Where Sleep Sensors Stop Being Independent: Measuring and Repairing Cross-Channel Interactions in Modular Sleep Staging

The most flexible sleep-staging model in the literature, a factorized diffusion model, can classify sleep from any combination of sensors without retraining. A diffusion model is a generator that learns by gradually turning random noise into samples. This one gets its flexibility from a simplifying bet: once the sleep stage is known, every sensor is treated as an independent witness, so the evidence from each channel is simply added up. Physiology says the bet is wrong in two opposite ways. Some channels repeat each other. ECG and the optical pulse sensor both report heart rate, so adding them counts the same evidence twice and makes the model overconfident. Other channels are only informative together. Rapid eye movements together with absent chin-muscle tone define REM sleep, while either signal alone is ambiguous. Environmental scientists have a mature habit for exactly this kind of question: before modeling, they test whether two drivers combined explain more than their sum, less, or the same, and whether the answer changes across conditions.

We propose to bring that habit into multimodal sleep modeling. First, we build an interaction map that measures, for every sensor pair and within strata of signal quality and body movement, how much the independent-witness assumption costs. The map separates cost that a simple per-channel reweighting can fix (redundancy) from cost that it cannot (synergy, or one channel overriding another). Second, we add learned correction terms only for the few pairs where the map finds irreducible interaction, and we keep the plug-in property that makes the factorized model useful. The claim that is new is not "model interactions," which any joint network does implicitly. The claim is that the departure from independence in sleep sensing is sparse, can be measured, and depends on the recording state. A small, targeted set of pairwise terms should therefore recover most of what a fully joint model gains while staying modular. The measurement is also built so that the opposite answer would show up clearly: violations might be mostly redundancy, and calibration might be all that is needed.

Background and the gap

The factorized score-based diffusion model of Van Gorp et al. trains a hypnogram prior and 36 separate per-channel likelihood networks. At inference it sums their score gradients, so any sensor subset can be scored zero-shot. It reports 85.6% accuracy (Cohen's κ 0.791) from single-channel EEG, 79.0% for a home-apnea-test montage (nasal flow, PPG, respiratory belts), and above 70% from unusual single channels such as leg EMG or SpO₂. It also defines a per-channel information-gain score. That score is univariate, so it cannot see pairs. Our work starts from this model and changes only the summation.

Two other lines of work handle multiple channels without testing independence. The anomaly-aware fusion of Fayyaz et al. uses per-channel autoencoder reconstruction error as a quality signal to gate a weighted sum of embeddings. It reaches AUROC of about 0.93 for apnea detection on pediatric data, against 0.86 for a CNN, and stays above 0.88 at 10 dB SNR. Its interaction model is still a weighted sum, and it treats channel failures one at a time. The contrastive pre-training study on Stanford Sleep Bench shows that cross-modal alignment helps clinical outcome prediction (C-index 0.743). Its representations, however, do not say which channel couplings carry the gain.

Two sparse-sensor papers motivate a state-dependent analysis. SleepNetZero found that removing the body-movement component of ballistocardiography badly hurt transfer, which suggests movement gates how far the cardiac and respiratory features can be trusted. Ballistocardiography senses the mechanical forces of heartbeat and breathing through the mattress. Krauss et al. report that radar staging stays weak on N1 even after transfer.

The environmental literature supplies the method, not the data. GeoDetector's interaction detector asks whether the explanatory power of two factors combined exceeds their sum or their maximum, and labels the pair as enhancing, independent, or weakening. Examples are the temperature × aridity interaction explaining 47.1% of vegetation variation in Shuhui Zhang et al., against at most 24.2% for any single factor, and land-development × elevation exceeding 80% in Xiaoyan Zhang et al.. This literature also shows that interactions can switch off past a threshold. Nitrogen's benefit under drought disappears at 20% soil moisture in Zhao and Xie. That is why we compute interactions within strata of recording quality and do not assume one global value.

GeoDetector also brings a known weakness: its statistic is sensitive to how continuous variables are cut into strata. We therefore replace its variance-based statistic with a model-based log-loss version. We stratify only on quality and movement covariates, and we run an explicit sensitivity analysis over the binning.

