What a Re-Estimation Output Needs to Show
A revised enrollment number is not self-validating. Its meaning depends on the nuisance estimate that produced it, the assumptions connecting that estimate to the planning model, and the sequence of rounding and attrition adjustments. A useful diagnostic therefore works backward: can the reported sample size be reproduced from the stated inputs, and do those inputs describe the trial as it is actually being run?
In blinded re-estimation, the aim is to update nuisance quantities—such as a standard deviation, pooled event rate, or intraclass correlation—without using a treatment-specific interim effect estimate to change the target effect. The target effect and the design assumptions must be specified independently of the observed nuisance estimate. Earlier material on blinded pooled-rate estimation, masked variance estimation, and cluster design effects provides the relevant component calculations; here the focus is auditing their combined output.
The report should distinguish analyzable participants from participants to enroll. If a required analyzable count is \(n\) per arm and the anticipated proportion retained for analysis is \(r\), the enrollment target per arm is \(\lceil n/r\rceil\). For cluster trials, the number of clusters, cluster size, and any participant-level attrition adjustment must also be stated; a rounded total alone is not enough to reproduce the design.
A Compact Audit Sequence
Confirm the target effect, type I error, power, allocation ratio, analysis, and whether the reported count is per arm or total. A blinded nuisance update does not, by itself, justify changing the target effect.
Verify its source, scale, timing, and calculation. Ask whether masking, treatment-effect contamination, sparse outcomes, site differences, or unequal cluster sizes could make the estimate unsuitable.
Substitute the reported values into the stated formula. Check the units and the arithmetic before applying any floor, cap, attrition adjustment, or rounding rule.
Recalculate over a reasonable range of nuisance values. Report how the proposed enrollment changes, and investigate a result that is unexpectedly insensitive or highly sensitive.
For a simple two-arm normal-approximation calculation with equal allocation, known or planning standard deviation \(\sigma\), target difference \(\delta\), two-sided significance level \(\alpha\), and power \(1-\beta\), the required analyzable number per arm is approximately
This follows because the variance of the difference between two independent arm means is \(2\sigma^2/n\). Under the target difference, the standardized signal is \(\delta/\sqrt{2\sigma^2/n}\). Setting that signal to the sum of the two-sided critical value and the power quantile, then squaring and rearranging, gives the displayed expression. The approximation assumes independent participants, a common within-arm variance, equal allocation, a normal-based test, and a suitable variance estimate. Material departures—such as marked site heterogeneity or a small-sample analysis requiring a larger critical value—need to be reflected in the planning calculation, not dismissed after the fact.
Worked Example: Auditing a Continuous-Outcome Update
Suppose a hypothetical two-arm trial plans to detect a difference of 5 points on a continuous outcome, with a two-sided \(\alpha=0.05\), 80% power, equal allocation, and 10% anticipated attrition. A blinded interim variance calculation reports \(s=12\) points. Assume the data are independent across participants, the pooled estimate is appropriate for the common planning variance, and the normal approximation is suitable.
The standard normal quantiles are \(z_{0.975}=1.960\) and \(z_{0.80}=0.8416\). Thus the coefficient is \(2(1.960+0.8416)^2=15.6979\), and the analyzable requirement is
Rounding up gives 91 analyzable participants per arm, or 182 total. To allow for 10% attrition, \(r=0.90\), so the enrollment target is \(\lceil91/0.90\rceil=102\) per arm, or 204 total. A report proposing 91 enrolled per arm has not made the attrition adjustment.
Now test sensitivity to a plausible interim standard deviation of 13.5 points, keeping the other assumptions fixed:
This requires 115 analyzable participants per arm and \(\lceil115/0.90\rceil=128\) enrolled per arm. The increase from 102 to 128 enrolled per arm is consistent with the fact that required sample size is proportional to the variance, \(\sigma^2\), not to \(\sigma\). A diagnostic should also ask whether the interim standard deviation was computed on the correct scale and whether large site-to-site differences make a single pooled standard deviation misleading.
