Choosing Which Ancestry Supplies Each Genetic Instrument

Mendelian randomization estimates whether an exposure, such as LDL cholesterol, causes a disease. It does this by using genetic variants as natural experiments, or "instruments." Almost all instruments are picked from European genome-wide association studies (GWAS, scans that test millions of variants for association with a trait), because those studies are by far the largest. The variants they pick are usually not the causal mutations. They are nearby markers that happen to be inherited together with the causal mutation in Europeans. In African or East Asian populations, that co-inheritance (linkage disequilibrium, LD) can weaken or disappear, so the instrument goes quiet exactly where it is being used. Today the choice is mostly binary: borrow European instruments wholesale, or rely on the small target-population GWAS alone.

We propose to make the choice per genomic region, using a rule borrowed from cellular networks. In networks that mix powerful distant towers with weak nearby small cells, a phone does not connect to the nearest station or to whichever looks strongest at this instant. It connects to the station with the highest average received power, meaning signal strength after the fast, random flicker of the channel has been averaged away. This is maximum average received power (MARP) association. The genetic analogue works as follows. For each region of the genome, we assign the instrument to whichever source cohort and marker gives the highest expected strength in the target population. That expectation is computed from region-level summaries of genetic architecture, not from the noisy single-variant z-score that currently drives selection. The aim is stronger, more stable, less biased instruments for non-European causal estimates, using summary statistics only.

Core Claim

Current cross-ancestry instrument selection behaves like "instantaneous max-SNR" association. It picks the variant with the most extreme observed statistic, usually in the largest (European) cohort. Two problems follow. First, the selection is driven by sampling noise, which is the winner's curse. Second, it ignores whether the marker still tags the causal variant in the target population.

The wireless literature shows why averaging matters. Matracia et al. (rural UAV networks; Coverage Analysis for UAV-Assisted Cellular Networks in Rural Areas) show that associating on long-term rather than instantaneous statistics avoids "ping-pong" switching between stations. Ben Salem et al. (hybrid terrestrial/LEO) show that an average-power rule correctly trades a satellite's high transmit power against its large path loss. The genetic counterpart of that trade-off is a large European sample against weaker cross-ancestry tagging. Neither wireless paper touches statistics. We use them only as the design principle.

The specific claim is this: a selection rule based on region-averaged expected target strength gives lower bias, better confidence-interval coverage, and more reproducible instrument sets than p-value selection. This should hold even when both rules feed the same downstream estimator and the same power-boosted target statistics.

For a genomic block $b$, a candidate marker $j$ and a source cohort $s$, define the expected target strength as

$$\bar P_t(j,s) = N_t \, \mathbb{E}\!\left[\beta_{t,j}^2 \,\middle|\, \hat\beta_{s,j},\ \hat h^2_{b,s},\ \hat h^2_{b,t},\ \hat\rho_b,\ r^2_{t}(j)\right].$$

The symbols are as follows:

  • $N_t$ is the target GWAS sample size.
  • $\beta_{t,j}$ is the true per-allele effect of marker $j$ on the exposure in the target population.
  • $\hat\beta_{s,j}$ is the source estimate.
  • $\hat h^2_{b,s}$ and $\hat h^2_{b,t}$ are the local heritabilities of block $b$ in source and target.
  • $\hat\rho_b$ is the local cross-ancestry genetic correlation.
  • $r^2_t(j)$ is how well $j$ tags its block's signal in target-population LD.

The block-level quantities pool many variants, so they play the role of the fading-averaged path loss. They shrink each single-variant estimate toward what the block's architecture supports. Each block is assigned to $\arg\max_{j,s} \bar P_t(j,s)$, subject to a minimum-strength threshold.

Research Program

The method has three pieces, and each reuses existing machinery.

Block-level summaries. The local heritability and co-heritability estimates come from LOG-TRAM (Xiao et al.). LOG-TRAM partitions the genome into 1-Mb windows, estimates local architecture by a closed-form method of moments, and borrows European power only where architecture is conserved. LOG-TRAM is used for association mapping and, by the authors' framing, covers two populations and one trait. We use its window estimates as inputs to an instrument-assignment rule. We extend that rule to more than two candidate sources by computing $\bar P_t$ separately for each source–target pair; this does not require a joint multi-population model.

Target-population LD. The target-population tagging term $r^2_t(j)$ comes from 1000 Genomes reference panels. The motivation is the evidence that shorter African LD blocks uncouple markers that are bound together in Europeans (Franceschini et al.; Ng et al.).

Estimation. Causal effects are estimated with target-population exposure and outcome statistics only, using inverse-variance weighting with HEIDI-style outlier removal as in GSMR (Zhu et al.). External cohorts therefore inform which instruments to use, never the effect sizes. This mirrors the separation between association and data transmission.

