Phone-based mental health models often read absence of activity as a sign of illness. Few unlocks, no calls, and a small mobility radius are taken as signs of withdrawal or low mood. But a phone that records nothing may be in a drawer, switched off, shared with a sibling, or running an operating system that throttles background logging. Who falls into those situations is not random: it depends on device, schedule, income and culture. A model that cannot tell "the person was quiet" from "the sensor could not see the person" will mistake differences in phone access for differences in mental state. It will then misjudge risk unevenly across groups and break when life circumstances shift.
We propose to make this distinction explicit. For every person and every time window, we estimate whether behavior was actually observable (exposed) before deciding whether an observed absence means anything. Only then do we measure how far today's behavior departs from that person's own baseline. The idea borrows from recommender systems, where an unclicked item is no longer treated as a disliked item until we know it was shown to the user. We transplant it into longitudinal digital phenotyping, the practice of tracking health through passive phone and wearable data over months or years. We then audit whether it narrows performance gaps across subgroups and across years.
Core Claim
Part of two known failures in passive-sensing depression prediction comes from confusing missing exposure with low engagement. The first failure is the collapse of accuracy across years. The second is the likely unevenness of accuracy across subgroups. The fix is a finer-grained treatment of negative implicit feedback. Raw counts that equal zero should be split into tiers: observed activity, exposed-but-silent, unexposed, and unknown. Personal baselines should then be computed only over windows where behavior was observable. The claim is falsifiable. If exposure-aware personal deviations do not beat plain personal baselines with missingness indicators, the mechanism is not doing the work we say it does.
Where This Sits
Three lines of work motivate the proposal.
Recommender research shows that the granularity of negative signals matters. Lee et al. split skips into quick and delayed and find that lumping them degrades user representations. Counterfactual Implicit Feedback Modeling (Counter-IF) sorts unobserved user–item pairs into definitely positive, highly exposed, highly unexposed and unknown tiers, using kernel hyperspheres. That paper supplies our method template. We depart from it in three ways. It operates on commercial benchmarks with static items, whereas we operate on longitudinal human behavior. It defines exposure geometrically with hand-set boundary hyperparameters, which the file flags as brittle; we estimate exposure from auxiliary signals that should not depend on mood. And it has no notion of protected groups.
The phenotyping literature shows what is at stake. GLOBEM reports within-year balanced accuracy up to 0.691 that falls to near the 0.500 majority baseline across years. It also shows that behavior–depression correlations flip after COVID-19 onset, and its order-shuffling self-supervision (Reorder) recovers 15.9% in cross-year balanced accuracy. GLOBEM treats the shift as a change in behavior. We ask how much of it is a change in observability: lockdown changed where phones were carried and how GPS and Bluetooth logged.
Feng et al. show on the College Experience Sensing (CES) data that personalization with user embeddings adds over 0.3 Macro-F1. Deviations from an individual's own baseline therefore carry the signal. This both supports our design and constrains it. Any proposal must be built on personal baselines rather than compared against models without them.
Prasad et al. find that 1,133 coarse internet-CBT interaction types add almost nothing over questionnaire scores. We read this as a warning that collapsed engagement counts may hide signal rather than lack it.
The fairness literature constrains how we evaluate. MIMIC-IF audits ICU mortality models and finds that deep models weight features differently across ethnic groups. Cameron et al. report that depression screening tuned to Western behavioral expression fails on Eastern cohorts. Together these argue that behavioral proxies are not group-neutral. Longitudinal Fairness with Censorship supplies two metrics for time-to-event settings: Concordance Imparity, which asks whether risk ranking is equally accurate across groups, and Fair Calibration. That paper evaluates only static tabular baselines; we apply its metrics to streaming behavioral data.
Research Program
The system has three parts.
