Counting Independent Instruments Across Ancestries in Mendelian Randomization

Mendelian randomization (MR) uses genetic variants as natural experiments. A variant that raises, say, LDL cholesterol is treated like a randomly assigned dose, and its association with disease is read as a causal effect. The method breaks when a variant also affects the disease through some other route, a problem called horizontal pleiotropy. It also breaks when the variant is only a stand-in for the real causal mutation. This second case is common, because the variants a genome-wide association study (GWAS) reports are usually "tags": markers inherited together with the causal mutation through linkage disequilibrium (LD), the correlation between nearby variants created by shared ancestry. LD patterns differ between populations, so a tag that tracks the causal variant well in Europeans may track it poorly in East Asian or African cohorts. The field currently treats this as a nuisance that makes European-derived findings travel badly.

This note argues that the difference in LD across ancestries is also information. A borrowed tool makes the point concrete. Work on parameterized quantum circuits counts how many truly independent directions a set of parameters can move a circuit's output. It finds this number from the rank of a derivative matrix and removes parameters that add no new direction. Applied to genetics, the question becomes how many independent directions a set of candidate instruments spans within one LD block. In a single European sample, a causal variant and a nearby pleiotropic variant may collapse into one direction, which makes them statistically redundant and impossible to separate. Stacked together with an East Asian sample whose LD differs, they may span two directions. That extra dimension is exactly what is needed to tell an exposure-driven effect from a pleiotropic one. We propose a noise-calibrated, per-block rank analysis of multi-ancestry summary statistics. It selects a minimal instrument set that adds no redundant directions and uses the dimensions gained across ancestries to test the assumption that variants act on the outcome only through the exposure (the exclusion restriction). Everything runs on classical hardware. Only the mathematics comes from the quantum-circuit literature.

Core Claim

Consider one LD block with $p$ candidate SNPs. Let $R_a$ be the $p\times p$ LD correlation matrix in ancestry $a$, and let $n_a$ be the GWAS sample size. Let $\gamma$ be the vector of true per-variant effects on the exposure, and let $\alpha$ be the vector of per-variant pleiotropic effects on the outcome. Assume for now that both are shared across ancestries. The marginal summary statistics then behave approximately as

$$ \hat\gamma_a \approx R_a\gamma + \epsilon_a, \qquad \hat\Gamma_a \approx R_a(\beta\gamma + \alpha) + \eta_a, $$

where $\hat\gamma_a$ and $\hat\Gamma_a$ are the SNP–exposure and SNP–outcome associations, $\beta$ is the causal effect of interest, and $\epsilon_a,\eta_a$ are sampling noise with variance roughly $1/n_a$. Within one ancestry, the directions along which $R_a$ has near-zero eigenvalues are directions in which $\gamma$ and $\alpha$ cannot be distinguished. A pleiotropic variant in tight LD with the causal variant is invisible there. The pooled information matrix

$$ G = \sum_a n_a R_a $$

is the genetic analogue of the state-derivative overlap matrix whose eigenvalues Hartung et al. use to find redundant gates. Its effective rank, meaning the number of eigenvalues above a noise-calibrated threshold, counts how many variant-level effects the combined data can resolve in the block.

The claim has two parts. First, for loci where ancestries differ in LD, the effective rank of $G$ exceeds that of any single $n_a R_a$. Second, the gained directions support a direct test of pleiotropy: at the resolved variant level, the outcome effect should be proportional to the exposure effect, and variants that break this proportionality are flagged. Neither heuristic LD clumping nor single-ancestry full-LD modeling can do this, because both operate inside one population's rank-deficient geometry.

Where the Idea Comes From and How It Differs

The redundancy side supplies the method. Funcke et al. define a circuit parameter as redundant when adding it does not raise the rank of the Jacobian of the output with respect to the parameters. They also show that this redundancy is local: a circuit reduced at one parameter setting can lose expressivity elsewhere. Hartung et al. make the test practical under hardware noise by thresholding the eigenvalues of derivative overlaps, observing that truly independent parameters give distinctly larger eigenvalues.

We reuse three things: the rank-increment criterion for greedy instrument selection, the eigenvalue thresholding under noise, and the lesson about locality. The genetic analogue of locality is that redundancy is local to a population. A SNP that is dead weight in Europeans may carry an independent signal in East Asians. The quantum literature's "noise versus redundancy" ambiguity has a direct counterpart here. It arises from GWAS sampling error and, more seriously, from small ancestry-matched reference panels used to estimate $R_a$. The threshold must be calibrated to both.

