Comparing Study Designs at a Fixed Budget

Why Compare Designs at a Fixed Budget?

A design that uses fewer participants is not automatically the best use of a study budget. A crossover study exposes each participant to both formulations, which can improve precision by removing stable between-participant differences. A replicate design adds treatment periods, however, and can estimate some within-participant variability that a conventional crossover cannot separate. A parallel study avoids repeated periods but usually needs more participants to achieve similar precision.

A useful comparison therefore asks two questions together: How much power does the budget buy, and what variance information does the design make estimable? The numerical comparisons below concern a log-transformed pharmacokinetic endpoint and average bioequivalence (ABE). They are planning approximations, not universal rankings: the answer depends on the assumed variance structure, equivalence limits, period costs, and the target estimand.

Definition: A parallel design assigns each participant to one formulation. A crossover design gives each participant both formulations in different periods. A replicate design repeats at least one formulation within participants; a partial replicate repeats the reference formulation, while a full replicate repeats both test and reference.

Variance Information and Standard Errors

Consider an idealized model for a log-transformed endpoint \(Y\). Let \(\mu_T-\mu_R=\delta\) be the population mean contrast of test versus reference. Suppose a participant has a stable random effect \(b_i\), with variance \(\tau^2\), and each period has an independent residual \(e_{ij}\), with variance \(\sigma^2\). Thus an observation on formulation \(f\) is represented as \(Y_{ij}=\mu_f+b_i+e_{ij}\). For this derivation, assume randomized and balanced treatment allocation, no carryover, no treatment-by-period interaction, and a correctly specified analysis. Period effects can be included in a real analysis; the simple formulas below presume they are absent or adequately adjusted for.

In a parallel design, the treatment groups contain different participants, so the stable participant effect does not cancel. With \(n_T\) and \(n_R\) participants in the two groups, the contrast variance is \((\tau^2+\sigma^2)(1/n_T+1/n_R)\). In a two-period crossover, each participant contributes a test-reference difference. The stable effect cancels, and independent period residuals give a difference variance of \(2\sigma^2\); with \(n\) participants, the contrast variance is \(2\sigma^2/n\).

In a three-period partial replicate, each participant receives test once and reference twice. Under the same idealized assumptions, compare the test observation with the participant’s mean of two reference observations. The stable effect again cancels. The residual variance of that within-participant contrast is \(\sigma^2+\sigma^2/2=1.5\sigma^2\), so its mean across \(n\) participants has variance \(1.5\sigma^2/n\). This calculation assumes balanced sequences and no unadjusted period effects; actual standard errors should come from the planned analysis model.

Key distinction: A conventional two-period crossover can estimate the treatment contrast efficiently, but with only one observation per formulation per participant it does not separately identify formulation-specific within-subject variances. A partial replicate supplies repeated reference observations and can estimate reference within-subject variance. A full replicate can supply repeated observations for both formulations, allowing estimation of both formulation-specific within-subject variances under an appropriate model.

Worked Example: Deriving the Replicate Contrast Variance

Suppose one participant in a three-period partial replicate has log outcomes \(Y_T\), \(Y_{R1}\), and \(Y_{R2}\). Under the stated random-intercept model, the within-participant contrast is \(D=Y_T-(Y_{R1}+Y_{R2})/2\). Substituting the model gives

D=\delta+e_T-\frac{e_{R1}+e_{R2}}{2}.

The participant effect \(b_i\) has canceled. If the three residuals are independent with common variance \(\sigma^2\), then

\operatorname{Var}(D) =\sigma^2+\frac{1}{4}(\sigma^2+\sigma^2) =1.5\sigma^2.

For \(n\) independent participants with the same contrast variance, the mean contrast has variance \(1.5\sigma^2/n\), and its standard error is \(\sqrt{1.5\sigma^2/n}\). This is an idealized derivation; sequence, period, and any additional random effects must be reflected in a real study’s analysis.

