Worked Example Of Binary-Marker Enrichment

From a Marker Assumption to an Enrichment Design

A binary predictive marker divides patients into two prespecified groups, such as marker-positive and marker-negative. An enrichment design uses that classification to direct recruitment toward a group expected to benefit more. The design problem is not only whether the marker-positive treatment effect is large enough. It also requires a defensible eligibility definition, enough marker-positive patients, a rule for deciding whether to enrich, and a final analysis whose claim matches the population actually studied.

The worked design below uses a continuous endpoint measured in units, with higher values defined as better. Every number is hypothetical. Assume the marker assay and cutoff have already been externally validated, the marker is measured before randomization, and treatment is randomized within marker-positive patients. The design uses a separate confirmatory stage so that the interim selection data do not also supply the efficacy test for the final marker-positive claim.

Specify the Population and Recruitment Before Calculating

Suppose the target population has marker prevalence \(\pi=0.40\). A trial first enrolls 200 patients as an all-comer stage, randomized equally between treatment and control. The expected marker-positive count is \(200(0.40)=80\), or about 40 per arm. These are expectations, not guaranteed counts: actual marker prevalence and arm-specific counts vary by chance. The assay is performed before randomization so that marker status can define eligibility and subgroup analyses without being affected by treatment.

If the trial proceeds to marker-positive-only recruitment, it must screen enough people to obtain the required number of eligible patients. With prevalence 0.40, obtaining 108 marker-positive patients would require an expected \(108/0.40=270\) people screened. The expected count is a planning quantity, not a promise; screening targets should allow for variation in prevalence, assay failures, and other exclusions. Recruitment projections should also use the prevalence expected at the actual sites and during the actual recruitment period.

Size the Confirmatory Comparison in the Target Subgroup

For a transparent calculation, assume the endpoint in each treatment arm is normally distributed within marker-positive patients, with the same known standard deviation \(\sigma=12\) units. Assume independent outcomes, independent randomization, no interference between patients, and a treatment effect expressed as a difference in means. Plan a two-sided test of \(H_0:\Delta_1=0\) at \(\alpha=0.05\), with 90% power to detect \(\Delta_1=8\) units. The known-\(\sigma\) normal calculation is an illustrative planning model; a real protocol would justify its variance assumption and use an analysis appropriate to the endpoint and missing-data plan.

With \(n\) evaluable marker-positive patients per arm, the estimated treatment-minus-control difference has standard error \(\sigma\sqrt{2/n}\). Under the alternative \(\Delta_1=8\), its standardized mean is \(8/(\sigma\sqrt{2/n})\). For a two-sided test, the usual normal-approximation sample-size formula is:

Here \(z_{1-\alpha/2}=1.960\), and 90% power means \(\beta=0.10\), so \(z_{1-\beta}=1.282\). The calculation is:

The result is rounded up to 48 evaluable patients per arm. Rounding down would not meet the planned sample size. At \(n=48\), the standard error under the assumed model is \(12\sqrt{2/48}=2.449\) units. The standardized mean under the target effect is \(8/2.449=3.266\); the probability of exceeding the upper two-sided critical value is approximately \(\Phi(3.266-1.960)=\Phi(1.306)=0.904\), with a negligible lower-tail contribution. Thus 48 per arm provides approximately 90.4% power under these assumptions.

Prespecify the Interim Selection Rule

In the hypothetical design, the all-comer stage enrolls 200 patients, with treatment randomized 1:1. An independent review occurs after this stage has complete endpoint data. The prespecified rule is to continue into marker-positive-only recruitment if (1) at least 35 marker-positive patients are evaluable in each arm, (2) the observed marker-positive treatment-minus-control difference is at least 4 units, and (3) no prespecified safety stopping condition is met. Otherwise, the trial does not proceed to the enriched confirmatory stage.

