Why Shared Controls Require Careful Interpretation
A platform trial can evaluate several treatments while using a common control group. This can conserve participants and make comparisons more efficient: instead of assigning a separate control group to every intervention, eligible participants assigned to control may contribute information to more than one treatment-control contrast. The efficiency is real only when each contrast uses a control group that represents the appropriate comparison.
That qualification matters in RECOVERY and REMAP-CAP. RECOVERY evaluates treatments for hospitalized patients through a platform in which treatment comparisons can share usual-care controls when the relevant participants and enrollment periods align. REMAP-CAP organizes randomization around intervention domains; control information can be shared for interventions in a domain when participants are eligible for the relevant comparison and the protocol's allocation scheme supports it. Neither description means that every control participant is automatically an appropriate comparator for every active treatment.
The central questions are therefore not simply “Was a control group shared?” but “For which contrast was it shared, among which eligible patients, and over what period?” A control group recruited under different eligibility rules or a different standard of care can distort a treatment contrast even when its sample size is large.
What Makes a Shared Control Valid?
Randomization supports a causal comparison within the population and period to which it applies: treatment assignment is made by chance under the trial's allocation procedure, rather than chosen according to prognosis. Concurrent randomization is especially important in a changing disease setting. When treatment and control participants are randomized during the same period, they are exposed, on average, to similar background changes in care and disease management. Randomization does not guarantee identical groups in a particular sample, but it protects the comparison in expectation.
Sharing control observations does not make the treatment contrasts statistically independent. If two estimated risk differences use the same estimated control risk, an unusually high or low control risk shifts both contrasts in the same direction. Analyses must account for this dependence when making joint inferences. Further, a shared group is not a substitute for prespecified multiplicity procedures when several treatment hypotheses are tested; how to control error across those hypotheses depends on the trial's inferential plan.
A useful working model for one binary outcome is independent binomial sampling within randomized groups: among \(n_T\) participants assigned to treatment, the event count has probability \(p_T\), and among \(n_C\) controls it has probability \(p_C\). The estimated risk difference is \(\hat{p}_T-\hat{p}_C\), where each sample proportion is the observed event count divided by its group size. This model presumes that the outcome definition and follow-up are comparable. It also presumes that the participants included in the contrast belong to the intended comparison; a large control sample does not correct a mismatch in eligibility or period.
Why the Shared Estimates Are Correlated
Suppose treatments A and B each have their own randomized treatment group, while both contrasts use the same randomized control group. Under independent binomial sampling across the three groups, the estimated treatment effects are \(\hat{p}_A-\hat{p}_C\) and \(\hat{p}_B-\hat{p}_C\). The control estimate appears in both. Since the variance of a difference is the sum of the variances minus twice the covariance, this shared term can be shown directly:
The second line uses the assumption that the three group estimates are independent except that the same control estimate occurs in both contrasts. Thus, the covariance is positive. Treating the contrasts as independent would discard this shared uncertainty and could misstate the uncertainty of a comparison between treatment effects or of a joint decision.
Worked Example: Two Contrasts With One Shared Control
Consider hypothetical concurrent randomization to treatments A and B and a common control. The observed event proportions are 40/200 for A, 30/200 for B, and 100/400 for control. Assume independent binomial outcomes across the three groups and a common outcome definition and follow-up period. These counts are hypothetical and do not describe either platform trial.
The estimated risk differences, expressed as treatment minus control, are:
The estimated event risk is 5 percentage points lower for A and 10 percentage points lower for B than for the shared control. For a binomial proportion, the estimated variance is \(\hat{p}(1-\hat{p})/n\). Therefore:
For B, the corresponding calculation is:
The covariance between the two estimated risk differences is the estimated control variance, \(0.0004688\). The estimates are therefore positively correlated, with estimated correlation \(0.0004688/(0.03562\times0.03326)=0.396\). These standard errors describe each contrast separately; a joint comparison of A and B must retain the covariance rather than regard the two estimates as independent. The calculation is appropriate here because the example stipulates concurrent randomization, independent group outcomes, and matching outcome measurement.
Calendar Time and Changing Standards of Care
In platform trials, interventions may open or close as evidence accumulates, and usual care can change as clinical practice changes. A control participant randomized while an intervention is available and eligible is generally more informative for that contrast than a control participant recruited long before or after it. The latter may have faced different background treatment, diagnostic practice, supportive care, or outcome risk.
A pooled control proportion can conceal this problem. If an intervention is mostly evaluated early but its control estimate pools participants recruited both early and late, the intervention and control groups may represent different mixtures of calendar periods. The resulting crude risk difference can reflect the mixture as well as the treatment. Concurrent randomization helps align those mixtures, but analysts still need to check the actual enrollment windows and prespecified analysis population.
Worked Example: Unequal Calendar-Time Mixtures
Suppose, hypothetically, a platform enrolls participants in an early and a late period, with event risks of 30% and 10% among concurrent controls. An intervention has event risks of 24% early and 8% late. These hypothetical risks imply a 6-percentage-point benefit early and a 2-percentage-point benefit late when each treatment group is compared with its concurrent controls. Assume that each within-period contrast is randomized and that the event and follow-up definitions remain comparable.
