Is Wearable Missingness Behavior or Optics? Separating Non-Wear from Signal Failure

Gaps in a smartwatch's heart-rate record are starting to be used as a health signal in their own right. People wear their devices differently in the days around a medical crisis, and the timing of those gaps can flag trouble even when the total number of missing hours does not change. A "missing" heart-rate minute, though, can mean two different things. The person took the watch off, or the watch was on the wrist but its optical sensor could not get a clean pulse reading. The second kind of gap depends on how tightly and where the band sits, and on skin pigmentation, because melanin absorbs the light the sensor relies on. If darker-skinned users produce more signal-failure gaps, and those gaps rise and fall over time, then a gap-based health alarm can raise false alarms at different rates for different groups while looking like a single behavioral measure.

This proposal splits the wearable missingness record into a behavioral non-wear channel and an optical signal-failure channel. It then tests three things: which channel carries the warning signal before cardiovascular emergency visits, whether signal-failure missingness differs across demographic groups in a way that per-person baselines do not absorb, and whether group-aware calibration restores equal alarm reliability. The validation data for the split will keep the disagreement among human adjudicators instead of collapsing it to a vote. The aim is to measure and correct a confound that sits inside an existing health signal, not to build a new foundation model.

Core Claim

Wearable Missingness as a Behavioral Signal turned each day of Fitbit heart-rate data from the NIH All of Us program into 96 fifteen-minute present/absent slots. It scored each day's departure from a personal baseline using Jensen-Shannon divergence, a standard measure of difference between two distributions. Wear-pattern anomalies rose from 6.46% at baseline to 9.39% in the week before a cardiovascular emergency visit and 12.9% in the week after, while total non-wear hours did not change (p = 0.87). That paper treats every absent slot alike.

Our claim is that the single binary mask mixes two processes with different causes. Behavioral non-wear is driven by routine, illness and fatigue. Optical signal failure is driven by contact pressure, band position and skin optics. The second process plausibly varies by demographic group and over time within a person. Separating them should do two things. It should show which process carries the prodromal (early-warning) signal, and it should make the alarm's error rates comparable across groups.

The supporting evidence comes from three places. WF-PPG shows that wrist contact pressure distorts photoplethysmography (PPG, the optical pulse measurement smartwatches use). RMSSD, a short-term heart-rate-variability measure, has an error of 0.13 ms at the fingertip reference but 10.95 ms at the wrist under suboptimal pressure. Tang et al. and Adaptive Parameter Optimization for Robust Remote Photoplethysmography document lower optical signal-to-noise ratio in darker skin. A device's built-in quality gate converts low signal-to-noise into absent readings, so placement and pigmentation feed directly into the missingness mask.

The split is not "remove artifact, keep behavior." Signal failure may carry physiological information too, for example through changes in perfusion, sweating, or swelling that loosens the band. The question is empirical: which channel carries the signal, and for whom.

Research Program

The decomposition uses a second signal the device records independently of optics: minute-level step counts from the accelerometer. A minute with no heart rate but nonzero steps must be a worn-but-unreadable minute, so it is labeled signal failure with certainty. A minute with no heart rate and zero steps is ambiguous. The person may be sitting still with a poorly seated band, or the watch may be on a nightstand. For these minutes we fit a latent-state model that estimates

$$ \pi_t = P(\text{non-wear at } t \mid \text{HR absent}, \text{steps}=0, c_t), $$

where $\pi_t$ is the probability that ambiguous minute $t$ is true non-wear, and $c_t$ is local context. That context includes the length of the gap, steps immediately before and after it, time of day, the person's historical certain-failure rate, and whether the gap begins mid-activity. A hidden-Markov structure is the natural choice, because non-wear comes in long contiguous blocks while signal failures are short and interleave with activity.

The model gives two soft masks per day. We then run the Luan et al. personal-baseline divergence score separately on each mask, and jointly as a two-channel score.

The model has to be trained and checked against ground truth that Fitbit data cannot provide, so the program includes a small prospective validation study. Participants will span Fitzpatrick skin phototypes, rated by a clinician. Each will wear a consumer optical wristband alongside a non-optical reference: a thigh accelerometer, which records wear independently, and an ambulatory chest ECG during scheduled sessions. They will also keep a wear diary. Within sessions we deliberately vary the placement factors that Transformer-based Models to Deal with Heterogeneous Environments in Human Activity Recognition and WF-PPG identify as drivers of degradation: band tightness, proximal versus distal wrist position, and dominant versus non-dominant arm. This yields a measured curve of signal-failure rate against placement and phototype, which was not previously available.

Diary, reference sensor and device stream will not always agree, so several annotators will independently adjudicate each ambiguous episode. Here the inter-observer variability literature constrains the design. More is more found that collapsing multi-rater labels to consensus raised calibration error from 0.050 to 0.183. The Latent Doctor Model showed that the spread of rater labels can be modeled directly. We will therefore train the decomposition on the full distribution of adjudicator labels rather than a majority vote, and we will report whether adjudicator agreement itself drops for darker phototypes. A drop would mean the "ground truth" is softer exactly where the bias concern is largest. An Open-Access Arrhythmia Database of Wearable Electrocardiogram resolved its two-cardiologist disagreements with a tie-breaker and discarded that information. We will not do that.

