Using Covariate Adjustment in Sample-Size Scenarios

Why Covariate Adjustment Matters for MAMS Planning

A prespecified baseline covariate can explain part of the outcome variation among participants. If the planned analysis adjusts for such covariates, the treatment-control comparison may be more precise than an unadjusted comparison of the same size. In sample-size planning, that potential gain can translate into fewer participants at each stage, a smaller maximum enrollment, or both.

The gain is not automatic. It depends on how much outcome variation the covariates explain, whether the planning assumption is credible in the trial population, and whether the analysis model is specified appropriately. In a multi-arm multi-stage (MAMS) design, the adjustment also affects interim statistics and therefore can change the probabilities that arms continue. Consequently, reducing stage sizes and recalculating expected enrollment are related but distinct tasks.

Assumptions and the Variance Calculation

The simple \(1-R^2\) variance reduction is a planning approximation for a continuous outcome. It is appropriate when the covariates are measured before randomization, are prespecified, and are prognostic for the outcome; the adjusted model is correctly specified; and the assumed \(R^2\) is relevant to the trial population. The usual calculation also assumes a common residual variance across randomized groups and a treatment effect that is not changed by adjustment. In practice, a model may include treatment and baseline covariates, with treatment contrasts estimated conditional on those covariates.

For a treatment group with \(n_t\) participants and a shared control group with \(n_0\), the approximate variance of an adjusted difference in means is \(\sigma^2(1-R^2)(1/n_t+1/n_0)\). This is a marginal variance for one comparison. Because MAMS comparisons share control observations, their test statistics are correlated; a joint design calculation must retain that shared-control structure rather than treating the comparisons as independent.

To see how this enters a sample-size calculation, suppose a one-sided comparison has a positive target effect \(\delta\), a normal critical value \(c\), and target power \(1-\beta\). With a normal approximation, the standardized mean under the alternative is \(\delta/SE\). Requiring power \(1-\beta\) means \(\delta/SE-c=z_{1-\beta}\), where \(z_{1-\beta}\) is the corresponding standard-normal quantile. If \(n_0=r n_t\), substitution and rearrangement give the required treatment-group size.

This derivation shows the key scaling result: with the effect, allocation ratio, critical value, and power target held fixed, the unrounded sample size is multiplied by \(1-R^2\) relative to the unadjusted calculation. It does not establish that a complete MAMS design's maximum or expected enrollment is reduced by exactly that factor. Stage boundaries, integer rounding, shared-control allocation, and continuation probabilities also matter.

From a Per-Comparison Calculation to Stage Sizes

A MAMS design uses cumulative sample sizes at successive analyses. For arm \(j\), let \(n_{j,k}\) be the cumulative number assigned to that treatment by stage \(k\), and let \(n_{0,k}\) be the cumulative number assigned to shared control. The stage increment is the new enrollment between consecutive analyses: for example, \(n_{j,k}-n_{j,k-1}\) in treatment arm \(j\). Applying the variance reduction to a per-comparison planning calculation is a starting point for setting these quantities, not a substitute for checking the design's stagewise operating characteristics.

For example, if an illustrative design uses 60% of its maximum per-group sample size at the first analysis, the 42-per-group adjusted calculation above gives \(0.60(42)=25.2\), rounded up to 26 per group at stage 1. The remaining increment is \(42-26=16\) per group. On the unadjusted calculation, \(0.60(65)=39\) per group at stage 1, with a further \(65-39=26\) per group. For two treatment arms and one shared control, these allocations correspond to cumulative stage-1 totals of \(3(26)=78\) and \(3(39)=117\), respectively, and maximum totals of \(3(42)=126\) and \(3(65)=195\). This comparison assumes the same per-group allocation for each arm and control and is an illustration of size translation, not a final calibrated MAMS design.

In an actual design, boundaries and the joint distribution of the test statistics determine power and continuation behavior. If those boundaries are recalibrated, or if the shared-control allocation differs from the simple equal-group illustration, the stage sizes must be checked using those design details. Covariate adjustment does not remove the correlation caused by shared control, and it does not justify scaling every stage quantity blindly.

Expected Enrollment Depends on Continuation Probabilities

Let \(N_1\) be the stage-1 total enrollment. At later stages, a treatment-arm increment is recruited only if that arm remains active, while a shared-control increment may be recruited if at least one treatment remains active. Let \(q_{j,k}\) be the probability that arm \(j\) is active at the start of stage \(k\), and \(q_{0,k}\) the probability that at least one treatment arm is active then. If the increments are fixed whenever their corresponding recruitment rule applies, expected total enrollment is the initial enrollment plus each increment multiplied by its probability of being recruited.

The expression follows by writing total enrollment as the initial cohort plus each possible later increment times an indicator that the increment is recruited. Taking expectations replaces each indicator with its recruitment probability. The probabilities are not generally interchangeable: the chance that at least one arm continues is not the same as the sum of the arm-specific probabilities, because both arms can continue together.

Efficiency Assumptions, Diagnostics, and Alternatives

The expected-enrollment formula makes clear why adjustment can affect enrollment through two channels. First, a credible efficiency gain can reduce the stage increments required for a chosen design target. Second, more precise interim statistics can change the continuation probabilities \(q_{j,k}\) and \(q_{0,k}\). The second channel has no universal direction: it depends on the treatment-effect scenario, boundaries, and which arms are active. For a fair scenario comparison, use continuation probabilities appropriate to each planned design rather than assuming they remain unchanged after the variance model changes.

A useful diagnostic is to vary the prespecified \(R^2\) over a plausible range and recompute both the stage-size inputs and scenario-specific continuation probabilities. Check that the assumed \(R^2\) refers to the analysis covariates and outcome in the relevant population, and verify that rounding has not caused a stage increment to become zero or changed the intended ordering of analyses. The joint design calculation should also retain the shared-control correlation and the planned decision boundaries.

An unadjusted analysis is a straightforward alternative: plan using the full outcome variance and do not claim a sample-size gain from covariates. This may be a prudent sensitivity case when the efficiency assumption is uncertain, although it can require more participants. A prespecified adjusted analysis uses the anticipated variance reduction but relies on model and population assumptions. Neither approach makes the treatment effect larger; adjustment changes precision, not the effect measured. For binary outcomes, the continuous-outcome shortcut \(\sigma^2(1-R^2)\) should not be applied mechanically: the variance and efficiency calculation must match the planned binary-outcome model and effect scale.

Common Mistakes and Practical Limits

• Using \(R^2\) as a percentage reduction in sample size without stating assumptions. The factor \(1-R^2\) applies to the unrounded variance-based calculation under the specified model and fixed design inputs. Stagewise rounding and boundary calibration can change the final design.
• Assuming adjustment changes the treatment effect. The planning gain described here is a reduction in variance under the stated assumptions, not a change in the target contrast.
• Scaling expected enrollment by the variance factor. Expected enrollment depends on stage increments and the probabilities that each arm-specific or shared-control increment is recruited. Those probabilities can change when the interim statistics change.
• Counting shared control once per treatment arm. In a multi-arm design, control recruitment follows the design's shared-control rule; use that rule and the probability that activates it.
• Treating the assumed efficiency as guaranteed. If the covariates explain less variation than expected, the realized precision and power can be below plan. Include plausible alternatives in sensitivity checks.

The main limitation is that a single \(R^2\) is a summary of a relationship that can vary across populations and outcomes. Moreover, the simple formula does not account by itself for model misspecification, treatment-by-covariate interactions, missing outcomes, or non-normal small-sample behavior. Those features require assumptions or calculations beyond the basic continuous-outcome efficiency adjustment.