Binary Outcomes: Check the Rate and the Target Effect Separately
For a binary outcome, a blinded pooled event rate can inform the variance of a planned risk-difference comparison, but it is not an estimate of the treatment effect. The risk difference used for planning remains the prespecified target. One normal-approximation formula, for equal allocation and a target risk difference \(\delta\), uses a common rate \(p\) under the null and alternative rates \(p_1=p-\delta/2\) and \(p_2=p+\delta/2\):
Here \(n\) is the analyzable number per arm. The formula assumes independent binary outcomes, equal allocation, probabilities within \([0,1]\), and a normal approximation adequate for the event counts. When events are rare or the expected counts are small, this approximation can be unreliable; a rare-event method or a design-specific calculation may be needed. The pooled rate’s construction must also be appropriate: a blinded pooled rate can be shifted by a true arm difference, so the analyst should check whether the estimation method addresses the contamination relevant to the design.
Worked Example: Checking a Pooled-Rate Sensitivity Analysis
Consider a hypothetical equal-allocation trial with a prespecified target risk difference of 0.15, two-sided \(\alpha=0.05\), and 80% power. Suppose the blinded nuisance estimate is \(p=0.38\). For this calculation, assume it is an appropriate estimate of the common planning rate, and that the normal approximation is reasonable. The planning alternatives are \(p_1=0.38-0.075=0.305\) and \(p_2=0.38+0.075=0.455\), both valid probabilities.
The null component is \(1.960\sqrt{2(0.38)(0.62)}=1.960\sqrt{0.4712}\approx1.3454\). The alternative component is \(0.8416\sqrt{(0.305)(0.695)+(0.455)(0.545)}=0.8416\sqrt{0.45995}\approx0.5708\). Therefore,
The requirement is 164 analyzable participants per arm. With 10% attrition, the enrollment proposal is \(\lceil164/0.90\rceil=183\) per arm, or 366 total. The calculation uses the pooled rate for variance, while the target risk difference remains 0.15; replacing 0.15 with an interim treatment contrast would no longer be this blinded nuisance re-estimation.
A useful sensitivity check changes \(p\) while holding the target effect and other design assumptions fixed. At \(p=0.30\), the planning rates are 0.225 and 0.375. Substitution gives
or 146 analyzable and \(\lceil146/0.90\rceil=163\) enrolled per arm. At \(p=0.45\), the planning rates are 0.375 and 0.525, and
or 172 analyzable and \(\lceil172/0.90\rceil=192\) enrolled per arm. Across these plausible pooled rates, the enrollment range is 163–192 per arm. That sensitivity is substantive and should be visible in the report. It does not show that the treatment effect is changing; it shows how the variance and resulting sample size depend on the nuisance rate.
Cluster Trials: Follow the Inflation and the Rounding
In a cluster trial, outcomes within the same cluster are generally correlated, so treating every participant as independent understates the variance. For approximately equal cluster size \(m\) and intraclass correlation \(\rho\), the design effect is
A basic approximation multiplies the individually randomized requirement by \(DE\), then converts the resulting participant count to whole clusters. This method assumes the chosen \(m\) and \(\rho\) are relevant, clusters are approximately equal in size, and the design effect adequately represents the clustering. It does not automatically account for all small-number-of-clusters effects, unequal cluster sizes, or cluster-level attrition. Those features may require a more suitable power calculation.
Worked Example: Auditing a Cluster-Trial Proposal
Suppose the continuous-outcome trial in the first example is instead cluster randomized. Use its unrounded individual-level requirement of 90.420 per arm. Assume an interim blinded ICC estimate of \(\rho=0.04\), 20 analyzable participants per cluster, equal numbers of clusters per arm, and no whole-cluster loss. The proposed estimate and cluster size are assumptions to check, not facts guaranteed by masking.
The design effect is \(1+(20-1)(0.04)=1.76\). The adjusted requirement is \(90.420(1.76)=159.14\) analyzable participants per arm. Dividing by 20 gives \(159.14/20=7.957\) clusters per arm, so rounding up gives 8 clusters per arm. That provides 160 analyzable participants per arm, or 16 clusters and 320 analyzable participants overall.
