Frame-Invariant Mendelian Randomization Across Ancestries

Mendelian randomization (MR) uses inherited genetic variants as natural experiments to estimate whether an exposure, such as body mass index, causes a disease, such as type-2 diabetes. When an MR estimate from European-ancestry data is applied to African or East Asian populations, it often weakens or changes. There are three possible reasons. The genetic markers may simply tag the true causal variant less well in the new population, which is an artifact. The markers may act on the disease through other biological pathways in that population. Or the causal effect may genuinely differ. Current practice cannot separate these explanations, and the first one, an artifact, is routinely mistaken for the second and third. This proposal borrows one idea from relative pose estimation in computer vision. That field stopped predicting an object's orientation in a fixed "canonical" coordinate system and began predicting transformations relative to an observed reference view, which keeps working when no canonical frame fits. We apply the same move to cross-ancestry causal inference. We estimate the difference in causal effect between a target ancestry and a reference ancestry directly. We build that estimate from locus-level quantities that do not depend on which population's correlation structure one is working in.

The key observation is simple. At a locus with a single causal variant, the ratio of a marker's association with the outcome to its association with the exposure (the Wald ratio) does not depend on how strongly that marker is correlated with the causal variant. The two associations are weakened by the same factor, and it cancels. Differences in local genetic correlation between ancestries, known as linkage disequilibrium (LD), therefore change how precise the locus-level causal estimate is, but they do not change its expected value. If per-locus causal estimates differ between ancestries beyond what their precision explains, that difference reflects pleiotropy (variants acting through other pathways) or true effect modification, not LD. We turn this invariance into an estimator, a diagnostic, and a benchmark.

Core Claim

Cross-ancestry MR should estimate a relative quantity: the target-minus-reference causal effect, together with a per-locus posterior on whether each locus shares the reference effect. Each ancestry should not be forced onto a European LD reference panel. Instruments should also be re-anchored in the target population's own genetic frame, meaning the lead marker at each reference-discovered locus is chosen using target-ancestry data. We claim this does two things better than running MR separately per ancestry and comparing the results. It keeps nominal error rates when LD differs but causal effects do not. And it detects genuine heterogeneity with more power, because every European-discovered locus contributes information about the target, including loci too weak to reach significance in the target.

The Mechanism

Take ancestry $a \in \{R, T\}$ (reference, target) and locus $j$. Let $r^a_j$ be the correlation between the chosen marker and the causal variant, $g^a_j$ the causal variant's effect on the exposure, $\theta^a$ the causal effect of exposure on outcome, and $\alpha^a_j$ any pleiotropic effect on the outcome. The marker's exposure and outcome associations are then

$$\gamma^a_j = r^a_j g^a_j, \qquad \Gamma^a_j = r^a_j\left(\theta^a g^a_j + \alpha^a_j\right),$$

so the Wald ratio $\Gamma^a_j/\gamma^a_j = \theta^a + \alpha^a_j/g^a_j$ contains neither $r^a_j$ nor any LD panel. The ratio also stays valid when the variant's effect on the exposure differs across ancestries ($g^R_j \neq g^T_j$). The locus-level cross-ancestry contrast $\delta_j = \Gamma^T_j/\gamma^T_j - \Gamma^R_j/\gamma^R_j$ therefore has expectation $\theta^T - \theta^R$ plus pleiotropy terms. LD loss only inflates its variance.

This is where the pose-estimation work supplies method rather than only analogy.

The first borrowed element is the relative estimand. It replaces absolute estimation in a canonical frame, as One2Any does by defining coordinates in a single reference camera's frame. The same shift is what What Do Single-View 3D Reconstruction Networks Learn? motivates, by showing that canonical-frame training produces template retrieval rather than real geometry.

The second is the notion of co-visibility. UNOPose predicts, per region, how much two views overlap, and its accuracy degrades beyond 50° viewpoint change, where overlap vanishes. We define the genetic counterpart as a per-locus "target visibility": the target-ancestry instrument strength. It sets how much each locus is trusted, rather than acting as a hard significance filter.

