Loud or Silent? A Reusable Framework for Per-Modality Failure Analysis in Multimodal Clinical AI
Quang Bui, Shlok Jaiswal, Samuel Paik-Heintz, Kevin Zhou, Kaushik Madapati, Krittaphas Chaisutyakorn, Noah Dane Hebdon, Dimitrios Proios, Sebastián Andrés Cajas Ordóñez, Kacper Dobek, Boya Zhang, Aly Dhedhi, Ahram Han, Kushul Reddy Palakala, Rahul Gorijavolu, Jacques Kpodonu, Leo Anthony Celi
cs.AI
2026-08-03
Dropping echo nearly doubles LVEF error (10.3 to 18.6) on a MIMIC-IV cohort; MIT's framework attributes the loss to specific modalities and flags failures monitoring misses.
Multimodal clinical models are graded in papers with every modality present: ECG, echocardiogram, lab panel, all at once, rolled into one accuracy. Deployment does not look like that. A bedside may have an ECG but no echo, because the ultrasound tech is off shift or the machine is elsewhere. Which modalities are present depends on what the hospital has and what can be done right then.
That hides a problem. When a modality goes missing, the prediction does not just get "a bit worse." The size of the loss is only the first question. Two more matter: which modality is responsible for the error, and whether the model fails loud (output lands near the decision boundary, where a monitor can catch it) or silent (it slips to the far wrong side and looks completely normal, so the monitor never fires).
These two failures have very different clinical consequences. Loud ones get absorbed by second reads and human review; silent ones can sail into a treatment decision. This paper, from MIT Critical Data, builds a model-agnostic evaluation harness that turns those two questions into a standard check you rerun every time you swap the model.
The framework takes three inputs: embeddings for N modalities, any mask-aware probe (a small model that knows which modalities are present), and labels. It returns three things.
First, a per-example failure taxonomy. Under each modality condition, every example is labeled Correct (gate right, regression error small), Imprecise (gate right but regression off), or Critical (gate wrong: the HFrEF case missed, or a false alarm). The "gate" here is the EF≤40% threshold that flags heart failure with reduced ejection fraction. Critical failures are the clinically dangerous ones, and a mean absolute error (MAE) buries them.
Second, a per-modality complementarity matrix. For each modality m it computes a leave-one-out value, how much error rises when m is removed, then attributes each example to the modality whose removal hurts most. This separates redundant modalities (drop them, no harm) from complementary ones (drop them, collapse), and can be stratified by sex, age band, and race for a fairness audit.
Third, a loud-vs-silent dropout profile. An example that the gate gets right with all modalities but gets wrong once modality m is dropped is an induced critical failure. Whether that failure is loud or silent depends on how far the prediction sits from the decision threshold τ: far away (|f−τ|≥κ) is silent, the prediction sits deep on the wrong side and looks unremarkable, so a margin-based monitor misses it; near the threshold (|f−τ|<κ) is loud, the output is visibly uncertain and invites a second look.
The key design choice is that the whole profile uses only deployment-observable signals, the prediction that was actually issued. It never needs the full-modality counterfactual, which is exactly what deployment cannot give you. That is what turns this from a lab attribution exercise into a check that runs at the bedside.
The harness ships as a small, unit-tested package; every artifact carries a manifest recording the git commit and resolved config, and runs are config-driven with fixed random seeds. The authors draw two deliberate lines against existing work. It is not post-hoc feature attribution like SHAP (that asks which input pushed a prediction when everything is present); it asks how the model behaves when an input is genuinely absent. And it is not EchoingECG-style distillation of echo into an ECG-only model; both modalities are kept, and the focus is inference-time degradation.
The authors first validate the harness itself on synthetic data with planted structure: echo encodes LVEF strongly, ECG weakly, except in an 18% subset where echo is deliberately uninformative and ECG must carry the signal. Across 12 seeds the harness recovers that structure cleanly: echo's leave-one-out value is 5.5±0.7 MAE versus 1.8±0.5 for ECG, echo is the more valuable modality in all 12 seeds, and it takes 0.67±0.04 of per-example wins while ECG correctly wins on the planted complementary subset. The loud/silent split is comparable for the two: 0.31±0.07 silent when echo is dropped versus 0.32±0.10 for ECG, with the ordering flipping across seeds. That is the intended behavior. The most valuable modality need not be the most dangerous to lose; value and detectability are separate axes.