We do not use quantum hardware. The corpus gives strong reasons not to. Gate-based feature selection in Quantum Feature Selection struggled with noise and convergence relative to the classical solver qbsolv. The gate-based causal testing design in A scalable quantum gate-based implementation for causal hypothesis testing needs over 6,000 qubits for a ten-variable graph. Pruning methods tied to circuit physics, such as the periodic-identity pruning of Quantum Neural Network Compression and the trajectory-based freezing of TITAN, exploit structure that has no genetic counterpart. We take only the rank geometry.

On the genetics side, three papers motivate the proposal and one constrains it. MR-LDP argues that clumping, which drops SNPs correlated with a lead SNP, throws away information. It instead models the full LD matrix from a reference panel with pleiotropy as a random effect. It remains single-population, however: it uses one panel's LD and cannot exploit differences between panels. GSMR maps 45 causal links from European data and removes pleiotropic outliers with its HEIDI filter. For example, removing 16 APOE-region SNPs made an apparent LDL–Alzheimer's association vanish. Its authors note that the European-only data constrain their conclusions. Zhang et al. run MR separately in European (UK Biobank, FinnGen) and East Asian (China Kadoorie Biobank, BioBank Japan) data and compare the results. That is the standard cross-ancestry practice: parallel replication, not joint geometry.

The constraining paper is LDAandLDAS. It shows that admixed genomes are mosaics of ancestral segments whose LD varies along chromosomes. A single $R_a$ per admixed cohort is therefore wrong, which is why we restrict the first program to relatively homogeneous European and East Asian cohorts. Finally, Invariant Ancestry Search shares our spirit of using several environments to find structure that is invariant across them. It searches over conditioning sets in a causal graph, however, rather than exploiting the linear geometry of variant correlations.

The Contradiction We Must Face

The shared-effect assumption, that $\gamma$ and $\alpha$ are the same in every ancestry, is exactly what the ancestry-bias literature warns against. That literature documents pleiotropic shifts and gene-by-environment effects that differ by population. If effects truly differ, the stacked system is misspecified, and a detected "pleiotropic" direction may simply be ancestry-specific effect heterogeneity.

We handle this in three ways. The model allows ancestry-specific deviations in $\gamma$ and $\alpha$ with a shrinkage prior, and we report the rank gain separately under shared and deviating effects. We also run a test that separates the two explanations. Pleiotropy predicts a non-proportional outcome effect for the same resolved variant in every ancestry. Heterogeneity predicts a proportional effect in each ancestry with a different slope. Loci where these two cannot be distinguished are reported as unresolved rather than forced into either category.

Research Program

The first component is the rank analysis itself. For each LD block around genome-wide significant loci for an exposure, we estimate $R_a$ from 1000 Genomes EUR and EAS panels, compute $G$, and choose an eigenvalue threshold. The threshold comes from a parametric bootstrap that resamples reference-panel individuals and adds GWAS-scale noise, so that the cutoff reflects the small size of the EAS reference panel.

We then build a minimal instrument basis greedily. A SNP enters only if it raises the thresholded rank of $G$ restricted to selected SNPs, which is the Funcke criterion applied to genetics. The output per block is the single-ancestry and stacked effective ranks, a minimal SNP set, and a resolved variant-level estimate of $\gamma$ and $\beta\gamma+\alpha$.

The second component is inference. We estimate $\beta$ by weighted regression of resolved outcome effects on resolved exposure effects, with a random-effect pleiotropy term as in MR-LDP. We also compute a per-block proportionality statistic restricted to the directions that exist only in the stacked system.

The third component is diagnostic. We characterize which loci gain rank, as a function of the eigenvalue gap between ancestries, so that users can predict in advance whether adding a non-European cohort will help a given exposure.

Baselines

The naive reference point is the standard pipeline. We clump SNPs at $r^2<0.001$ within each ancestry, run inverse-variance-weighted MR per ancestry, and combine the two estimates with a fixed-effects meta-analysis. This is what Zhang et al. effectively do when they report parallel estimates (depression on glaucoma, European OR 1.15, $p=0.20$; East Asian OR 1.38, $p=0.30$). It must be beaten because it is what practitioners run. Both it and our method receive identical summary statistics and reference panels.

