Clinical prediction models usually see a short slice of a patient: the first 24 hours of an intensive care stay, 15 minutes after anesthesia induction, a few hours of emergency-department vital signs. Explanation methods then tell the clinician which variable "drove" the prediction. This proposal argues that these explanations fail in a specific way that can be measured. A short window cannot separate a value that is high because the patient has always been that way (a chronic baseline) from a value that is high because something is going wrong now (an acute shift), and it cannot separate a slow trend from a passing spike. Current attribution methods answer anyway, and they often answer confidently. The work has two parts. First, a benchmark with known ground truth that measures how often clinical attributions credit the wrong time scale as the observation window shrinks. Second, a simple attribution method that splits each variable's credit into level, trend, and fast-fluctuation parts and labels a part "unresolved" when the window is too short to identify it.
The motivation comes from two literatures that rarely meet. Work on limited temporal scope in environmental and mobility science shows that short observation windows behave like high-pass filters: they keep fast fluctuations and erase slow structure, so transient swings get mistaken for lasting trends. Examples include soil-moisture evaluations that miss freeze-thaw seasons (Jiang et al.) and drought records where decadal oscillations look like permanent drying (Jiao). Clinical interpretability work has documented its own failures on time series, but it treats window length as a fixed preprocessing choice. Bringing the first lens into the second turns a vague worry ("short windows might bias explanations") into a testable claim with a concrete remedy.
Core Claim
Our central claim is that on short clinical windows, standard attributions are often confidently wrong, not merely noisy. Specifically, they assign large, stable credit to a variable's level when the outcome actually depends on its trend, and the reverse, and they show no warning. Because the error is systematic rather than random, it survives resampling. Bootstrap stability checks therefore will not catch it, and the method that fixes it must reason about what the window can and cannot reveal.
The closest existing work comes at this from different directions, and none of it does what we propose.
Two papers vary the window but explain little. Flexible-Window Predictions on Electronic Health Records trains one sequence generator that works across observation/prediction splits and shows attention heatmaps. Those heatmaps reveal that adults' predictions lean on the earliest data while children's lean on the most recent. That result directly challenges the recency assumption built into RETAIN, whose reverse-time attention decomposes a prediction into exact per-visit, per-code contributions. Neither paper asks whether attributions are correct as the window is cut. Optimal intensive care outcome prediction over time shows that ICU accuracy peaks on day 2 rather than day 1, which implies that day-1 explanations come from a truncated view. Its models were black boxes, however, and it extracts no attributions.
Two papers target attribution quality on time series but hold the window fixed. Benchmarking Deep Learning Interpretability in Time Series Predictions shows that saliency methods mix up when with what, and fixes this with Temporal Saliency Rescaling (TSR), which first scores time steps and then scores features within them. Time-series attribution maps with regularized contrastive learning, called xCEBRA, proves that its attribution maps are identifiable, meaning unique up to the stated assumptions, but only in the limit of infinite data. Both methods tell you which variable at which time mattered. Neither tells you whether the window was long enough to know what kind of signal that variable was carrying.
Interpretability in Deep Time Series Models Demands Semantic Alignment comes closest conceptually. It distinguishes instantaneous concepts, such as current blood pressure, from accumulated concepts, such as physiological wear. It offers architecture and theory, with heavy concept annotation, and no measurement under truncation. We take its distinction as the target of measurement and replace concept annotation with a cheap, model-agnostic signal decomposition.
Research Program
The method rests on one observation. Within a window of length $L$, each variable $c$ can be split exactly into three parts:
$$x_c(t) = m_c + b_c\,(t-\bar t) + r_c(t),$$
Here $m_c$ is the window mean (the level), $b_c$ is the least-squares slope around the window's center time $\bar t$ (the trend), and $r_c(t)$ is the remaining fast fluctuation. Because the split is linear and exact, we can rewrite the model's input in terms of $(m_c, b_c, r_c)$ and run Integrated Gradients, a path-integral attribution method, in that coordinate system. Integrated Gradients has a completeness property: attributions sum to the difference between the prediction and its value at a reference input. With that property, each variable's total credit divides exactly:
$$A_c = A_c^{\text{level}} + A_c^{\text{trend}} + A_c^{\text{fast}}.$$
The same split can wrap TSR or xCEBRA as the underlying attributor, so the decomposition is an add-on rather than a competitor to them.
