Supplementary material available at Biostatistics online, it is omitted.

Theorem 3.1

Given C1–C3, the stratum and with defined in (B.4),

(3.4)

4. Efficiency gains from sharing controls

4.1. Motivation

In this section, we will demonstrate the statistical efficiency that can be gained from running a platform trial with a shared control arm as opposed to using separate control arms, as is done in more traditional clinical trial designs. Two forms of gains can be realized by using a platform design.

The first follows immediately from the design’s use of a shared control arm. In particular, a platform trial conducted contemporaneously with and in the same population as separate, intervention-specific trials will generally attain the same statistical power for marginal evaluation of each active intervention as can the separate trials, while enrolling fewer participants on control. Indeed, due to the use of a shared control arm, fewer total participants can be enrolled in a platform trial than in separate, intervention-specific trials, while still maintaining the same sample sizes for the comparison of each active intervention versus control. This point is illustrated in Table 2, which compares a 3-arm platform trial to two separate 2-arm trials. The 3-arm platform trial in that table corresponds to the same setting as was illustrated in Table 1, except for being limited to only two interventions and using to label the shared control arm. The corresponding separate trials enroll the same number of individuals to each active intervention in the same windows but enroll twice as many controls in windows where both active interventions are under randomization.

Table 2.

Randomization schemes and the expected enrollment size per active intervention arm in each window under an illustrative 3-arm platform trial versus two 2-arm separate trials, where the expected enrollment size per arm in Window is denoted by , , for both trials

The second advantage enjoyed by platform designs, which is a key finding of this work, involves a gain in efficiency for comparisons of the efficacy of different active interventions. Such comparisons are useful, for example, when aiming to evaluate the noninferiority of one intervention relative to another. Before providing theoretical insights as to the reasons for and generality of this gain, we present a simple numerical example illustrating how significant it can be in practice. To do this, we provide simulation results in a simple, binary outcome setting in which no covariates are measured. This setting can be seen to be a special case of the more general right-censored setup studied in this article by letting , with denoting the end of follow-up, taking the covariate to be a degenerate random variable that only takes the value 0, and taking the function used to define to be the identity function. Since is trivial and there is only one-time point of interest, we write , rather than , to denote the relative risk of in this example. We compare the statistical power for various hypothesis tests based on data from 3-arm platform trials versus two separate 2-arm trials.

• (a) a standard 3-arm platform trial with a single window in which both active interventions are under randomization and the sample size is selected to achieve 90 power for marginal tests of via 0.025-level Wald tests at the design alternative of , ,

• (b) two separate 2-arm trials with sample sizes similarly selected for 90 power, and

• (c) an expanded 3-arm platform trial that contains a single randomization window as (a) does, but whose total sample size (controls and active interventions combined) is equal to the sum of the total sample sizes of the two separate trials in (b).

For settings (a) and (b), we select the sample sizes of each arm to ensure power to marginally detect via 0.025-level Wald tests at the design alternative of , . The power calculations used to determine sample sizes for (a) and (b) result in 1750 participants enrolled to each active intervention and 1750 participants enrolled to each control arm, namely the shared control in (a) and each separate control arm in (b). With marginal significance levels of 0.025, the null hypotheses to be tested are , , and , where Wald tests are used in all settings. In Table 3, we present the power of rejecting these null hypotheses, along with the enrollment sizes of intervention and control arms in each data set. Consistent with the earlier discussion regarding the equal power for marginal tests obtained by platform designs and separate trial designs that enroll the same number of participants to each active intervention, the platform trial (a) and the separate trial (b) achieve the same power for the tests of and . As the increasing sample size increases power, it also follows naturally that the expanded platform trial (c) attains higher power than (a), and therefore (b) as well, for these marginal tests. It is perhaps more surprising that both platform trials considered attain considerably higher power (19–28 on an absolute scale) for testing than do the separate trials in (b). This is true for (a) in spite of the fact that fewer total participants are enrolled in that trial than in the combined separate trials. In the remainder of this section, we provide analytical arguments establishing the generality of this improvement in power that platform designs enjoy for comparisons of the efficacies of different active interventions. When giving these arguments, we consider the general case where the outcome may be right-censored, covariates may be conditioned upon or adjusted for, and several interventions may be under randomization in any given window.

