Genetic epidemiologists are starting to replace questionnaire answers ("how often do you nap?") with wrist-worn accelerometer measurements, and then use those measurements as the exposure in Mendelian randomization (MR). MR is a method that treats genetic variants as natural experiments to estimate whether one trait causes another. The switch looks like pure gain, because sensors do not misremember. But a wearable-derived trait is produced by a person, a device, and a cleaning pipeline together. How long someone keeps the device on, when they take it off, and how noisy their recording is are behaviors. Behaviors are partly heritable, tied to health, and shaped by socio-environmental context, and that context differs across ancestry groups. Our central claim is that the corruption process of a wearable sensor is itself a genetically influenced trait that leaks into the variant–exposure associations MR depends on. Because the size of this leak depends on population-specific wear behavior, it can create or hide apparent differences in causal effects between ancestries that have nothing to do with biology.
The opportunity comes from one fact: unlike biological pleiotropy, this contamination is observable. Non-wear time, gap structure, and signal noise can be measured for every participant. We propose to measure them, estimate their genetic basis, and remove their contribution from the causal estimate at the level of genetic summary statistics. The goal is a corruption-aware MR procedure plus a diagnostic that splits cross-ancestry disagreement in MR estimates into a "biology" part and a "measurement channel" part. This matters now because two recent MR studies named objective wearable exposures and non-European replication as their next steps. Dissecting the causal association between social or physical inactivity and depression reported a physical-inactivity-to-depression odds ratio of 3.67 from self-report and called for actigraphy and diverse cohorts. Genetic determinants of daytime napping and effects on cardiometabolic health used accelerometer-measured daytime inactivity only to validate self-reported napping loci, and restricted its analysis to Europeans. Our concern is that doing both at once, naively, will produce misleading answers.
Core Claim
Let $\tilde X$ be the sensor-derived exposure, such as accelerometer-measured daytime inactivity. It equals the true behavior $X$ plus a measurement component $M$ generated by wear and cleaning. For genetic variant $j$, the estimated variant–exposure effect is $\beta_{jX}+\beta_{jM}$, where $\beta_{jM}$ is the variant's effect on the measurement component. Suppose the outcome is also shifted directly by the same processes that drive non-wear; for example, ill people charge or remove devices differently. Then the per-variant ratio estimate of the causal effect $\theta$ is
$$\hat\theta_j \approx \frac{\theta\,\beta_{jX} + \alpha_j}{\beta_{jX} + \beta_{jM}},$$
where $\alpha_j$ is the variant's effect on the outcome through routes other than $X$. The expression follows directly from the standard ratio estimator with the numerator and denominator decomposed. When $\beta_{jM}$ differs between ancestry groups, the pooled estimate $\hat\theta$ differs across groups even if $\theta$ is identical. Differences in linkage disequilibrium (LD, the population-specific correlation between nearby variants) already make instruments weaker or pleiotropic across ancestries. A measurement channel adds a further source of apparent non-portability that current methods cannot distinguish from LD effects or true effect heterogeneity.
Our fix uses corruption indicators $C$ that are measured for every participant, including non-wear fraction, the placement of gaps within the day, and the signal noise floor. We run a genome-wide association study (GWAS) on $C$ to obtain $\beta_{jC}$. We then estimate $\theta$ jointly with a nuisance effect of $C$ in a multivariable summary-statistic model:
$$\hat\gamma_{jY} = \theta\,\hat\gamma_{j\tilde X} + \phi\,\hat\beta_{jC} + \alpha_j,$$
where $\hat\gamma_{jY}$ and $\hat\gamma_{j\tilde X}$ are the variant–outcome and variant–exposure estimates and $\phi$ absorbs the measurement channel. The regression runs on genetic effect sizes, not individuals. This avoids the collider bias that would come from adjusting the exposure GWAS for a heritable covariate such as wear time.
Relation to Prior Work
The closest work is Causal Inference with Corrupted Data. It cleans corrupted covariates by projecting them onto a low-rank subspace using principal component analysis, then applies doubly robust estimation. It shows that unadjusted corruption can flip the sign of two-stage least squares estimates. That paper motivates our concern, but its assumptions also limit it. It explicitly excludes endogenous missingness and confounded noise, which is exactly the regime of heritable, health-linked non-wear. We therefore reuse its lesson that corruption must enter the estimator itself, and we reject its exogenous-noise model. The low-rank cleaning tradition it shares with Load Curve Data Cleansing and Imputation Via Sparsity and Low Rank assumes corruption is sparse and missing at random. Neither assumption holds when who is missing is part of the signal.