The third is a multimodal likelihood rather than a single averaged answer. RelPose models relative rotation with an energy-based distribution so that symmetric objects are not assigned an invalid mean pose. We model the $\delta_j$ as a mixture of a "shared" component centered at $\theta^T - \theta^R$ and diffuse "diverged" components. This keeps a few strongly pleiotropic loci from being averaged into a false intermediate effect.

Fitting uses an errors-in-variables likelihood over $(\gamma^T_j, \Gamma^T_j, \gamma^R_j, \Gamma^R_j)$ rather than raw ratios, because ratios are heavy-tailed when $\gamma^T_j$ is small. Robust initialization comes from consensus sampling over loci, in the style of RANSAC (repeatedly fitting on small random subsets and keeping the fit most loci agree with), as in the correspondence alignment of Zero-Shot Category-Level Object Pose Estimation.

The invariance breaks where the vision analogy predicts it will: at "symmetric" loci. These are loci with several causal variants whose LD patterns differ by ancestry, so that no single marker tags them in fixed proportion. We handle them in two ways. The mixture absorbs them as diverged loci. We also run a sensitivity analysis restricted to loci that per-ancestry fine-mapping suggests carry a single signal.

Research Program

The method has three parts.

The first part is target re-anchoring. Loci are discovered in a large reference GWAS (genome-wide association study). For each locus, the instrument is then the target ancestry's own strongest marker within the LD block. That marker is selected on an independent split or a third sample, so that the selection step does not inflate its apparent strength (winner's curse).

The second part is the mixture likelihood for $\theta^T - \theta^R$. It returns a posterior per locus for "shared" versus "diverged", with interval estimates that account for weak target instruments.

The third part is a decomposition report for any exposure–outcome pair. It states how much of the naive difference between separate per-ancestry IVW (inverse-variance weighted) estimates is explained by instrument attenuation, how much by pleiotropy concentrated at identifiable loci, and how much remains as a shared shift consistent with effect modification.

The method intersects directly with X-Wing, Quantifying portable genetic effects and improving cross-ancestry genetic prediction with GWAS summary statistics. X-Wing shows that genetic sharing between ancestries is highly localized: about 1% of the genome carries over 60% of the European–East Asian covariance for mean corpuscular volume. It also improves cross-ancestry prediction $R^2$ by 14.1–119.1%. X-Wing depends on LD reference panels, and it targets prediction, not causal effects. We use its portability map in two ways: as a prior on which loci belong to the shared component, and as an ablation. Our estimator never needs a target LD panel, which addresses the admixed-population limitation X-Wing itself flags.

The method also reuses the standard MR machinery of GSMR, Causal associations between risk factors and common diseases inferred from GWAS summary data, including its HEIDI outlier filter. It differs in that HEIDI removes pleiotropic loci within one ancestry's LD frame, whereas we identify loci that disagree across frames.

Baselines

The naive reference point is European transfer. The European IVW causal estimate is applied unchanged as the target estimate, using European-selected lead markers looked up in target summary statistics. This is what much practice implicitly does. Beating it means covering the true target effect in simulation when the true effects differ, and it is also the anchor for the "LD-only" simulations described below.

The strongest existing approach, and the one a reviewer will reach for, is separate per-ancestry MR followed by a comparison. It is run as in the psychiatric-disorders–glaucoma study, with IVW, MR-Egger, weighted median, MR-PRESSO, and Steiger filtering applied within European and East Asian data, and a Cochran's Q test (a standard test for heterogeneity) on the two estimates. GSMR with HEIDI filtering, run per ancestry, is the within-ancestry state of the art. As a real-data reference, GSMR reports a 3.29-fold increase in type-2 diabetes risk per SD of BMI in Europeans. For cross-ancestry MR contrasts specifically, no reported result was found on Lacuna.

Every method receives the same summary statistics, the same locus definitions, the same independent sample for instrument selection, and the same outlier-method settings, with no method-specific tuning beyond published defaults. Beating this baseline means holding type-I error for "effect differs across ancestries" at nominal levels when only LD differs, while achieving higher power at matched error when effects truly differ.

