Hospital Load as a Hidden, Uneven Shift in ICU Risk Models

When intensive care units fill up, patients die at higher rates even after accounting for how sick they were on arrival. A nationwide Israeli study of 22,636 COVID-19 inpatients found 14-day mortality 22–27% above expectation once severe-case load passed about 500 patients, well below the official 800-patient ceiling (Hospital load and increased COVID-19 related mortality in Israel). The machine-learning mortality models that hospitals use for triage and capacity planning are trained on pooled records and ignore how full the unit was when each patient was admitted. Those models already perform worst on the demographic groups with the highest baseline mortality (MIMIC-IF). This note asks whether hospital load is a hidden distribution shift that makes these models under-predict risk exactly when capacity is scarce, and whether that under-prediction falls unevenly across racial, ethnic and ancestral groups.

The core idea fits in two sentences. First, measure how a standard ICU mortality model's calibration drifts as a function of unit occupancy, separately for each patient group. Second, test whether a small post-hoc correction indexed jointly by load and group repairs the drift better than simply feeding load and group into the model as extra inputs. The second question is borrowed from statistical genetics. There, adding ancestry as a covariate next to an uncalibrated score produced unstable, spurious effects, while regressing the score on continuous ancestry repaired risk stratification (Ancestry Calibration of Polygenic Risk Scores). The downstream stake is triage. If model error under load concentrates in one group, a capacity-limited system for deferring hard cases to clinicians will push that group into the human queue at the moment the queue is blocked.

Core Claim

We claim, as a testable hypothesis, that the gap between predicted and observed mortality grows with unit load. We also claim that the slope of that growth differs by group, which is the new and falsifiable part. Existing saturation models apply one uniform degradation factor. Gorji et al. double the case fatality rate above ICU capacity (Dynamic modelling to identify mitigation strategies), and Rossman et al. estimate a single population-level excess. Existing fairness audits such as MIMIC-IF treat ICU stays as independent and never condition on concurrent census. Neither line asks whether the load penalty is group-specific.

The correction we test is a load-and-group calibration map. Let $p$ be a frozen model's predicted mortality, $L$ the normalized unit occupancy at admission (current census divided by that unit's own 95th-percentile census), and $g$ the patient's group. The calibrated risk is

$$ \hat p = \sigma\big(a_g(L) + b_g(L)\,\mathrm{logit}(p)\big), $$

where $\sigma$ is the logistic function. The functions $a_g$ and $b_g$ are low-degree splines in $L$, shrunk toward a shared curve across groups. The scientific quantity of interest is the between-group spread in $a_g(L)$ at high $L$. If the spread is near zero, the uniform-penalty assumption in saturation models is adequate, and the proposal reduces to "recalibrate on load."

Research Program

Load construction. The first obstacle is data, and it constrains the design. Computing load requires true concurrent admission times. To our understanding, MIMIC-IV shifts dates independently per patient, and eICU exposes only offsets, time of day and year. Neither lets us reconstruct cross-patient census reliably. The public benchmarks are therefore used to develop the models, and the load question is answered in two other settings. The first is a semi-synthetic stress test on eICU and MIMIC-IV. We attach simulated occupancy trajectories to real stays and inject load-dependent excess mortality whose magnitude is anchored to Rossman's 22.1% and 27.2% estimates. The injected slopes are either uniform or group-heterogeneous, and we check which methods detect and correct each case. The second is a real timestamped ICU cohort from a health system spanning COVID-19 surge and non-surge periods, obtained under a data use agreement. It records self-reported race and ethnicity, and, where biobank-linked, continuous genetic ancestry. Continuous ancestry lets us apply the Vargas-style continuous calibration directly rather than using categorical race.

Measurement. On the real cohort, the base model is a CatBoost mortality model in the style of E-CatBoost, trained on low-load periods. We estimate its calibration curve as a function of $L$ within each group. Hospital fixed effects and case-mix adjustment follow Rossman's covariates: age, sex, admission severity and prior hospitalization. The aim is to separate load from "sicker patients arrive during surges."