Now suppose the intervention group is 80% early and 20% late, while the pooled control group is 20% early and 80% late. The intervention's pooled risk is:
The pooled control risk is:
The crude pooled difference is \(0.208-0.140=0.068\), suggesting an event risk 6.8 percentage points higher under treatment. Yet the intervention risk is lower in both periods: the early difference is \(0.24-0.30=-0.06\), and the late difference is \(0.08-0.10=-0.02\). With equal weights for the two periods, the standardized treatment risk is \((0.24+0.08)/2=0.160\), and the standardized control risk is \((0.30+0.10)/2=0.200\), giving a standardized difference of \(-0.040\). The discrepancy arises because the pooled groups have different period weights. In a real analysis, the relevant weights and estimand must be justified by the trial question; this example shows why a control group should not be pooled across periods without checking comparability.
Eligibility and Platform-Specific Comparisons
Calendar time is not the only source of mismatch. In RECOVERY, the treatment options available and the relevant eligibility criteria define which randomized participants can inform a particular comparison. A usual-care participant may be a valid control for one treatment comparison but not another if the intervention's eligibility or enrollment period differs. In REMAP-CAP, domain-based randomization makes this issue explicit: the control information relevant to a domain-based contrast is determined by the participants eligible for that domain and by the protocol's randomization and analysis rules. Sharing should follow those rules rather than be assumed from the fact that participants belong to the same overall platform.
The following hypothetical calculation illustrates why eligibility matters. Assume an intervention is studied only in high-risk patients, but a pooled control group includes many low-risk patients. The treatment group and pooled control then do not represent the same target population.
Worked Example: A Control Pool With Different Eligibility
Suppose 100 high-risk control participants have 40 events, while 900 low-risk control participants have 90 events. A hypothetical intervention group of 100 high-risk participants has 30 events. Assume treatment and control participants are randomized within the high-risk eligible population, and that the outcome and follow-up are otherwise comparable.
The pooled control event risk is \((40+90)/(100+900)=130/1000=0.13\). Comparing the high-risk treatment risk, \(30/100=0.30\), with that pooled risk gives a crude difference of \(0.30-0.13=0.17\), or 17 percentage points higher under treatment. But the eligible high-risk control risk is \(40/100=0.40\). The relevant high-risk comparison is \(0.30-0.40=-0.10\), or 10 percentage points lower under treatment.
The pooled comparison is misleading because low-risk controls dilute the event rate for a treatment group composed only of high-risk participants. Restricting the control group to the eligible high-risk population restores the intended comparison. The numerical example does not establish that every risk subgroup should be analyzed separately; it demonstrates that the analysis population must match the question and the randomization structure.
Practical Checks, Alternatives, and Limitations
When interpreting a shared-control contrast in RECOVERY or REMAP-CAP, check the comparison rather than treating “control” as one universal category. In particular, examine:
- Concurrent enrollment: Were the treatment and control participants randomized during overlapping periods when the intervention was available?
- Eligibility: Were controls eligible for the specific intervention comparison, under the same relevant criteria?
- Care and measurement: Were background care, outcome definitions, and follow-up sufficiently comparable?
- Allocation and analysis: Does the analysis follow the platform's randomization scheme, account for shared-control dependence, and use the stated analysis population?
- Changing effects: Is there a reason to assess whether treatment effects vary by period or participant group, rather than relying only on an average contrast?
Warning signs include a treatment arm and its controls having sharply different enrollment windows, a pooled control group containing people ineligible for the intervention, changes in endpoint ascertainment over time, or analyses that treat correlated contrasts as independent. These checks cannot prove that every assumption holds; they identify where a reported contrast may need qualification or a more restricted analysis.
The main alternatives each involve a trade-off. Separate concurrent control groups can make the comparison groups clearer and reduce dependence between contrasts, but require more control participants and may be inefficient. A common concurrent control can use participants efficiently, provided eligibility and time alignment are maintained and the analysis handles the resulting correlation. Historical or nonconcurrent controls may add information when concurrent control data are limited, but are more vulnerable to changes in care, patient mix, and measurement. Statistical adjustment for calendar time or measured baseline factors can help address recorded differences; it cannot guarantee removal of unmeasured differences or restore randomization across nonconcurrent periods.
A shared control therefore supports a stronger design only when sharing is planned and comparison-specific. It does not turn several treatment arms into one experiment with interchangeable controls, nor does it make an average treatment effect universal across changing standards of care. The treatment contrast remains an estimate for the participants, periods, outcomes, and allocation conditions represented in that comparison.
Check Your Understanding
Answer each question, then compare your reasoning with the solutions.
- Two estimated risk differences use the same control proportion. Under independent binomial sampling across treatment groups and control, what is the covariance between the estimated differences?
- Why can a pooled control risk from early and late periods be misleading if the treatment group has a different mix of periods?
- A treatment is restricted to high-risk participants, but the shared control pool includes low-risk participants. What should be checked before using that pool?
- Name one efficiency advantage and one inferential requirement of using a shared control rather than separate controls.
Solutions. (1) The covariance equals the variance of the shared control proportion, \(\operatorname{Var}(\hat{p}_C)\), because the same control estimate enters both treatment-minus-control contrasts. (2) Different period weights can make the pooled treatment and control risks reflect different background event risks, so the crude contrast may not represent a within-period randomized comparison. (3) Check that controls are eligible for the treatment comparison and represent the same target population; in this case, a high-risk control comparison may be needed rather than the full pool. (4) Sharing can reduce the number of control participants needed for several comparisons; joint inference must account for the correlation induced by reusing the control observations.