When a hospital cannot treat every cancer patient at once, someone has to decide who waits. Today that decision rests on fixed rules of thumb drawn from retrospective studies, such as "intermediate-risk prostate cancer tolerates about four months." This proposal builds a model that answers a more specific question for each patient: how much worse their expected outcome becomes for every extra week before definitive treatment, given everything their record shows so far. We call this a personal delay curve.
The main obstacle is not model capacity. Historical records are biased against the answer. Clinicians speed up treatment for patients who look worse, so in the data, short waits travel with bad outcomes. A model that simply predicts outcome from waiting time will learn that waiting is harmless, or even protective. The bias is worse because the signals that trigger expediting, such as a rising lab value or a new interval scan, appear during the wait. Removing it therefore needs longitudinal reasoning that tracks how the record changes over time, not a snapshot at diagnosis. The same records also show that waits are unevenly distributed across populations and sites. Any learned delay curve may therefore be reliable for some groups and pure extrapolation for others.
Core Claim
Estimating delay tolerance is a problem of cause and effect under feedback that changes over time. It should be solved with methods built for that, not with better prediction. Our central claim is that a longitudinal encoder becomes valuable when it serves as the adjustment set for confounding that develops during the wait. In that role it recovers known delay effects that both static-covariate survival models and large prognostic models with "delay" as an input feature get wrong. We also claim that the COVID-19 backlog, which imposed delays for system reasons rather than patient reasons, can serve as a quasi-prospective test. It lets us check delay curves learned from pre-pandemic data without running a randomized trial. Finally, we claim that population bias here takes a specific form. Some groups rarely appear with short waits, so their curves cannot be estimated from the data, and this can be measured and reported per group.
Formally, for patient $i$ with record history $H_i(t)$ up to time $t$, potential outcome $Y_i(d)$ (for example, two-year metastasis-free survival) under wait $d$, and a reference wait $d_0$ (for example, 4 weeks), the target is the delay curve
$$\tau_i(d) = \mathbb{E}\left[\,Y_i(d) - Y_i(d_0) \mid H_i(t_{\text{dx}})\,\right],$$
where $t_{\text{dx}}$ is the diagnosis time. A queue policy needs $\tau_i(d)$ and its uncertainty, not a risk score.
Why This Intersection, and What Exists
The clinical literature motivates the target and supplies anchors with known answers. Meta-analyses of radical prostatectomy timing (Chan et al.) report worse pathology beyond 4 months and lower biochemical recurrence-free survival beyond 6 months. BCG timing after bladder tumor resection shows a hazard peak for progression near 18 weeks (Krajewski et al.). In urothelial carcinoma, the survival harm of waiting for surgery disappears in patients given neoadjuvant chemotherapy (Leow et al.). Low-risk prostate cancer on active surveillance tolerates years of delay, and neoadjuvant hormone therapy buys months (Mohamad et al.). In small renal tumors, delay can raise mortality without visible growth (Chan et al., RCC). That last finding argues that the relevant trajectory includes more than tumor size.
The same papers also limit what we can claim. All of them are retrospective, they define "delay" inconsistently, and Mohamad et al. note there is no prospective trial evidence on acceptable windows. We use these results as population-level anchors that a correct method should approximately reproduce, not as ground truth for individuals.
The closest existing system is oFM. It is a multimodal temporal Transformer trained on 1.67 million real-world oncology records that predicts survival and which therapy helps. It reports a mean overall-survival AUC of 0.774 against 0.563 for expert-curated features. oFM supplies the method we reuse, a long-horizon patient encoder, but it implicitly assumes treatment starts instantly. Its authors also acknowledge confounding in how treatments were assigned. We change the question from which therapy to when, and we change the estimation from prediction to adjustment for confounding that evolves over time.
Temporal imaging models motivate using change over time rather than snapshots. These include BioViL-T, which separates current state from interval change; DeltaNet, which encodes differences against a prior scan; and CRONOS, which reconstructs series in continuous time under irregular sampling. Only CRONOS was built for irregularly spaced, arbitrary-length histories. That property matters because waits generate exactly such histories. All three, however, output diagnoses or reports and never a quantity a scheduler could act on.