The 4-unit threshold is a decision threshold for this hypothetical design, not a proof of efficacy or predictive value. It balances the possibility of an encouraging but noisy stage-one estimate against the cost of continuing. The minimum subgroup count guards against making the decision from an extremely sparse comparison. The rule must be fixed before examining the interim outcomes, with the endpoint definition, analysis set, missing-data handling, timing, and safety review also specified in the protocol.

Confirmatory Analysis and the Scope of the Claim

After selection, the trial randomizes new marker-positive patients, independently of the stage-one participants, to treatment or control. The confirmatory target is 48 evaluable patients per arm. Under the planned model, a stage-two comparison uses the difference in means and its standard error. For this simple design, a two-sided test is conducted at \(\alpha=0.05\). The final confirmatory claim is restricted to marker-positive patients represented by the assay-defined eligibility rule and trial setting.

The separation of selection and confirmation has a useful error-rate justification. Let \(S\) denote the stage-one data and the decision to continue, and let \(Z_2\) be the stage-two confirmatory statistic. Under the null hypothesis for the marker-positive effect, suppose the stage-two data are independent of \(S\) and the prespecified stage-two test has size \(\alpha\). Then, for every selection outcome \(S\) that leads to continuation, \(P(\text{reject }H_0\mid S)\leq\alpha\). Averaging over the possible selection outcomes gives:

Thus the stage-two test retains its type I error bound despite selection based on stage one, provided the confirmatory observations and test are genuinely independent of the selection data and the analysis is prespecified. This justification does not license unplanned pooling of stage-one and stage-two observations or reuse of a stage-one p-value as if it were independent confirmation.

Predictive Evidence, Population Effects, and Limitations

A statistically significant treatment effect among marker-positive patients is evidence about \(\Delta_1\). It is not, by itself, evidence that the marker is predictive. A predictive claim concerns whether treatment effects differ by marker status, represented by the interaction contrast \(\Delta_1-\Delta_0\). Finding a significant result in the positive group and a nonsignificant result in the negative group does not establish that contrast: the two subgroup estimates may differ only because their precision differs. The earlier material on interaction tests and within-subgroup tests distinguishes these questions.

Likewise, a marker-positive efficacy result does not establish benefit in the full target population. If both subgroup effects and prevalence were known and the target population were represented by those assumptions, the population-average treatment difference would be \(\pi\Delta_1+(1-\pi)\Delta_0\). For example, with \(\pi=0.40\), \(\Delta_1=8\) units, and \(\Delta_0=1\) unit, the weighted difference is \(0.40(8)+0.60(1)=3.8\) units. A positive-only confirmatory stage does not estimate \(\Delta_0\), so it cannot alone support that all-patient average-effect calculation.

The design also depends on the assay correctly classifying patients at the validated cutoff, the prevalence being sufficiently close to its planning value for recruitment, the assumed endpoint variance being credible, and the treatment effect target being clinically meaningful. Prevalence affects how many people must be screened, but does not change the definition of the marker-positive treatment effect. If the clinical setting, assay performance, or patient mix differs materially from the validation setting, transport of the result requires separate justification.

A common mistake is to call the marker predictive because the marker-positive subgroup has a small p-value while the marker-negative subgroup does not. That reasoning compares two significance labels, not the subgroup effects themselves. The correction is to distinguish a positive-subgroup efficacy claim from a predictive claim: the former tests \(\Delta_1\), while the latter requires direct evidence about \(\Delta_1-\Delta_0\) under a design and analysis that support that comparison.

Other warning signs include fewer evaluable marker-positive patients than planned, screening yield far below the prevalence assumption, major imbalance in subgroup counts, incomplete interim endpoint data, or an assay/cutoff change after outcomes are seen. These can undermine power, the selection decision, or the scope of generalization. The stated normal model is also an approximation: skewness, heavy tails, unequal variances, site effects, or informative missingness may require a different analysis and sample-size calculation. A design should state its assumptions, monitor recruitment and data quality, and not reinterpret a failed or altered design as if the original confirmatory claim were unchanged.