Mendelian randomization (MR) uses inherited genetic variants as natural experiments. Because alleles are assigned at random at conception, a variant that raises, say, body mass index (BMI) can be used to estimate how BMI causally affects diabetes, without the usual confounding. Almost all of this evidence comes from European-ancestry cohorts. When researchers do combine ancestries, they pool one causal estimate per cohort. They use either a fixed-effect average, which assumes a single true effect, or a standard random-effects average. The random-effects version is a meta-analysis that allows the true effect to vary between studies, with spread $\tau^2$. Both versions share a flaw. Any disagreement between ancestries is treated as one kind of thing. Yet two very different processes produce disagreement. The causal effect itself may genuinely differ across populations, for example through diet or gene–environment interaction. Or the genetic instruments may simply stop working properly outside Europe: a variant chosen because it tracks a causal mutation in Europeans can track a different, pleiotropic mutation in East Asians or Africans, because the local correlation structure between nearby variants (linkage disequilibrium, LD) differs.
We propose a random-effects model that separates these two sources. The idea is simple. A true causal difference in an ancestry shifts the estimate from every instrument in that ancestry by the same proportional amount. An instrument failure is specific to individual variants, and it should be larger exactly where the local genetic architecture is poorly shared between ancestries, which can be measured independently. A crossed random-effects model, with one component shared across variants within an ancestry and one specific to each variant-by-ancestry pair, can therefore estimate a "causal heterogeneity" variance that is not contaminated by instrument breakdown. With only three to five ancestries in typical data, the classical between-study variance cannot be estimated this way. Here the many instruments per ancestry supply the replication instead.
Core Claim
Between-ancestry heterogeneity in MR estimates is identifiable as two parts. The first is a causal part, $\tau_c^2$, which is common to all instruments within an ancestry. The second is an instrument part, whose variance grows with how poorly each instrument's genomic region is shared across ancestries. Modeling the second part explicitly does two things. It yields calibrated ancestry-specific causal estimates. It also stops portability failures from being misread as biology, and stops them from being averaged away.
Concretely, let $\hat\Gamma_{jp}$ and $\hat\gamma_{jp}$ be the estimated effects of variant $j$ on the outcome and the exposure in ancestry $p$. Let $r_{jp}$ be the local cross-ancestry genetic correlation of the roughly 1 Mb region containing $j$, comparing ancestry $p$ with the discovery ancestry. The model is
$$\hat\Gamma_{jp} = (\mu + u_p)\,\hat\gamma_{jp} + \alpha_{jp} + \varepsilon_{jp},\qquad u_p \sim N(0,\tau_c^2),\quad \alpha_{jp}\sim N\!\big(0,\ \omega^2 e^{\lambda(1-r_{jp})}\big).$$
Here $\mu$ is the cross-ancestry mean causal effect, and $u_p$ is ancestry $p$'s true causal deviation. The term $\alpha_{jp}$ is variant-by-ancestry pleiotropy, with baseline variance $\omega^2$. That variance grows at rate $\lambda$ as local sharing falls. The term $\varepsilon_{jp}$ is sampling error with known variance from summary statistics. The hypothesis "instrument failure tracks portability" corresponds to $\lambda > 0$. The hypothesis "causal effects truly differ" corresponds to $\tau_c^2 > 0$.
Relation to Prior Work
Several papers motivate the gap. Causal associations between risk factors and common diseases inferred from GWAS summary data developed GSMR, which handles multiple variants and filters pleiotropic outliers with the HEIDI test, and mapped 45 causal associations. The authors state that the results rest on European data and that their transfer is unproven. Genetic association of serum calcium, phosphate, vitamin D, parathyroid hormone, and FGF23 with the risk of aortic stenosis found FGF23 to be a causal driver of aortic stenosis and raised the same caveat. Precision diagnosis for monogenic diabetes requires ethnicity specific criteria for genetic testing is a reminder that criteria derived in White populations can fail elsewhere.
Our method borrows from two lines of work. The first models pleiotropy as a random effect. MR-LDP treats horizontal pleiotropy as a random effect under LD within one ancestry and keeps Type-I error near 5% where standard inverse-variance-weighted (IVW) MR inflates. MR-LDP assumes a single ancestry-matched LD panel, so it has no ancestry dimension. We add that dimension and make the pleiotropy variance depend on portability. The second line supplies the portability covariate. LOG-TRAM estimates local co-heritability in 1 Mb windows and borrows European power only where architecture is shared. X-Wing shows how concentrated portability is: for mean corpuscular volume, about 1% of the genome carries over 60% of European–East Asian genetic covariance. Both methods are for association mapping and polygenic prediction, not causal estimation. We reuse their local-correlation scans as an input to a causal variance model.