Work on triage connects urgency to deployment but stays cross-sectional. Examples are the sepsis trigger of Horng et al., the mammography worklist simulation of Yala et al., and the LLM emergency-triage study of Lee et al.. Horng et al. explicitly warn that a retrospective AUC of 0.86 says nothing about whether acting on the alert changes outcomes. This is the gap between retrospective and prospective validation that our pandemic test targets. Differentiable Learning Under Triage jointly optimizes a model and a human deferral rule under a capacity budget. However, it treats each case statically and ignores the fact that deferral itself adds waiting time.
Research Program
The work has four parts.
Part 1: build the delay cohort. We construct a delay-analysis cohort from a longitudinal real-world oncology corpus of the kind used by oFM (access through the Tempus collaboration or an equivalent multi-site registry). We fix a single delay definition: biopsy date to definitive treatment start. Indications are chosen where the anchors exist: localized prostate cancer by risk group, high-grade non-muscle-invasive bladder cancer awaiting BCG, urothelial carcinoma awaiting cystectomy or nephroureterectomy, and small renal masses. Each patient's history is encoded as irregularly timed events (labs such as PSA, imaging reports, pathology, systemic therapy start) with an oFM-style temporal encoder using continuous-time position encodings.
Part 2: estimate the curve. Here the longitudinal reasoning does its main work. We fit a sequential, g-formula-style estimator, which simulates outcomes under hypothetical waiting schedules while accounting for what was observed along the way. Week by week, it models two things from the encoded history so far: the hazard of being treated and the outcome. Events during the wait that both trigger expediting and predict prognosis are therefore adjusted for, not ignored. Treatment-timing propensities give a per-patient overlap score: how often patients with similar histories were actually observed at each wait length. Neoadjuvant systemic therapy enters as a time-varying modifier, so the model can learn the "stopping the clock" buffer instead of having it imposed.
Part 3: audit by population. For each group defined by race, ethnicity, payer, site, and their intersections, we report three things: the overlap distribution, the calibration of predicted delay effects, and how far the curve shifts when we swap demographic fields in otherwise identical histories. The swap test adapts the counterfactual token-swapping audit of Lee et al. from acuity labels to delay curves. A group with poor overlap receives a curve flagged as extrapolated, not a confident number.
Part 4: simulate queue policies. We replay historical queues and ask what each policy would have done. The policies are first-come-first-served, guideline windows, and ordering by $\tau_i(d)$. We estimate their outcomes with doubly robust off-policy evaluation, which combines the outcome model and the treatment-timing model so that an error in either one alone does not bias the estimate. We also report how each policy redistributes waiting time across groups. This test matters because a tolerance-based policy could quietly shift waits onto exactly the groups whose curves are least reliable.
Baselines
The naive reference is current practice: first-come-first-served scheduling plus fixed guideline windows by risk group, taken from the meta-analyses above. Against this baseline, the question is whether personalization adds anything beyond the published thresholds. We count a win only if the proposed policy improves estimated outcome at matched capacity, and does so without increasing wait disparities.
The standard retrospective analysis is a Cox survival model of outcome on delay, adjusted for baseline stage, risk group, and comorbidity. This is how most delay thresholds in the file were derived. It runs on the same cohort with the same outcome definition. Beating it means recovering the anchors more closely. Two anchors are especially telling: the flattening of the delay effect under neoadjuvant therapy and the near-zero effect in low-risk prostate cancer on surveillance.
The strongest existing competitor is an oFM-style longitudinal prognostic model with wait time added as an input. We read its curve off by varying that input. For prognosis, oFM reports a mean overall-survival AUC of 0.774 against 0.563 for expert-curated features (oFM). We found no reported result on Lacuna for any method estimating individual treatment-delay effects. This baseline uses the same encoder architecture, pretraining data, compute, and tuning budget as our estimator, so the only difference is how it is estimated. We expect it to match or beat us on prognostic AUC and lose on effect recovery. That dissociation is the point of the comparison.
The key ablation keeps our estimator but restricts adjustment to the diagnosis-time snapshot. It drops events that occur during the wait. If this ablation performs as well as the full model, then longitudinal reasoning is not needed for this problem, and we would report that.
Why not just…?
