Biostatistics

The Science of Sample Size: Statistical Strategies in Ziftomenib and Revumenib Trials

Analyzing how two groundbreaking menin inhibitors utilized different statistical frameworks—Exact Binomial Distribution vs. Simon's Two-Stage Design—to optimize their clinical trial trajectories.

1. The Crucial Role of Sample Size in Clinical Oncology

In the development of novel targeted therapies for acute myeloid leukemia (AML), calculating the appropriate sample size is not merely a mathematical exercise; it is a profound strategic decision. Enroll too few patients, and the trial lacks the statistical power to prove efficacy. Enroll too many, and the sponsor wastes invaluable time, resources, and potentially exposes more patients than necessary to an ineffective experimental drug. The development programs for the menin inhibitors ziftomenib and revumenib illustrate how trial phase, disease subtype, endpoint, and stopping rules influence statistical design. These examples should not be interpreted as a head-to-head comparison of drug efficacy.

2. Ziftomenib: The Exact Binomial Distribution Approach

Ziftomenib was evaluated in the KOMET-001 trial, specifically focusing on its registration-enabling Phase II portion for patients with relapsed/refractory NPM1-mutated (NPM1-m) AML. Because this portion of KOMET-001 was intended to support a potential registration strategy, the study used a prespecified single-arm response-rate design. Such a design evaluates whether the observed response rate is inconsistent with a prespecified null rate; it does not provide the same randomized comparative evidence as a controlled trial.

To achieve this, the statisticians utilized an exact binomial test. The design used a 12% null CR/CRh rate and a 25% target response rate, with a one-sided alpha of 0.025. The publication reports that at least 85 patients were planned, providing 89% power under these assumptions. Power is the probability of rejecting the null hypothesis if the assumed 25% response rate is true; it is not the probability that the drug works or that the trial will succeed. A fixed-N design does not mean that the drug's safety or efficacy is already established. It means that the protocol commits to a planned analysis size rather than using a Simon-style early futility boundary. Its suitability depends on the clinical question, endpoint maturity, feasibility, and the value of early stopping—not simply on how much Phase I data are available.

Reconstructing the Ziftomenib fixed-N decision threshold

Using the published design assumptions (85 evaluable patients, null response rate 12%, one-sided alpha 0.025), an independent exact-binomial reconstruction gives a minimum of 17 CR/CRh responders out of 85 to reject the null hypothesis: the upper-tail probability under p = 0.12 is approximately 0.0232. If the true response rate were 25%, the probability of reaching that threshold would be approximately 88.5%, consistent with the reported 89% power after rounding.

This is a reconstruction from the published assumptions, not a substitute for the protocol or statistical analysis plan. It illustrates how a design translates a target effect and error rates into an operational decision boundary.

What happened when the Ziftomenib results were reviewed?

The later FDA review shows why a well-powered design is only as reliable as its endpoint definition, analysis population, and benchmark. In the sponsor's prespecified Phase II analysis, CR/CRh was 21.7% and the one-sided P value was 0.0058. After FDA response adjudication, the Phase II cohort had 17 responses among 92 patients (18.5%; 95% CI 11.1%–27.9%); the 95% confidence interval included the 12% benchmark.

The FDA statistical reviewer also questioned the relevance of the 12% historical benchmark because it was based loosely on a different endpoint (CR/CRi) in a population that was mostly treated after at least two prior lines. This is a key design lesson: a numerically precise sample-size calculation cannot repair a clinically mismatched historical control or an endpoint-assessment rule that was not sufficiently prespecified.

The FDA's final efficacy assessment relied on the pooled Phase Ib and Phase II efficacy cohort (24/112; 21.4%; 95% CI 14.2%–30.2%) to establish clinical benefit; the review recommended regular approval. The point is not that the original design was invalid, but that statistical success in a protocol-defined analysis and the regulator's final evidence assessment are related yet distinct questions.

3. Revumenib: Simon's Two-Stage Design for Rapid Go/No-Go

In contrast, Revumenib was evaluated in the AUGMENT-101 trial, which was designed as a seamless Phase I/II study treating patients with relapsed/refractory KMT2A-rearranged (KMT2Ar) acute leukemia. Because Phase I and II were integrated, the sponsor needed a flexible statistical mechanism to quickly halt the trial if the drug proved ineffective in Phase II, thereby saving resources and protecting patients.

To allow a prespecified early futility decision, the study used a Simon two-stage design. They set a null hypothesis of a 10% CR+CRh rate against an alternative (target) rate of 25%, aiming for 90% power and a 2.5% one-sided significance level. Simon's minimax design split the enrollment into two distinct phases:

  • Stage 1 (Interim Analysis): The trial first enrolled 38 efficacy-evaluable adult patients. The rule was strict: if fewer than 5 patients (out of 38) responded, the trial would be immediately terminated for futility.
  • Stage 2: If 5 or more patients responded in Stage 1, the trial would get a "Go" decision and continue enrollment until reaching a total of 64 evaluable adult patients to confirm the final efficacy.

The timing of the futility look matters: the first 38 adults had to reach 6 months of follow-up or discontinue therapy before the response count was assessed. The publication also describes a separate interim efficacy boundary of at least 12 responders among 57 efficacy-evaluable adults and children with KMT2A-rearranged acute leukemia. That 57-person, mixed-age interim efficacy analysis is not the same denominator or decision rule as the 38-adult Simon futility boundary. Keeping these analyses separate avoids conflating distinct populations and objectives.

💡 My Practical Perspective: Strategic Judgment in Trial Design

In clinical trials, there is no single "correct" method for determining sample size; rather, it is a matter of strategic judgment based on the specific stage of the drug's pipeline.