Power Comparison Under a Fixed Period Budget

For ABE, the usual log-scale equivalence limits are \(-\Delta\) and \(+\Delta\), where \(\Delta=\log(1.25)\approx0.2231\). The two one-sided tests procedure at significance level \(\alpha=0.05\) declares equivalence when the corresponding 90% confidence interval for \(\delta\) lies wholly within those limits. For a transparent design comparison, assume the true contrast is zero and treat each standard error as known. The normal approximation to power is then

\text{Power}\approx \max\left\{0,\;2\Phi\left(\frac{\Delta}{SE}-z_{0.95}\right)-1\right\}, \qquad z_{0.95}=1.645.

This expression is the probability that the estimated contrast falls between the two limits after accounting for the one-sided critical value. It is a planning approximation: finite-sample analyses generally use estimated variances and \(t\)-based critical values, and their power should be calculated using the planned model or simulation.

Worked Example: Comparing Designs With 120 Treatment Periods

Assume, hypothetically, that each treatment period has the same cost and the budget permits 120 periods. Compare a parallel study with 60 participants per group, a two-period crossover with 60 participants, and a three-period partial replicate with 40 participants. Let the stable between-participant standard deviation on the log scale be \(\tau=0.25\), and the residual standard deviation be \(\sigma=0.35\). Assume the true formulation ratio is 1, so \(\delta=0\), and use the normal approximation above.

Parallel. Each observation has variance \(\tau^2+\sigma^2=0.25^2+0.35^2=0.1850\). With \(n_T=n_R=60\),

SE=\sqrt{0.1850\left(\frac{1}{60}+\frac{1}{60}\right)} =\sqrt{0.0061667} =0.07853.

Thus \(\Delta/SE-z_{0.95}=0.2231/0.07853-1.645=2.841-1.645=1.196\). Approximate power is \(2\Phi(1.196)-1\approx2(0.884)-1=0.768\), or about 76.8%.

Two-period crossover. The stable participant effect cancels, giving

SE=\sqrt{\frac{2(0.35^2)}{60}} =\sqrt{0.0040833} =0.06390.

Here \(\Delta/SE-z_{0.95}=0.2231/0.06390-1.645=3.491-1.645=1.846\). Approximate power is \(2\Phi(1.846)-1\approx2(0.9676)-1=0.935\), or about 93.5%.

Three-period partial replicate. There are 40 participants, each contributing three periods:

SE=\sqrt{\frac{1.5(0.35^2)}{40}} =\sqrt{0.0045938} =0.06778.

Then \(\Delta/SE-z_{0.95}=0.2231/0.06778-1.645=3.292-1.645=1.647\). Approximate power is \(2\Phi(1.647)-1\approx2(0.9502)-1=0.900\), or about 90.0%.

Under these assumptions, the crossover has the greatest approximate power per 120 treatment periods, followed by the partial replicate and parallel designs. This ranking is not intrinsic to the design labels: it follows from the specified variance components, period costs, and model. The replicate also provides repeated-reference information that the crossover and parallel study do not provide in this setup.

Which Variances Must Be Known or Estimable?

A power calculation needs variance inputs that match the design and estimand. For the idealized parallel comparison above, the relevant observation variance is \(\tau^2+\sigma^2\). For a conventional crossover, the treatment-difference variance depends on within-subject residual variability, not the total between-person spread. Applying a parallel-study standard deviation to a crossover calculation, or vice versa, can substantially distort the estimated power.

The required variance information also depends on the bioequivalence question. For average bioequivalence, a treatment contrast and its uncertainty are central. Population and individual bioequivalence can require additional variance components; their planning may therefore favor a replicate design when the needed components are not otherwise available. The earlier material on replicate design planning for individual bioequivalence treats those design-specific requirements in more detail.

Worked Example: What Repeated Reference Doses Estimate

Suppose, hypothetically, 18 participants in a partial replicate each receive reference twice. After appropriate adjustment for period, the sample standard deviation of the within-participant log-reference differences is \(s_D=0.500\). Under independent, equal-variance residuals, a difference between two reference observations has variance \(2\sigma_{wR}^2\), where \(\sigma_{wR}^2\) is the reference within-subject variance. Therefore,

\widehat{\sigma}_{wR}^2=\frac{s_D^2}{2} =\frac{0.500^2}{2} =\frac{0.2500}{2} =0.1250, \qquad \widehat{\sigma}_{wR}=\sqrt{0.1250}=0.3536.

