Many cancer biomarkers do not behave like "more is better." Tumor mutational burden, for example, can have a "Goldilocks zone" where intermediate values carry different risk than either extreme. Designs that enroll patients above a single biomarker cutoff cannot find such a window. Methods that find windows in historical registries cannot say whether treating patients inside that window actually helps. This note proposes a sequential trial design that treats ordered biomarker bands as the options in a bandit problem, meaning a sequential experiment that chooses which option to try next based on outcomes so far. The design assumes the treatment benefit rises and then falls across the bands, which is called unimodality. Retrospective registry data are allowed to influence only which bands the trial recruits from next. They are never allowed to influence the evidence required to stop and declare a winning band.
The reason for this split is a known property of fixed-confidence stopping rules. The error guarantee comes from the stopping test alone and holds for any rule that picks what to sample. A biased, prognostic-only historical signal therefore cannot inflate the chance of a wrong conclusion. It can only make the trial cost more patients. Under unimodality, the stopping test itself is cheap, because it only compares the leading band against its immediate neighbors. The research question is whether this split lets registry data shorten the expensive "find the neighborhood of the peak" phase of unimodal search, which is exactly the phase that is ethically costly in a trial, without inheriting the known failure modes of retrospective studies.
Core Claim
Consider a biomarker cut into $K$ ordered bands. Each band $v$ has an unknown treatment effect $\mu(v)$, measured as the difference in restricted mean survival time (RMST, the area under the survival curve up to a fixed horizon $t^*$) between treatment and control inside that band. The claim has three parts.
First, if $\mu$ is unimodal on the line of bands, a local generalized likelihood ratio (GLR) stopping rule is enough to certify the best band. This is the rule of Poiani et al.: stop once the empirical leader is confidently better than its two neighbors. Its error stays below a target $\delta$ regardless of how enrollment was steered.
Second, prior information can help, because those authors also prove the cost of locating the peak neighborhood grows linearly in $K$ in the worst case. A registry-derived guess of the peak location can plausibly remove most of that cost.
Third, mixing registry-guided enrollment with a fixed fraction of prior-free unimodal allocation bounds the damage when the registry is wrong. The worst case is a constant factor of the prior-free design.
The closest existing trial designs cannot do this for two reasons. Biomarker-guided adaptive enrichment learns a single monotone cutoff over two batch stages. Safe dose-finding bandits such as SEEDA-Plateau exploit a plateau shape but act on dose, not on biomarker-defined subpopulations, and only with binary outcomes.
Research Program
The design has three components.
The first component is the stopping test. At each interim look we compute, for the current leader $\hat v$ and each neighbor $u \in \{\hat v - 1, \hat v + 1\}$, the GLR statistic $Z(\hat v, u)$. This statistic measures how strongly the accumulated data reject "$u$ is at least as good as $\hat v$." We stop when
$$\min_{u \in \mathcal{N}(\hat v)} Z(\hat v, u) > \beta(n, \delta),$$
where $\mathcal{N}(\hat v)$ is the set of neighbors, $n$ is the number of matured outcomes, and $\beta$ is the usual threshold growing like $\log(1/\delta) + O(\log n)$.
The per-band RMST contrasts are estimated from right-censored data, meaning survival times still unknown for patients who have not yet had the event. They are approximately Gaussian with estimable variance, so we use the Gaussian GLR on them. Validating that approximation under censoring and delayed maturation is itself a deliverable, since existing unimodal theory covers only simple exponential-family rewards.
The second component is enrollment steering, which decides which band to screen and enroll next. We fit a flexible survival model to registry cohorts, in the style of the fully connected hazard networks of Anaya et al.. This yields a prior guess $\hat v_0$ of the peak and a rough effect profile. Steering follows the prior in proportion $1-\alpha$ and the prior-free UniTT allocation of Poiani et al. in proportion $\alpha$.
We will prove that expected sample size is at most $1/\alpha$ times UniTT's when the prior is adversarial. This follows because the forced UniTT stream alone would eventually trigger the stopping test. We will also characterize the gain when $\hat v_0$ lies within one band of the true peak.
This separation is the direct response to the prognostic-versus-predictive gap of Buhmann et al.. Registries show how outcomes vary with the biomarker under one treatment, not the treatment contrast. So they are admitted only as a steering heuristic.
The third component is operational robustness. Ötles et al. found that live pipelines lost more discrimination to infrastructure shift (AUROC loss 0.016) than to temporal shift, and failed outright on 10 of 356 days. Because the stopping test is a function of accumulated matured data only, missed interim looks delay the trial without invalidating it. We will verify this under simulated outage and delayed-outcome patterns. We will also check that band assignment computed from live-feed biomarker values rather than curated ones does not break the guarantee.
Baselines
The naive reference point is a fixed all-comer randomized trial. It enrolls regardless of biomarker and reports a single effect. The only reported figure on the file's JAVELIN Lung 200 re-design is that it needs 940 patients for 90% power (adaptive enrichment). It is run on the same simulated populations with the same $t^*$.
