Evaluating Biomarker-Enriched Trial Designs

Why Enrichment Requires Simulation

A biomarker-enriched trial enrolls patients selected by a biomarker result or threshold, rather than enrolling the full eligible population. Enrichment can raise the expected treatment effect in the randomized sample when treatment works better in a biomarker-defined subgroup. But the test used to select patients may misclassify them, the biomarker-positive population may be uncommon, and treatment effects may vary across subgroups. These features affect both trial precision and the number of people who must be screened.

Simulation makes these trade-offs explicit. A useful comparison specifies the target population, the assay's operating characteristics, the treatment effect in each biomarker subgroup, the endpoint distribution, the enrollment rule, and the analysis used to evaluate the trial. It then generates complete trials under those assumptions and estimates operating characteristics, such as power or the probability of reaching a decision criterion. The simulation evaluates a defined design and analysis; it does not establish that the assumptions are true.

For prevalence \(\pi=P(B=1)\), sensitivity \(Se\), and specificity \(Sp\), the probability that a screened person tests positive is \(r=P(A=1)=Se\pi+(1-Sp)(1-\pi)\). By Bayes' rule, the true-positive fraction among assay-positive enrollees is \(q=P(B=1\mid A=1)=Se\pi/r\). An assay-positive enrollment rule therefore selects a mixture of the two true biomarker subgroups unless its false-positive rate is zero. A different assay threshold can change both the yield \(r\) and the composition \(q\).

Translate Selection Into Effects and Variability

Suppose the treatment effect, defined as the treatment-arm mean minus the control-arm mean, is \(\tau_1\) for true biomarker-positive patients and \(\tau_0\) for true biomarker-negative patients. If treatment assignment is randomized within the enrolled population and the subgroup mixture is the same in expectation across arms, the expected treatment contrast among assay-positive enrollees is \(\tau_A=q\tau_1+(1-q)\tau_0\). For an all-comer population, the corresponding expected contrast is \(\tau_{\mathrm{all}}=\pi\tau_1+(1-\pi)\tau_0\). Thus, assay-positive enrollment does not make every enrolled patient truly positive; its expected effect depends on the assay's predictive value.

An effect mixture also affects endpoint variability. For example, suppose the control outcome has the same mean and variance \(\sigma^2\) in both true subgroups, and treatment outcomes have subgroup means separated by \(\tau_1-\tau_0\), with within-subgroup variance \(\sigma^2\). In an enrolled population with true-positive fraction \(q\), the treated-arm variance is \(\sigma^2+q(1-q)(\tau_1-\tau_0)^2\). The added term is between-subgroup variation in treatment-arm means. The control-arm variance remains \(\sigma^2\) under these assumptions. This matters because a larger average effect does not by itself guarantee a smaller standard error or greater power.

Compare Designs Under Explicit Assumptions

A comparison is only interpretable when its basis is stated. Holding the randomized sample size fixed asks how much performance differs for trials of the same size, but it does not account for the additional screening needed to fill an enriched trial. Holding screening capacity fixed asks how many randomized patients each rule can yield. Other comparisons can hold cost, calendar time, or a target precision fixed. These are different design questions, so simulation results should name the constraint.

The following calculation gives a simple normal-endpoint approximation for a fixed-size comparison. Assume independent patients, equal allocation, normally distributed outcomes within each true subgroup, common within-subgroup standard deviation \(\sigma=10\) units, and the subgroup effects from the previous example. Also assume a common control mean across subgroups and a treatment-arm subgroup mean difference of \(8-1=7\) units. These assumptions make the variance calculation transparent; a simulation should use the endpoint model and analysis intended for the actual design.

A different threshold can produce a different trade-off between enrichment and yield. Its characteristics should come from the intended assay and threshold, not be inferred from the positive-test calculations above. For instance, consider a hypothetical stricter threshold with positive yield \(r=0.20\) and positive predictive value \(q=0.90\). Those values describe a separate operating point. They imply a mean effect of \(0.90(8)+0.10(1)=7.30\) units and an expected screening requirement of \(160/0.20=800\) people to obtain 160 positive enrollees. Higher enrichment may raise the expected effect while sharply increasing screening burden.

Simulation Workflow, Diagnostics, and Alternatives

A practical simulation can repeat the following sequence for each candidate design and each replicate:

Check the simulated quantities against their theoretical expectations before interpreting performance. In a large set of screening draws, the assay-positive proportion should approach \(r\), and the true-positive fraction among assay-positive people should approach \(q\). Under randomization, treatment assignment should not systematically alter baseline biomarker composition. Compare simulated endpoint means and variances with values implied by the data-generating model. The earlier material on Monte Carlo error is relevant when deciding whether apparent differences between designs are larger than simulation noise; the earlier material on validation invariants helps catch coding errors such as enrolling assay-negative patients under a positive-only rule.

Common failure modes include treating assay-positive status as identical to true biomarker-positive status, using sensitivity as if it were positive predictive value, and simulating subgroup effects without the resulting mixture variance. Another is comparing designs at equal randomized sample size while presenting the result as if screening cost were also equal. If prevalence, assay performance, or treatment effects are uncertain, a single assumed value can make the comparison fragile. Evaluate plausible scenarios or parameter distributions and report which conclusions change.

A fixed-threshold enriched design is not the only option. All-comer enrollment avoids screening exclusions and can estimate effects across the broader population, though its average effect may be smaller under strong treatment-effect heterogeneity. Enrichment based on a more specific threshold may increase the selected-population effect but reduce yield. A broader threshold can retain more participants while diluting enrichment. Designs that enroll multiple biomarker groups can provide direct subgroup information, but require a clearly specified analysis and may change sample-size and decision requirements. The later material on stratified randomization addresses subgroup balance; here the central comparison is how the enrollment rule changes who enters the trial and what that implies for performance and screening.

Common Mistake and Key Interpretation

A tempting but incorrect argument is: “The assay is 85% sensitive, so 85% of assay-positive enrollees are truly biomarker-positive.” Sensitivity is the proportion of truly positive people who test positive, \(P(A=1\mid B=1)\); the desired enrollment fraction is the positive predictive value, \(P(B=1\mid A=1)\). The latter also depends on prevalence and specificity. In the worked example, sensitivity is 0.85 but the positive predictive value is only about 0.785.