Choosing a Target Power Under Planning Uncertainty

Why the Power Target Is a Design Choice

A sample size calculation does not produce a uniquely correct enrollment until the planner specifies a target power. A higher target generally requires more evaluable participants, which costs more and may extend recruitment. A lower target saves resources but leaves a greater chance that a study will not demonstrate equivalence even when the assumed treatment effect and variability are correct. Choosing a target is therefore a decision about the consequences of these competing risks, not a purely mathematical convention.

The earlier material on Defining the Power Target for Equivalence Studies establishes the role of power in an equivalence design. Here the emphasis is how to choose among common targets when planning assumptions are uncertain. A target such as 80%, 90%, or 95% is not a guarantee about a particular study, nor is it the probability that a regulator will accept its results. It is the desired probability of meeting the specified statistical success criterion under a stated model and set of assumed inputs.

Definition: The target power is the planned minimum probability of rejecting the relevant null hypothesis under a specified alternative, using the intended design, analysis, significance level, and assumed parameter values. The achieved power is the power calculated for a particular sample size and those same assumptions. It is conditional on the assumptions being correct.

For average bioequivalence, success is ordinarily assessed using two one-sided tests (TOST): the confidence interval for the test-to-reference effect must lie within the prespecified equivalence limits. Thus, a power target concerns the probability of satisfying both one-sided requirements, not the probability of passing just one. The calculations below use a normal approximation to make the comparison transparent. Operational planning should use the power method appropriate to the planned analysis; when exact TOST power is required, use the exact method rather than treating this approximation as exact.

A Planning Model for Comparing Targets

Let $\theta$ be the true mean test-minus-reference difference on the log scale, $M$ the symmetric log equivalence limit, $\sigma$ the standard deviation of within-subject log differences, and $n$ the number of evaluable participants in a two-period crossover design. The standard error in this planning approximation is $SE=\sigma/\sqrt{n}$. With one-sided significance level $\alpha=0.05$, the normal critical value is $z_{1-\alpha}=1.6449$.

For the numerical comparison, assume the true effect is $\theta=-\delta$, where $\delta>0$. Under the normal approximation, the TOST power is the probability that the estimated effect falls between the two rejection boundaries:

\text{Power}(n) = \Phi\left(\frac{M-\delta}{SE}-z_{1-\alpha}\right) + \Phi\left(\frac{M+\delta}{SE}-z_{1-\alpha}\right)-1.

Here $\Phi$ is the standard normal cumulative distribution function. This expression accounts for both one-sided tests. The second term is not omitted just because it may be small: when the estimated effect can approach the opposite equivalence boundary, that boundary also affects the probability of success.

Assumptions for this illustration: the design is a two-period crossover; $n$ counts evaluable participants; within-subject log differences are normally distributed with known planning standard deviation $\sigma$; the treatment effect and equivalence limits are fixed at their assumed values; the tests use $\alpha=0.05$; and there are no other sources of failure, such as nonevaluable profiles. These assumptions define a planning calculation, not a claim that real studies are free of uncertainty.

The normal model makes power increase as $n$ increases: $SE=\sigma/\sqrt{n}$ decreases, so the rejection region captures a larger fraction of the assumed sampling distribution. Since enrollment is integer-valued, the practical rule is to choose the smallest $n$ whose calculated power meets or exceeds the target. A sample size just below that value should be checked as well; rounding a noninteger estimate down can miss the target.

Worked Comparison of Common Targets

Worked Example: Selecting the Minimum Sample Size for Each Target

Suppose a hypothetical two-period crossover study uses equivalence limits of $0.80$ to $1.25$, a planned true test-to-reference ratio of $1.0526$, and a within-subject standard deviation of $\sigma=0.4000$ on the log scale. The log upper limit is $M=\ln(1.25)=0.22314$, and the assumed effect magnitude is $\delta=\ln(1.0526)=0.05126$. Use $\alpha=0.05$ and the normal approximation above.

