Which Time Scale Is the Model Listening To? Scale-Resolved Attribution for Cross-Site Bias in ICU Time Series

Before a clinical model sees a patient's vital signs, the data are almost always smoothed. Someone picks a window, often a rolling average over a few hours, and applies it to every channel, every patient, and every hospital. This note argues that the window is not a harmless cleaning step. It decides which time scales of the signal the model can use. Some fine-scale content is real physiology, such as a sudden blood-pressure drop. Some is an artifact of a particular hospital: how often nurses chart, how its monitors round values, how its records are formatted. If a model leans on fine-scale content that differs by site, it will look accurate at home and fail elsewhere, and patient groups who are charted differently will be hit hardest.

We propose a simple diagnostic and test what it is worth. For each input channel, split the signal into a smoothed trend and the leftover residual the smoother removes. Then measure exactly how much of the model's prediction comes from that residual, across a ladder of window widths. The output is a "scale profile" that shows, in clinically readable terms, whether the model is responding to the heart-rate trend or to heart-rate jitter. The central empirical question is whether this profile predicts which models will degrade at unseen hospitals and in which demographic subgroups. The method question is whether choosing smoothing per channel from the profile beats the obvious alternative of tuning one global window for worst-group accuracy.

Core Claim

Reliance on fine-scale residual content that is also predictive of hospital identity is a measurable signature of a temporal shortcut in clinical time-series models. Here a shortcut means a feature that predicts the label at the training site for reasons unrelated to disease. Removing that content selectively, channel by channel, should narrow cross-site and cross-subgroup performance gaps more than any single global smoothing window, without the peak-flattening losses that uniform smoothing causes.

To make reliance exact rather than heuristic, let $f$ be the trained model, $x$ a patient's multichannel series, and $S_w$ a smoother of width $w$ (a uniform moving average or a Savitzky–Golay local polynomial filter). We define the residual reliance as

$$\Delta_w(x) = f(x) - f(S_w x) = \sum_{c,t} A_{c,t}(x; S_w x),$$

where $A_{c,t}$ is the integrated-gradient attribution to channel $c$ at time $t$, computed along the straight path from the smoothed input $S_w x$ to the raw input $x$. Integrated gradients add up exactly to the change in output between the two endpoints, so this decomposition is exact. Using the smoothed series as the starting point, instead of zero, is what makes the attribution answer the question "what did the removed content contribute?"

We then fit a small classifier that predicts hospital identity from each channel's residual. A channel whose residual carries large reliance and also strongly identifies the site is the flag the diagnostic raises.

Relation to Prior Work

Two papers supply the motivation. MIMIC-IF benchmarks 12 attribution methods on MIMIC-IV mortality using Remove-and-Retrain. It finds that attention weights are unfaithful and that ArchDetect is the most robust attribution method. It also shows that models weight features differently across ethnic groups and that groups with higher baseline mortality get lower AUC. However, it treats the 164 temporal variables as given and never asks what preprocessing did to them. Towards Large-scale Clinical Multi-variate Time-series Datasets harmonizes more than 600,000 ICU stays across the US, Europe, and China. It shows that transfer is much better within a region than across regions, but it offers no explanation of what the models latch onto. Our diagnostic is aimed squarely at that unexplained cross-region gap.

One paper supplies the closest method. Gradient-based Model Shortcut Detection flags "point shortcuts," meaning isolated spikes, using the share of gradient mass concentrated at one time step. It reports 83.3% detection on 40 UCR datasets with synthetic spikes and 100% specificity on clean data. We differ in three ways. We resolve reliance by time scale rather than by single point. We test on real multi-site clinical data where the shortcut is unknown. We link the diagnostic to subgroup and site gaps rather than to detection accuracy on planted spikes.

Two papers constrain the design. EpiFlow and The Application of FFT Analysis on the Feeder Current show that uniform averages blunt and shift peaks, while Savitzky–Golay filters preserve peak height and timing. For that reason we treat the smoother's family as an experimental factor rather than assuming a moving average.

Simplicity Creates Inequity cuts against the proposal and has to be addressed directly. It proves that coarsening a predictor washes out high-performing members of disadvantaged groups, and it names smoothing as an open case. Our intervention is a form of coarsening. We therefore cannot assume it helps minority groups. Our evaluation must be able to show that targeted smoothing widens subgroup gaps, and if it does, we will report that as the result.

Research Program

The work has three parts.

The first part validates the diagnostic under controlled conditions, following the planted-shortcut design of the shortcut-detection paper. In the harmonized cohort, we inject a site-specific artifact into one hospital's data, for example measurement jitter or value rounding at a site-specific charting cadence, correlated with the label. We then check whether the scale profile and the site-predictiveness score flag the corrupted channel and window. Planted physiological peaks serve as negative controls that should not be flagged.

The second part is the observational study on unmodified data. We train GRU, Transformer, and IMV-LSTM models on single US sites and on pooled data. We compute scale profiles at windows from 2 to 24 hours and correlate per-channel flagged reliance with the drop in performance at held-out hospitals in the other region, and with subgroup AUC gaps by ethnicity, insurance, age, and sex as defined in MIMIC-IF. We will also check the scale-profile flags against ArchDetect rankings under Remove-and-Retrain, so that the diagnostic does not inherit the unfaithfulness MIMIC-IF found for attention.