Why not just add delay as a feature to a strong prognostic model? Such a model learns the association between waiting and outcome, and in historical data that association is confounded by expediting. High prognostic accuracy is compatible with a delay coefficient of the wrong sign. The semi-synthetic experiment below tests this directly. We impose expediting driven by trajectory with a known true effect on real histories, and measure whether each method recovers it.
Why not just use the published guideline thresholds? This is a real threat. For some indications, population thresholds may capture nearly all the actionable variation, and Mohamad et al.'s surveillance results suggest that risk group alone already separates patients who can wait years from those who cannot. The off-policy queue replay settles the matter per indication. Wherever personalized curves fail to beat guideline windows at matched capacity, we will say the guideline suffices there.
Why not just run a randomized trial of delay windows? Trials are what ultimately settle this, but randomizing cancer patients to longer waits is ethically fraught, which is why Mohamad et al. find none. This work does not replace a trial. It produces candidate windows, together with the patient subsets where uncertainty is largest. That tells us where a pragmatic trial or stepped deployment would be most informative and least risky.
Why not just reweight minority groups during training? The problem is not too few samples. It is that some groups were systematically observed only at certain wait lengths. Reweighting cannot create overlap that does not exist. FairDiffusion (paper) found that sample balancing does not track where subgroup error concentrates, and RETFound (Zhou et al.) found that scale alone entrenches majority patterns. We therefore measure overlap explicitly and refuse to emit confident curves where it fails.
Proposed Experiments
Semi-synthetic recovery. We keep real patient histories and simulate outcomes with known delay curves that include nonlinear tipping points and neoadjuvant buffers. We then impose treatment-timing rules in which worsening interim labs or scans trigger expediting, at increasing strength. The metric is the error of each method's estimated $\tau_i(d)$ against the truth, overall and by subgroup. The prediction is that the oFM-with-delay baseline and the diagnosis-time-only ablation degrade as expediting strength grows, while the full estimator does not.
Anchor recovery on real data. Population-averaged curves should reproduce three published patterns. First, harm beyond roughly 4 to 6 months in intermediate- and high-risk prostatectomy (Chan et al.). Second, a peak near 18 weeks for BCG (Krajewski et al.). Third, the neutralizing effect of neoadjuvant chemotherapy (Leow et al.). As a negative control, the effect should be near zero for low-risk prostate cancer on surveillance. A method that fails the negative control is disqualified regardless of its other scores.
Pandemic temporal holdout. This is the decisive test of the gap between retrospective and prospective validation. We train only on pre-2020 records and evaluate on patients whose treatment was postponed during the COVID-19 backlog. During that period, delay was driven far more by system capacity than by patient condition, as the triage experiences reported by Teoh et al. and Rodríguez-Carrasco et al. document. The test compares predicted against observed outcome differences across bins of imposed delay, within strata of predicted tolerance. If curves learned from confounded pre-pandemic data do not predict who was harmed by exogenous postponement, the method has not closed the gap. We would report that negative result.
Population and site transfer. We train at a subset of sites and test at held-out sites. We report delay-effect calibration and overlap by race, ethnicity, payer, and their intersections, along with the demographic-swap sensitivity of curves. The queue replay additionally reports the change in median wait per group under each policy. A policy that improves average outcome but lengthens waits for a group with low overlap counts as a failure, not a trade-off.
References
- Effects of Delayed Radical Prostatectomy and Active Surveillance on Localised Prostate Cancer—A Systematic Review and Meta-Analysis
- Delaying BCG immunotherapy onset after transurethral resection of non-muscle-invasive bladder cancer is associated with adverse survival outcomes
- A systematic review and meta-analysis on delaying surgery for urothelial carcinoma of bladder and upper tract urothelial carcinoma: Implications for the COVID19 pandemic and beyond
- Delayed definitive management of localized prostate cancer: what do we know?
- Delayed surgery for localised and metastatic renal cell carcinoma: a systematic review and meta-analysis for the COVID-19 pandemic
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- Learning to Exploit Temporal Structure for Biomedical Vision-Language Processing
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- FairDiffusion: Enhancing Equity in Latent Diffusion Models via Fair Bayesian Perturbation
- A foundation model for generalizable disease detection from retinal images
- Intravesical therapy for bladder cancer in the pandemic of Covid-19
- COVID-19 and endoscopic management of superficial gastrointestinal neoplastic lesions: a multinational cross-sectional survey