Table 3.

Power of various tests under (a) a standard 3-arm platform trial with a single window in which powered at 90for tests of the marginal nulls, (b) two 2-arm separate trials with sample sizes similarly selected for 90power, and (c) an expanded 3-arm platform trial with a single randomization window as in trial (a), but whose total sample size (controls and interventions combined) is equal to the sum of the total sample sizes of the two separate trials in (b). The total sample size reflects the total number of participants enrolled in the platform trial or across the two separate trials. The arm-specific sample sizes listed reflect the expected number of participants to be on control (shared control for the platform trial, sum of the two control arms for the two separate trials) or active interventions (total participants on interventions 1 and 2)

	Sample size				Null
	Total	Controls	Interventions
(a) Platform	5250	1750	3500		0.99	0.90	0.69
(b) Separate	7000	3500	3500		0.99	0.90	0.50
(c) Expanded platform	7000	2333	4667		1.00	0.95	0.78

4.2. Theoretical guarantees

We consider the case where the goal is to compare the relative risks of two candidate interventions and within a stratum and at a given time point . We allow this comparison to be made based on a differentiable contrast function , and we refer to as the relative efficacy of interventions and . For brevity, we let , where the values of , , , and are treated as fixed for the remainder of this subsection. Our analysis will apply to any contrast function that satisfies the following condition.

• (C4) for all .

The above is satisfied by additive and multiplicative contrasts of the relative risks, namely and . In Appendix C of the Supplementary material available at Biostatistics online, we argue that the above condition is in fact natural whenever is to be used to determine the superiority or noninferiority of relative to .

To quantify the efficiency gains that can be realized by running a platform trial, we compare the widths of confidence intervals for based on data from two settings. In the first, the data arise as iid observations in a platform trial (see Section 2.2). In the second, the pooled data from separate independent trials are used. Specifically, these pooled data take the form , where contains the data from the individual separate trial evaluating active intervention . We suppose that each is an iid sample from some distribution . The data structure observed in each separate trial is similar to that observed in the platform trial, except that no window variables are observed and has support in , where denotes the control arm in the separate trial for intervention . As in the platform trial, the observed time is the minimum of an event time and a censoring time , and . We similarly suppose conditionally independent censoring and randomization, in this case that is independent of given and is independent of . The overall size of this pooled data set is .

In our theoretical analysis, we focus on the case where the platform trial and the separate trials are identical in all regards except for the fact that a shared control arm is used in the platform trial, whereas a different control arm is used in each of the separate trials. We, therefore, wish to ensure that the population enrolled, the efficacy of each intervention, and the distribution of the censoring and event times is similar across the two settings. To formalize this, we impose a condition relating the distribution that gave rise to data in the separate trial for intervention to the conditional distribution of under conditionally on and . Below, we denote this conditional distribution by and use to mean equality in distribution.

• (C5) Platform and separate trials enroll from the same population: For all , , where , and .

Under this condition, the relative risk of intervention as compared to control through time , conditionally on covariate level , is the same in the platform trial and in the separate trials. This condition also implies that the active intervention is assigned with probability in each separate trial.

We also require that the platform trial and separate trials provide similar relative precision for estimating and for any active interventions and . We formalize this notion in terms of the standard errors for nonparametric estimators of these two quantities. In the separate trials, the standard error of the estimator of will be on the order of . In the platform trial, it will be on the order of , where denotes the number of observations that are expected to be used in the evaluation of the relative risk of active intervention . The following condition imposes that, asymptotically, the ratio of the standard errors between interventions and should be the same across the two trials.

• (C6) Platform and separate trials have the same relative precision across interventions: For all , it holds that .