For each candidate $n$, calculate $SE=0.4000/\sqrt{n}$, substitute it into the power expression, and check the adjacent smaller integer. For $n=47$, $SE=0.05835$, and:

\begin{aligned} \text{Power}(47) &= \Phi\left(\frac{0.22314-0.05126}{0.05835}-1.6449\right) + \Phi\left(\frac{0.22314+0.05126}{0.05835}-1.6449\right)-1\\ &\approx \Phi(1.301)+\Phi(3.058)-1\\ &\approx 0.9022. \end{aligned}

At $n=46$, the same calculation gives power approximately $0.897$, below 90%. Thus 47 evaluable participants is the minimum integer for a 90% target under these assumptions.

Applying the same calculation to the other targets gives the following checks. At $n=34$, power is approximately $0.796$, while at $n=35$ it is approximately $0.807$; the 80% target therefore requires 35. At $n=58$, power is approximately $0.948$, while at $n=59$ it is approximately $0.951$; the 95% target requires 59. These are approximate normal-model results, reported to three significant figures.

Target power	Minimum evaluable $n$	Power at selected $n$	Power at $n-1$
80%	35	0.807	0.796
90%	47	0.902	0.897
95%	59	0.951	0.948

The table shows the marginal cost in evaluable sample size of the higher targets: moving from 80% to 90% adds 12 participants, and moving from 90% to 95% adds another 12. Those increments are specific to the assumed effect, variability, limits, and approximation; they are not universal conversion factors.

Balancing Cost and the Consequences of Failure

The same sample-size difference can have different importance in different settings. A modest increase may be justified when a failed study would lead to substantial delays, repeat manufacturing work, or loss of a development opportunity. Conversely, a very large increase may not be reasonable if the extra precision has limited value for the decision and recruitment is difficult. Cost should be considered alongside the scientific and operational consequences of failing to meet the equivalence criterion.

Worked Example: Translating a Target Into a Hypothetical Budget

Suppose, purely for illustration, a hypothetical study has a fixed cost of \$60,000 and a variable cost of \$3,000 for each evaluable participant. Using the sample sizes above, total costs are calculated as fixed cost plus variable cost multiplied by $n$.

At the 80% target, the cost is $\$60{,}000+35(\$3{,}000)=\$165{,}000$. At 90%, it is $\$60{,}000+47(\$3{,}000)=\$201{,}000$. At 95%, it is $\$60{,}000+59(\$3{,}000)=\$237{,}000$. In this hypothetical budget, each increase from one target to the next costs an additional \$36,000.

The arithmetic does not identify the best target by itself. If a failed study would cost much more than \$36,000 in delay and repetition, the higher target may be economically defensible. If recruitment is exceptionally burdensome and a later study is feasible, a lower target might be considered, provided the risks and rationale are explicit. These comparisons should use realistic study-specific costs rather than treating the illustrative amounts as typical.

Power also gives a conditional failure probability: under the model and assumed effect, it is $1-\text{Power}$ that a study does not meet its statistical success criterion. This is not the probability that the treatment is not bioequivalent. It is a repeated-sampling statement conditional on the assumptions.

Worked Example: Comparing Conditional Failure Risks

Using the achieved powers in the table, the approximate probability of not demonstrating equivalence is $1-0.807=0.193$ at the 80% target, $1-0.902=0.098$ at the 90% target, and $1-0.951=0.049$ at the 95% target. In repeated studies conducted under the same assumed conditions, these correspond to about 19.3%, 9.8%, and 4.9% that the statistical criterion is not met.

This comparison is useful only when its conditions are kept in view. It does not include the chance that the true effect or variability differs from the planning values, and it does not include other operational causes of an unsuccessful study. A target-power choice addresses one source of risk: sampling variability under a specified model.

Planning Uncertainty: Stress-Test the Choice

A nominal target is only as informative as its inputs. In a crossover calculation, power depends especially on the expected treatment effect relative to the equivalence limits and on within-subject variability. A planning choice should therefore be checked against plausible alternatives, not only evaluated at a single best guess. The purpose of this stress test is to show how sensitive the design is; it is not a formal probability distribution over uncertain inputs.

Worked Example: A Larger Variability Than Planned

Suppose the 90% target calculation above was based on $\sigma=0.4000$, giving $n=47$. Consider a plausible planning scenario with $\sigma=0.4400$, while holding the effect, limits, and significance level fixed. Under this normal approximation, maintaining the same standard error requires $n/\sigma^2$ to remain constant. Scaling the sample size gives:

n_{\text{new}} \approx 47\left(\frac{0.4400}{0.4000}\right)^2 = 56.87.

