Worked Sample-Size Planning for a Longitudinal Endpoint

From the Estimand to the Enrollment Target

A sample-size calculation for a longitudinal endpoint is only as relevant as the treatment effect it is designed to detect. The endpoint, assessment time, treatment contrast, covariance assumptions, and handling of missing outcomes must describe one coherent plan. This tutorial develops that plan for a continuous outcome measured at baseline and at a primary follow-up visit.

Suppose the primary question is whether the mean change from baseline to week 24 differs between an active treatment and control. The treatment contrast is active minus control, so a negative value would favor active treatment if lower scores are better. The numerical example uses arbitrary outcome points and hypothetical inputs; it does not represent a real study.

The calculation below assumes the week-24 change is the primary response. A mixed model represents repeated outcomes jointly, but the worked calculation uses the contrast in arm-specific mean changes. If an analysis instead estimates the contrast by using all follow-up visits, baseline covariate adjustment, or a different missing-data strategy, its treatment-contrast variance may differ and should be calculated for that planned analysis.

Model and Covariance Assumptions

For each participant, write the repeated outcome vector as \(\mathbf{Y}_i=(Y_{i0},Y_{i24})^\mathsf{T}\). A linear mixed-effects model specifies the mean at each visit using treatment, visit, and their interaction, and describes the within-participant dependence through a covariance matrix. For this two-visit planning calculation, assume a common covariance matrix in both treatment arms:

Here, \(\sigma_0^2\) and \(\sigma_{24}^2\) are the baseline and week-24 variances, and \(\sigma_{0,24}\) is their covariance. The treatment contrast in the group-by-visit pattern is the difference between mean changes. For the simple balanced calculation, assume independent participants, no clustering, equal allocation, the same change-score variance in both arms, and normally distributed changes (or a sample size large enough for the normal approximation to be adequate). The calculation also treats the variance as known at its planning value.

These assumptions are planning choices, not facts guaranteed by randomization. In particular, the correlation between repeated measurements affects the variance of change, while the treatment effect \(\delta\) and the change-score variability must come from defensible external or pilot evidence. The introductory material on repeated-measure correlation and effective sample size explains why repeated observations cannot be counted as independent participants.

Deriving the Treatment-Contrast Variance

The change for one participant is \(D_i=Y_{i24}-Y_{i0}\). Applying the variance rule for a difference gives:

The factor of two is essential: the covariance contributes twice when the variance of a difference is expanded. Let \(\bar{D}_T\) and \(\bar{D}_C\) be the sample mean changes in the active and control arms, with \(n_T\) and \(n_C\) participants, respectively. Independence between participants and between randomized arms implies:

With equal allocation, \(n_T=n_C=n\), the standard error is \(SE=\sqrt{2\sigma_D^2/n}\). For a two-sided test of \(H_0:\delta=0\) at significance level \(\alpha\), the normal-approximation sample size per arm for power \(1-\beta\) is:

The expression follows by requiring the expected standardized treatment contrast under the planned alternative to exceed the null rejection boundary by the desired power quantile. In other words, the noncentrality \(|\delta|/SE\) is set to \(z_{1-\alpha/2}+z_{1-\beta}\). Squaring and substituting \(SE^2=2\sigma_D^2/n\) gives the formula above. The \(z\) values are standard normal quantiles. For small samples, or when the variance is estimated rather than known, a noncentral-\(t\) calculation is preferable; it can require iterative evaluation because the degrees of freedom depend on sample size.

Worked Sample-Size Plan

A defensible plan proceeds from the estimand to the variance, then to the test and its power, and finally to enrollment. Each input should be stated in context, including units. The sample size is not a stand-alone number: it is conditional on these assumptions.

Dropout, Diagnostics, and Alternatives

The simple inflation rule is \(n_{\text{enroll}}=\lceil n_{\text{complete}}/(1-r)\rceil\) per arm, where \(r\) is the expected proportion without usable primary endpoint data. It assumes the loss rate is reasonably predictable and that the analysis can still estimate the intended contrast without material bias. It is an approximation when participants contribute partial longitudinal data to a mixed model: such participants may provide information even without a week-24 observation, so dividing by \(1-r\) may overstate or understate the required enrollment.

Before accepting a plan, check that the covariance estimates are plausible for the chosen scale and visit schedule, that the derived variance is nonnegative, and that the assumed treatment effect is clinically meaningful rather than merely statistically detectable. Check the exact-sidedness of the test and the quantiles used. For an implemented design, compare the assumed and observed visit patterns, arm-specific endpoint availability, and fitted covariance behavior; large differences can make the original power calculation a poor description of the study.

A direct change-score calculation is transparent and is appropriate when the planned primary estimator is the difference in mean changes. An ANCOVA that adjusts the endpoint for baseline can have a different variance and may be more efficient under its model assumptions. A repeated-measures mixed model can use multiple post-baseline visits and incomplete outcome histories, but its contrast variance depends on the full mean and covariance model and the missing-data assumptions. Fisher information calculations or simulation are useful alternatives when the design has unequal visits, unequal allocation, more complex covariance, or a nonlinear model; they should target the same estimand and analysis as the proposed study.

A common mistake is to treat the baseline and endpoint measurements as independent, or to use the endpoint standard deviation alone as the standard deviation of change. The correction is to calculate \(\sigma_D^2=\sigma_{24}^2+\sigma_0^2-2\sigma_{0,24}\) using the planned within-person covariance. Another mistake is to inflate for dropout and assume this guarantees valid power. Inflation addresses expected sample loss only; it cannot by itself correct an inappropriate estimand, misspecified covariance, or informative missingness.