Population Synthesis with a Selection Model for Biased Biomarker Cohorts

Astrophysicists who study binary stars rarely fit their models directly to the stars they observe. They first simulate a full synthetic population of millions of star pairs from assumed birth distributions, then run that population through a model of the telescope survey, which decides which simulated stars would have been bright enough, close enough, or short-period enough to be catalogued. Only that filtered synthetic catalogue is compared with the real one. This method is called binary population synthesis. We propose to bring this workflow into longitudinal biomarker studies, where clinicians track lab values such as albumin or neutrophil counts over time and relate them to death or disease progression. In those studies the analysed cohort is often a small, heavily filtered remnant of the patients who were actually treated. One acute myocardial infarction study ended with 288 analysable patients out of 3,235, largely because serial albumin values were missing (Zhang/Yang et al.). An ICU study kept 5,056 patients with complete data out of more than 30,000 (Salciccioli et al.). In intensive care, labs are also ordered more often when patients look sicker.

In two sentences, the idea is this. We simulate the whole patient population, including patients who would never make it into the published cohort. We then apply an explicit, code-level model of how measurements get taken and how patients get excluded, and fit the simulator so that its filtered output matches the observed cohort. The payoff is a test of whether the trajectory–outcome associations reported in this literature, such as S-shaped risk curves, inflection points, and odds ratios, describe biology or describe who got measured.

Core Claim

Our claim is that a selection-aware forward simulator, calibrated by comparing distributions of the filtered population, recovers true trajectory–outcome effects more reliably than per-patient likelihood models when two conditions hold. The first is that the observation process depends on the latent disease state. The second is that cohort inclusion is defined by rules, such as "at least k measurements," "complete blood count on day 1," or "survived 48 hours." The second condition matters because these rules are easy to write as code but awkward to write as a likelihood. The claim is falsifiable on semi-synthetic data, where the true effect is known. It is also checkable on real data through a specific posterior predictive test: a model fitted to the full MIMIC-III population should predict what a complete-case analysis of that same database will report.

What We Borrow, and What Constrains Us

Three astrophysics papers supply the method. Meskhi et al. forward-modelled 681 supernova progenitors under six nuclear equations of state. They compared the resulting remnant-mass distributions with LIGO/Virgo and pulsar catalogues using Kullback–Leibler divergence (a measure of how much one probability distribution differs from another) and total-variation distance, with bootstrap uncertainty. We reuse this design: candidate physical models are ranked by distributional distance between synthetic and observed populations, rather than by per-object likelihood. Their simulator is deterministic and has no selection stage, and adding a selection stage is exactly our contribution. POSYDON and POSYDON v2 show how to make an expensive simulator usable at population scale. They first apply a k-nearest-neighbour classifier, which assigns each new binary the outcome of its most similar simulated neighbours, to choose an outcome class. They then interpolate continuous properties within that class, reporting median relative errors "typically 1% or better." We adopt this classify-then-interpolate emulator, a fast approximation that stands in for running the simulator, for patient outcome regimes (survived, died before the next scheduled measurement, discharged early). This emulator is what lets us run inference over many simulator parameters. The work on stellar profile emulators supports the same amortisation strategy.

Two further astrophysics results motivate the selection stage. Abate et al.'s carbon-enhanced metal-poor star work (2015 model, orbital periods) shows a field arguing over whether a mismatch between predicted and observed orbital periods, and a missing population of dwarf stars, reflect missing physics or survey selection against long-period, faint systems. It is the same ambiguity clinicians face with exclusion-filtered cohorts. F. Zhang et al. show the cost of leaving a subpopulation out of the forward model. Omitting binary-interaction products biases inferred galaxy ages by several gigayears. We expect that omitting unmeasured patients similarly biases inferred hazard ratios.

On the clinical side, two papers motivate the gap. The albumin study's S-shaped mortality curve, with inflection points near −3.27 and 0.92 g/L, was estimated on the 288-patient survivor-of-selection cohort (Zhang/Yang et al.). Salciccioli et al. found that the neutrophil-to-lymphocyte ratio carried no prognostic signal in sepsis, attributing this to saturation, and their analysis used complete-data patients only (Salciccioli et al.). Our method can ask whether the sepsis null partly reflects who had complete counts.