Core Claim

Write $x$ for the hypnogram (the sequence of 30-second sleep-stage labels) and $y_m$ for channel $m$'s signal. The exact posterior score equals the factorized score plus pairwise and higher-order corrections. Keeping only pairwise terms gives

$$\nabla_x \log p(x\mid y) \approx \nabla_x \log p(x) + \sum_m w_m(q_m)\,\nabla_x \log p(y_m\mid x) + \sum_{(a,b)\in S} \nabla_x \log \frac{p(y_a,y_b\mid x)}{p(y_a\mid x)\,p(y_b\mid x)}.$$

Here $w_m(q_m)$ is a per-channel weight that depends on that channel's quality estimate $q_m$. The last term is the gradient of the conditional pointwise mutual information between channels $a$ and $b$ given the stage. $S$ is a small set of pairs chosen by measurement.

To choose $S$, for each pair and each quality stratum $h$ we compute three held-out stage cross-entropies. $\ell^{\text{ind}}$ is the plain factorized model. $\ell^{\text{w}}$ is the factorized model with the best per-channel weights for that stratum. $\ell^{\text{joint}}$ is a model trained on the pair jointly. The independence gap then splits as

$$\ell^{\text{ind}}_{ab,h} - \ell^{\text{joint}}_{ab,h} = \underbrace{(\ell^{\text{ind}}_{ab,h} - \ell^{\text{w}}_{ab,h})}_{\text{redundancy: fixable by reweighting}} + \underbrace{(\ell^{\text{w}}_{ab,h} - \ell^{\text{joint}}_{ab,h})}_{\text{synergy or override: needs a pair term}}.$$

A pair enters $S$ only if its second term clears a bootstrap noise floor in some stratum. This is the GeoDetector logic, enhancement versus independence versus weakening computed within strata, restated so that it separates "count this evidence less" from "these channels mean something together."

We make specific predictions before running anything. EOG × chin EMG should be strongly synergistic for REM. Respiratory belt × ECG should be synergistic in quiet NREM, because breathing-driven heart-rate oscillation is a coupled signature, and should collapse into redundancy or weakening during movement. ECG × PPG should be almost purely redundant.

Research Program

The work has three stages.

The first stage reproduces the factorized model. We reimplement the per-channel likelihood score networks and the hypnogram prior on the SOMNIA, HealthBed and Sleep-EDF data used by Van Gorp et al.. We add the multi-channel PSG cohorts of the National Sleep Research Resource used by SleepNetZero, which contain EEG, EOG, EMG, ECG, SpO₂, airflow and belts. Before attributing any gain to interactions, we confirm that our reimplementation is within a small margin of the reported single-EEG and home-apnea-test accuracies.

The second stage builds the interaction map. For all pairs among roughly a dozen clinically relevant channels, we train small joint pair-likelihood networks and compute the decomposition above. We stratify by two covariates: autoencoder reconstruction error, the quality signal of Fayyaz et al., and an actigraphy or movement index. The pediatric NCH and CHAT data from the same paper serve as the setting with real compound artifacts, where one rollover corrupts several channels at once. We also inject synthetic artifacts in two forms. In the first, artifacts are independent across channels. In the second, a single simulated movement event produces correlated disturbances across channels: baseline wander in ECG, spikes in the belts, and dropout in the oximeter. This tests whether compound corruption causes non-additive increases in error, which is the "force multiplier" reading of Gap 2 in the research file. We report the map with confidence intervals for three bin counts and two binning rules, because of the discretization sensitivity noted above.

The third stage is the targeted correction model. We implement the equation above. The pair terms are trained as density-ratio networks on top of the frozen per-channel networks, and each pair term is conditioned on the quality covariates so that it can switch off when the recording state changes. This keeps the system modular. Adding a new channel needs only its own likelihood network plus pair terms for whichever pairs the map flags. Nothing is retrained end to end. We also carry the analysis to sparse montages: ballistocardiography decomposed into heartbeat, respiration and movement on BCG265, and radar-derived movement, heart and respiration features on EmpkinS. There we test whether movement acts as a measurable override of the cardiac and respiratory channels, as the SleepNetZero ablation implies.

Baselines

The naive reference points are two. The first is the single best channel. The second is the unmodified factorized sum ($w_m = 1$, $S$ empty) as reported by Van Gorp et al.: 85.6% accuracy and κ 0.791 for single EEG, 79.0% for the home-apnea-test montage. Every method is evaluated on the same subject-level splits with the same channel subsets.