If 15% participant-level attrition is expected, plan to enroll 24 participants per cluster: the expected retained number is \(24(0.85)=20.4\), slightly above the 20-person planning size. The proposed enrollment is therefore \(8(24)=192\) per arm, or 384 overall. This calculation assumes clusters remain in the study. If whole clusters may be lost, inflating only the participant count is inadequate; the cluster count must be adjusted as well.
The ICC deserves a sensitivity check because it enters the design effect directly. At \(\rho=0.02\), \(DE=1.38\), giving \(90.420(1.38)/20=6.239\), or 7 clusters per arm after rounding. At \(\rho=0.08\), \(DE=2.52\), giving \(90.420(2.52)/20=11.39\), or 12 clusters per arm. With 24 enrolled per cluster, those alternatives imply 336 and 576 participants overall, respectively. The large range signals that the ICC estimate is consequential. Also check whether the planned analysis has enough clusters for its inference method: a design-effect calculation alone does not establish that a normal approximation or large-sample test is adequate with only 14–24 clusters.
Failure Modes and Alternatives
A diagnostic output should make it possible to identify not only an arithmetic error, but also a mismatch between the calculation and the trial. Common warning signs include:
- Unclear denominators. The output says “sample size 200” without stating whether that means per arm or total, analyzable or enrolled, participants or clusters.
- Nuisance estimate on the wrong scale. A variance, standard deviation, event rate, or ICC is plugged into a formula that expects a different quantity.
- Unexamined contamination or heterogeneity. A pooled estimate is treated as automatically unbiased for planning despite a possible arm difference, site variation, or changing cluster composition.
- Rounding in the wrong direction. Required counts are rounded down, attrition is applied to the wrong denominator, or cluster size is treated as divisible when whole clusters are required.
- Precision beyond the data. A single interim nuisance estimate is reported as certain, even when sparse events or few clusters make it unstable.
The main alternatives answer different questions. A fixed sample size avoids interim nuisance updating but cannot respond to a material mismatch between assumed and observed variability. A blinded nuisance update changes the planned size using masked variability information while keeping the target effect fixed. An unblinded adaptive update can use treatment-specific interim information, but it raises different design and inferential issues and should not be conflated with blinded re-estimation. No method makes a poorly chosen nuisance estimate reliable; each requires assumptions suited to the endpoint, allocation, and analysis.
Sensitivity analysis is a diagnostic, not a license to choose whichever enrollment is most convenient. State a defensible range of nuisance values and show its effect on enrollment. If the proposal changes sharply, examine whether the interim estimate is stable enough and whether the selected planning value is defensible. If it barely changes when the formula implies it should, recheck the code, units, and rounding. Finally, distinguish sampling uncertainty in the estimate from operational constraints such as a prespecified floor or cap; a cap can limit enrollment, but it does not restore the planned power when the uncapped requirement is larger.
Check Your Understanding
Answer each question, then compare with the brief solutions below.
- A continuous-outcome update reports a standard deviation in centimeters, but the target difference is entered in millimeters. What should be checked before interpreting its sample size?
- In a binary trial, why should the blinded pooled rate and the prespecified target risk difference be identified separately?
- A cluster calculation requires 8.2 clusters per arm. How many clusters per arm should be planned, and why?
- At 15% attrition, how many participants should be enrolled per arm if 85 analyzable participants per arm are required?
- A cluster proposal reports a design-effect-adjusted participant count but no number of clusters. What essential diagnostic information is missing?
Solutions. (1) Convert both quantities to the same units before applying the formula; a mismatch by a factor of 10 in the effect scale can greatly distort the required sample size. (2) The pooled rate informs outcome variance, whereas the target risk difference defines the effect the design is intended to detect; substituting an interim treatment contrast changes the method. (3) Plan 9 clusters per arm because a fractional cluster cannot be enrolled and rounding down would fall short of the calculated requirement. (4) Enroll \(\lceil85/0.85\rceil=100\) per arm. (5) The rounded number of clusters per arm, cluster size, and resulting total enrollment are needed; participant totals alone conceal the discrete cluster rounding and may conceal inadequate cluster-level information.