Fixed Enrichment In Biomarker-Positive Populations

What Fixed Enrichment Targets

A fixed-enrichment trial determines eligibility using a biomarker before randomization and enrolls only participants classified as marker-positive. The biomarker rule is held fixed: the trial does not begin by enrolling a broader population and later change eligibility. The central design consequence is that the randomized comparison directly targets treatment effects among marker-positive participants, not among all patients who might receive the treatment in practice.

The marker, assay, positivity threshold, and timing of assessment therefore need to be specified before recruitment. The assay must be applied consistently, and treatment assignment must be randomized among eligible participants. The earlier material on population-specific estimands distinguishes the population an estimand refers to; here that population is the group meeting the prespecified marker-positive rule.

Definition: In a fixed-enrichment design, eligibility is restricted before randomization to participants classified as biomarker-positive by a prespecified assay and rule. For a continuous outcome \(Y\), a simple target estimand is the difference in mean outcomes under treatment and control among that eligible population: \(\Delta_{+}=E(Y^{(1)}-Y^{(0)}\mid M=1)\). Here \(M=1\) denotes marker-positive status, and \(Y^{(1)}\) and \(Y^{(0)}\) are the outcomes that would be observed under treatment and control, respectively.

Randomization supports a causal comparison within the trial’s eligible population, subject to appropriate conduct, outcome ascertainment, and analysis. It does not make the enrolled population representative of marker-negative patients or of all patients with the condition. The result may support an efficacy claim for the population defined by the assay rule; broader claims require evidence and assumptions beyond this restricted randomized comparison.

Assumptions for a Basic Sample-Size Calculation

Consider a two-arm, 1:1 randomized trial with one prespecified continuous primary outcome. Let \(\delta\) be the treatment effect used for planning, expressed as the treatment-minus-control mean difference, and let \(\sigma\) be the common within-arm standard deviation in the marker-positive population. A conventional planning calculation assumes independent participants, an approximately normal sampling distribution for the difference in means, a common outcome variance across arms, and a fixed analysis at the planned sample size. It also specifies a two-sided type I error rate \(\alpha\) and desired power \(1-\beta\).

These assumptions concern the endpoint and analysis population; they should not be borrowed automatically from an all-comer population. If marker-positive participants have different outcome variability, the planning value of \(\sigma\) should reflect that population. The formula below is an approximation, commonly reasonable when the outcome means are well behaved and the sample sizes are not very small. It counts participants with usable primary-outcome measurements; expected loss to follow-up must be handled separately.

Planning result: With equal allocation, a two-sided normal-approximation test, common standard deviation \(\sigma\), and target difference \(\delta\), the approximate analyzable sample size per arm is \(n=2\sigma^2(z_{1-\alpha/2}+z_{1-\beta})^2/\delta^2\). The result is rounded up to a whole participant. Here \(z_q\) is the \(q\) quantile of the standard normal distribution.

The formula follows from the standard error of a difference between two independent sample means. Under the planning model, that standard error is \(\sigma\sqrt{2/n}\). Under the alternative with true difference \(\delta>0\), the standardized estimate is approximately normal with mean \(\delta/(\sigma\sqrt{2/n})\) and variance 1. For a positive effect, approximate power is dominated by crossing the upper two-sided critical boundary:

1-\beta \approx P\left(Z>z_{1-\alpha/2}-\frac{\delta}{\sigma\sqrt{2/n}}\right) =\Phi\left(\frac{\delta}{\sigma\sqrt{2/n}}-z_{1-\alpha/2}\right).

Setting this approximate power equal to \(1-\beta\) gives \(\delta/(\sigma\sqrt{2/n})=z_{1-\alpha/2}+z_{1-\beta}\). Squaring and rearranging yields \(n=2\sigma^2(z_{1-\alpha/2}+z_{1-\beta})^2/\delta^2\). The approximation neglects the small probability of rejection in the opposite tail under this positive-effect alternative; exact methods can be used when that approximation is inadequate.

