Reconstructing "Any Heart" to Separate Artifact from Arrhythmia in ICU Alarms

Bedside monitors in intensive care units sound alarms for life-threatening heart rhythms, but most of those alarms are false. Studies of ICU arrhythmia alarms report false alarm rates of 80 to 88.8 percent (False arrhythmia alarm reduction in the intensive care unit; A contrastive learning approach for ICU false arrhythmia alarm reduction). Staff learn to ignore them, a failure known as alarm fatigue. Many of these false alarms come from noise rather than from the heart: an electrode slips, a patient shivers, and the trace shows a burst that looks like ventricular tachycardia. The usual anomaly detection recipe makes this worse. That recipe trains a model to rebuild normal signals and flags whatever it cannot rebuild. Noise cannot be rebuilt either, so it produces the same large error as real disease.

We propose to change the question the reconstruction answers. The usual question is "could this be normal for this patient?" We ask a different one: "could any heart have produced this?" A decoder whose outputs are restricted to electrophysiologically valid waveforms can rebuild a ventricular beat, because hearts produce ventricular beats. It cannot rebuild a motion artifact, because no heart produces one. Whatever this decoder fails to explain is evidence of artifact, not of disease. A second, patient-specific comparison then asks whether the explainable part differs from the patient's own recent rhythm. Real alarms should show a small artifact error and a large change from the patient's baseline. Noise-driven false alarms should show a large artifact error.

Core Claim

Our claim is that reconstruction error can only be used for alarm adjudication once it is split along a physiological axis. One part is a plausibility residual: the signal left unexplained by a decoder that can only output sums of cardiac waves. The other is a baseline deviation: how far the decoded wave parameters move from the patient's pre-alarm beats. Together these two numbers should separate true alarms from false ones well enough to filter false VT, VF and tachycardia alarms. They should do this at a sensitivity close to 100 percent. They should also need far fewer labels than supervised classifiers and keep working on alarm types never seen during training.

Concretely, let $g(\theta)$ be a waveform built from Frequency Modulated Möbius (FMM) waves. These are analytic pulse shapes with amplitude, timing, width and direction parameters $\theta$. They are fitted per beat and can describe P, QRS and T components, including wide ventricular complexes. Let an encoder $f$ predict $\theta = f(x)$ for an alarm window $x$. We define

$$r_{\text{phys}}(x) = \frac{\| x - g(f(x)) \|^2}{\| x \|^2}, \qquad r_{\text{pat}}(x) = d\big(f(x), \{f(b_k)\}\big),$$

where $b_k$ are beats from the pre-alarm baseline window of the same patient. The function $d$ is a Mahalanobis distance from the alarm-window parameters to the distribution of baseline parameters. The alarm decision is a small calibrated rule over $(r_{\text{phys}}, r_{\text{pat}})$, plus a second-channel term when an arterial pressure or pulse-oximetry pleth signal is present.

Relation to Prior Work

The decoder comes directly from FMM-Head. That work replaces a neural autoencoder's decoder with FMM wave equations. It improves anomaly detection AUROC on PTB-XL by up to 0.31 and cuts inference time by up to 91 percent. FMM-Head trains on normal ECGs and treats every reconstruction failure as an anomaly. It is also evaluated on clean diagnostic databases, not on noisy ICU alarms. We train the same kind of head on morphologically diverse ECGs, including ectopic and ventricular beats, so that pathology is deliberately rebuilt. We then read its failures as noise.

The idea that reconstruction must be paired with a learned comparison comes from DRÆM. DRÆM shows that plain subtraction is a weak anomaly score and adds a discriminative network over input and reconstruction. Its Perlin-noise synthetic defects do not resemble electrode motion. We replace them with recorded artifacts from the MIT-BIH Noise Stress Test Database (NSTDB). We also keep the comparator deliberately small: a two-dimensional rule, not a network.

Two papers motivate the patient-baseline half of the method and also constrain it. The contrastive Siamese network of A contrastive learning approach for ICU false arrhythmia alarm reduction compares the alarm segment to a 10-second pre-alarm segment and reaches a Challenge score of 84.47. That shows the pre-alarm baseline carries strong signal. The same comparison done naively, as the Self-Beat Bank in False arrhythmia alarm reduction in the intensive care unit, kept only 0.116 of true VT alarms despite 0.960 specificity. We read that failure as a sign that raw beat-to-beat distances mix noise variability with morphological change. Comparing in fitted wave-parameter space, after an artifact check, is our proposed fix, and the ablations test it directly.

The closest prior system is A Diffusion Model with Contrastive Learning for ICU False Arrhythmia Alarm Reduction. It trains a conditional diffusion model, a generator that learns by gradually removing noise from random samples, to produce the claimed arrhythmia. It labels an alarm false when the observed signal does not match that generated arrhythmia, reaching a real-time VT score of 74.10. This approach models the abnormal class specifically. It therefore needs many labeled true arrhythmias, and an unusual true VT that the generator never learned could be silenced. It also requires many sequential sampling steps. Our decoder models the space of all physiological waveforms, not one arrhythmia class. It trains without alarm labels and runs in one forward pass.

Denoisers such as the fully convolutional denoising autoencoder improve signal-to-noise ratio by 15.49 dB at −1 dB input on NSTDB, but they discard the information we need. Removing noise hides the fact that it was present. The plausibility residual keeps exactly what a denoiser throws away and turns it into a measurement.

