Reporting Calibration in Cross-Ancestry Mendelian Randomization

Genetic studies increasingly ask whether a cause-and-effect estimate found in European biobanks holds in East Asian or other populations. The tool is Mendelian randomization (MR), which uses inherited genetic variants as natural experiments. Because genes are assigned at conception, a variant that shifts an exposure such as drinking or physical activity can reveal that exposure's effect on disease without the usual confounding. When European and East Asian estimates disagree, the field usually points to biology. The candidate explanations are that the marker variants track the real causal DNA differently in each population, that variants act through other pathways, or that genes interact with different environments.

This proposal argues that a large share of that disagreement may come from the questionnaire rather than the genome. Many MR exposures in biobanks are self-reported. Social desirability bias, the habit of reporting what sounds good rather than what one does, differs in strength across cultures. If one population compresses or exaggerates its reported activity or alcohol intake more than another, every genetic effect on the reported exposure is rescaled by a population-specific factor. The MR estimate is then divided by that same factor. We propose to measure this factor directly, within each population, by comparing genetic effects on the self-reported version of a trait to genetic effects on an objectively measured version. The resulting correction lets us separate "the cause works differently here" from "people describe the cause differently here."

Core Claim

Differential reporting leaves a signature that is distinct from biological sources of cross-ancestry discordance. The distinguishing feature is that it is uniform across variants, while the biological sources are specific to each variant. Suppose the self-reported exposure $R$ in population $p$ relates to the true behavior $X$ as

$$R = \alpha_p + \lambda_p X + \pi_p^\top G + \varepsilon,$$

where $\lambda_p$ is the population's reporting slope ($\lambda_p<1$ means answers are compressed toward a socially approved middle), $G$ is genotype, $\pi_p$ captures variants that affect the tendency to present oneself favorably rather than the behavior itself, and $\varepsilon$ is noise. The effect of variant $j$ on the reported trait is then

$$\gamma^R_{pj} = \lambda_p\,\gamma^X_{pj} + \pi_{pj},$$

where $\gamma^X_{pj}$ is its effect on the true behavior. The MR estimate built on the self-reported trait therefore targets $\beta_p/\lambda_p$, where $\beta_p$ is the true causal effect.

Two consequences follow. First, the European-to-East-Asian ratio of raw MR estimates equals the true ratio multiplied by $\lambda_{\text{EAS}}/\lambda_{\text{EUR}}$. Methods that hunt for misbehaving variants cannot see this, because every variant is rescaled alike. Second, $\lambda_p$ can be estimated inside a single population. We regress $\gamma^R_{pj}$ on $\gamma^X_{pj}$, where $X$ is an objectively measured version of the trait. Both sets of effects share the same linkage disequilibrium (the population-specific correlation between neighboring variants), so the ancestry-specific tagging problem cancels out. The $\pi_{pj}$ terms behave exactly like pleiotropy in an ordinary MR. That means existing robust MR machinery can estimate $\lambda_p$ while tolerating many "reporting variants."

Research Program

The work has three parts.

The first part is a calibration estimator. For each population and trait pair, we take the variants associated with the objective measure. We then estimate $\lambda_p$ as the slope of self-report effects on objective effects. We reuse MR-LOVA, a latent-variable MR method fit by stochastic expectation-maximization that tolerates up to 70% invalid instruments, as the robust slope estimator. We also reuse the measurement-error and winner's-curse corrections of MAGIC, a mediation-MR method that fixes attenuation and instrument-selection bias in summary statistics. These corrections matter because objective-measure GWAS (genome-wide association studies) are often smaller and noisier. Here these methods supply the technique, but we point them at a different target: the measurement model itself, not the disease effect.

The second part is a discordance decomposition. We compare calibrated and raw cross-ancestry MR estimates. We test whether the remaining SNP-by-SNP heterogeneity is consistent with a single rescaling or requires variant-specific (biological) differences. The variants that sit off the calibration line are the estimated $\pi_{pj}$. We characterize them as candidate "self-presentation" variants and ask whether they replicate across ancestries. The file's Gap 3 predicts they will not.

