Keeping the Backup Channels: Redundancy as Insurance Against Cross-Hospital Missingness

Clinical prediction models are usually built on one hospital's data and then deployed at another. The second hospital rarely measures the same things at the same rate: one site checks lactate routinely, another almost never does; one charts invasive arterial pressure, another only cuff pressure. A standard instinct in high-dimensional modeling is to strip out redundant inputs (overlapping blood pressure channels, kidney markers that move together) to get a compact, well-conditioned model. We argue that this instinct goes wrong exactly when a model crosses datasets. The redundant channel that looks useless at the source hospital is often the only observed substitute when the "important" channel is missing at the target.

This note proposes to treat redundancy among time-series channels as insurance rather than waste. We build a training procedure that teaches a model to fall back on substitute channels, and a channel-selection rule that keeps substitutes in proportion to how often their primaries go missing across hospitals. The central technical move is to split each patient's missingness pattern into two parts. The first is a site-level part: which channels this hospital records at all, and how often. The second is a patient-level part: when a clinician chose to order a test for this patient, which is known to carry signal about how sick the patient is. We resample only the site-level part from other hospitals during training. This keeps the informative part intact while exposing the model to realistic foreign measurement regimes.

Core Claim

Under cross-dataset deployment, how badly an ICU mortality model degrades at a new hospital is predicted by its uncovered predictive mass: the share of the model's reliance that sits on channels the target hospital does not record, with no observed correlated substitute. Two things should follow. Training with site-level masks borrowed from other hospitals, while preserving each patient's own observation timing, should reduce that uncovered mass and the worst-hospital performance loss. Selecting channels for coverage under foreign masks, rather than for in-dataset importance, should beat importance-based pruning on held-out hospitals, even though it loses slightly in-dataset.

Where This Sits in Prior Work

Three papers motivate the gap. Missingness-Aware Conformal Prediction Under Cross-Hospital Distribution Shift shows on eICU/GOSSIS and MIMIC-IV that missingness masks shift strongly between hospitals and break uncertainty guarantees. It responds with a post-hoc calibration wrapper that splits patients by the single most-shifted missingness indicator. It does not change what the model learns or which channels it uses, and it treats missingness as a static per-admission indicator rather than a time-varying pattern. We borrow its label-free Kolmogorov-Smirnov shift statistic as a diagnostic and attack the problem one stage earlier, in training and selection. E-CatBoost prunes 65 eICU features to 10 using SHAP with a loss of only 0.01–0.04 AUROC, and its authors flag that external validation is missing. That untested step is the one where we expect importance pruning to fail. Looking for Out-of-Distribution Environments in Critical Care runs leave-one-hospital-out evaluation over 127 eICU hospitals. It finds that pooled training beats local training and that smaller recurrent models transfer better. This constrains us: any gain we claim must survive comparison with a small, pooled model.

Two lines of work supply ideas we reuse or contrast with. Redundancy-reduction methods push in the opposite direction from us. TS-Fingerprint forces latent tokens toward orthogonality with a coding-rate penalty. EMTC masks out low-importance variates during training. An EEG Channel Selection Framework keeps the top 10 channels by class-activation voting. All three assume every channel is available at test time, which is exactly the assumption cross-hospital deployment breaks. The EEG study also finds that dropping below about 10 channels collapses accuracy, an early hint that reserve capacity matters.

On the missing-data side, No Imputation Needed (SLAN) and BRITS handle absent observations natively, but only within one dataset. Learning compressed representations of blood samples time series with missing data shows that observation timing itself carries clinical signal. That finding is why we refuse to resample the patient-level part of the mask.

Research Program

The first component is a harmonized multi-source cohort. We use MIMIC-III through the MIMIC-Extract pipeline to get unit-harmonized hourly variables with leakage-safe gap times. We map eICU, PhysioNet 2012 and MIMIC-IV onto a shared vocabulary of physiological and laboratory channels. Channels are grouped by clinical substitutability, such as invasive versus non-invasive pressures or SpO2 versus arterial oxygen. We also compute data-driven groups from source-site partial correlations, so that the hand-built groups can be checked rather than trusted.

The second component is mask decomposition and transfer. For patient $i$ at site $s$, we write the observed mask as $m_{i,c,t}$, which equals 1 if channel $c$ is observed at hour $t$. Each site gets an availability profile $a_{s,c}\in[0,1]$, the fraction of that site's stays in which channel $c$ is ever recorded, and a per-channel sampling rate $r_{s,c}$. During training we draw a donor site $s'$ from the other source hospitals and form the training mask

$$\tilde m_{i,c,t} = m_{i,c,t}\cdot z_{i,c}\cdot u_{i,c,t},$$

where $z_{i,c}\sim\text{Bernoulli}(a_{s',c}/a_{s,c})$, capped at 1, removes whole channels at the donor's availability. The term $u_{i,c,t}\sim\text{Bernoulli}(\min(1, r_{s',c}/r_{s,c}))$ thins surviving observations to the donor's rate. Because the operation only removes the patient's own observations, the timing of whatever remains still reflects that patient's care. The model is never shown a measurement pattern that no clinician produced.