The second ingredient is a resolvability rule. Window length limits identification in two ways. A slope estimated from $L$ hourly samples with noise level $\sigma$ has standard error that grows as $\sigma / L^{3/2}$, which follows from the variance of an ordinary least-squares slope on evenly spaced points. So a trend attribution is reported only if the estimated slope clears its own uncertainty band and $L$ exceeds a calibrated multiple of the variable's typical drift time scale. A level attribution is labeled "baseline-ambiguous" whenever no measurement from before the window exists. In that case the window physically cannot separate a chronic offset from an acute shift. The calibration constants are set on the semi-synthetic benchmark described below and then frozen before real-data tests.
The output a clinician sees is therefore not "creatinine: +0.31" but something like "creatinine level: +0.28, cannot tell chronic from acute in this window; creatinine trend: +0.03, resolved." The AICare user study (AICare) found that senior clinicians interrogate model factors against edge cases while junior clinicians lean on trajectories as a scaffold. Separately, Dinu et al. found that random attributions persuaded users as well as or better than real ones. Together these make an explicit, machine-generated statement of what the window cannot resolve more useful than another heatmap. We treat the human side as secondary, though. The primary claims are measured against ground truth.
Baselines
The naive reference is what clinical benchmarks do by default. A recurrent model (GRU), a temporal convolutional network, and a transformer are trained under the Yet Another ICU Benchmark (YAIB) pipeline on a fixed 24-hour window and explained with vanilla Integrated Gradients and gradient saliency over raw inputs. YAIB reports mortality AUROC of 0.84 to 0.87 across its databases. Our reimplemented models must land in that range, so attribution comparisons are made on competent predictors. Every attribution method is applied to the same trained checkpoints, with the same reference inputs and the same number of model evaluations per explanation. That holds compute fixed, which matters because TSR is known to be expensive.
The strongest existing attribution competitor on the "which variable, when" question is TSR. Its paper reports that TSR raises attribution AUPR, the area under the precision-recall curve for recovering ground-truth informative regions, from 0.331 to 0.399 on the synthetic "Middle Box" task (Benchmarking Deep Learning Interpretability in Time Series Predictions). We rerun TSR on our benchmark instead of quoting that number, because the task differs. The second strong competitor is xCEBRA. Its paper reports 98.2% AUROC for recovering ground-truth connectivity on synthetic series, against roughly 85% for feature ablation, Shapley values, and Integrated Gradients (xCEBRA). It is the method most likely to degrade gracefully under short windows, given its identifiability guarantee. We also include RETAIN as the inherently interpretable alternative, scoring its $\alpha\beta w$ contribution coefficients. RETAIN reports heart-failure AUROC of 0.8705 on Sutter Health (RETAIN), but no reported result was found on Lacuna for RETAIN on ICU attribution accuracy.
Beating these baselines means two things on the benchmark's time-scale ground truth. First, higher component-level attribution AUPR at windows of 12 hours or less, with no loss at 48 hours. Second, a lower "confident-wrong rate," defined as the fraction of explanations whose top credited component is the wrong time scale while bootstrap variance is in the lowest tercile. Two ablations isolate the key ingredients. One is the decomposition without the resolvability rule, which tests whether splitting alone helps. The other is the resolvability rule applied to raw-input attributions, using window length and pre-window data availability alone. If the second ablation matches the full method, the decomposition is unnecessary and we will say so.
Why not just…?
Why not just give the model the patient's pre-window history and baseline labs? This is the most serious alternative. Where baseline data exist, as with pre-ICU hospital labs in MIMIC-IV, adding them may remove much of the ambiguity in both prediction and attribution. We include it as a baseline arm. Our method's value lies in the cases where such history is missing: first encounters, emergency arrivals, and intraoperative monitoring as in Beyond Thresholds. In those cases the right output is an honest "unresolved," not a guess. The experiments report results separately for patients with and without baseline data. If baseline augmentation closes the gap even where history is sparse, the contribution shrinks to the benchmark itself.
Why not just use TSR or xCEBRA, which already fix known time-series attribution failures? Both locate informative variables and time steps, but the failure we target is about signal type within a correctly located variable. A rising creatinine and a chronically high creatinine light up the same cells. xCEBRA's identifiability result is also an infinite-data limit, so short windows are exactly where it is unproven. Both are run as baselines and as underlying attributors inside our decomposition. If either alone achieves comparable component-level accuracy, that falsifies the need for our method.
