Comparing Blinded And Unblinded Rules In A Worked Design

Why Compare the Rules in the Same Design?

A sample-size re-estimation rule can respond to uncertainty about nuisance parameters, such as outcome variance, or to interim evidence about the treatment effect. Those are different information sources. A blinded variance rule aims to revise the sample size without examining the treatment contrast; an unblinded conditional-power rule explicitly uses that contrast. Comparing them in one trial makes the distinction concrete, but neither rule can be judged from its formula alone. Its type I error, power, expected enrollment, and operational demands depend on the complete prespecified design.

The worked design below is hypothetical. It uses a continuous endpoint and equal allocation to two groups. The comparison is illustrative: the simulated operating characteristics are properties of the specified rules and assumptions, not universal values for blinded or unblinded re-estimation.

Model, Rules, and Assumptions

Suppose the endpoint is measured in points, and outcomes in the two groups are independent normal observations with a common variance \(\sigma^2\). The treatment effect is the treatment-group mean minus the control-group mean. There are no interim efficacy or futility stops, no changes to the endpoint or target contrast, and no losses from the sample-size accounting. An interim analysis occurs after 43 participants per group have endpoint data. The final test is a two-sided pooled two-sample \(t\) test at \(\alpha=0.05\).

The planned detectable difference is \(\delta^*=5\) points, and the target power for re-estimation is 90%. The initial minimum is 86 participants per group and the maximum is 120 per group. Let \(n\) denote the final sample size per group; total enrollment is \(2n\). The minimum prevents a rule from reducing the design below its initial size, and the maximum is a prespecified feasibility limit.

For the blinded rule, the interim variance estimate is calculated across all interim outcomes without treatment labels, around their common grand mean. The target-size calculation is the normal-approximation formula

Here \(s_{\mathrm{blind}}^2\) is the blinded interim variance estimate, and \(z_q\) is the \(q\)-quantile of the standard normal distribution. The expression is a planning approximation for equal group sizes, not the final \(t\)-test itself. The common-variance normal model, adequate endpoint data, prespecified limits, and consistent handling of interim participants are important assumptions. In particular, a pooled blinded variance can include some treatment-effect variation; it is not automatically a treatment-neutral estimate under every alternative.

For the unblinded rule, write \(n_1=43\) for the interim size per group and \(d_1=\bar{x}_{T,1}-\bar{x}_{C,1}\) for the observed interim contrast. Conditional power is calculated under the assumption that the future treatment effect will be \(\delta^*=5\) points. Using the interim pooled standard deviation \(s_p\), the approximate conditional distribution of the final standardized contrast at a proposed final size \(n\) has mean and standard deviation

With \(c=z_{0.975}\), the two-sided conditional power is

where \(\Phi\) is the standard normal cumulative distribution function. The rule selects the smallest integer \(n\) from 86 through 120 with \(CP(n)\geq0.90\), or selects 120 if no permitted size reaches the target. This plug-in calculation is approximate: it uses estimated interim quantities and a normal critical value, whereas the specified final test is a \(t\) test.

Why Conditional Power Can Change Error Rates

Under the null hypothesis, the true treatment effect is zero. An unblinded rule may nevertheless increase sample size when the interim contrast happens to be positive, because a positive interim estimate raises the calculated conditional power at larger sample sizes. The final nominal test is then applied after a data-dependent choice of sample size. This selection can change the null distribution of the final test statistic and can raise the probability of rejection above 0.05.

A blinded rule does not use the labeled interim contrast directly, but that fact alone does not prove exact type I error control. The estimate, rounding, cap, final test, and any association between the blinded variance estimate and the final statistic all matter. Under the null, the rule may perform close to nominal in a particular design; under alternatives, treatment-effect variation can affect the pooled blinded estimate. Simulation is therefore used to evaluate the full algorithm, rather than to replace a prespecified statistical justification.