The strongest existing competitor is MR-LDP. It already refuses to clump, models the full LD matrix, and treats pleiotropy as a random effect, so it isolates whether our gain comes from cross-ancestry geometry or merely from keeping correlated SNPs. We run it three ways: separately per ancestry with ancestry-matched panels, then meta-analyzed; and once on each ancestry's full data with the same candidate SNP set as ours. Its reported simulation result is a stable 5% type-I error rate, whereas IVW and MR-Egger were inflated. Its positive controls (Height–Height, CAD–CAD) gave estimates of 1 with narrower intervals than pruning-based methods; no numerical interval width is reported on Lacuna for those controls. Beating MR-LDP means matching its 5% type-I error while achieving higher power to detect injected pleiotropy near causal variants, and narrower intervals on positive controls with coverage held at nominal levels.

We also include GSMR with HEIDI outlier removal (GSMR), because it is the established pleiotropy filter. Its APOE result gives a real case where filtering changed the conclusion.

The key ablation keeps our entire estimator but replaces $G$ with a single ancestry's $n_aR_a$ scaled to the same total sample size. If the stacked version wins only because of more samples, this ablation will match it. If it wins because of complementary LD, it will not. A second ablation replaces rank-increment selection with random selection of the same number of SNPs, which tests whether the geometric criterion matters.

All methods share the same blocks, reference panels, and summary statistics. Tuning is limited to the threshold for our method and the published defaults for the others, each given an equal bootstrap-based calibration budget.

Why not just…?

Why not just clump and meta-analyze across ancestries? Clumping runs inside each population and discards exactly the correlated SNPs whose differing correlations across ancestries carry the separating signal. Meta-analysis then averages two estimates, each of which is already blind to nearby pleiotropy. The MR-LDP simulations already show that clumping-based IVW inflates false positives under pleiotropy. Our simulations inject a pleiotropic variant at controlled LD distances from the causal variant to measure how much of that inflation survives meta-analysis.

Why not just run MR-LDP in each ancestry? This is the real threat, because MR-LDP already uses the full LD structure. Its limitation is structural: within one ancestry, a pleiotropic variant in near-perfect LD with the causal variant lies in a near-null direction of $R_a$, so no single-population likelihood can separate them. Running it twice and comparing gives two blurred answers, not one sharp one. The same-sample-size ablation settles this. If per-ancestry MR-LDP matches us on pleiotropy detection at loci with large LD differences, the central claim fails and we will say so.

Why not just use LASSO to pick a sparse instrument set? Sparsity penalties choose among correlated SNPs somewhat arbitrarily, and they do so within whatever LD matrix they are given. Selection is therefore unstable exactly where the rank analysis says information is missing, and the penalty never reports which directions are unidentifiable. Quantum Feature Selection also found that linear-weight ranking missed dependency structure that a redundancy-aware objective caught. We include a cross-ancestry LASSO in the same pipeline as an additional comparison, scored on selection stability across bootstrap resamples.

Why not just fine-map each locus first? Fine-mapping aims at the same resolved variant effects, and multi-ancestry fine-mapping partly overlaps with our first component. The difference is that we couple resolution to the exposure–outcome proportionality test and report per block whether the gained dimensions exist at all. We treat a fine-mapping-then-MR pipeline as a legitimate competitor within the ablation study rather than claim it is dominated.

Proposed Experiments

The first experiment is a simulation. We build genotypes from 1000 Genomes EUR and EAS haplotypes, place a causal exposure variant and an optional pleiotropic variant at a range of LD distances, and generate summary statistics at UK Biobank-like and BioBank Japan-like sample sizes. The decisive check is a figure of pleiotropy-detection power against the difference in EUR and EAS LD between the two variants. Our method should rise with that difference, and the MR-LDP and same-sample-size ablations should stay flat. Type-I error must stay near 5% under the null for every method compared.

The second experiment uses real positive and negative controls. We run BMI on type-2 diabetes, where GSMR reports a 3.29-fold risk per SD of BMI in Europeans, as a strong positive control. We compare interval width and cross-ancestry agreement. We run the psychiatric exposures on glaucoma from Zhang et al. as a negative control, where the method must not create signal. We also run exposure-on-itself controls analogous to MR-LDP's Height–Height test, where the estimate must be 1.

The third experiment is a pleiotropy case study. For LDL cholesterol and Alzheimer's disease, conditional on East Asian summary data being available, we ask whether the stacked rank analysis flags the APOE directions without HEIDI's outlier rule. If no suitable East Asian data exist, we report that as a limitation rather than substituting an unrelated trait.

We report per-block effective ranks, how often the stacked rank exceeds the single-ancestry rank, and the calibration of the eigenvalue threshold against reference-panel size. The proposal succeeds only if gains concentrate where LD differs and vanish where it does not. That pattern is the signature that separates a real geometric effect from a sample-size artifact.