This procedure is model-agnostic. We apply it to three backbones that accept masks and time gaps: a small mask-aware recurrent network of the kind found to transfer best by Spathis and Hyland, SLAN, and CatBoost with native missing handling.

The third component is coverage-aware channel selection. We run greedy forward selection where each candidate channel set is scored by its average validation AUROC under masks drawn from held-out source hospitals, rather than by its importance on the source alone.

The fourth component is the uncovered-mass diagnostic, which tests the mechanism directly. For a trained model we compute per-channel reliance with input-times-gradient attributions on the source. At each target hospital, we sum the reliance on channels that are absent there and have no correlated partner present. We then test whether this label-free number predicts the target hospital's AUROC drop.

Baselines

The naive reference point is mean or last-value imputation feeding a pooled logistic regression on all harmonized channels. It shows how much any learned handling of missingness buys across sites.

The strongest existing in-dataset reference on the shared clinical benchmark is BRITS, which reports in-hospital mortality AUC 0.850 on PhysioNet 2012 (BRITS). SLAN reports AUPRC 55.20 on the same dataset. On eICU, E-CatBoost reports AUROC 0.83–0.91 with 10 features and 0.86–0.92 with 65, within one database. No reported result was found on Lacuna for any of these methods under MIMIC→eICU or leave-one-hospital-out transfer. We therefore rerun them ourselves under our protocol rather than quote in-dataset numbers as targets.

The strongest competitor on our actual question is pooled training of a small mask-aware recurrent model with no mask transfer. Spathis and Hyland found that pooled, underparameterized models are the most robust option across eICU hospitals. A pooled CatBoost with SHAP pruning to 10 channels, following E-CatBoost, is the strongest pruning-based competitor. SLAN trained on pooled sources tests whether native handling of absent channels already solves the problem.

Every method sees the same source hospitals, the same harmonized channels, the same held-out targets and an equal hyperparameter search budget, with tuning done on source-hospital validation folds. No target labels are used for tuning.

The key ablations isolate the two ingredients. The first replaces donor-site masks with uniform random channel dropout matched in overall dropout rate. The second resamples the entire mask from the donor, which destroys patient-level timing. The third removes channel thinning and keeps only whole-channel removal. Beating the competitors means improving worst-decile target-hospital AUROC and the mean target AUPRC by more than the spread across five seeds. In-dataset AUROC may sit no more than about 0.01 below the unaugmented model.

Why not just…?

Why not just use uniform random channel dropout? This is the most serious threat, because generic dropout also teaches models to use substitutes. Our bet is that real site profiles are highly structured: whole lab panels and monitoring modalities disappear together, which uniform dropout rarely produces. The rate-matched uniform-dropout ablation decides this directly. If it matches donor-site masks on worst-hospital AUROC, the contribution reduces to the selection rule and the diagnostic, and we will report it that way.

Why not just prune with SHAP and let CatBoost handle missing values? E-CatBoost shows that this works within eICU. Its top-10 channels are, by construction, the ones most predictive where they are recorded, and that says nothing about whether they are recorded elsewhere. The comparison between coverage-aware and importance-based selection on held-out hospitals tests this. We expect importance pruning to win in-dataset and lose on the hospitals with the most shifted availability, as ranked by the Kolmogorov-Smirnov statistic of Missingness-Aware Conformal Prediction.

Why not just pool all hospitals and use a small model? Spathis and Hyland's evidence makes pooling a genuine contender, and it is our main baseline. Pooling only exposes the model to the availability profiles present in the pool, in their natural proportions. Mask transfer reweights toward rare and extreme profiles. If pooled small models already have low uncovered mass, our method should add little, and the diagnostic will show that.

Why not just rely on an imputation-free architecture like SLAN? SLAN skips absent sensors, but nothing in its training pushes it to build fallback routes when a sensor it relied on is absent for a whole stay. We train SLAN with and without mask transfer, which separates architecture from training signal.

Proposed Experiments

The main experiment trains on MIMIC-III plus a random half of eICU hospitals and evaluates 48-hour in-hospital mortality on the held-out eICU hospitals, on PhysioNet 2012, and leave-one-unit-out on MIMIC-IV. We report mean and worst-decile per-hospital AUROC and AUPRC, given the class imbalance MIMIC-Extract documents.

The first decisive check is whether uncovered predictive mass, computed without target labels, correlates with per-hospital AUROC drop across held-out eICU hospitals. A weak correlation would undermine the mechanism even if accuracy improves.

The second decisive check is a controlled substitution test on PhysioNet 2012. We remove one channel from a known substitute group at test time, for example invasive pressure while cuff pressure remains. We then measure how much of the lost AUROC each model recovers when the substitute is present versus also removed.

Finally, we pass all models through missingness-aware Mondrian conformal calibration. On GOSSIS, that calibration reduced the maximum subgroup coverage gap from 0.028–0.044 to 0.015–0.021. The question is whether mask-transferred models narrow those gaps further, which would show that training and calibration fix different parts of the shift.