Planning Sample Size for Repeated-Measures Endpoints

Why Sample Size Depends on the Repeated-Measures Design

For a repeated-measures endpoint, the sample size cannot be planned from the number of observations alone. Several measurements from one participant are related, so four visits do not provide the same information as four independent participants. The benefit of additional visits depends on the within-participant covariance, the contrast the trial is designed to estimate, and whether the assumed trajectory is plausible.

This tutorial develops a concrete design case in which the primary treatment contrast is the average difference between treatment groups across scheduled post-baseline visits. The goal is to use a specified outcome model to simulate trial data under candidate designs, fit the planned analysis, and estimate both power and precision. The result is conditional on the assumptions supplied to the simulation; it is not a guarantee of a future trial's outcome.

Specify the Estimand and a Planning Model

Let \(Y_{ij}\) be participant \(i\)'s endpoint at post-baseline visit \(j\), with \(m\) scheduled visits. For this design case, define the participant's endpoint summary as the arithmetic average across those visits. The treatment contrast \(\Delta\) is the difference between treatment-group means of that summary. Thus, if the treatment effect is constant across visits, \(\Delta\) is also the common treatment difference at each visit. This definition makes the visit schedule part of the estimand: changing which visits are included changes the average being targeted.

Assume equal allocation, \(n\) participants per group, complete measurements at all \(m\) visits, and a common covariance structure in both groups. For planning, suppose the visit outcomes are multivariate normal with marginal standard deviation \(\sigma\) and exchangeable correlation \(\rho\): every pair of distinct visits has the same correlation. The model allows visit means to change over time, but assumes the treatment difference is constant across visits. Under these assumptions, a comparison of participant-level visit averages is a valid analysis of the defined contrast. The two-sample \(t\)-test uses \(df=2n-2\).

The first expression is the variance of one participant's average. It follows by adding the \(m\) marginal variances and the \(m(m-1)\) ordered covariance terms, then dividing by \(m^2\). The second expression follows because the treatment contrast subtracts independent group means, each based on \(n\) participants. These formulas show why extra visits help less when visits are highly correlated.

From Variance to a Candidate Sample Size

For a two-sided test at significance level \(\alpha\), power depends on the assumed treatment contrast \(\Delta\) relative to its standard error. With the \(t\)-test, the test statistic follows a noncentral \(t\) distribution under the planning alternative, with \(df=2n-2\) and noncentrality parameter \(\lambda=\Delta/SE(\hat{\Delta})\). The sample size can be found by evaluating this power over candidate values of \(n\). A useful initial approximation replaces the \(t\) critical value with a normal critical value:

where \(1-\beta\) is the target power and \(z_q\) is the \(q\)-quantile of the standard normal distribution. Round the result up, then evaluate the actual planned test at that integer sample size. The approximation is a starting point, not a substitute for checking power under the analysis that will be used.

Use Simulation to Compare Designs

A simulation evaluates the entire design-and-analysis process rather than relying only on an approximate formula. For every replicate, generate a participant's vector of repeated outcomes from the assumed multivariate distribution, assign the specified treatment effect, apply the trial's analysis, and record whether the \(H_0:\Delta=0\) test rejects at \(\alpha=0.05\). The estimated power is the proportion of simulated trials that reject. Repeating this for several sample sizes shows how much enrollment is needed under the stated assumptions.

For the four-visit case, the covariance matrix has diagonal entries \(100\) and off-diagonal entries \(50\), since the variance is \(10^2\) and the covariance is \(\rho\sigma^2=0.50(100)\). The treatment group has a mean four points lower at each visit than the control group; the control visit means may vary over time, but their exact values do not affect the variance of the contrast in this constant-effect setup.

Visit Schedules and Covariance Assumptions

The next example changes the number of visits and the within-participant correlation while holding the marginal standard deviation and target contrast fixed. This isolates how assumptions about repeated observations affect the planned enrollment. The calculations use the same normal approximation for 90% power, so they are comparisons of planning scenarios rather than final sample-size recommendations.

Justification and Practical Simulation Workflow

The variance result follows directly from the covariance structure. Let \(Y_{i1},\ldots,Y_{im}\) have variance \(\sigma^2\) and pairwise covariance \(\rho\sigma^2\). Since \(\bar{Y}_i=m^{-1}\sum_{j=1}^{m}Y_{ij}\), the variance of a sum is the sum of all variances and covariances:

The term \(m(m-1)\) counts ordered pairs of distinct visits. For independent visits, \(\rho=0\), the variance falls to \(\sigma^2/m\). As \(\rho\) approaches one, the visits provide nearly redundant information, and the variance approaches \(\sigma^2\). This derivation explains both the benefit of added visits and its dependence on covariance.

A defensible simulation plan proceeds in a fixed sequence:

Diagnostics, Alternatives, and Limitations

A simulated result is only as credible as the model and analysis used to produce it. Check that the covariance matrix is mathematically valid, that simulated variances and correlations match the inputs, and that the fitted analysis targets the intended contrast. Under the null, verify that the estimated type I error is near \(\alpha\); under alternatives, check bias and confidence-interval coverage as well as rejection probability. Increase the number of replicates when Monte Carlo uncertainty is large relative to the decision threshold.

The exchangeable model is deliberately simple. Actual longitudinal data may have correlations that decline with the time separating visits, unequal variances across visits, or treatment effects that grow or diminish over time. The primary analysis may also use all visit-level data in a mixed model rather than reduce each participant to an average. In those settings, simulate from and fit the proposed longitudinal model, and define the contrast explicitly. Do not use the visit-average formula as though it automatically represented a time-specific contrast or an analysis with a different covariance structure.

A closed-form calculation is fast and useful for screening candidate designs when assumptions are simple and balanced. Simulation is more flexible: it can reproduce the intended estimation procedure and examine irregular visit schedules, missingness, unequal allocation, or more complex covariance patterns. The trade-off is that simulation requires more assumptions and can conceal errors if the data-generating and analysis steps are not checked. An analytic result is not inherently safer if its assumptions are implausible; a simulation is not inherently realistic merely because it is detailed.

Important failure modes include planning from an optimistic correlation estimate, treating repeated observations as independent, selecting a treatment difference without clinical justification, and ignoring loss of information from incomplete visits. If the true correlation is higher than planned, power may be lower than expected; if treatment effects differ across visits, the average contrast may obscure a meaningful time pattern. Sensitivity analyses should therefore vary the assumptions most likely to change the decision, particularly the covariance, treatment-effect size, visit schedule, and missing-data process.