Why not just report bootstrap or seed-variance confidence intervals on attributions? Uncertainty intervals catch noise, but our hypothesis is that truncation error is systematic. A 6-hour window of a stable chronic kidney disease (CKD) patient will consistently show high creatinine. The confident-wrong rate is designed to test this directly. If wrong attributions turn out to coincide with high variance, intervals suffice and we will report that.
Why not just train with randomly sampled window lengths, as flexible-window models do? Window augmentation, as in Flexible-Window Predictions, makes predictions robust across splits, but robustness of the prediction does not make the attribution identifiable. No training scheme can recover a pre-window baseline that was never observed. We train an augmented variant of each model and apply all attributors to it, so the effect of augmentation on attribution correctness is measured, not assumed.
Proposed Experiments
The semi-synthetic benchmark is built on real trajectories so that noise, missingness, and irregular sampling are realistic. We use hourly MIMIC-III stays extracted with MIMIC-Extract (stays of 12 hours to 10 days, 104 clinical aggregates) and YAIB cohorts from MIMIC-IV, eICU, HiRID, and AUMCdb. Into a chosen channel we plant one of three signal types: a constant offset that begins before the window, a slow linear drift, or a short transient bump. The label is generated from exactly one planted type, and decoys of the other two types are planted independently, so the ground-truth component is known for every patient. Windows are cut at 6, 12, 24, and 48 hours. Results are reported as component AUPR and confident-wrong rate against window length. The expected signature is that baseline methods' level and trend errors grow sharply below the time scale of the planted drift, while our method instead converts those cases into "unresolved." Over-abstention is penalized by also reporting coverage, the fraction of explanations given a resolved label.
The decisive real-data check uses a clinical definition as ground truth. For acute kidney injury (AKI) prediction in MIMIC-IV, the clinical standard (KDIGO criteria) defines AKI relative to the patient's own baseline creatinine. We take patients with pre-ICU baseline creatinine and form two groups with similar in-window creatinine levels: stable CKD patients, whose elevation is chronic, and patients whose creatinine is rising acutely. A correct explanation on the first 6 to 12 hours should not credit creatinine level equally in both groups. If the window lacks the baseline, it should flag the level attribution as ambiguous. The test is whether baseline methods assign similar creatinine-level credit across the groups, and whether that difference only appears once the window or the baseline-augmented input reveals the history. An analogous minute-level test on INSPIRE varies the window from 15 to 30 and 60 minutes post-induction and the full case. It asks whether trajectory-driven risk in statically "low-risk" patients is credited to fast fluctuations or to trends. In that subgroup, Beyond Thresholds reports a +0.223 AUROC gain from trajectories.
Finally, a small reader study with clinicians compares raw attributions, decomposed attributions, and decomposed attributions with resolvability flags on matched cases, some of which are deliberately truncated. The outcome is how often readers accept an explanation that the ground truth marks as wrong. The study is sized modestly, in line with AICare's 16-clinician design. It is reported as supporting evidence, and the benchmark results stand on their own. The project fails, and we would report it as such, if decomposed attributions show no lower confident-wrong rate than TSR or xCEBRA at short windows, or if baseline augmentation removes the effect even for patients without history.
References
- Evaluation of Multiple Downscaled Microwave Soil Moisture Products over the Central Tibetan Plateau
- Spatiotemporal Comparison of Drought in Shaanxi-Gansu-Ningxia from 2003 to 2020 Using Various Drought Indices in Google Earth Engine
- Flexible-Window Predictions on Electronic Health Records
- RETAIN: An Interpretable Predictive Model for Healthcare using Reverse Time Attention Mechanism
- Optimal intensive care outcome prediction over time using machine learning
- Benchmarking Deep Learning Interpretability in Time Series Predictions
- Time-series attribution maps with regularized contrastive learning
- Interpretability in Deep Time Series Models Demands Semantic Alignment
- Augmenting Clinical Decision-Making with an Interactive and Interpretable AI Copilot: A Real-World User Study with Clinicians in Nephrology and Obstetrics
- Challenging common interpretability assumptions in feature attribution explanations
- Yet Another ICU Benchmark: A Flexible Multi-Center Framework for Clinical ML
- Beyond Thresholds: Learning Perioperative Risk from Intraoperative Physiological Trajectories
- MIMIC-Extract: a data extraction, preprocessing, and representation pipeline for MIMIC-III