In addition to the interpretation given above, C6 can be interpreted in terms of the relative sizes of the different active intervention arms in the platform trial and the separate trials. To see this, note that a total of and participants are expected to be randomized to intervention in the separate and platform trials, respectively. Moreover, by straightforward calculations, the above condition implies that (see the proof of Lemma B.9 in Appendix B.4 of the Supplementary material available at Biostatistics online for these calculations). Hence, C6 requires allocating the same fraction of the total active intervention to participants across the separate trials to the trial for intervention as was allocated in the platform trial.

We now exhibit an estimator for the relative risk based on the data from the separate trial for a given active intervention . For a covariate level , let . We estimate the relative risk through time via

where, for , is the stratified Kaplan–Meier estimator of the probability that within the stratum where equals based on data from the separate trial for intervention .

We now provide the forms of the confidence intervals for that we consider based on data from the platform trial and separate trials. Each of these intervals is built based on asymptotic normality results that appear in the Supplementary material available at Biostatistics online. Lemma B.6 of the Supplementary material available at Biostatistics online shows that the estimator based on platform data satisfies , where denotes convergence in distribution and the form of is given in (B.11). Similarly, Lemma B.7 of the Supplementary material available at Biostatistics online establishes that the estimator based on separate trial data satisfies , where is defined in (B.13). Let and denote consistent estimators of and , respectively. Fix a significance level and let denote the quantile of a standard normal distribution. Asymptotically valid two-sided confidence intervals for the relative efficacy are given by

These intervals are based on the platform trial and separate trial data, respectively. The interval is a Wald-type interval based on an estimator of that is asymptotically efficient within the nonparametric model where the only assumption made on the platform trial data-generating distribution is that intervention assignment is randomized (see C1), and is similarly based on an efficient estimator in the model where the only assumption made on the separate trial data-generating distributions is that intervention assignment is randomized. As a consequence, if the platform trial interval were to be asymptotically shorter than the separate trial interval , then the platform trial would enable a more efficient estimation of the contrast . The following theorem shows that this is indeed the case. Below denotes a probability limit.

Theorem 4.1

Suppose that C1–C6 hold and in such a way that for some . Let . Denote the widths of and by and , respectively.

• (i) If , then the platform trial interval is shorter asymptotically, that is, .

• (ii) If , then the platform trial interval is no longer asymptotically, that is, .

The above theorem shows that, under conditions, running a platform trial will never harm the precision of a confidence interval contrasting two different interventions and will improve it in some cases. To see the lack of harm, note that is never greater than one, and therefore Theorem 4.1 implies that the confidence interval based on the platform trial data is never wider than that based on the separate trial data if . In fact, a stronger conclusion holds: the platform trial confidence interval is asymptotically no wider than that separate trial confidence interval provided the expected number of participants that are enrolled to each active intervention is equal in these two settings—that is, for all ; the conclusion can be shown to hold since in these cases (see Lemma B.9 in Appendix B.4 of the Supplementary material available at Biostatistics online). Because the platform trial utilizes a shared control arm, enforcing the same number of expected participants enrolled on the active interventions allows for the platform trial to be smaller () whenever there is at least one window in the platform trial in which two or more interventions are under randomization. More generally, when there is at least one such window, the platform trial can yield shorter confidence intervals even in cases where it enrolled fewer participants—this is true, in particular, when . In fact, as we show in our simulations, there are realistic cases where this gain in precision is considerable.

5. Adaptive noninferiority test

We now provide a testing procedure to investigate the noninferiority of a specified intervention—assumed to be intervention 1 here without loss of generality—as compared to the most efficacious of the other interventions. We call intervention 1 noninferior to intervention if , where is a specified noninferiority margin, and noninferior to the most efficacious of the other interventions if . Note that the event considered in this work is harmful (e.g., COVID-19 infection), so smaller relative risks are preferable and the minimum is taken. If the event is desirable (e.g., recovery), the maximum should be used instead. If it is not a priori known whether any of the other interventions are in fact efficacious, noninferiority alone is insufficient to determine that an intervention has clinically meaningful efficacy. To handle such cases, it is natural to further require that the relative risk of intervention 1 falls below some specified threshold . This leads to a null hypothesis test of