Worked Example: Planning the Positive-Population Sample Size

Suppose a hypothetical fixed-enrichment trial compares a new treatment with control on a continuous symptom score among marker-positive participants. Lower scores are better, and the planning difference in the treatment-minus-control direction is \(\delta=-5\) points. For sample-size calculation use the magnitude \(|\delta|=5\) points, a common standard deviation of 8 points, two-sided \(\alpha=0.05\), and 80% power. Assume 1:1 allocation and the normal approximation.

The standard normal quantiles are \(z_{0.975}=1.960\) and \(z_{0.80}=0.8416\). Substitution gives

n\approx\frac{2(8^2)(1.960+0.8416)^2}{5^2} =\frac{128(7.84896256)}{25} \approx 40.1867.

Round upward: the design needs 41 participants with usable primary-outcome data per arm, or 82 in total. If 10% of randomized participants are expected to lack a usable outcome, the enrollment target per arm is \(41/(1-0.10)=45.56\), which rounds up to 46. The resulting target is 92 randomized marker-positive participants. This calculation supports the chosen power only under the stated assumptions and planning values; it does not guarantee that the realized effect will be statistically significant.

Recruitment Yield and Eligibility

The randomized sample-size target is not the number of people who must be screened. Screening yield depends on the prevalence of marker positivity in the recruitment source and on whether screened people can be assessed and enrolled. If prevalence is \(p\), and every screened person can be classified and otherwise eligible, the expected number of screens required to randomize \(N_{+}\) positive participants is approximately \(N_{+}/p\). This is a planning expectation, not a guarantee: the realized number of positive participants varies.

Worked Example: Translating the Target Into Screening

Continue with the hypothetical target of 92 randomized marker-positive participants. Suppose the expected prevalence of marker positivity among otherwise eligible people is \(p=0.25\), and assume for this simple calculation that every screened person has a valid assay result and meets the remaining eligibility criteria.

The expected screening requirement is

N_{\text{screen}}\approx\frac{N_{+}}{p} =\frac{92}{0.25}=368.

Thus, about 368 people would need to be screened on average to identify 92 marker-positive participants. This does not mean screening exactly 368 guarantees 92 eligible participants. If some assays are unevaluable or some positive participants do not enroll, the usable yield is lower and the screening target should increase. Investigators should also check whether the prevalence estimate applies to the actual recruitment setting rather than assuming that a population-wide estimate predicts local yield exactly.

The positivity definition is part of the design, not a post hoc convenience. Changing a threshold during recruitment can change who is eligible and therefore the population to which the treatment-effect estimate refers. Assay qualification, consistent measurement, and clear handling of invalid results are important to preserve a coherent eligibility rule. Biomarker misclassification can also mean that the trial’s operationally defined positive group differs from the underlying biological group; conclusions should identify the assay-based population actually studied.

What the Randomized Result Can Support

A treatment comparison among randomized marker-positive participants estimates the effect for the trial’s marker-positive target population under the specified treatment strategies and outcome definition. It does not, by itself, estimate the treatment effect among marker-negative participants, nor does it establish that marker status predicts differential treatment benefit. To assess whether treatment effects differ by marker status, evidence on both biomarker groups and a treatment-by-biomarker comparison is needed; a positive-only trial has no randomized marker-negative comparison.

Generalization also depends on how trial participants relate to the intended clinical population. A trial may enroll only a subset of marker-positive patients because of age limits, disease severity, comorbidities, site access, or willingness to participate. Even within the positive group, transport to patients unlike those enrolled may require additional evidence and assumptions. A precise estimate for the enrolled positive population is not automatically a precise estimate for every setting in which the assay might be used.

The principal alternative relevant to the target population is an all-comer trial that enrolls both marker-positive and marker-negative participants. Such a design can directly observe outcomes in both strata and may support broader-population questions, but it spends enrollment on people outside a positive-only target and requires its own plan for the intended claims. The later material on all-comer trials considers prespecified subgroup claims. Fixed enrichment is attractive when the intended treatment claim is specifically for assay-positive patients and enrolling other groups is not necessary to answer the primary question.

Worked Example: Interpreting a Positive-Group Result

In a hypothetical trial restricted to marker-positive participants, 70 participants per arm have an outcome measurement. The treatment-minus-control mean difference is 5 points, and the pooled within-arm standard deviation is 10 points. Assume independent observations, approximately normal outcomes, and equal variances so that the pooled two-sample \(t\) procedure is suitable. The estimated standard error is

SE=10\sqrt{\frac{1}{70}+\frac{1}{70}} =10\sqrt{\frac{2}{70}} \approx 1.690.