A short justification explains the conditional-power expression. Given the interim data, the interim contribution \(n_1d_1\) to the final contrast numerator is fixed. The future group-mean difference has assumed mean \(\delta^*\) and variance \(2\sigma^2/(n-n_1)\). When expressed as the final standardized contrast, the future random component has variance \((n-n_1)/n\). Substituting the plug-in value \(s_p\) for \(\sigma\) gives \(m(n)\) and \(v(n)\) above. The probability of falling outside the two-sided boundaries \(-c\) and \(c\) is the sum of the two tail probabilities in \(CP(n)\).

Illustrative Simulation Comparison

Consider 100,000 hypothetical trials generated under each scenario. In every replicate, interim outcomes are observed for 43 participants per group, the applicable rule selects a final size between 86 and 120 per group, and additional outcomes are generated until that size is reached. Under the null, both group means are 100 points; under the alternative, the control mean is 100 and the treatment mean is 105 points. Both groups have normal outcomes with variance 100 points squared. The final decision in every replicate uses the two-sided pooled \(t\) test at \(\alpha=0.05\).

For the blinded rule, the interim variance is calculated across the 86 outcomes around their grand mean. For the unblinded rule, conditional power uses the interim contrast and within-group pooled variance, with future effect fixed at 5 points. The rules, limits, and final test are otherwise held constant. The following rounded values represent an illustrative hypothetical simulation output; small Monte Carlo differences are expected if the simulation is repeated.

These figures illustrate a plausible trade-off, not a general ranking. In this example, the blinded rule stays near the nominal type I error and has lower expected enrollment, while the unblinded rule has higher simulated power under the specified alternative but exceeds the nominal type I error and uses more participants, especially under the null. The expected enrollment differs by scenario because the adaptation reacts differently to interim data: under the null, a positive interim contrast can lead the conditional-power rule to select a large sample even though the assumed future effect is not the true effect.

A Monte Carlo estimate is itself uncertain. With 100,000 replicates and an estimated type I error near 0.05, its approximate Monte Carlo standard error is \(\sqrt{0.05(0.95)/100000}\), about 0.00069. Thus, a reported difference of a few ten-thousandths should not be overinterpreted. The larger illustrative difference here is not explained by that level of simulation noise, but its magnitude remains design-specific.

Diagnostics, Alternatives, and Operational Limits

A useful simulation report includes more than one overall power and error-rate estimate. Check error rates across plausible nuisance variances, effect sizes, and distributions; report the frequency of minimum- and maximum-size decisions; and inspect whether estimates are sensitive to the interim timing or to the assumed future effect. For this design, normal equal-variance data are assumptions, not universal truths. Skewness, outliers, unequal variances, missing interim endpoints, or a different final model can make the simple formulas poor approximations. Simulating the intended analysis and realistic data mechanisms is essential.

The principal statistical alternative to applying the nominal final test after an unblinded size change is to use a design and test procedure specifically calibrated for the adaptation. For example, a prespecified error-control procedure can account for the interim information and the rule used to change sample size. Calibration may preserve the desired type I error, but it can affect power and must be evaluated in the same simulations. A blinded nuisance update is another alternative when the scientific aim is to respond to variance uncertainty without making interim treatment-effect decisions. Neither approach is universally preferable: the choice depends on the objective, the acceptable operating characteristics, and the ability to implement the rule reliably.

Operationally, a blinded update requires a genuine firewall: the person calculating the variance should not receive treatment labels or a treatment contrast, and access controls and data-transfer procedures should make that separation credible. The unblinded rule needs restricted access to comparative interim results, validated software for conditional-power calculations, independent review, and a clear decision process. Both approaches require complete interim data, a fixed analysis time, reproducible calculations, a maximum enrollment budget, and documentation of rounding and boundary cases. If the rule cannot be executed as written, its simulated properties do not describe the trial that is actually run.

A common mistake is to conclude that blinding guarantees type I error control, or that reaching a chosen conditional-power target guarantees it. Neither follows. The first ignores possible dependence between the masked estimate and the final statistic, as well as model and implementation details. The second confuses a conditional planning probability under an assumed future effect with a test’s repeated-sampling false-positive rate under \(H_0\). The correction is to define the complete algorithm, specify the final test, and evaluate error rates and power across scenarios; if the nominal error rate is not met, revise or calibrate the design before the trial.