Two ablations isolate the ingredients. The first uses European lead markers in place of target re-anchoring, which tests whether the viewer-centered choice of instrument matters. The second collapses the mixture to a single Gaussian component, which tests whether the multimodal likelihood matters beyond simple robust weighting. A third ablation uses X-Wing portable segments as a hard instrument filter followed by standard IVW, which tests whether portability selection alone gives the benefit.

Why not just…?

Why not just run MR separately in each ancestry and compare? This is the serious threat. When both cohorts are large, separate estimates plus a Q test may be all one needs, and the concordant European and East Asian nulls for psychiatric disorders and glaucoma (depression OR 1.15 in Europeans versus 1.38 in East Asians, both non-significant) show that it can give sensible answers. Its weakness is that it discards European-discovered loci that fail significance in the smaller target cohort. It also conflates attenuated instruments with divergent effects. Our simulations directly test whether the relative estimator gains power at matched error. If it does not gain meaningfully at realistic target sample sizes, around 200,000 in the combined China Kadoorie Biobank and BioBank Japan data, we will report that the simple approach suffices except for very small cohorts.

Why not just filter instruments with X-Wing's portability map and run standard MR? This could capture most of the gain, which is why it is an explicit ablation. It needs target LD panels, which are noisy or missing for admixed groups. It also converts a graded signal into a hard cutoff. We expect the relative estimator to match it where panels are good and to beat it in admixed samples such as PAGE, where panels are poor. If it matches us everywhere, our contribution reduces to the diagnostic decomposition.

Why not just pool ancestries with principal-component adjustment, or shift thresholds as in the monogenic diabetes work? Ancestry-specific BMI cutoffs doubled detection of monogenic diabetes (MODY) from 8.8% to 16%, yet South Asian detection stayed at 11% versus 39% in White participants (Precision diagnosis for monogenic diabetes). A global adjustment helps, but it cannot fix discordance that X-Wing shows is local to specific loci. Pooling also estimates a single effect by construction, so it cannot answer whether the effect differs across ancestries.

Why not just rely on existing robust MR (MR-PRESSO, weighted median) within a pooled analysis? These methods detect outliers relative to one frame's consensus. They do not use the paired structure of the same locus observed in two ancestries, which is the source of our LD-invariance test. The Gaussian-collapse ablation shows how much the paired mixture adds over this style of robustness.

Proposed Experiments

The decisive test is a semi-synthetic simulation built on real genotypes from the European and non-European subsets of UK Biobank. The simulated phenotypes follow four scenarios with ground truth known exactly. In the first, only LD differs. In the second, pleiotropy is present at a controlled fraction of loci. In the third, a true uniform effect difference is imposed. In the fourth, effect modification is concentrated at a few loci. The proposal fails if, in the LD-only scenario, it declares heterogeneity more often than nominal, or produces worse coverage of $\theta^T - \theta^R$ than per-ancestry IVW. We report bias, 95% interval coverage, heterogeneity power at fixed type-I error, and accuracy of locus-level "diverged" calls, each as a function of target sample size.

The real-data evaluation has three arms. The first uses positive controls with strong priors of shared causation, namely BMI→type-2 diabetes and LDL→type-2 diabetes, comparing UK Biobank with BioBank Japan. Here the method should report a contrast near zero with most loci in the shared component, and should localize any outliers. One example is the APOE region, where HEIDI removed 16 markers in GSMR. The second arm uses negative-control nulls: psychiatric disorders→glaucoma across FinnGen/UK Biobank and CKB/BBJ. The method should not manufacture effects there. The third arm uses admixed PAGE data, where target LD panels are weakest and where the ablation against the X-Wing filter should separate most clearly.

A final analysis concerns multi-signal loci, the genetic counterpart of symmetry. We check whether the loci the mixture flags as diverged are enriched for multiple credible fine-mapping signals rather than for known pleiotropic genes. That tells us whether the diagnostic is picking up an LD failure of the invariance or a genuine difference in causal pathways.