The strongest existing clinical competitor is the two-stage RMST threshold-enrichment design with calibration-weighted estimators. On JAVELIN Lung 200 it reports 845 patients for 90% power, a 10% reduction, with family-wise Type I error below 2.5% (adaptive enrichment). We will re-implement it on identical simulated populations and analysis horizon, with its Stage I size tuned over the same grid budget we give our mixing fraction $\alpha$. We will also run a strengthened variant that replaces the single cutoff with the two-cutoff window of Anaya et al., so that it is not handicapped by a monotone assumption. Beating these means matching their error control while enrolling fewer patients overall and fewer patients in non-benefiting bands, across a range of effect shapes. Merely beating them on inverted-U shapes they were never designed for does not count.
The strongest bandit competitor is cold-start UniTT with the same local GLR stopping. It isolates whether registry steering adds anything. No reported result was found on Lacuna for UniTT sample complexity in numeric form; the paper reports only figures.
The key ablation keeps the registry prior but also lets it enter the stopping decision, via a Bayesian posterior. This is in the spirit of the admissible-set Thompson sampling of the JMLR dose-finding designs. The ablation should show the error inflation that our separation avoids when the registry is misleading.
On the dose-finding side, SEEDA-Plateau is the reference. It reports 86.6% correct optimal-dose recommendation versus 47.2% for base SEEDA on synthetic curves. We will use its synthetic scenarios only as a sanity check that our unimodal machinery is competitive when the ordered arms are doses.
Why not just…?
Why not just run the two-stage enrichment design with two cutoffs instead of one? This is the real threat. It is simple, regulator-friendly, and may capture most of the benefit when the window is wide. Its weakness is that Stage I must be sized in advance to find two boundaries from all-comer data, so it cannot concentrate patients near the peak as evidence accumulates. The head-to-head comparison over wide versus narrow windows and varying $K$ settles this. If the two-cutoff design matches ours whenever $K \le 5$, we will say so and restrict the claim to finer biomarker resolutions.
Why not just enroll the band that the registry says is best and skip exploration? Registries encode prognosis under a single treatment, curated collection, and past standards of care, as documented by Zhang et al. and Zhong et al.. A registry peak can therefore sit away from the true treatment-contrast peak. Our "trust the registry" arm will quantify how often this commits the trial to the wrong band in scenarios where prognostic and predictive shapes differ.
Why not just put the registry into a Bayesian prior, as Thompson-sampling dose designs do? That is exactly the ablation above. With a well-calibrated prior it may be more efficient than our design. But its error rate then depends on the prior being right, and that is precisely what retrospective validation cannot guarantee. The comparison reports both sample size and realized error against $\delta$ as the registry–truth mismatch grows.
Proposed Experiments
The testbed is semi-synthetic, because no public dataset contains randomized treatment contrasts across fine biomarker bands.
The retrospective prior comes from TCGA SKCM tumor mutational burden. There, window-based stratification gave $p = 4.9 \times 10^{-5}$ versus $p = 3.7 \times 10^{-2}$ for a median split (Anaya et al.). The "prospective" population is drawn from a different cohort, GENIE BPC or MSK, to mimic repository shift. We use that cohort's biomarker distribution and baseline hazards. Treatment-effect curves are specified in families that include monotone thresholds, plateaus, inverted-U shapes, and deliberately bimodal shapes. The prognostic curve seen in the registry is set to agree, partially agree, or disagree with the predictive curve. A second testbed reuses the JAVELIN Lung 200 re-design settings so our numbers sit next to the reported 845 and 940.
Metrics are total enrolled patients to stopping, probability of identifying the true peak band, realized error rate against targets $\delta \in \{0.05, 0.1\}$, fraction of patients enrolled in bands with no benefit, and robustness under injected pipeline outages at the rate of 10 of 356 days.
Three results decide the question. The first is whether realized error stays at or below $\delta$ in every agreement regime, while the prior-in-stopping ablation exceeds it under disagreement. The second is whether registry steering cuts enrollment relative to cold-start UniTT when the registry peak is within one band of the truth, while staying within the predicted $1/\alpha$ factor when it is not. The third is whether the design beats the two-cutoff enrichment design at $K \ge 8$ bands with comparable error control.
Bimodal scenarios are included to expose honestly the case where unimodality fails and the local certificate is wrong. There we will report the cost of adding a small forced sample in every band as a guard.
References
- Best-Arm Identification in Unimodal Bandits
- Biomarker-guided adaptive enrichment design with threshold detection for clinical trials with time-to-event outcome
- Learning for Dose Allocation in Adaptive Clinical Trials with Safety Constraints
- Characterization of Non-Monotonic Relationships between Tumor Mutational Burden and Clinical Outcomes
- A Seven-Marker Signature and Clinical Outcome in Malignant Melanoma: A Large-Scale Tissue-Microarray Study with Two Independent Patient Cohorts
- Mind the Performance Gap: Examining Dataset Shift During Prospective Validation
- On Multi-Armed Bandit Designs for Dose-Finding Trials
- Unveiling the Prognostic Power and Immune Landscape of MyD88 in Breast Cancer: an Integrative Bioinformatics and IHC Approach
- Transcriptome analysis reveals the link between lncRNA-mRNA co-expression network and tumor immune microenvironment and overall survival in head and neck squamous cell carcinoma