The third part is the intervention. For each channel, we choose the window width and the smoother type (uniform or Savitzky–Golay). The choice minimizes flagged reliance, subject to a cap on loss of in-site validation AUROC. Selection uses only training-site data, so the held-out-site evaluation stays clean.

Baselines

The naive reference point is raw hourly inputs with no smoothing, alongside the common practice of a single fixed rolling mean applied to all channels.

The strongest existing method on the cross-site question is LightGBM on extracted window features. The harmonized-dataset paper reports that it "often [was] the best-performing model" in transfer. No reported numerical transfer score was found on Lacuna for it. We will rerun it on identical splits and match its tuning budget to the neural models. For within-site reference, MIMIC-IF reports AUROC 0.955 and AUPRC 0.769 for IMV-LSTM on MIMIC-IV in-hospital mortality. On MIMIC-III, Multitask Learning and Benchmarking with Clinical Time Series Data reports in-hospital mortality AUC-ROC of 0.870 for a channel-wise LSTM and 0.848 for logistic regression. Our reproductions must land near these numbers before any comparison counts.

The baseline most likely to make the proposal unnecessary is global window selection by worst-group validation AUROC. This picks one window width from the same grid we search, using the same validation data and the same number of trained models. Beating it means a smaller held-out-site worst-subgroup AUROC gap at equal or better overall AUROC, across at least three of the four cross-region transfer pairs.

Two ablations isolate the key ingredient. The first chooses per-channel windows at random from the same grid, which tests whether any per-channel heterogeneity helps. The second chooses per-channel windows by reliance alone, ignoring site-predictiveness, which tests whether the site link matters. Every condition is run with both uniform and Savitzky–Golay smoothers.

Why not just…?

Why not just tune one global smoothing window against worst-group accuracy? This is the real threat, because it is cheap and directly targets the outcome we care about. Our bet is that the right time scale differs by channel. Heart rate and lab values are charted at very different rates, so one window either over-smooths fast physiology or under-smooths slow artifacts. If the global-window baseline matches our per-channel selection on held-out regions, the intervention claim fails. The diagnostic would then survive only as an auditing tool, and we will report it that way.

Why not just use LightGBM with summary statistics, which already smooths implicitly and transfers best? It may well transfer best overall. But its window aggregates are fixed by hand, and its split-based partitions are exactly the coarsening that Simplicity Creates Inequity warns about. We will run our scale-profile diagnostic on LightGBM itself, using the same residual decomposition with feature extraction applied after smoothing. That tells us whether its transfer advantage comes from discarding site-specific fine scale. If so, that is a mechanistic finding about why it transfers. If our smoothed neural models do not close the gap to LightGBM, we will say so.

Why not just train with random smoothing or noise augmentation so the model becomes invariant to fine scale? This removes fine-scale reliance everywhere, including where the fine scale is real physiology, such as acute deterioration. It also gives no account of which channels were the problem. We include augmentation over the same window grid as a baseline. Our planted-peak negative controls measure whether it destroys legitimate fast signals that targeted smoothing keeps.

Why not just reweight subgroups or pool more hospitals? The harmonized-dataset paper shows that pooling 600,000 stays still leaves a cross-region gap. Group reweighting does nothing about a site-specific input artifact the model can still read. We include group-reweighted training as a baseline and also test it in combination with our smoothing.

Proposed Experiments and Decisive Checks

The data are the harmonized cohort, which includes MIMIC-IV, eICU, HiRID, AmsterdamUMCdb, and SICdb. The tasks are in-hospital mortality, decompensation, and length of stay. We transfer US to Europe and Europe to US, keeping within-region transfer as a control. Subgroup labels follow MIMIC-IF wherever the source datasets record them.

The metrics are overall AUROC and AUPRC; worst-subgroup AUROC and the subgroup gap at held-out sites; and peak preservation on planted events, measured as amplitude and timing error. Attribution faithfulness is measured by Remove-and-Retrain degradation, so the scale-profile flags can be checked against ArchDetect.

Three outcomes are decisive.

First, in the planted-artifact study, the diagnostic must flag the corrupted channel and window while leaving planted physiological peaks unflagged. If it cannot, the program stops.

Second, on unmodified data, flagged reliance at the training site must correlate with held-out-site degradation across models and channels more strongly than total attribution mass does. Total mass is the right comparison because it is what a plain attribution audit would show.

Third, diagnostic-guided per-channel smoothing must narrow the held-out worst-subgroup gap relative to both global worst-group window tuning and random per-channel windows, without lowering the worst subgroup's own AUROC. Watching the worst subgroup's own AUROC is the check that Simplicity Creates Inequity demands: a gap can narrow simply because the best-off group got worse. Savitzky–Golay should beat uniform averaging on peak preservation. If it does not on hourly ICU data, that finding limits how far the EpiFlow results generalize.