Optional coupled assignment. We also test a version in which neighbouring blocks compete for the same instruments. This happens when target-LD clumping would discard one of two chosen markers. Sun, Hong and Luo (Joint Downlink Base Station Association and Power Control) show that coupled association problems can become NP-hard but reduce to weighted bipartite matching on log-gains under restrictive conditions. We implement matching on $\log \bar P_t$ as an option and report whether it ever differs from the per-block greedy rule. We expect coupling to be weak, and if it is, we will say the matching layer is unnecessary.

Theory. We will bound the correlation between the selection score and the estimation noise. Block-level averaging should shrink this correlation roughly as one over the number of informative variants in the block, because each variant's noise contributes only its share to the pooled moment estimate. That correlation is what drives the winner's curse. MAGIC (Lyu et al.) corrects selection bias, including the "loser's curse," under the assumption of independent, non-overlapping GWAS. Our approach does not assume that independence. Instead it reduces the dependence between selection and estimation at the source.

Baselines

Naive reference. European instruments are selected at genome-wide significance in UK Biobank, clumped on European LD, and their effects estimated in the target GWAS. This is the current default and the "do nothing" point. The ICML 2026 representation-learning paper (Addressing Instrument-Outcome Confounding in MR) reports that standard raw-genotype two-stage least squares and MR-Egger show bias "up to 0.3" in a semi-synthetic All of Us design. That number is from their design, not ours, so we re-run the naive pipeline in every one of our settings.

Strongest competitor. The target GWAS is power-boosted with LOG-TRAM, then instruments are selected by the boosted p-value and estimated by inverse-variance weighting. It is the strongest competitor because it already borrows European power locally. LOG-TRAM reports a 49% average increase in effective sample size over Biobank Japan GWAS, and 842 novel lead SNPs across 29 traits (Xiao et al.). No reported result found on Lacuna for LOG-TRAM-based instrument selection in Mendelian randomization; we construct that pipeline ourselves.

Selection-correction competitor. This is MAGIC-style bias correction applied to p-value-selected instruments. Lyu et al. report coverage holding at 95% where two-step MR and multivariable MR fall to 70–80% in their simulations.

Fairness. All methods receive identical summary statistics, LD references, clumping windows and outcome estimator. Every tunable threshold gets the same grid search, scored on a held-out simulation seed and never on the evaluation data.

Ablations. Two ablations isolate the key ingredient. In the first, we replace the block-averaged expectation with the plug-in single-variant value $N_t \hat\beta_{s,j}^2 r^2_t(j)$; this is "instantaneous" assignment and isolates the averaging. In the second, we restrict to European-only sources with our rule, which isolates multi-source assignment.

What counts as beating. We beat the strongest competitor if we reduce root-mean-squared error and keep coverage within one point of nominal while it does not, across most simulation regimes.

Why not just…?

Why not just use LOG-TRAM-boosted target statistics with ordinary p-value selection? This is the real threat, because LOG-TRAM already encodes local cross-ancestry similarity. Our rule differs only in what decides selection. If boosted p-values are already a good proxy for expected target strength, the two will tie. That outcome is the decisive head-to-head below, and if they tie we will report that the averaging rule adds nothing.

Why not just split the sample, or apply MAGIC's correction? Splitting removes the winner's curse, but it halves an already small non-European sample. The documented power deficits in underrepresented cohorts (Agarwal et al.) make that costly. MAGIC's guarantees assume independent cohorts, which interconnected biobanks violate. We include both as baselines rather than dismiss them.

Why not just use the representation-learning estimator? It needs individual-level genotypes from several diverse environments and a hand-chosen latent dimension. Its authors note that the instrument can leak confounding if that dimension is too large. Our method needs only summary statistics. Where individual-level data exist, in the All of Us semi-synthetic setting, we run both. Our rule can also feed that estimator.

Proposed Experiments

Simulations. Genotypes are drawn from 1000 Genomes European, East Asian and African haplotypes. Source sample sizes are large (European) and target sizes small. We vary the local genetic correlation across blocks, from conserved to divergent, and plant region-specific pleiotropy. Metrics are:

  • bias, root-mean-squared error and 95% coverage of the causal effect;
  • mean first-stage F-statistic in the target;
  • instrument-set stability, measured as Jaccard overlap across bootstrap resamples of the summary statistics. This is our "ping-pong" measure.

Real-data positive controls. We use UK Biobank and Biobank Japan with BMI→type 2 diabetes and LDL→type 2 diabetes as positive controls. GSMR reports a 3.29-fold diabetes risk per standard deviation of BMI in Europeans, and a protective LDL effect.

First decisive check. We test whether predicted target strength $\bar P_t$ actually predicts realized instrument strength in the independent WeGene Chinese cohort, measured by rank correlation. A competing test asks whether boosted p-values predict it equally well.

Second decisive check. We run the head-to-head against LOG-TRAM plus p-value selection under divergent-architecture regimes. If our rule shows no gain in root-mean-squared error or stability there, the MARP analogy has no statistical payoff, and we will report that negative result.