Correction. We compare the calibration map above against retraining with load and group as features.

Deferral consequence. Following Differentiable Learning Under Triage, the optimal deferral rule defers a patient when the model's expected error exceeds the clinician's. We make the clinician budget $b$ shrink as $L$ rises and record the group composition of deferred patients. We then compare deferral driven by raw model confidence against deferral driven by load-calibrated expected error.

Baselines

Do nothing. The naive reference is the frozen low-load CatBoost model with no load information. As an external discrimination anchor on the same task family, E-CatBoost reports AUROC 0.83–0.91 with 10 features on eICU (E-CatBoost). MIMIC-IF reports AUROC 0.955 and AUPRC 0.769 for IMV-LSTM on MIMIC-IV (MIMIC-IF). We re-implement IMV-LSTM as a second base model so the conclusions do not depend on one architecture.

Strongest competitor: load-as-feature retraining. Here the same model is retrained with $L$, group, and their interaction as inputs. This is the most direct fix and could plausibly win. It gets the same training data and the same hyperparameter search budget as the full CatBoost pipeline, while the calibration map is fit on a held-out calibration split of equal size. Beating it means a lower within-group expected calibration error in the top load quintile. The difference must hold under bootstrap confidence intervals over hospitals, with no loss in AUROC.

Group-only recalibration. This fits $a_g, b_g$ without load, like standard per-group Platt scaling. It isolates whether load adds anything beyond ordinary group calibration.

Uniform-load ablation. This fits $a(L), b(L)$ shared across groups, mirroring the single degradation factor in Gorji and Rossman. It is the ablation that isolates our key ingredient, the group-by-load interaction.

Deferral baselines. For triage we compare confidence-based deferral with the co-optimized triage of Okati et al. No reported numerical error rate is found on Lacuna for Differentiable Triage, whose results appear only as budget curves, so we re-run it on our splits.

Why not just…?

Why not just add unit census as a model feature? This is the real threat, and the proposal is built to settle it rather than argue around it. High-load admissions are rare in training data, so the load-by-group interaction terms rest on few events. That is the regime in which Vargas et al. found covariate inclusion produced unstable, artifactual effects that post-hoc calibration avoided (Ancestry Calibration of Polygenic Risk Scores). The semi-synthetic test shows which method recovers injected group-specific slopes at realistic high-load sample sizes. If retraining matches calibration there and on real data, we report that retraining suffices. In that case the contribution is the audit showing that load must be modeled, not the correction.

Why not just recalibrate each group and ignore load? It would repair average miscalibration but not drift during surges. Rossman's model matched observed mortality within 0.6% at low load, yet under-predicted by 22–27% at high load. A static per-group fix tuned on mostly low-load data would inherit that gap. The group-only baseline measures this directly.

Why not just impose a per-group quota on deferrals? Quotas cap who reaches clinicians but do not fix the underlying error. A quota would push misestimated high-risk patients back to automated handling, which is the harm MIMIC-IF's high-risk, low-AUC pattern warns about. We run confidence deferral with quotas as a baseline. We score it on deaths among automated-handled patients per group, not only on deferral share.

Decisive Checks

The first check is the semi-synthetic benchmark. With uniform injected load effects, the group-heterogeneous map must not invent spurious between-group differences; the false-positive spread in $a_g(L)$ must stay within bootstrap noise. With heterogeneous effects, it must recover the injected slopes more accurately than load-as-feature retraining.

The second check is on the real cohort. The primary outcome is whether the between-group difference in calibration slope at the top load quintile has a confidence interval excluding zero after hospital and case-mix adjustment. A null here is informative. It would say saturation models' uniform penalty is justified for this population, and the fairness gaps in MIMIC-IF are not amplified by load.

The third check is triage. As $b$ shrinks with $L$, we compare how much each group's deferral share rises, and each group's mortality among automated-handled patients, under raw-confidence versus load-calibrated deferral. Success means load-calibrated deferral reduces the gap between groups in excess automated-handled mortality without raising overall error.