The main analysis then applies the decomposition to All of Us Fitbit-linked participants with emergency-visit records. It extends beyond Luan et al.'s 390 participants as far as the linked cohort allows, and stratifies by self-reported race and ethnicity. Self-reported race is a crude proxy for skin optics, and the validation study is what links race-stratified effects back to phototype. The last step is calibration. Missingness-Aware Conformal Prediction Under Cross-Hospital Distribution Shift showed that pooled conformal calibration hides subgroup under-coverage when missingness patterns differ between groups. Conformal calibration means setting alarm thresholds on held-out data to guarantee a target coverage rate. That paper grouped patients by the missingness indicator with the largest distribution shift. We group instead by each person's estimated signal-failure rate, and compare that grouping against grouping by demographic label.

Baselines

The naive reference point is total daily missing hours compared with a personal baseline. Luan et al. already show that it carries no detectable pre-visit signal (p = 0.87). We rerun it on our cohort only to confirm that it remains flat within each demographic group.

The strongest existing method is the Luan et al. single-mask personalized divergence detector, with its reported anomaly rates of 6.46% at baseline, 9.39% in the pre-visit week and 12.9% in the post-visit week. We will reimplement it with their 96-slot binarization and warm-up baseline length, on exactly the participants, visits and weeks used for our method. Our method will be judged on two things. It should match or exceed the baseline's pre-visit lift and its area under the ROC curve (AUROC) for classifying pre-visit weeks. It should also reduce the between-group spread in false-alarm rate, meaning the anomaly rate in weeks far from any visit. No reported result found on Lacuna for subgroup-stratified false-alarm rates of this detector, so we establish that number ourselves. Beating the baseline means a smaller false-alarm spread with no loss of aggregate lift. A gain in aggregate lift alone would not count.

A learned alternative is a masked sequence model that sees the raw missingness mask together with steps, in the spirit of LSM-2. LSM-2 treats naturally occurring gaps as "inherited masks" during self-supervised pretraining. If its weights are not available, we will train an equivalent model with inherited-plus-artificial masking on the same All of Us data, with the same tuning budget we give our decomposition model. This baseline tests whether an unconstrained model finds the split on its own.

Two ablations isolate the key ingredient. The first keeps only the certain signal-failure minutes (heart rate absent, steps nonzero) and drops the latent model for ambiguous minutes. It tests whether the probabilistic resolution matters. The second trains the decomposition on majority-vote adjudications instead of soft labels. It tests whether keeping rater disagreement changes the downstream error rates for each group.

For calibration, pooled split-conformal thresholds and the demographic-label Mondrian grouping serve as baselines. We cite You et al.'s reduction of the maximum subgroup coverage gap from 0.028–0.044 to 0.015–0.021 on GOSSIS ICU data only as a reference for effect size, since it comes from a different domain.

Why not just…?

Why not just rely on the personal baseline, which already absorbs anyone's typical signal-failure rate? This is the most serious threat, and it may be correct. Luan et al.'s detector compares each person against themselves, so a constant excess of signal failures in one group cancels out. The decomposition matters only if signal failure varies within a person over time, for example with season, activity, sweating or band wear, and does so more in some groups. The experiments measure this directly. We will estimate within-person week-to-week variance of the certain signal-failure rate by group. If that variance is negligible and the single-mask detector's false-alarm rates are already equal across groups, we report that the confound is real at the level of rates but harmless to the detector. That is still a useful negative result.

Why not just use step-count gaps as the non-wear signal and ignore heart rate? Zero-step minutes do not distinguish a sleeping or sedentary wearer from a watch on a table. Applying that rule would misclassify exactly the low-activity periods that matter around illness. The first ablation (certain minutes only) and a steps-only detector will show how much signal is lost by not resolving the ambiguous minutes.

Why not just impute the missing heart rate and stop treating gaps as features? Imputation erases the timing signature that Luan et al. found to be informative. RoVTL explicitly lists informative missingness (missingness that depends on the patient's state) as unsolved under its random-dropout training. Imputation also does not answer the question here, which is about why data are missing.

Why not just train a large masked model and let it learn the distinction? It might learn it. That is why the LSM-2-style model is a baseline and not a strawman. Two things count against relying on it. Large pretraining can widen subgroup gaps rather than close them (Luo et al.,). And a learned model provides no audit of which channel drives an alarm. If it matches our false-alarm parity, the remaining contribution is interpretability plus the validation measurements, and we will say so.

Decisive Checks

Four results decide the outcome.

First, in the validation study, does the rate of signal failure rise with phototype and loose placement, and does the decomposition recover diary and reference-sensor truth with comparable accuracy across phototypes? If accuracy collapses for darker skin, the method fails where it is most needed.

Second, in All of Us, does the pre-visit anomaly lift live mainly in the behavioral channel, the signal-failure channel, or both? We will report this separately by group.

Third, does the two-channel detector narrow the between-group false-alarm gap relative to the single-mask detector without losing pooled AUROC?

Fourth, does grouping conformal thresholds by estimated signal-failure rate equalize coverage across race groups as well as or better than grouping by race directly? If it does, it offers a way to calibrate fairly that does not require demographic labels at deployment, which matters for datasets like Pulse-PPG that lack race metadata entirely.