The null rewrites as a union of marginal null hypotheses. In particular, holds if and only if at least one of the following marginal nulls holds: or for some . Consequently, the alternative hypothesis corresponds to the intersection of the complementary marginal alternatives, namely , with varying over . These observations suggest testing the null at significance level by running (unadjusted) -level tests of the marginal nulls versus , with varying over and rejecting if and only if all of these marginal tests reject. This test of versus , which we refer to as an intersection test, necessarily controls the type-1 error asymptotically provided the marginal tests do so, since

(5.5)

where denotes the distribution of independent draws from and the final inequality holds because, under , there is at least one for which holds. The intersection test asymptotically has type-1 error of exactly when there is only one such that holds and all of the marginal tests are both consistent against all fixed alternatives and have type-1 error against all null configurations (see Appendix E of the Supplementary material available at Biostatistics online for a proof). A natural implementation of the intersection test, which is the one we employ in our simulations, bases the marginal tests on Wald-type confidence intervals constructed using Lemma B.5 of the Supplementary material available at Biostatistics online. The marginal test of rejects if the upper bound of a two-sided confidence interval for is smaller than and the marginal test of , , rejects if the upper bound of a two-sided confidence interval for is smaller than .

6. Numerical studies

We now present numerical studies to imitate the evaluation of vaccines in a placebo-controlled platform trial versus in multiple separate trials. Within each window, enrollment is uniform over calendar time. Table S1 of Appendix F of the Supplementary material available at Biostatistics online summarizes the enrollment timelines of active interventions by windows (until 3 months post-trial initiation), along with the window widths and the enrollment size per arm in each window. A four-category baseline variable is measured for each participant, where the distribution of this variable depends on the enrollment window. In particular, is equal to (0.1, 0.2, 0.3, 0.4) when and (0.4, 0.3, 0.2, 0.1) otherwise. Within each stratum of , placebo participants have piecewise-constant hazard functions that change values only at the calendar times indicating a transition between windows (Months 1, 1.5, 2, and 2.5). The strata where are the lower-risk strata, and their hazard functions across windows (1, 2, 3, 4, 5) are such that the corresponding 6-month attack rates in the placebo arm are equal to (12, 12, 6, 4, and 4). The strata where are the higher-risk strata, and the hazard functions are chosen so that the 6-month attack rates are twice those as in the lower-risk strata. Though the event is somewhat rare, all vaccine-versus-shared-placebo comparisons include 150 events shortly after enrollment opens—the median across Monte Carlo repetitions ranges from a median 2.5 months for intervention 4–4.5 months for intervention 5. The hazard ratio vaccine efficacy—defined as one minus the hazard ratio of vaccine versus placebo recipients—is presented in Table S1 of the Supplementary material available at Biostatistics online. For simplicity, this vaccine efficacy is made to be constant over time. The time for loss to follow-up is taken to follow a distribution that is independent of all other variables under consideration, so that there is 10 annual loss to follow-up during the study, which runs for a total of 18 calendar months.

We consider estimators in two cases: (i) reducing to a constant variable and estimating the marginal relative risk and (ii) taking and estimating the conditional relative risk. All results in the main text pertain to the estimation of the marginal relative risk, and results for estimators of the covariate-stratified relative risk are reported in Appendix H of the Supplementary material available at Biostatistics online. We compare the statistical efficiency of using data from a platform trial (total sample size of 40 400) rather than separate trials (total sample size of 69 800) in the estimation for relative risk ratios of intervention 7 versus other interventions at or 6 (months) postenrollment, under moderate loss to follow-up and administrative censoring at 6, 9, 12, or 18 calendar months post-trial initiation. The efficiency gain is measured by confidence-interval-width ratios—the lower the values of these ratios are, the more efficient the platform trial will be as compared to the separate trials.