Research Program

The first step is to build the plausibility decoder. A 1D convolutional encoder predicts per-beat FMM parameters for single- and two-lead windows. It is pretrained on unlabeled MIMIC-IV-ECG and PTB-XL records with a reconstruction loss. Records with ectopy and ventricular rhythms are intentionally kept in the training data. Noise is never shown to the decoder as a reconstruction target. We will extend FMM-Head's single-lead form to share timing parameters across leads. This adds a constraint: a real beat appears in all leads at once, while electrode motion often does not.

The second step is to calibrate the two residuals. On MIT-BIH, we inject NSTDB electrode motion, muscle artifact and baseline wander at controlled signal-to-noise ratios. This lets us measure how $r_{\text{phys}}$ grows with noise on normal rhythm and how it stays flat on clean ventricular runs. These controlled pairs are also the only training data for the artifact side of the decision rule.

The third step is the decision rule. We fit a monotone two-feature rule, optionally with the second-channel pulse term, on the PhysioNet 2015 training records. Thresholds are set so that sensitivity is at least 0.99 on held-out folds. The rule is chosen to be auditable: a clinician can see the fitted beat overlaid on the raw trace, the unexplained residual, and which wave parameters changed from baseline.

Known limitations shape the scope. Asystole false alarms often come from a lead falling off, and a flat line is physiologically plausible. Ventricular fibrillation is chaotic and may fit FMM sums poorly. We therefore treat VT and extreme tachycardia as the primary targets; VT alone contributes 252 of the false alarms in the training set. VF and asystole are reported separately without claims of superiority.

Baselines

The do-nothing reference is the monitor itself: every alarm sounds. This gives sensitivity 1 and specificity 0 and fixes the false-alarm burden we aim to cut. The rule-based reference is the multimodal regular-activity test from False arrhythmia alarm reduction in the intensive care unit. It checks whether pressure or pleth channels keep pulsing during an ECG alarm and reports sensitivity 0.908, specificity 0.838 and Challenge score 75.6. We will reimplement it on our folds.

The strongest existing method is the contrastive Siamese CNN of A contrastive learning approach for ICU false arrhythmia alarm reduction. It reports a Challenge score of 84.47, 96 percent true positive rate, and 86 percent of false alarms identified. It is the strongest competitor because it already uses the patient baseline and full supervision. We will retrain it on the identical cross-validation folds of the 750 training records, with the same hyperparameter search budget and GPU hours as our method. Beating it means one of two things. Either we match its Challenge score on the same folds while reaching higher specificity at sensitivity 0.99, or we clearly exceed it when trained on 10 to 20 percent of the labels or on alarm types held out from training. The diffusion system of Wu et al. is the closest generative baseline. Its reported real-time VT score is 74.10, against 66.27 for TAnoGAN and 44.04 for the 2015 rule-based winner. We will rerun it on our VT folds and compare both accuracy and per-alarm latency.

Four ablations isolate the key ingredient. The first uses $r_{\text{pat}}$ alone, which is essentially a parameter-space Self-Beat Bank. The second uses $r_{\text{phys}}$ alone. The third replaces the FMM head with an unconstrained neural decoder of equal size; if that decoder rebuilds artifacts, the plausibility residual should collapse, which tests the identical-shortcut concern. The fourth removes the second channel.

Why not just…?

Why not just train a supervised classifier on labeled alarms? This is the real threat. The contrastive CNN's 84.47 shows that supervision plus a patient baseline already works well on the PhysioNet distribution. We do not expect to win by a large margin when training and test alarms come from the same distribution. Our claim rests instead on label efficiency, transfer to held-out alarm types, and specificity at very high sensitivity. The label-fraction and leave-one-alarm-type-out experiments decide this. If the supervised model degrades no more than ours under those conditions, the plausibility residual is worth only its interpretability, and we will report it that way.

Why not just cross-check the pressure and pleth channels? When those channels are clean, this is hard to beat, and our rule includes them. But the regular-activity test still lets 3.6 percent of true alarms be falsely silenced. It also does nothing when invasive arterial pressure is absent or the pleth probe is displaced, which is common outside surgical ICUs. We will report results on the subset of records with ECG only, where this alternative cannot run.

Why not just denoise first and run the existing detector? Denoising erases the evidence that noise was present. When electrode motion mimics a ventricular complex, a strong denoiser may also "clean" it into a plausible beat. We will run the FCN denoising autoencoder followed by the contrastive classifier as a pipeline baseline. We will also check whether denoised artifact windows end up more or less likely to be classified as true VT.

Decisive Checks

The first check is controlled and cheap. On MIT-BIH, the plausibility residual must rank NSTDB-corrupted normal rhythm above clean ventricular runs with AUROC well above chance. It must still do so when the injected noise contains PVC-like electrode-motion bursts. If an FMM decoder trained on diverse morphology also explains these bursts, the core idea fails, and we would know before touching ICU data.

The second check uses PhysioNet 2015. We report Challenge score (TP+TN)/(TP+TN+FP+5·FN), specificity at sensitivity of at least 0.99, and partial AUROC restricted to the high-sensitivity region. We give confidence intervals across folds and per alarm type. The few true VFB alarms (6) are reported but not interpreted.

The third check covers transfer and label budget. We train the decision rule on all but one alarm type and test on the held-out type, and we repeat the main comparison at 10, 20 and 100 percent of labels against the contrastive CNN.

The fourth check is CPU latency per alarm, compared with the diffusion baseline, since a bedside filter must decide within the monitor's alarm delay.