The third part is a simulation benchmark. We generate two-population summary statistics that jointly vary four ingredients: tagging strength (linkage disequilibrium mismatch), correlated pleiotropy that violates the InSIDE (instrument strength independent of direct effect) assumption, gene-by-environment scaling, and the reporting slopes $\lambda_p$. This lets us check that the decomposition attributes discordance to the right source.

The motivating evidence comes from three studies:

  • Zhao et al. ran MR of self-reported physical and social inactivity on depression in UK Biobank. They report physical inactivity OR = 3.67 (odds ratio, the multiplier on the odds of disease). They flag both touchscreen self-report bias and their European-only restriction as limitations, without quantifying either.
  • The UK Biobank alcohol spouse studies (observational vs MR; assortative mating) show that self-report-based concordance (0.37) exceeds the genetic estimate (0.26). They also warn that the ADH1B instrument rs1229984 is strongly tied to ancestry.
  • Zhang et al. ran parallel European and East Asian MR of psychiatric traits on glaucoma. Depression gave OR 1.15 in Europeans and 1.38 in East Asians, both null. Such point-estimate gaps are exactly what our decomposition would interpret rather than ignore.

The survey literature on culture-specific inflation (Enticott et al., Barros et al., Pedron et al., Tan et al.) shows that reporting slopes plausibly differ across settings. That literature never connects this to genetic effect sizes. Dai et al. validated a self-management scale against HbA1c and fasting glucose. Their work is the phenotypic analogue of what we do genetically: anchoring a self-report to a biomarker.

Three studies constrain the design. Jones et al. show European-derived criteria fail in non-White groups, so calibration must never be transported between populations. Gorfine et al. show two-stage predictor substitution is biased for binary outcomes because logistic models are non-collapsible. We therefore work on the linear scale for continuous exposures and report binary-outcome results as log-odds with that caveat. The accelerometer clustering study shows that objective activity summaries are sensitive to processing choices. It reports R² for waist circumference of about 25% whether one uses clusters or the simple time-active mean. We therefore use simple, pre-registered objective summaries rather than learned clusters as the anchor.

Baselines

The naive reference point is raw ancestry-stratified inverse-variance-weighted (IVW) MR on the self-reported exposure, followed by a test of cross-ancestry heterogeneity. This is the analysis Zhang et al. ran. It is fair to run with identical instruments, clumping thresholds and outcome GWAS in each population. In simulation, "beating it" means correctly attributing discordance to reporting when only $\lambda_p$ differs. In real data, it means narrowing cross-ancestry gaps for self-reported exposures.

The strongest existing method is robust per-ancestry MR with MR-LOVA. Amente et al. report 0.92 sensitivity for identifying valid instruments, compared with 0.37 for IMRP and 0.25 for MR-ConMix, while holding a 5% false-positive rate under correlated pleiotropy. They also report that traditional estimates of BMI on metabolic syndrome of 0.70–0.88 shrink to 0.52. We run it on the same summary statistics with the same permutation budget as our calibrated pipeline, which also calls MR-LOVA internally. The comparison therefore isolates the calibration step rather than the robust estimator.

The second strong comparator is MAGIC-style measurement-error correction. It reports 95% interval coverage where two-step MR and multivariable MR fall to 70–80%. We apply it per population to the self-reported exposure. MAGIC corrects sampling error in estimated SNP effects. It does not correct a systematic reporting slope, so we expect it to leave the $1/\lambda_p$ bias intact. Beating it means better coverage of the objective-exposure MR estimate, which is our reference truth in real data.

We run two ablations. The first replaces population-specific $\lambda_p$ with a single pooled slope. This isolates the claim that reporting differs by population. The second replaces genetic calibration with within-population standardization of the self-report to SD units.

Why not just…?