Three other papers constrain the design. Robust Mendelian randomization in the presence of residual population stratification, batch effects and horizontal pleiotropy (MR-SENSEMAKR) shows that standard "robust" MR estimators reach 46–80% false positives in biobank-scale samples with slight pleiotropy. Any pooled multi-ancestry estimate dominated by a huge European cohort inherits this "large-N trap." We therefore report ancestry-specific estimates and their uncertainty, not only a pooled $p$-value. Genome-Wide Assessment of Pleiotropy Across >1000 Traits from Global Biobanks used multi-ancestry meta-regression (MR-MEGA) to model effect-size heterogeneity of variant–trait associations across about 1.8 million people. It found that 80% of loci are pleiotropic, but it estimated no directed causal effects. That pervasive pleiotropy is why $\omega^2$ cannot be assumed small. Finally, Inverse-Variance Weighting for Estimation of Heterogeneous Treatment Effects shows that precision weighting under heterogeneity changes what is being estimated. Under fixed-effect weights, the "pooled" effect is effectively the European effect. We address this directly by defining $\mu$ as an unweighted mean over ancestries and making the shrunken $\mu + u_p$ the primary output.
Research Program
We will build the estimator in three stages, all from summary statistics. Stage one is instrument harmonization. Instruments are selected in the discovery ancestry, and their exposure and outcome effects are re-estimated in each target ancestry. Each instrument is annotated with $r_{jp}$ from a LOG-TRAM-style local scan using matched 1000 Genomes reference panels. Stage two is fitting. We fit by restricted maximum likelihood, with a Bayesian variant that places a weakly informative prior on $\tau_c^2$. Many exposure–outcome pairs share the same few ancestries, so we also fit a hierarchical version that pools information about $\tau_c^2$ and $\lambda$ across trait pairs. This targets the known weakness of $\tau^2$ estimation when the number of groups is small. Stage three is inference. We use likelihood-ratio tests for $\tau_c^2 = 0$ and $\lambda = 0$ and a parametric bootstrap for calibration. We will also extend the MR-SENSEMAKR robustness value so that it is benchmarked against each ancestry's own principal components, which gives an ancestry-specific statement of fragility.
The analysis question is identifiability, and it has a sharp limit. If an entire ancestry's instruments are all poorly portable, then a common causal shift and correlated instrument failures can mimic each other. We will characterize when this happens. We expect separation to require variation in $r_{jp}$ within an ancestry. We will report a diagnostic, the spread of $r_{jp}$, that tells users when the decomposition is uninformative.
Baselines
The first reference point is fixed-effect IVW pooling of per-ancestry MR estimates. This is common practice, and it is close to doing nothing about ancestry. It will be run on identical harmonized instruments. We expect European dominance and narrow intervals. Beating it means correct coverage of ancestry-specific effects, which fixed-effect pooling does not provide at all.
The second baseline is the obvious combination: per-ancestry IVW MR, then a DerSimonian–Laird or REML random-effects meta-analysis across ancestries, with Cochran's $Q$ for heterogeneity. It is the strongest generic competitor because it already allows causal effects to differ. It gets the same instruments and the same per-ancestry estimates. Beating it means two things in simulation. Our $\tau_c^2$ should stay near zero when only instruments break, where the standard $\tau^2$ is expected to inflate. Our ancestry-specific intervals should reach nominal coverage with three to five ancestries.
The third baseline is per-ancestry robust MR (MR-Egger, weighted median, MR-PRESSO) followed by random-effects pooling. This represents the "pleiotropy is already handled" view. We will also run an MR-LDP-style random-pleiotropy model fitted separately in each ancestry, because it is the strongest existing pleiotropy-as-random-effect method. The reported numbers we will compare against are MR-LDP's maintenance of a nominal 5% Type-I error where IVW and MR-Egger inflated (MR-LDP) and the 46–80% false-positive rates of robust estimators in large samples (MR-SENSEMAKR paper). No reported result was found on Lacuna for any method's accuracy in estimating between-ancestry causal heterogeneity, so these baselines will be run fresh under identical simulations and tuning budgets.