On the genetics side, two methods supply our machinery and act as competitors. GSMR removes variants whose causal estimates are heterogeneous (the HEIDI-outlier filter). It also introduced mtCOJO, a way to condition one trait's GWAS on another's at the summary level, and our multivariable step borrows this idea. MR-LOVA models direct effects as a latent variable and keeps Type I error near 5% even with 70% invalid instruments. Both methods infer invalid instruments from inconsistency patterns and assume the exposure statistics measure the intended trait. We differ by measuring the contaminating channel directly rather than inferring it.
X-Wing found that cross-ancestry genetic correlation is concentrated in small genomic regions. We use its local correlation scan to ask a new question: are the measurement-channel loci portable across ancestries, or ancestry-specific?
On the sensor side, Self-supervised learning for human activity recognition using 700,000 person-days of wearable data pretrained an activity model on UK Biobank accelerometry. Pretraining here means learning from unlabeled recordings using tasks such as detecting whether a clip runs backward. Its authors note that the pretraining corpus is predominantly white British. We treat its features as one candidate exposure pipeline, alongside classical summary measures, and test whether they encode wear behavior.
Research Program
The work has three parts, all built on the UK Biobank accelerometer cohort and its genotypes.
The first part is characterization. For each participant we compute a vector of corruption indicators directly from the raw 100 Hz traces. We then test three things about these indicators: whether they are heritable, whether they differ across the UK Biobank's self-identified and genetically inferred ancestry groups, and whether their GWAS hits overlap the instruments for derived exposures. We examine two exposures: daytime inactivity duration, mirroring the napping study, and overall physical activity, mirroring the depression study. If $C$ has negligible heritability or no genetic correlation with the exposures, the core claim is false, and we will report that as a useful negative result for the field.
The second part is estimation. We fit the multivariable model above, using GSMR-style LD handling and optionally combining it with MR-LOVA's latent direct-effect model. The aim is to separate the measurement channel ($\phi$) from biological pleiotropy ($\alpha_j$).
The third part is the cross-ancestry diagnostic. We fit the model within each ancestry group available with accelerometry. We then decompose the between-group difference in $\hat\theta$ into three terms: one explained by differing $\beta_{jM}$, one explained by LD-driven instrument weakening, and a residual we interpret as candidate true heterogeneity. The non-European accelerometer subsample of UK Biobank is small; the file gives no count, so we do not state one. Real-data cross-ancestry results will therefore carry wide intervals, and the main evidence for the decomposition will come from semi-synthetic experiments.
Baselines
The naive reference point is standard two-sample MR on the raw sensor-derived exposure, using GSMR with HEIDI-outlier filtering, applied identically in each ancestry group. Current practice would be exactly this, simply swapping the questionnaire for the accelerometer. For the real data, its published anchors come from self-report exposures: 0.18 SD for systolic and 0.25 SD for diastolic blood pressure per napping category (napping study), and OR 3.67 for physical inactivity on depression (depression study). We will report how the accelerometer-exposure estimates compare to these anchors before and after correction.
The strongest existing competitor is MR-LOVA, because correlated pleiotropy is the form the measurement channel would take if it were just another invalid-instrument mechanism. Its reported performance is a 5% Type I error with up to 70% invalid instruments and an instrument-validity sensitivity of 0.92, against 0.37 for IMRP (MR-LOVA). We run it on the same summary statistics, instrument sets, and LD references as our method, using the authors' default tuning. Our method beats it if it holds nominal Type I error and coverage in semi-synthetic settings where MR-LOVA does not. Those settings are the ones where measurement-channel variants are numerous and their effect on the exposure scales with their effect on the outcome. Separately, our method must shrink the cross-ancestry discrepancy in $\hat\theta$ when the true $\theta$ is shared, and preserve it when $\theta$ truly differs.
The corruption-adjustment competitor is the data-cleaning-adjusted estimator of Agarwal et al.. We apply it to the minute-level activity matrix before deriving the exposure, then run standard MR on the result. It is expected to succeed under the exogenous noise it was designed for and to fail under heritable non-wear. We will test both regimes so that the comparison is fair to it.
Two ablations isolate our key ingredient, which is using measured corruption genetics as a nuisance exposure. The first uses $\hat\beta_{jC}$ only to discard instruments strongly associated with corruption, testing whether filtering suffices. The second adjusts the individual-level exposure GWAS for wear time as a covariate, testing whether the summary-level treatment matters.
Why not just…?