Similar coverage was observed for the confidence intervals based on platform trial data and separate trial data. In particular, the empirical percentiles (0, 25, 50, 75, and 100) of the confidence interval coverage across the total of 72 scenarios considered were (91.8, 93.7, 94.5, 95, and 95.7) for the platform trial and (91.4, 93.4, 94, 94.5, and 95.6) for the separate trials. Figure S2 of Appendix H of the Supplementary material available at Biostatistics online displays the efficiency gain of running a platform trial over running separate trials for the marginal and conditional estimands. Across all settings considered, analyses based on the platform trial were at least as efficient, and often more efficient, than those based on the separate trial data. This is true in spite of the fact that the platform trial enrolled over 40 fewer participants than the separate trials. This result is consistent with our theoretical guarantees in Section 4.2. Further details on these efficiency gains, broken down by evaluation time and administrative censoring time can be found in Figures S3 and S4 in Appendix H of the Supplementary material available at Biostatistics online. There we also present results under scenarios in which the sample size is smaller (Figures S5–S7 in Appendix H.1 of the Supplementary material available at Biostatistics online) and the constancy condition C2 fails (Figures S8 and S9 in Appendix H.2 of the Supplementary material available at Biostatistics online).

We evaluated the performance of the adaptive noninferiority test described in Section 5. The evaluation of this test contains two scenarios: one with intervention 7 serving as the prespecified candidate whose noninferiority will be evaluated, and the other with intervention 9 serving as this candidate. Relative efficacy was quantified using the differences of the marginal relative risk of the prespecified candidate and that of the other active interventions. We also evaluate the performance of a likelihood ratio type test, which is described in Appendix D of the Supplementary material available at Biostatistics online. We set the significance level at and the efficacy threshold at . In Figure 1, we report the empirical rejection rates (over 1000 Monte Carlo simulation runs) to evaluate the power and type-1 error control based on the data from the platform trial and the data from separate independent trials, with all the observations censored at and under moderate loss to follow-up. From the figure, we see that type-1 errors of both the intersection test and the likelihood ratio type test are conservatively controlled by the test data from either trial. The tests based on the data from the platform trial yields higher power than the one based on separate independent trials, and the intersection tests attain considerably higher power than the likelihood ratio type tests.

Fig. 1.

The empirical rejection rates of the intersection test and the likelihood ratio type test for different preselected active interventions based on data from the platform trial and separate trials, evaluated at (in months postenrollment) with varying margin values, the significance level of and the efficacy threshold , when all the observations are censored at 6 calendar months post-trial initiation and subject to moderate loss to follow-up.

We also evaluated an oracle noninferiority test that tested a simpler null hypothesis than the intersection test, namely the hardest-to-be-rejected null among the total marginal null hypothesis tests (of and , the prespecified intervention ) described in Section 5. The hardness of a marginal null hypothesis was quantified via the statistical power of testing this marginal null. The oracle test imitates an idealized setting where it is possible to set a priori a single benchmark intervention for the noninferiority test. This setting is certainly unrealizable in practice since evaluating it relies on knowing the true operating characteristics of tests of the total marginal null hypotheses. As the intersection test must reject all of these null hypotheses, it will necessarily have lower power than the oracle. Nevertheless, the intersection test achieved only slightly lower power than did the oracle test in all considered scenarios. In particular, the power of the intersection test relative to that of the oracle test ranged from 0.4 to 11.6 lower on an absolute scale when intervention 7 was preselected and from 0 to 4.3 when intervention 9 was preselected.

7. Data illustration

In two parallel AMP trials, referred to as HVTN 703 and HVTN 704, participants were randomly assigned in a 1:1:1 ratio to control group, low-dose intervention group, and high-dose intervention group (Corey and others, 2021). The primary endpoint was the post-trial days to type-1 human immunodeficiency virus (HIV-1) infection through the week 80 study visit. The annual loss to follow-up rates were 6.3 in HVTN 703 and 9.4 in HVTN 704. The two trials were conducted in different populations, with HVTN 703 enrolling at-risk women in sub-Saharan Africa and HVTN 704 enrolling at-risk cisgender men and transgender persons in the Americas and Europe. Following Corey and others (2021), we stratified our analyses by trial, thereby reporting separate prevention efficacy estimates for the two trials.