The key ablation fixes $\lambda = 0$. This keeps the crossed structure but removes the portability link. A second ablation thresholds instruments on $r_{jp}$ and then runs the standard random-effects baseline. Together they isolate whether the gain comes from the crossed decomposition, from the portability covariate, or merely from discarding bad instruments.
Why not just…?
Why not just run a standard random-effects meta-analysis across ancestries? With three to five ancestries, the between-study variance is poorly estimated, and the clinical meta-analyses in the file rely on many more studies, such as 29 cohorts. More importantly, the single $\tau^2$ absorbs instrument breakdown along with real causal differences. The simulations below inject only instrument failure. If the standard $\tau^2$ stays near zero there, this alternative is adequate and our model adds nothing. We expect it not to stay near zero, because LD-driven pleiotropy inflates per-ancestry estimate scatter.
Why not just keep only portable instruments? This is the real threat. If thresholding on local genetic correlation and then pooling performs as well as our model, the simpler recipe wins, and we will say so. Our expected advantage has two parts. Thresholding discards power in under-represented ancestries, where instruments are already scarce. It also offers no test of whether the residual disagreement is causal. The thresholding ablation settles the question directly on coverage, interval width, and held-out prediction.
Why not just select instruments within each ancestry's own GWAS? This avoids transfer, but non-European cohorts often yield few genome-wide significant instruments, which brings weak-instrument bias. We include ancestry-native instrument sets as an extra arm. Where they are strong, as in Biobank Japan for lipids and BMI, they act as an external check on our estimates of $u_p$.
Why not just apply MR-Egger or MR-PRESSO per ancestry? These methods assume pleiotropy behaves the same throughout one sample. The MR-SENSEMAKR paper documents their high false-positive rates at biobank scale. Neither method uses the cross-ancestry structure that lets us separate a common shift from variant-specific failure.
Proposed Experiments
The first experiment is a simulation with known truth. We will simulate exposures and outcomes on 1000 Genomes haplotypes across African, East Asian, European, South Asian, and admixed American panels. We vary five things independently: true $\tau_c^2$, portability-linked pleiotropy $\lambda$, cohort size imbalance (European cohorts ten to a hundred times larger), the number of instruments, and the within-ancestry spread of $r_{jp}$. Metrics are bias and coverage of $\mu + u_p$, Type-I error for $\tau_c^2 = 0$ and $\lambda = 0$, and the confusion rate between the two sources.
The second experiment uses positive and negative controls in real data. We will use UK Biobank, Biobank Japan, PAGE, and the multi-ancestry strata of the global biobank consortium (pleiotropy atlas). Exposure-on-itself analyses, such as height on height, have true $\beta = 1$ and $\tau_c^2 = 0$ in every ancestry, so any nonzero estimated causal heterogeneity there is a false finding. Outcomes with no plausible causal link serve as negative controls. For BMI on type 2 diabetes, the European anchor is GSMR's reported 3.29-fold increase in risk per standard deviation of BMI (GSMR). We ask whether the East Asian and African estimates differ causally, or only through instruments.
The third experiment is the decisive held-out test. We fit on the discovery biobanks, then predict ancestry-specific per-variant Wald ratios in All of Us. We score held-out predictive log-likelihood and interval coverage against every baseline. The proposal succeeds if three things hold: $\lambda$ is reliably positive, controls show near-zero $\tau_c^2$ while the standard random-effects $\tau^2$ is inflated, and held-out coverage beats the thresholding ablation at equal or narrower interval width. If the thresholding ablation matches it, the honest conclusion is that portability-aware instrument filtering suffices, which is itself a useful and simpler recommendation.
References
- Causal associations between risk factors and common diseases inferred from GWAS summary data
- Genetic association of serum calcium, phosphate, vitamin D, parathyroid hormone, and FGF23 with the risk of aortic stenosis
- Precision diagnosis for monogenic diabetes requires ethnicity specific criteria for genetic testing
- MR-LDP: a two-sample Mendelian randomization for GWAS summary statistics accounting for linkage disequilibrium and horizontal pleiotropy
- Leveraging the local genetic structure for trans-ancestry association mapping
- Quantifying portable genetic effects and improving cross-ancestry genetic prediction with GWAS summary statistics
- Robust Mendelian randomization in the presence of residual population stratification, batch effects and horizontal pleiotropy
- Genome-Wide Assessment of Pleiotropy Across >1000 Traits from Global Biobanks
- Inverse-Variance Weighting for Estimation of Heterogeneous Treatment Effects
- Risk factors of epidural hematoma in patients undergoing spinal surgery: a meta-analysis of 29 cohort studies