With only two modalities, per-example attribution is partly degenerate (dropping one equals using the other), so they exercise the general path on a three-modality instance: echo, ECG, and a simulated "labs" channel, 225 test examples. The complementarity matrix shows echo alone at 9.7 MAE, ECG at 12.9, labs at 13.4; every echo-containing pair (8.3) beats the ECG-plus-labs pair (11.3). Per-example wins are echo 125, ECG 56, labs 44, flagging echo as irreplaceable and the other two as weak and partly redundant.
The real-world validation is on a paired MIMIC-IV cardiac cohort, 245 held-out test examples, using frozen EchoJEPA-L and HuBERT-ECG embeddings with a cross-attention fusion probe as the primary model:
| Inference condition | LVEF MAE↓ | EF≤40% AuROC↑ |
| Full (echo + ECG) | 10.28 | 0.766 |
| Echo dropped (ECG-only) | 18.57 | 0.693 |
| ECG dropped (echo-only) | 15.13 | 0.750 |
Dropping echo nearly doubles LVEF error, from 10.28 to 18.57. For reference, EchoJEPA-L reports 5.97 LVEF MAE on its internal Toronto cohort, and an AI-ECG screen for EF≤35% reports 0.93 AuROC on a Mayo cohort (Attia et al., 2019), but those are on cleaner single-center internal data with frozen backbones as a lower bound, not a head-to-head on the same split.
The cohort construction is itself a finding. Starting from 7,243 echo studies, matching to structured measurements, keeping those with an LVEF reading, requiring the patient to also have an ECG, then requiring the ECG within a ±24h window leaves only 1,678 studies and 1,326 patients, and confining to a single admission drops it to 1,208 studies and 1,003 patients. Echo and ECG rarely co-occur within 24 hours in real records, and that narrow overlap is itself a deployment constraint for cardiac foundation models.
The contribution is not a new model; it is an evaluation habit. It maps onto three real pain points in deploying multimodal clinical models.
Models get replaced constantly. Today's backbone is EchoJEPA, tomorrow's is something stronger, but "which modality matters and will the loss be caught" has to be reanswered each time. The harness consumes embeddings rather than a specific model, so swapping a backbone means swapping a probe and rerunning the same evaluation. For anyone iterating on medical models, that removes a lot of repeated one-off work.
Second, it isolates silent failure. A model that quietly misclassifies deep on the wrong side of the boundary is far more dangerous than one that visibly hesitates, because existing confidence- and margin-based monitors will not flag it. Knowing the silent-failure rate tells you how much human backup you actually need.
Third, the cohort finding. Cardiac foundation-model papers often assume echo and ECG are available together like matching bricks, but real records rarely have both inside a 24-hour window. The multimodal capability trained on paired data degrades at a single-modality bedside, and this kind of per-modality analysis is how you quantify the discount.
The authors list several. MIMIC-IV is a single US academic center, so external validation is missing. The backbones are frozen, so absolute accuracy is a lower bound, not what fine-tuning would achieve. EF≤40% prevalence is modest in the paired cohort. The loud/silent split uses distance from a threshold, not a calibrated confidence.
Two are more fundamental. The synthetic validation is circular: the structure is planted by the authors, so recovering it proves the harness mechanics, not that either modality is clinically superior in real patients, and per-example attribution has no ground truth in real data. Also, with only two modalities per-example attribution is degenerate, so the method is most informative at N≥3, while the real echo-plus-ECG case is exactly two modalities.
One more concern after reading. Loud/silent uses geometric distance to a fixed threshold τ as a proxy for monitorability, but whether a monitor actually catches a failure depends on how the deployment's alert threshold is set and whether a human review loop exists. That proxy is never calibrated against a real alerting system in the paper.