Why not just drop participants with poor wear time? Complete-case analysis selects people on a heritable, health-linked behavior. Among the retained participants, this manufactures associations between the variants for wear compliance and the outcome. Agarwal et al. flag endogenous selection of this kind as outside what standard estimators handle. It also removes a larger share of already-small minority samples if wear behavior differs by group, which part one will measure. We include complete-case MR in the semi-synthetic benchmark to show the bias directly, rather than assert it.
Why not just adjust the exposure GWAS for non-wear time? This is the most natural fix. It is flawed because non-wear time is partly caused by the same variants and conditions that affect the exposure. Conditioning on it at the individual level opens a collider path. The second ablation tests this head to head. If covariate adjustment matches our summary-level model in simulation and real data, the methodological contribution shrinks to the diagnostic, and we will say so.
Why not just trust MR-LOVA or HEIDI to catch the contaminated instruments? This is a real threat. MR-LOVA was built precisely for correlated pleiotropy. If measurement-channel variants behave like ordinary invalid instruments, it may handle them. Two things could still go wrong. HEIDI may discard valid biological instruments that also carry a modest measurement component, which costs power. And neither method can attribute cross-ancestry differences to the measurement channel, because neither observes it. The semi-synthetic benchmark settles the estimation question. The diagnostic's value does not depend on winning it.
Why not just go back to questionnaires? Both motivating studies document recall bias and misclassification in self-report and explicitly recommend objective measurement. Self-report also has a reporting channel that can differ across groups, and this one cannot be measured per person. Wearables at least make their corruption visible, and our proposal uses that visibility.
Proposed Experiments
The semi-synthetic benchmark starts from real UK Biobank accelerometer traces and real genotypes. We simulate a true exposure effect $\theta$, which is either shared or different across ancestry groups. We then inject non-wear gaps and noise whose probability depends on a polygenic score for "wear behavior." The strength of that score effect differs by ancestry group, and in some settings it also has a direct effect on the outcome. We vary four factors: the heritability of corruption, the fraction of exposure instruments that overlap corruption loci, the strength of the direct outcome effect, and the ancestry difference in corruption. The metrics are bias, Type I error at $\theta=0$, confidence-interval coverage, and the error of the between-ancestry discrepancy estimate.
We also vary the exposure pipeline: classical daytime inactivity, overall acceleration, and activity classes predicted by the self-supervised model of Hang et al. A linear probe (a simple classifier on frozen features) tests whether that model's embeddings predict non-wear and ancestry group beyond the activity labels. Such leakage would mean that foundation-model-derived exposures carry an extra measurement channel. We add a sensor-level check on Capture-24, which has camera-annotated activity: we inject structured gaps and measure how the derived exposures shift. This isolates pipeline sensitivity from genetics.
The real-data analysis estimates napping-to-blood-pressure and inactivity-to-depression effects from accelerometer exposures, with and without the measurement channel. For each, we report the fitted $\phi$ and the per-ancestry decomposition. A local genetic correlation scan in the style of X-Wing then asks whether corruption loci are shared across the available ancestry groups. The file lists no accelerometry for Biobank Japan or PAGE (no reported result found on Lacuna for wearable exposures in those cohorts). Cross-ancestry real-data conclusions will therefore stay within UK Biobank and will be stated as limited by sample size.
The decisive checks are as follows. First, is corruption heritable and genetically correlated with the exposures? If not, the idea fails early and cheaply. Second, in semi-synthetic data, does the multivariable correction restore nominal Type I error and coverage where GSMR, MR-LOVA, filtering, and covariate adjustment do not? Third, when the true effect is shared across ancestries, does the correction remove the spurious between-group discrepancy, and when the effect truly differs, does it leave the discrepancy intact? Fourth, does the measured corruption indicator, used as a negative-control exposure, show near-zero causal effect on the outcome after correction? A clearly nonzero value would indicate a direct health-to-wear pathway that MR cannot remove, and would mark the limit of what any sensor-based MR can claim.
References
- Dissecting the causal association between social or physical inactivity and depression: a bidirectional two-sample Mendelian Randomization study
- Genetic determinants of daytime napping and effects on cardiometabolic health
- Causal Inference with Corrupted Data: Measurement Error, Missing Values, Discretization, and Differential Privacy
- Load curve data cleansing and imputation via sparsity and low rank
- Causal associations between risk factors and common diseases inferred from GWAS summary data
- A latent outcome variable approach for Mendelian randomization using the stochastic expectation maximization algorithm
- Quantifying portable genetic effects and improving cross-ancestry genetic prediction with GWAS summary statistics
- Self-supervised learning for human activity recognition using 700,000 person-days of wearable data