The strongest modular competitor is the factorized model with learned, quality-conditioned per-channel weights and no pair terms. It is the cheapest fix for double counting, and if redundancy is the whole story it should match our method. It gets the same validation data and the same hyperparameter search budget as the pair terms. A second modular competitor is gated fusion in the style of Fayyaz et al.: unimodal encoders whose embeddings are gated by reconstruction error and summed. We retrain it for staging on identical inputs. Its own reported reference is apnea AUROC of about 0.93 on clean pediatric data, a different task, so it is only an anchor for robustness behavior.

The strongest non-modular competitor is a single transformer trained jointly on all channels with random modality dropout. It can learn any interaction but must be retrained to add sensors. We treat it as an upper reference, matched on parameter count and GPU hours. For NSRR staging the closest published reference is SleepNetZero's 0.803 accuracy and κ 0.718. That figure comes from a cardiorespiratory-and-movement model, not a full montage, so it is context and not a target.

The key ablations isolate the measurement step. One replaces $S$ with the same number of randomly chosen pairs. Another uses pair terms that ignore the quality covariates.

Beating the baselines means three things. The targeted model must improve κ and N1 F1 over the weighted factorized model by more than the bootstrap interval on sparse montages and under correlated artifacts. It must recover at least half of the gap between that model and the joint dropout transformer. It must do this with pair terms for fewer than about a fifth of all pairs.

Why not just…?

Why not just train one joint network with modality dropout? On accuracy for montages seen in training this may match or beat us, and we expect it to. It is the real upper bound. What it gives up is modularity. Adding a radar or a new wearable means retraining the whole model, and it says nothing about which couplings matter. Krauss et al. also show that sparse contactless features learned without structure stay weak (MCC 0.25 from scratch, 0.47 with transfer on EmpkinS). We test the joint model directly on sensor combinations held out of its dropout schedule. If it handles those as well as the targeted model, modularity has no advantage and we will say so.

Why not just reweight or temper the per-channel evidence? This is the most serious threat, because double counting between redundant channels probably accounts for much of the independence gap. The decomposition is designed to answer this question directly: the redundancy term is exactly what reweighting fixes. If the synergy term is negligible across pairs and strata, so that reweighting closes most of the gap, the proposal turns into a calibration result. That would be a useful finding, since it would justify the factorized design. We would then drop the pair terms and not argue for them.

Why not just discard epochs below a signal-quality threshold? Hard rejection throws away information that partial channels still carry. Van Gorp et al. show that even leg EMG or SpO₂ alone stage above 70%. Rejection also cannot express the case where one channel stays useful only because another is clean. We include threshold rejection in the artifact experiments and report both accuracy and the fraction of the night left unscored.

Why not just fit classical bilinear interaction terms between features? A constant product term assumes that an interaction has the same strength in every state. The environmental results suggest it does not: interactions vanish past thresholds, and the physiology predicts a belt × ECG coupling that disappears during movement. The quality-conditioned ablation tests this. If pair terms that ignore quality perform as well as conditioned ones, state dependence is unnecessary.

Proposed Experiments and Decisive Checks

On SOMNIA, HealthBed, Sleep-EDF and NSRR we report accuracy, κ, macro-F1, per-stage F1 with N1 broken out, negative log-likelihood and expected calibration error. Calibration matters because redundancy shows up first as overconfidence. We cover full PSG, the home-apnea-test montage, and cardiorespiratory-only subsets. On NCH and CHAT, together with the synthetic artifact suite, we compare independent against correlated corruption at matched per-channel SNR. If error under correlated corruption exceeds what the sum of single-channel degradations predicts, compound artifacts act as force multipliers, and we test whether quality-conditioned pair terms reduce that excess. On BCG265 and EmpkinS we ask whether movement × cardiac and movement × respiration pairs show override behavior, meaning a large synergy term concentrated in high-movement strata, and whether adding those terms narrows SleepNetZero's drop from 0.803 to 0.697 accuracy, or the radar gap to PSG features (MCC 0.47 against 0.60).

Three outcomes would decide the question. First, the pre-registered physiological predictions either appear in the map or fail to: EOG × EMG synergy for REM, ECG × PPG pure redundancy, and belt × ECG coupling that is state-dependent. Second, the detector-chosen pairs either beat random pairs at equal count or do not. Third, the synergy share of the gap is either large enough to justify pair terms or so small that calibrated reweighting is the right fix. Each outcome changes how modular sleep models should be built.