This estimate is based on repeated reference observations and is useful only under the model assumptions stated. It estimates reference within-subject variability, not test within-subject variability. A full replicate, with both formulations repeated, can provide the observations needed to estimate both formulation-specific within-subject variances. The value \(0.3536\) is a point estimate; with only 18 participants, uncertainty in that estimate should also be considered in planning.

Budget, Diagnostics, and Design Limitations

A “fixed budget” can mean fixed enrollment, fixed treatment periods, or fixed total cost. These are different constraints. The numerical comparison used equal cost per treatment period and ignored recruitment, screening, washout, sampling, assay, and analysis costs. If a crossover requires long washouts or expensive additional visits, its cost advantage can shrink. If participant recruitment is the main bottleneck but period costs are modest, extra periods per participant may be attractive. Recalculate the comparison using the actual cost components rather than assuming that every period costs the same.

Before relying on a comparison, check that the assumed design can estimate the target contrast and all variance components needed for the intended decision. Review sequence balance, the number of participants contributing to each sequence, period effects, missing periods, and plausible carryover. A treatment contrast can be poorly identified if formulation and period are confounded. Dropout can also undermine the assumed balance and reduce information, especially in crossover designs where a participant’s paired contribution may be lost if a period is missing.

An important limitation of the simple power formula is that it treats \(SE\) as fixed. In a real study it is estimated, degrees of freedom may differ across designs, and a small-sample \(t\) critical value is typically larger than 1.645. Uncertain variance inputs can make a plug-in power estimate optimistic. Where the design or variance model is complex, simulation under the planned analysis is a more defensible comparison; simulation precision and variance uncertainty should be represented rather than hidden by a single assumed value.

Common pitfall: “The crossover has fewer participants, so it is always cheaper and more powerful.” This reasoning ignores the within-subject variability, period and washout costs, dropout, and whether repeated formulations are needed to estimate variance components. Compare designs under the same explicit budget, model, and estimand, then check that each design supplies the information required for the scientific question.

Choosing Among the Main Approaches

Design	Potential advantage	Important limitation
Parallel	No repeated periods or within-participant carryover; each participant receives one formulation.	Stable between-participant variation contributes to the treatment-contrast variance; generally needs more participants for a given precision.
Two-period crossover	Within-participant comparison removes stable participant effects and can be efficient for the treatment contrast.	Requires suitable washout and period assumptions; one observation per formulation does not separately estimate formulation-specific within-subject variances.
Partial replicate	Retains within-participant comparisons and estimates reference within-subject variability from repeated reference doses.	Uses more periods per participant; does not by itself provide repeated test observations for estimating test-specific within-subject variance.
Full replicate	Can estimate within-subject variability for both formulations under an appropriate model.	More treatment periods and operational complexity can increase cost and participant burden.

No design is best independently of its objective. A useful decision sequence is to specify the estimand and required variance components, identify which designs can estimate them, then compare power and feasibility under the actual budget. If two designs have similar power, the one with simpler conduct or more relevant variance information may be preferable; if a design cannot estimate a required component, a favorable power number for a different estimand does not repair that gap.

Check Your Understanding

Answer each question using the design assumptions and formulas discussed above. Brief solutions follow.

With \(\tau^2=0.04\), \(\sigma^2=0.09\), and 40 participants per group, what is the idealized standard error of the parallel treatment contrast?
Why can a two-period crossover be more precise than a parallel study even when both use the same number of participants?
In a partial replicate, which within-subject variance can be estimated directly from repeated doses, and which cannot?
Under a fixed treatment-period budget, name two reasons the design with the largest approximate power might not be the preferred design.

Solutions. (1) \(SE=\sqrt{(0.04+0.09)(1/40+1/40)}=\sqrt{0.0065}=0.08062\) log units. (2) The crossover contrast subtracts two observations from the same participant, so a stable participant effect cancels; the parallel contrast includes between-participant variation. This advantage depends on the crossover assumptions being credible. (3) Repeated reference doses permit estimation of reference within-subject variance; a partial replicate with test given once does not directly estimate test-specific within-subject variance. (4) The highest-power design may cost more once visits and washouts are included, may have greater dropout or operational risk, or may fail to estimate variance components needed for the target question.