The test statistic is \(t=5/1.6903\approx2.958\), with \(df=70+70-2=138\). The two-sided \(p\)-value is approximately 0.003644. At a two-sided 0.05 level, the result is statistically significant. Using \(t_{0.975,138}\approx1.977\), an approximate 95% confidence interval is

5\pm1.977(1.6903) \approx 5\pm3.342 =(1.658,\ 8.342)\text{ points}.

Under the stated model and trial conduct, the interval is compatible with a mean treatment benefit between about 1.658 and 8.342 points in the trial’s marker-positive population, in the direction represented by the positive treatment-minus-control difference. The interval does not state a probability that the fixed true effect lies within these particular endpoints. Nor does this positive-only comparison establish the effect in marker-negative patients or in all patients.

Diagnostics, Limitations, and Common Mistakes

Before interpreting the result, examine whether the design and analysis match the assumptions: confirm that randomization was implemented as planned, summarize missing outcome data by arm, inspect the outcome distributions and outliers, and assess whether variability is plausibly comparable between arms if using a pooled-variance analysis. A large departure from the planning standard deviation can reduce power or make the planned sample size inadequate. Substantial differential missingness can compromise the randomized comparison, even if the nominal enrollment target was met.

Using an all-comer variance without checking relevance. Outcome variability in the marker-positive population may differ. Use a defensible estimate for the target population and examine sensitivity to uncertainty in \(\sigma\).
Treating expected screening yield as certain. The ratio \(N_{+}/p\) is an expectation. Prevalence variation, invalid assays, and other eligibility exclusions can require more screening.
Changing the assay rule after seeing outcomes. This can change the target population and make the reported claim depend on outcome-informed eligibility decisions. Prespecify the rule and report deviations transparently.
Overgeneralizing a significant result. A small \(p\)-value in marker-positive participants is evidence against the tested null for that population under the analysis assumptions. It is not evidence that marker-negative participants benefit, or that marker status predicts benefit.
Confusing statistical significance with clinical importance. Compare the effect estimate and confidence interval with a clinically meaningful difference, not only with the significance threshold.

Fixed enrichment can provide an efficient, focused answer when the intended use is treatment of patients meeting a validated marker-positive rule. Its limitations follow from that focus: no direct randomized estimate for excluded marker-negative patients, dependence on assay performance and recruitment context, and potential restriction of generalizability even within the positive group. The efficacy statement should name the population, assay rule, outcome, and comparison that the trial actually studied.

Key takeaway: Plan the randomized sample size using assumptions appropriate to the marker-positive population, separately account for screening yield and attrition, and restrict the efficacy claim to the population defined by the prespecified positive assay rule unless additional evidence supports broader inference.

Check Your Understanding

Answer each question, then compare your reasoning with the solutions.

A trial targets a mean difference of 4 points, with common standard deviation 7 points, two-sided \(\alpha=0.05\), and 90% power. Under equal allocation and the normal approximation, what analyzable sample size per arm is needed?
A positive-only randomized trial finds a treatment effect in the marker-positive group. Does this result establish that marker status predicts treatment benefit? Why or why not?
If the positive-group randomized target is 120 and expected marker prevalence is 0.30, how many people must be screened on average under the assumption of no other screening losses?
Name two reasons why an efficacy estimate from enrolled marker-positive participants might not generalize to every marker-positive patient.

Solutions. (1) Use \(z_{0.975}=1.960\) and \(z_{0.90}=1.2816\): \(n\approx2(7^2)(1.960+1.2816)^2/4^2=98(10.50797056)/16\approx64.3613\), so round up to 65 analyzable participants per arm. (2) No. A positive-only trial has no randomized marker-negative comparison, so it cannot establish a treatment-by-marker difference. (3) \(120/0.30=400\) people on average; realized screening needs may differ. (4) Examples include eligibility restrictions that exclude some positive patients and differences in care, adherence, or outcome measurement between trial sites and the intended setting.