Revumenib utilized a Simon's two-stage design (minimax) because it was a seamless Phase 1/2 study. This approach is a highly efficient "Go/No-go" strategy, allowing the sponsor to perform an interim analysis with a minimal initial cohort (38 patients). It enables rapid termination if the drug lacks efficacy, thereby conserving resources and protecting patients from unnecessary exposure.

Conversely, Ziftomenib was evaluated in a single-arm Phase II study intended to support a potential registration strategy. The reported design used an exact binomial approach with a planned cohort of 85 patients and prespecified response-rate assumptions. A fixed sample-size design can be appropriate when its assumptions and operating characteristics match the clinical question; it does not guarantee approval or eliminate uncertainty. These examples illustrate different design choices, not proof that one approach is inherently superior. The design should follow the primary estimand, endpoint, clinically meaningful target effect, acceptable type I and type II error rates, operational constraints, and regulatory strategy.

4. Worked Example: A Two-Arm Response-Rate Trial

The designs above are single-arm oncology examples. To illustrate a different question, suppose a hypothetical randomized Phase II study compares a new treatment with control and expects response rates of 30% and 10%, respectively. With equal allocation, a two-sided type I error of 5%, and 80% power, a common normal-approximation calculation for two independent proportions gives approximately 62 evaluable participants per arm.

Assumptions

  • Control response rate: 10%; treatment response rate: 30%
  • Two-sided α = 0.05; power = 80%; allocation ratio = 1:1
  • Approximate sample size: 62 evaluable participants in each arm
  • If 10% of participants are expected to be unevaluable, enroll about 69 per arm (62 ÷ 0.90, rounded up)

This is an illustrative planning calculation, not a recommendation for a real protocol. The estimate can change with the chosen test, continuity correction, exact methods, multiplicity control, stratification, and the definition of the primary endpoint. A response-rate endpoint also needs a clinically justified target difference, not merely a difference that produces a convenient sample size.

Do not apply this two-arm formula directly to the Ziftomenib or Revumenib examples above. Their registration strategies used single-arm response-rate hypotheses and different design assumptions. Cross-trial differences in disease subtype, eligibility criteria, endpoint definitions, follow-up, and analysis populations also prevent a simple head-to-head efficacy comparison.

Before finalizing a protocol, have a trial statistician verify the design and reproduce the calculation with validated statistical software. The worked example is educational and does not replace a prespecified statistical analysis plan.

5. A Practical Framework for Selecting a Phase II Design

Start with the clinical question and primary estimand—not with a preferred sample-size formula. The table below is a planning aid for common oncology development settings; it is not a substitute for protocol-specific statistical design.

Development questionDesign often consideredWhat the design answersKey limitation to state
Is there enough preliminary activity to justify further study in a defined population?Single-arm, fixed-N exact binomial designWhether response data are inconsistent with a prespecified uninteresting response rate.Historical benchmarks may not be comparable; this does not estimate a randomized treatment effect.
Can an inactive regimen be stopped early while limiting exposure?Simon two-stage or another prespecified futility designWhether an interim response count crosses a continuation boundary, with operating characteristics controlled under stated assumptions.The interim rule, evaluability window, and handling of delayed responses must be operationally feasible and prespecified.
Is the experimental regimen promising relative to a concurrent control?Randomized Phase II designA comparative estimate of treatment effect against the selected control under the trial's randomization and analysis plan.The control, allocation ratio, endpoint, and target effect drive sample size; a single-arm response-rate formula is not interchangeable.
Is the signal primarily a delay in progression or another time-to-event outcome?Event-driven time-to-event designA comparison based on the planned number of events under assumptions about the hazard ratio and event process.Enrollment is not determined by the hazard ratio alone; accrual, follow-up, censoring, event rate, and analysis timing matter.

Protocol design worksheet

  1. Define the question and population. Specify disease subtype, line of therapy, eligibility criteria, treatment setting, and intended population.
  2. Lock the primary endpoint and estimand. State what counts as a response or event, the assessment window, analysis population, and how missing, unevaluable, or early-discontinued participants are handled.
  3. Justify the null and target values. For a single-arm activity design, explain why the null response rate (p₀) is clinically uninteresting and why the target rate (p₁) would justify further development. Support both with comparable evidence.
  4. Choose error rates and operating characteristics. Prespecify type I error (α), power (1 − β), and whether the design is one- or two-sided. Explain why those choices fit the decision.
  5. Specify interim rules before enrollment. For a two-stage design, document stage sizes, response-count boundaries, timing, data maturity, and whether stopping is for futility only or also for efficacy.
  6. Translate evaluable sample size into enrollment. Account for expected non-evaluability, withdrawal, and time needed to observe the endpoint. An arbitrary dropout percentage is not a substitute for an endpoint-specific evaluability plan.
  7. Check safety and feasibility separately. A design powered for efficacy may still be too small to characterize uncommon toxicities. Review exposure, follow-up duration, monitoring, and whether a safety expansion is needed.
  8. Document the decision rule and next step. State what result would support stop, revise, expand, or proceed—and what uncertainty remains even if the statistical threshold is met.

Simon optimal vs. minimax

Both are two-stage designs with prespecified error constraints, but they optimize different objectives. The optimal design minimizes expected sample size when the true response rate is at the null level; the minimax design minimizes the maximum possible sample size. The preferred design depends on whether expected enrollment under an inactive treatment or maximum enrollment burden is the more important operational constraint. Neither is universally best.

FDA's oncology master-protocol guidance recommends considering designs such as Simon two-stage designs in nonrandomized activity-estimating studies with response rate as the primary endpoint, while allowing other approaches when their rationale and statistical analysis plan are adequately described. The appropriate design remains specific to the development question and should be reviewed by a qualified trial statistician.