Planning Sample Size for Multiple Strengths

Why Multiple Strengths Change the Planning Problem

A study may need to compare several strengths of a test formulation with a reference. The enrollment question is not simply how many subjects give adequate power for one comparison. If the study succeeds only when every required strength meets its bioequivalence criterion, the relevant operating characteristic is the probability that all those comparisons succeed together. That probability depends on both the power of each comparison and the dependence among their estimates.

Two broad strategies are to conduct separate two-treatment comparisons or to include the reference and multiple test strengths in a shared-subject design. The latter can estimate several contrasts in the same participants. Its efficiency depends on the covariance of measurements within participants, while its feasibility also depends on the number of periods, treatment sequences, and potential missing profiles. The study objective and the required claims must therefore be fixed before enrollment is calculated.

Set the Comparison and the Success Criterion

For an average bioequivalence comparison, let \(\theta_k\) be the true difference between the population mean log pharmacokinetic measure for test strength \(k\) and reference. A common bioequivalence interval on the ratio scale is 0.80 to 1.25, corresponding to log limits \(\ln(0.80)\) and \(\ln(1.25)\). Since these are equal in magnitude, write the limits as \(-\Delta\) and \(\Delta\), where \(\Delta=\ln(1.25)\approx0.22314\). The comparison succeeds when its confidence interval for \(\theta_k\) is wholly inside those limits, as assessed by two one-sided tests (TOST).

The planning target should specify the desired probability that all required comparisons succeed, not just a nominal power for one contrast. If the protocol requires both AUC and Cmax for each strength, there are multiple criteria per strength as well. The earlier material on joint power for AUC and Cmax addresses combining endpoint requirements; here the focus is on how the strengths and study design affect planning.

For a transparent first calculation, suppose an estimated log contrast is approximately normal with mean zero under the planning alternative and standard error \(SE\). Assume a known or adequately approximated variance, a prespecified type I error \(\alpha\) for each TOST, and no material bias in the estimated contrast. In this normal approximation, the confidence interval is inside the equivalence limits when the estimate lies between \(-\Delta+z_{1-\alpha}SE\) and \(\Delta-z_{1-\alpha}SE\). Thus the approximate power for one comparison is:

provided the inner bound is positive. Here \(z_q\) is the \(q\) quantile of the standard normal distribution and \(\Phi\) is its cumulative distribution function. This calculation is a planning approximation: a final analysis with estimated variance and finite degrees of freedom should use the relevant \(t\)-based power calculation or a validated exact method.

From a Joint Target to a Component Target

One practical way to plan for all \(K\) comparisons is to allocate a total failure probability \(\delta=1-\text{target joint power}\) across them. If each comparison has power at least \(1-\delta/K\), then the probability that any comparison fails is at most \(\delta\), regardless of the dependence among comparisons. This follows from the union bound:

Consequently, a sufficient component-power target is \(1-\delta/K\). This is conservative when comparisons are dependent or when their true joint success probability exceeds the bound. If the comparisons are independent and have equal power \(p\), joint power is exactly \(p^K\); that product is not valid merely because each comparison has the same marginal power.

For the common goal of claiming equivalence for every required comparison, applying TOST at \(\alpha\) to each comparison is an intersection-union test: the global claim is made only if every comparison passes. No multiplicity adjustment is required to control the type I error of that all-comparisons claim. That does not make multiplicity irrelevant to planning: the chance of passing every comparison can be substantially lower than the power of any one comparison. Procedures differ if the goal is to claim only selected successful comparisons or to claim that at least one comparison is equivalent.

Separate Two-Period Crossover Comparisons

For one balanced two-period crossover comparison with \(n\) complete subjects, assume the log-scale within-subject residual variance is \(\sigma_w^2\), periods and sequences are appropriately handled, and the paired contrast has variance \(2\sigma_w^2/n\). Then \(SE=\sqrt{2\sigma_w^2/n}\). Combining this with the normal power formula gives a useful approximate enrollment requirement for a component power \(p\), when the expected contrast is zero:

A coefficient of variation (CV) on the original scale can be converted to log-scale variance using \(\sigma_w^2=\ln(1+CV^2)\), with the CV expressed as a proportion. The formula assumes the planning mean ratio is one. If the expected ratio differs from one, the distance from that expected contrast to each equivalence limit is unequal; use the corresponding power calculation rather than this centered shortcut.

Shared-Subject Designs and Contrast Covariance

In a shared-subject crossover, each participant receives the reference and multiple test strengths, with treatment order randomized and periods arranged to estimate treatment contrasts without confounding them with period or sequence effects. For strength \(k\), the variance of a subject-level test-minus-reference contrast is:

Here \(Y_{ik}\) and \(Y_{iR}\) are the log measurements for participant \(i\) under test strength \(k\) and reference. If both have residual variance \(\sigma^2\) and correlation \(\rho\), the contrast variance is \(2\sigma^2(1-\rho)\). Positive correlation reduces the contrast variance relative to independent residuals. It must be estimated or justified from relevant design information; assuming a favorable correlation without support can understate enrollment.

When several contrasts use the same reference observations, their estimates are generally correlated. A single-contrast sample-size formula can calculate marginal power, but it does not by itself determine joint power. Joint power can be obtained from a multivariate distribution for all estimated contrasts when its covariance structure is specified, or by simulation of the planned model and analysis. The approximation that multiplies individual powers is appropriate only when independence is justified.

Joint Power, Diagnostics, and Design Choices

A small example shows why marginal power cannot stand in for joint power. If three independent comparisons each have 90% power, the probability all three pass is \(0.90^3=0.729\), or 72.9%, not 90%. If the comparisons are dependent, that product is not justified. A shared-subject design can induce dependence through the common reference and subject-level measurements; the direction and magnitude of the effect on joint success should be calculated from the planned covariance model rather than assumed.

The Bonferroni component target is useful when a conservative guarantee is acceptable and dependence is uncertain. A multivariate calculation can be less conservative when the covariance matrix is credible. Simulation is useful when the design is unbalanced, has complicated missingness, or uses an analysis model for which a convenient joint-power formula is unavailable. In either case, simulate or calculate the probability of the actual protocol success rule—not a surrogate such as “at least one strength passes” when the protocol requires all strengths to pass.

Before accepting a proposed sample size, check that the design and assumptions match the intended study:

• Contrast definition: Confirm the required strengths, reference, endpoints, equivalence limits, and whether every comparison must pass.
• Variance and correlation: Check that the CV and shared-subject correlations are supported by relevant data and correspond to the planned log-scale model.
• Sequence and period structure: Ensure the treatment sequences permit estimation of all contrasts and that period effects are not confounded with treatment.
• Complete-data count: Distinguish complete evaluable participants from the number enrolled; account for dropout and nonevaluable profiles.
• Finite-sample confirmation: Check rounded, sequence-balanced sample sizes with the actual \(t\)-based or model-based power method, not only the normal approximation.
• Sensitivity: Recalculate under plausible higher variability, lower correlation, and a planning ratio closer to an equivalence boundary.

A warning sign is a shared-subject calculation that predicts a large reduction in enrollment solely because measurements are “paired,” without specifying the variance of each contrast or its covariance. Another is reporting a high power for each strength while leaving the probability of passing them all unexamined. The normal approximation also becomes unreliable with small samples, uncertain variance estimates, or strongly imbalanced data; rounding the normal result does not remove those limitations.