Rounding up gives 57 evaluable participants. The rounding direction matters: 56 does not preserve the original standard error, because $56(0.4000/0.4400)^2\approx46.28$, below the 47-participant reference calculation. Thus a design planned for 90% power at $\sigma=0.4000$ would not retain that target under the larger-variability scenario. This scaling is a normal-approximation sensitivity calculation, not a substitute for recalculating power with the final planned analysis.

The assumed effect also matters. If the true ratio is closer to 1.00 than the planned ratio of 1.0526, the effect lies farther from the equivalence boundaries and power will generally be higher at the same $n$. If the true ratio is farther from 1.00 but remains inside the limits, power can be lower. A robust planning discussion should state which plausible effect and variability scenarios were examined and whether the selected $n$ remains acceptable in them.

This does not mean that planners should always size the study for the most extreme conceivable inputs. An implausibly pessimistic scenario can make a study infeasible without improving the decision. Instead, the design rationale should distinguish the primary assumptions from credible stress scenarios and explain what risk the chosen target is intended to manage.

Choosing Among Targets and Recognizing Limits

A practical decision considers at least three issues: the consequences of a study that does not demonstrate equivalence, the incremental resources needed for a higher target, and the credibility of the assumed effect and variability. A higher target is more compelling when a false start is costly, when repeating the study would be difficult, or when uncertainty in the assumptions could materially reduce power. A lower target may be defensible when resources are constrained and the consequences of failure are manageable, but it should not be selected merely because it produces a convenient sample size.

There is no universal rule that 80%, 90%, or 95% is always the correct target for every bioequivalence study. Regulatory expectations and the protocol-specific design must be considered. A target power does not replace prespecified equivalence limits, appropriate analysis, adequate conduct, or interpretation of the resulting confidence interval. Nor does 95% power mean a 95% probability of regulatory approval: approval depends on the study results and the broader evidential and regulatory context.

The normal approximation used here is also a limitation. It treats the planning standard deviation as known and uses a normal critical value. In an actual study, the analysis may use a $t$ distribution and an estimated variance, and exact power can differ, particularly at smaller sample sizes. Use the calculation method that matches the planned analysis and verify the final integer sample size with that method. Further issues such as uncertainty in the variance estimate, formal adaptation, joint endpoints, and attrition require their own planning methods; they are not resolved simply by choosing a higher target.

A common mistake is to say, “If I choose 90% power, there is a 90% chance this study will succeed.” That statement drops the conditions. The correction is: if the assumed effect, variability, design, analysis, and other model conditions hold, the planned study has approximately a 90% probability of meeting its statistical success criterion under the specified alternative. If those assumptions are wrong, achieved power can be lower or higher. This is why target selection and sensitivity analysis belong together.

Key takeaway: Choose a target power by weighing the cost of additional evaluable participants against the consequences of a failed study, then stress-test the choice under plausible planning scenarios. Report the assumptions and the method used; a target is a conditional design objective, not a guarantee of success.

Check Your Understanding

Answer each question, then compare with the solutions below.

In the worked comparison, why was 47 rather than 46 selected for a 90% target?
Under the stated assumptions, what is the approximate conditional probability of not demonstrating equivalence with 90% target power?
If the planned standard deviation increases from 0.4000 to 0.4400, why does the approximate sample size increase by a factor related to the square of the ratio of standard deviations?
Does a 95% target power mean a 95% probability that a regulator will accept the study? Explain.
Name two planning assumptions that should be stress-tested when choosing a target power for a crossover bioequivalence study.

Solutions. (1) At $n=46$, power is approximately 0.897, below 0.900; at $n=47$, it is approximately 0.902, so 47 is the smallest checked integer meeting the target. (2) The conditional probability is approximately $1-0.902=0.098$, or 9.8%, given the model and assumed inputs. (3) Since $SE=\sigma/\sqrt{n}$, preserving the same standard error requires $\sigma/\sqrt{n}$ to stay constant, so $n$ must scale with $\sigma^2$. (4) No. Power is the probability of meeting the statistical criterion under specified assumptions; regulatory acceptance depends on the results and broader context. (5) Examples include the expected test-to-reference effect and the within-subject variability. Both can materially change power if they differ from the planning values.