Why not just run MR on the objectively measured exposure and skip self-report entirely? Where an adequately powered objective GWAS exists in every population, this is the right answer, and our calibrated estimate should reproduce it. We use it as the reference truth. The problem is coverage. Even in UK Biobank, Zhao et al. relied on touchscreen answers for about 460,000 people because accelerometry covered only a subset. The file gives no indication that CKB or BBJ have biobank-scale device data. The proposal's value is that a modest anchored subset can calibrate the full self-reported GWAS. Experiment 2 tests exactly this by subsampling the anchor. If calibration needs an anchor as large as the objective GWAS itself, the idea fails and we will say so.

Why not just standardize the exposure to SD units within each ancestry? This is a real threat, because it does absorb part of any scale difference. However, the SD of the reported trait equals $\sqrt{\lambda_p^2\,\mathrm{Var}(X) + \mathrm{Var}(\pi^\top G) + \mathrm{Var}(\varepsilon)}$. It therefore mixes the reporting slope with noise and with differences in true behavioral variance across populations. It equals the needed correction only when noise is negligible and true variances match. The standardization ablation measures how much of our gain it recovers in simulation and on real traits. If it recovers nearly all of it on real data, we will recommend it as the practical fix and narrow our claim to diagnosing when it fails.

Why not just use robust MR (MR-LOVA, weighted median, MR-Egger) per ancestry? These methods look for variants whose ratio departs from the majority. A reporting slope moves every variant's ratio by the same factor, so the majority moves with it and nothing looks invalid. They remain essential, but in our pipeline they estimate $\lambda_p$ and the remaining disease effect. They cannot substitute for the calibration step. Experiment 1 shows this directly on scenarios where only $\lambda_p$ differs.

Why not just add genetic principal components and a Marlowe-Crowne lie scale? Principal components adjust for ancestry-related allele-frequency structure. They do not rescale a questionnaire. A general lie scale is unavailable in these biobanks' summary statistics. Domain studies (Yang et al.; Sun et al.) also show that inflation is domain-specific in ways a generic scale would miss.

Proposed Experiments

Experiment 1 is the simulation benchmark. We generate two-population summary statistics with differing linkage disequilibrium, correlated pleiotropy, gene-by-environment scaling and reporting slopes, run at biobank-like sample sizes of 200,000–500,000 (matching those in the file). The metrics are:

  • bias and 95% coverage of $\beta_p$;
  • accuracy of attributing the European–East Asian discordance to reporting versus variant-specific sources;
  • recovery of the planted $\pi$ variants.

The decisive check has two sides. When only $\lambda_p$ differs, raw IVW and MR-LOVA should both report significant cross-ancestry heterogeneity in the causal effect, while the calibrated pipeline should not. When only tagging differs, the calibrated pipeline must still flag heterogeneity.

Experiment 2 is calibration against device data in UK Biobank. We use self-reported and accelerometer-measured activity, in the subset with devices, with depression as the outcome. This re-examines Zhao et al.'s OR = 3.67 for physical inactivity. It is a within-population test, so we do not expect to overturn that result. We subsample the anchored set to find how small it can be before $\hat\lambda$ becomes unstable.

Experiment 3 is the cross-ancestry test. We use UK Biobank, CKB and BBJ for trait pairs where both a self-reported and a measured version exist. Before any modeling, we audit which pairs these biobanks actually provide. Height serves as a positive control: it is hard to misreport, so we expect $\lambda_p\approx 1$ everywhere. We expect larger departures for socially loaded traits such as alcohol intake and activity. Alcohol is attractive because rs1229984 is a functional missense variant, so it is less exposed to tagging differences.

The decisive empirical check is a specific pattern. Calibration should shrink cross-ancestry gaps in MR estimates for self-reported exposures while leaving gaps for measured exposures unchanged. The estimated reporting variants should replicate across populations worse than the calibration-line variants. If calibration shrinks gaps equally for height and alcohol, the correction is fitting noise rather than reporting, and the core claim is falsified.

References

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  4. Alcohol consumption and mate choice in UK Biobank: comparing observational and Mendelian randomization estimates
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  6. Mendelian randomization study shows no causal relationship between psychiatric disorders and glaucoma in European and East Asian populations
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