Sample Size for Replicate Crossover Average Bioequivalence

Why Replication Changes the Sample-Size Calculation

A replicate crossover gives participants more than one exposure to at least one treatment. That repetition can make a study more informative about within-subject variability, but it also changes the variance of the estimated test-to-reference contrast. A sample-size calculation that uses the two-period crossover variance without adjustment can therefore be too large or too small for the planned replicate layout.

The planning target is usually the log-scale mean treatment difference for a pharmacokinetic endpoint such as AUC or Cmax. Average bioequivalence is assessed by testing whether this difference lies within prespecified log-scale limits. Sample size depends on how far the expected difference is from those limits, the target power and significance level, and the variance of the contrast under the particular crossover design.

For the common limits corresponding to ratios 0.80 and 1.25, \(L=\ln(0.80)\approx-0.22314\) and \(U=\ln(1.25)\approx0.22314\). If the expected test-to-reference ratio is \(GMR\), the planning value of the log difference is \(\theta=\ln(GMR)\). The calculation below assumes that the limit, expected ratio, and variability refer to the same log-transformed endpoint.

Deriving the Replicate-Design Variance

Consider a simple within-subject error model on the log scale. Each observed value consists of a treatment mean, any modeled period contribution, and a within-subject error. Assume the within-subject errors from distinct periods are independent, have mean zero, and share variance \(\sigma_w^2\). The treatment contrast uses averages of a subject’s observations under test and reference, so its error variance is the sum of the variances of those two averages. This is the key design-specific step.

Here \(r_T\) and \(r_R\) are the number of test and reference observations contributing to the subject-level contrast. The calculation assumes equal within-subject variances for the two treatments. If the design or planning model allows treatment-specific variances or a different covariance structure, use the variance of the actual contrast under that model instead.

In a fully replicated four-period design, such as TRTR/RTRT, each subject receives test twice and reference twice. Thus \(r_T=r_R=2\), giving \(v_D=\sigma_w^2\). In a partially replicated three-period design, such as TRR/RTR/RRT, test is observed once and reference twice. Thus \(v_D=\sigma_w^2+\sigma_w^2/2=1.5\sigma_w^2\). By contrast, in a two-period crossover each treatment is observed once, so the corresponding variance is \(2\sigma_w^2\). These factors are not interchangeable.

When variability is supplied as a within-subject coefficient of variation \(CV_w\), convert it to log-scale variance using \(\sigma_w^2=\ln(1+CV_w^2)\), with \(CV_w\) expressed as a proportion. Then apply the design-specific multiplier. This distinction matters: using \(\sigma_w^2\) directly as the contrast variance in a two-period crossover would omit a factor of two, while applying that same factor to a fully replicated contrast would overstate its variance under the stated model.

Approximate Sample-Size Calculation

For a planning approximation, treat the estimated log treatment difference as normally distributed with mean \(\theta\) and standard error \(SE=\sqrt{v_D/N}\). At significance level \(\alpha\), average bioequivalence is declared when the estimate is sufficiently far from both limits. Under this approximation, the probability of passing both one-sided tests is

Here \(\Phi\) is the standard normal cumulative distribution function, and \(z_q\) is its \(q\) quantile. The first term is the probability of satisfying the upper-bound test; subtracting the second term removes the probability of failing the lower-bound test. For a centered expectation \(\theta=0\) and symmetric limits \((- \Delta,\Delta)\), this simplifies to \(2\Phi(\Delta/SE-z_{1-\alpha})-1\). Solving for the approximate sample size at target power \(1-\beta\) gives

The \(z_{1-\beta/2}\) quantile appears because power is the probability of passing both one-sided tests: at the centered value, each tail of the acceptance event receives half of the total non-equivalence probability. The expression is an initial normal approximation, not a guarantee that the final integer sample size will attain the target under a finite-sample analysis. In practice, evaluate candidate integer sample sizes using the planned model and an appropriate finite-sample power calculation; also respect the design’s sequence allocation.

When the Expected Ratio Is Not One

A nonzero expected log difference reduces the distance to one equivalence limit and increases the required sample size. The centered closed-form expression no longer applies directly; use the two-term power expression and examine integer candidate sizes. The following example illustrates why sequence balance can affect the final planned total even when the normal approximation is used.

Assumptions, Checks, and Alternatives

These calculations are only as credible as their assumptions and inputs. The design must be specified correctly, including which treatments are repeated and how sequences are allocated. The within-subject variability must be relevant to the endpoint, population, and study conditions being planned. The simple variance derivation assumes independent period errors with a common variance; period and sequence effects must be handled by the analysis model rather than confused with within-subject error. The expected log ratio and equivalence limits must also be stated on the same scale.

A practical workflow is to identify the treatment contrast and its replication pattern, derive or obtain its variance under the planned model, convert any coefficient of variation to log-scale variance, and calculate power across feasible sequence-balanced totals. Then verify the selected total using a finite-sample method consistent with the planned analysis. Degrees of freedom, variance estimation, and the test statistic can make exact or model-based power differ from the normal approximation, especially at small sample sizes.

Diagnostics for a planning calculation are mostly checks on inputs and structure. Verify that the CV is entered as a proportion, that the logarithm is natural, and that the contrast-variance multiplier matches the replicate layout. Check whether rounding for sequence balance changes the candidate total, and inspect power at the selected total and the preceding feasible total. If the required sample size changes sharply under modest changes in CV or expected ratio, report that sensitivity rather than presenting one planning number as certain.

The two-period crossover is the main alternative when replication is not required: its contrast variance is \(2\sigma_w^2\) under equal within-subject variances. A fully replicated design has contrast variance \(\sigma_w^2\), while the stated partially replicated design has \(1.5\sigma_w^2\). Replication can therefore improve precision for the treatment contrast under these assumptions, while also requiring additional periods and a design-specific allocation and analysis. These variance comparisons alone do not establish which design is preferable; feasibility, burden, and the study’s objectives also matter.

A common mistake is to take a CV-derived \(\sigma_w^2\) and use \(2\sigma_w^2\) for every crossover, or to use \(\sigma_w^2\) as though it were always the contrast variance. The correction is to count the observations contributing to each treatment average and calculate the contrast variance under the planned covariance model. Another mistake is to round a normal-approximation result upward and call it the final required sample size. It is only a candidate: sequence balance and finite-sample power still need checking.