Exposure estimator. For each person $i$, window $t$, and behavioral channel, an exposure estimator outputs a probability $e_{i,t}$ that the channel could have recorded behavior had it occurred. Its inputs are chosen to be largely mood-independent: sensor uptime and data-yield measures where the released feature set includes them, wearable wear-time, cross-sensor co-occurrence (for example, Fitbit steps logged while phone GPS is silent), and device platform. Weak labels come from windows where an independent channel confirms the person was active, or confirms the device was dead. We calibrate the estimator rather than thresholding it. This avoids the brittle boundary hyperparameters of Counter-IF.
Tier assignment. Each zero-or-low reading is assigned a soft tier: observed activity, exposed-silent, unexposed, or unknown. This mirrors Counter-IF's structure, but the tiers are now indexed in time.
Exposure-weighted personal deviation. We compute personal baselines only from observable windows:
$$d_{i,t} = \frac{x_{i,t} - \mu_i}{\sigma_i}, \qquad \mu_i = \frac{\sum_s e_{i,s}\, x_{i,s}}{\sum_s e_{i,s}},$$
Here $x_{i,t}$ is the behavioral feature, and $\mu_i$ and $\sigma_i$ are the person's exposure-weighted mean and standard deviation over past windows $s$. The sequence model, a Transformer like the strongest CES model in Feng et al., receives $d_{i,t}$ together with $e_{i,t}$. It is never asked to interpret an unexposed zero as a behavioral zero. The estimator and predictor are first trained in two stages. We then test a joint variant in which the predictor's loss also updates the exposure estimator, which addresses the file's noted lack of end-to-end training. A leakage penalty keeps $e$ from simply re-encoding the label.
"Granularity" here deliberately means the granularity of absence. GLOBEM and CES expose coarse telemetry, not sub-click dynamics of the kind studied by Fan et al. and Liu. We do not pretend otherwise. If the mechanism works on coarse data, the natural follow-up is within-app micro-behavior, where the same exposed-versus-unexposed question applies to scrolls and dwell.
Baselines
Naive reference. A Transformer on raw daily features with missing values imputed as zero, which is the "silence is a symptom" assumption. Its role is to show the size of the problem.
Personalized model with explicit missingness. This is the strongest direct competitor. It uses the same Transformer with per-user embeddings and per-user z-scored features, following Feng et al., plus binary missingness indicators for every feature. It is the competitor that matters because personalization is the largest known gain on this kind of data, and missingness flags are the standard cheap answer to absent data. Feng et al. report Transformer Macro-F1 of 0.5808 on CES. For subgroup-level performance on GLOBEM or CES, no reported result found on Lacuna.
Strongest cross-year method. GLOBEM's Reorder. Its authors report balanced accuracy up to 0.691 within year and near 0.500 across years for baselines, with Reorder giving a 15.9% cross-year improvement. We stack our features on top of Reorder as well as comparing against it, since the two are complementary.
Fairness-constrained competitor. Fair Survival Random Forests from Longitudinal Fairness with Censorship, run on the time-to-elevated-symptoms formulation using the same input features. On SUPPORT that paper reports C-index 76.17% and Brier 13.23%; on COMPAS it reports Concordance Imparity falling from 25.32% to 9.63%. No reported result found on Lacuna for it on passive-sensing data.
Ablations. The key ablation replaces $e_{i,t}$ with a constant of one. This keeps everything else, including personalization, and isolates exposure weighting. A second ablation feeds the exposure inputs (uptime, wear-time, platform) directly as extra features without the weighting. This tests whether the structure matters or only the information.
Fair comparison. All neural models share the same splits (leave-one-year-out and within-year), the same hyperparameter search budget, and the same seeds. Any input the exposure estimator uses is also handed to the second ablation, so no method sees data the others lack.
What counts as winning. The proposal beats the personalized baseline if it does both of the following on leave-one-year-out GLOBEM, with confidence intervals excluding zero across seeds and folds: it raises cross-year balanced accuracy, and it shrinks the worst-subgroup balanced-accuracy gap. Winning on fairness alone at a cost in accuracy would count as a partial result, not a win.
Why not just…?