To illustrate our developed testing procedure, we created open platform trial data sets by subsampling data from the parallel, multiarm AMP trials as described below. A subset of the participants in the original trial were enrolled in the platform trials we considered. In these platform trials, we fixed the total number of participants enrolled to each active intervention to be approximately 320 in HVTN 703 and 450 in HVTN 704, which is approximately half the total number of participants enrolled to the active arms in the original trials. To enroll participants, the data for each trial were divided into four chronological windows, each containing a quarter of the sample; the resulting sample sizes for intervention groups over windows are presented in Figure S10 of the Supplementary material available at Biostatistics online. Participants were resampled, without replacement, from HVTN 703 or HVTN 704 to generate platform trial data sets that have a desired level of overlap in the control arm. More concretely, we sought to fix the proportion of controls shared at a value ranging from 0.25 to 0.50, where this proportion is defined as the number of controls that are shared by the two arms divided by the total number of controls enrolled in the platform trial. Details can be found in Appendix I of the Supplementary material available at Biostatistics online.

We report inference for the relative efficacy of the low-dose intervention relative to that of the high-dose intervention (on an additive scale), where lower relative efficacy values indicate more favorable performance of the low-dose intervention. Because the trial results were already public when we received the data, we were not able to prespecify a noninferiority margin or efficacy threshold . Therefore, here we focus on reporting the widths of 95 confidence intervals for the relative efficacy through week 80, averaged across the data sets considered. Figure 2 displays these widths. In both trials, there is a trend towards more shared control data between two dose groups yielding tighter confidence intervals.

Fig. 2.

The confidence interval widths of the relative efficacy (on an additive scale) of the low-dose intervention relative to the high-dose intervention in HVTN 703 and HVTN 704, evaluated at week 80.

8. Conclusion

This article established that platform trials can lead to more precise estimation of the relative efficacy of two different interventions. To this end, the joint distributions of estimators of the efficacy of multiple active interventions versus contemporaneous control were established. Such joint distributions were also shown to enable adaptive tests of noninferiority wherein the identity of the most efficacious comparator intervention need not be known in advance. Simulations were provided to support this asymptotic theory. In this study, a platform trial enrolled approximately 67 as many participants as would have separate, independent trials and yet yielded up to 25 narrower confidence intervals for contrasts of the efficacies of two interventions.

Though the positive correlation that we established for the joint distribution of the efficacy estimates across the different arms is advantageous for contrasting the efficacy of different interventions, it also has a disadvantage. To see why, note that, due to the use of a single-shared placebo arm, there is a possibility that, by random chance, an unusually high or low number of events will be observed on the placebo arm. As a consequence, many of the arm-specific efficacy estimators may provide unusually high or low estimates of efficacy. This can, in turn, lead to scenarios where many interventions are falsely suggested to be efficacious or inefficacious (Howard and others, 2018). Though such challenges may be avoided by employing an appropriate multiple testing correction, such procedures have previously been viewed as undesirable for platform trials that involve many stakeholders since they can disincentivize participation in these economical designs in favor of conducting more costly, intervention-specific trials. Therefore, as mentioned in Section 1, recent platform trials have followed multiarmed trials in not using a multiplicity adjustment (WHO Solidarity Trial Consortium, 2021; Howard and others, 2021). An alternative means to avoid elevated false (non)discovery rates in platform designs is to simply increase the size of the placebo arm. Rather than reducing the correlation between arm-specific estimates, this instead directly reduces the variance of these estimates. Since the efficiency gains that we showed in this article allowed the platform trials to be substantially smaller than the corresponding separate trials, the placebo arm could be substantially increased in size while still resulting in a smaller-sized trial than would have been two separate trials and improved precision for comparing the efficacy of multiple interventions. In any given setting, pretrial simulation studies can be conducted to determine whether modifying the platform trial allocation ratio in this manner yields a design with the investigators’ desired operating characteristics.

Software

Code can be found at https://github.com/tzujunghuang/ImprovedEfficiency_via_PlatformDesigns.

Supplementary Material

Supplementary material is available online at http://biostatistics.oxfordjournals.org.

Funding

The National Institutes of Health (NIH) (DP2-LM013340 and 5UM1AI068635-09).