The joint-model literature constrains the design and supplies the strongest baselines. The multivariate Gaussian-process joint model of Joint Longitudinal-Survival with Multiple Biomarkers treats each patient's correlated biomarkers as a smooth random curve. It already shows that handling death-truncation properly changes the albumin hazard ratio from 3.4 under last-observation-carried-forward to 5.1. Any proposal must therefore beat a model that already handles dropout due to death. The roughness-based joint model of Weighted biomarker variability shows that trajectory volatility is itself predictive, with a hazard ratio of 1.14 per standard deviation of systolic blood pressure variability. So our simulator must generate realistic volatility and not only smooth means. GALE links individual trajectories to a population-level trend, but it is a retrospective representation learner with no generative or selection component, so it is a contrast rather than a competitor. MIMIC-Extract supplies the reproducible preprocessing pipeline. Its exclusion rules (stays of 12 hours to 10 days, outlier clipping, gap windows) are themselves part of the selection operator we model.

Research Program

The simulator has three stages, mirroring the structure of binary population synthesis. The first stage is an initial-condition sampler. It draws admission state (age, comorbidity, latent severity) from distributions fitted to every admission in the database, not just to analysable ones. The second stage is an evolution engine: a low-dimensional stochastic differential equation, a model in which each quantity drifts deterministically and also receives random kicks, for two or three coupled biomarkers. For MIMIC these are albumin, neutrophil-to-lymphocyte ratio, and creatinine. The drift encodes mean reversion and coupling, and a volatility term reproduces the roughness effect. A hazard depends on the latent levels, with parameters $\theta$ that include the effect sizes we want to estimate. The third stage is the selection operator $S_\phi$, written as executable code. It contains a measurement-intensity model in which lab-ordering rate rises with latent severity, death and discharge truncation, and the literal inclusion rules of each target study.

Calibration fits both parameter sets by matching filtered synthetic data to observed data:

$$ (\hat\theta, \hat\phi) = \arg\min_{\theta,\phi} \; D\big(S_\phi(P_\theta),\, O\big), $$

where $P_\theta$ is the synthetic population before selection, $O$ is the observed cohort, and $D$ is a distributional distance. Following Meskhi et al., $D$ is total variation over binned summaries: measurement counts per patient, inter-measurement gaps, biomarker level and change at each measurement, and outcome. In practice we run simulation-based inference with the POSYDON-style emulator so that posterior samples over $(\theta,\phi)$ are affordable.

Identifiability is the central technical risk. Disentangling "sick patients get measured more" from "high values predict death" requires variation that the selection model cannot absorb. We obtain it from two sources. The first is fixed-schedule measurements, such as routine morning labs, whose timing does not depend on severity. The second is the contrast between the full admission population and the filtered subsets. We will report the posterior correlation between $\theta$ and $\phi$, and we will declare a parameter unidentified rather than report it when its posterior does not concentrate.

Baselines

The naive reference point is the published analysis style. This means complete-case Cox or logistic regression on baseline or last-observation-carried-forward values, applied to the filtered cohort. On DaVita this approach gave an albumin hazard ratio of 3.4 against 5.1 from the joint model (Joint Longitudinal-Survival). For neutrophil-to-lymphocyte ratio on MIMIC-II it gave an adjusted odds ratio of 1.71 for the top quartile and an AUC rise from 0.746 to 0.757 over the SAPS I severity score (Salciccioli et al.). We rerun it on our MIMIC-III cohort with identical variable definitions.

The strongest existing method is the multivariate Gaussian-process joint longitudinal-survival model (Joint Longitudinal-Survival). It is the strongest competitor because it already models cross-biomarker correlation and death-truncated dropout, which are the two mechanisms most likely to explain away our gains. We fit it to the same filtered cohorts, with the same biomarkers and the same compute budget for Markov chain Monte Carlo sampling. Because the original reports that fully Bayesian sampling is intractable beyond about 10,000 patients, we subsample if necessary and report this. The second joint-model baseline is the roughness model (Weighted biomarker variability), run with matched spline knot budgets. We also add inverse-probability weighting, which reweights each analysed patient by the inverse of the estimated probability of being included, applied to the joint model. Inclusion probabilities come from a gradient-boosted classifier trained on admission covariates with the same tuning budget as our emulator.