Why not just normalize each person against their own baseline? This is the real threat. Feng et al.'s 0.3 Macro-F1 personalization gain shows how much stable between-person differences matter. Per-user normalization absorbs a person's habitual level of phone use. It does not absorb time-varying exposure. A student who starts leaving the phone at home, or whose logging degrades after an OS update or a lockdown, produces deviations from baseline that look exactly like withdrawal. Our first ablation is designed to settle this: personalization plus missingness flags versus personalization plus exposure weighting. If the gap is negligible, we will report that per-user normalization suffices and that the exposure confound is small in these cohorts.
Why not just feed the uptime and platform signals as extra features? A flexible model could in principle learn the interaction itself. Our second ablation tests this directly. We expect the explicit structure to help most under shift. A model that learns "low uptime and low unlocks means not depressed" from one year's data can relearn the wrong mapping in the next year. Exposure weighting instead fixes how unobservable windows are treated, independent of the label.
Why not collect a more diverse cohort instead? That is ultimately necessary, and nothing here replaces it. But the file gives reasons to doubt that scale alone helps. The account of RETFound (Zhou et al.) describes majority-group features dominating despite large data, and FairDiffusion finds disparities that do not track subgroup sample size. More importantly, exposure confounding grows with diversity, because phone access patterns diverge more. A diverse cohort without an exposure model would bake the confound in more deeply.
Why not prompt a large language model with behavior summaries? Feng et al. report Macro-F1 around 0.44 for Qwen and GPT-4 against 0.5808 for a Transformer on CES. We include one LLM condition only as a reference point.
Proposed Experiments
Experiment 1: semi-synthetic test. This is the decisive mechanistic check because ground truth is known. On GLOBEM we inject exposure dropouts whose rate depends on a synthetic group label and is independent of depression. We vary the dropout strength. The naive and personalized baselines should show a growing subgroup gap as injected dropout rises. The exposure-aware model should stay flat. If it does not, the estimator is failing and the real-data results cannot be trusted.
Experiment 2: real data. We run leave-one-year-out evaluation on GLOBEM, with CES as a second cohort, reporting balanced accuracy and Macro-F1. Subgroups are whatever attributes the datasets release. Device platform is a minimum, since logging behavior differs by operating system. Recorded demographics such as sex are used where available, and cohort year serves as a temporal population. We report worst-subgroup accuracy, the largest pairwise gap, and per-group calibration. We also test the specific prediction that the pre/post-COVID year boundary shows the largest improvement, since that is where observability changed most.
Experiment 3: censored time-to-event formulation. We recast the task as time from a window to first elevated weekly symptom score, which is naturally censored. Models are scored with C-index, Concordance Imparity and Fair Calibration from Zhang & Weiss, comparing FSRF against FSRF given exposure-aware deviations as inputs.
Diagnostic: is exposure quietly encoding the label? We report how well $e_{i,t}$ alone predicts depression. If it predicts well, exposure is a symptom channel rather than a nuisance, and the tiers must be reconsidered.
Limitation. Both cohorts are students. A positive result therefore establishes the mechanism, not cross-population validity. That validity would have to be confirmed on a non-student cohort with richer demographic variation.
References
- Exploiting Fine-Grained Skip Behaviors for Micro-Video Recommendation
- Counterfactual Implicit Feedback Modeling
- GLOBEM Dataset: Multi-Year Datasets for Longitudinal Human Behavior Modeling Generalization
- A Comparative Study of Traditional Machine Learning, Deep Learning, and Large Language Models for Mental Health Forecasting using Smartphone Sensing Data
- Deep learning for the prediction of clinical outcomes in internet-delivered CBT for depression and anxiety
- MIMIC-IF: Interpretability and Fairness Evaluation of Deep Learning Models on MIMIC-IV Dataset
- Multimodal Gender Fairness in Depression Prediction: Insights on Data from the USA & China
- Longitudinal Fairness with Censorship
- Search Action Sequence Modeling With Long Short-Term Memory for Search Task Success Evaluation
- Keynote
- A foundation model for generalizable disease detection from retinal images
- FairDiffusion: Enhancing Equity in Latent Diffusion Models via Fair Bayesian Perturbation