Beating these baselines means lower absolute bias and nominal 90% interval coverage for the true hazard coefficient and the true inflection locations in the semi-synthetic benchmark, across at least three of our four selection severities. On real data it means a better posterior-predictive match to held-out complete-case statistics. No reported result was found on Lacuna for bias or coverage of these models under informative measurement selection, so those numbers will be established here. As a predictive sanity floor, MIMIC-Extract reports mortality AUROCs of 0.85 to 0.90 (MIMIC-Extract). We do not aim to beat this, but if our hazard model falls far below it, the simulator is misspecified.

The key ablation removes the selection operator, setting $S$ to the identity on analysed patients while keeping the same simulator and the same distributional calibration. This isolates whether gains come from modelling selection or merely from mechanistic simulation. A second ablation keeps selection but swaps the distributional distance for a per-patient likelihood where one is tractable. This tests whether the Meskhi-style population comparison matters.

Why not just…?

Why not just fit a joint model, which already handles informative dropout? Shared-random-effect joint models handle dropout caused by death or by the latent trajectory. They condition on the observed measurement times, however, and they are fitted to whoever passed the inclusion rules. When labs are ordered because a clinician sees deterioration, and the cohort is defined by having enough labs, the analysed patients are selected on the outcome pathway itself. This is a real threat, though: if inclusion depends only on the latent trajectory, a joint model could be nearly unbiased. The semi-synthetic benchmark includes exactly this condition (selection depending on the latent trajectory only) as a setting where we predict no advantage. If we find the joint model ties us across all four severities, the proposal's claim fails. We would then report that the selection-function borrowing adds nothing beyond joint modelling.

Why not just reweight with inverse-probability weights for inclusion? Weighting corrects selection that is random conditional on observed admission covariates. It fails when inclusion depends on unmeasured in-stay severity, which is precisely the clinician-ordering mechanism. Weights also become extreme when, as in the albumin study, fewer than 10% of patients are retained (Zhang/Yang et al.). We include weighting as a baseline. Our prediction is that it matches us when selection depends only on admission covariates and degrades as selection depends on latent severity. The benchmark varies exactly this.

Why not just train a deep generative model of EHR trajectories and sample synthetic patients from it? A learned generator trained on recorded data reproduces the recorded data, selection artefacts included. It has no separate selection stage that can be switched off to reveal the unselected population. The Abate et al. debate (orbital periods) shows that separating "physics" from "survey" requires the two to be distinct, interpretable components. A flexible generator could still serve as the evolution engine. We keep the engine low-dimensional for identifiability, and we treat a learned engine as a follow-up only if the mechanistic one fails posterior-predictive checks.

Proposed Experiments

The first experiment is a semi-synthetic ground-truth benchmark. We sample populations of 30,000 synthetic ICU stays from the simulator with known hazard coefficients and a known S-shaped albumin-change effect. We apply four selection severities, ranging from random measurement to strongly severity-driven ordering combined with an inclusion rule of at least k measurements retaining about 9% of patients, the albumin study's ratio. Every estimator is then fitted. Metrics are bias, root-mean-square error, and 90% interval coverage for the hazard coefficient and the inflection points. Each cell uses 50 replicate populations, with bootstrap uncertainty in the style of Meskhi et al.

The second experiment, the decisive real-data check, is a predictive test on MIMIC-III processed with MIMIC-Extract. We calibrate the simulator on all eligible admissions. We then apply, in simulation, the complete-blood-count inclusion rule and quartile cut-points of Salciccioli et al. From the simulated cohort we predict the odds ratio, the AUC gain over a severity score, and the sepsis-subgroup interaction that a complete-case analysis will produce. Only then do we run that analysis on the real filtered cohort. Because Salciccioli et al. reported 1.71 and 0.746→0.757 on MIMIC-II, a direct match is not expected; the test is against our own MIMIC-III replication. A model that predicts the filtered-cohort statistics from the unfiltered population, while the no-selection ablation does not, is strong evidence that the selection stage captures something real. We then report the simulator's selection-corrected estimate, especially whether the sepsis null persists once selection is modelled.

The third experiment changes the regime. On ADNI, dropout comes from visit attrition rather than lab ordering. We ask whether baseline-only versus longitudinal p-Tau217 conclusions shift under modelled attrition, using the Random Survival Forest result of AUROC 0.787 for baseline p-Tau217 (Chen et al.) as the reference to replicate first. A null result here would be informative too. It would indicate that population synthesis with a selection model helps in acute care, where measurement depends on severity, but not in scheduled-visit cohorts, which is a scope statement we would publish.