Seeded Instruments: Lowering the Diversity Needed for Ancestry-Robust Mendelian Randomization

Mendelian randomization (MR) uses genetic variants as natural experiments to ask whether an exposure, such as a blood biomarker, causes a disease. It breaks when the variants are also tied to ancestry, and ancestry is also tied to the disease. A recent method trains an autoencoder, a network that compresses and reconstructs its input, to split each genotype into two parts. One part is meant to act the same way in every population and serves as a clean instrument. The other part carries population-specific confounding. The method only works when the training populations are "different enough" to reveal the split, and that condition is least likely to hold in the smaller, less diverse cohorts where fixing ancestry bias matters most.

We borrow one idea from metallurgy. Foundries do not refine grain structure by adding more bulk material. They add a trace amount of foreign seed particles, which lowers the energy barrier for crystals to start forming. We propose the statistical analogue: seed the instrument side of the autoencoder with a small amount of biological prior knowledge about which variants are likely functional. The testable claim is that seeding lowers the population diversity needed before the learned instrument becomes unbiased. Pure analogy is not the point. The proposal lives or dies on whether the bias-versus-diversity curve actually shifts.

Core Claim

Addressing Instrument-Outcome Confounding in Mendelian Randomization through Representation Learning supplies the base method. It splits genotypes into an invariant instrument $\hat W$ and a population-variant part $\hat V$ using two penalties:

  • Maximum Mean Discrepancy (MMD) penalizes differences in the distribution of $\hat W$ across ancestry groups ("environments").
  • The Hilbert-Schmidt Independence Criterion (HSIC) penalizes dependence between $\hat W$ and $\hat V$.

In semi-synthetic All of Us experiments at the GLP1R locus, standard two-stage least squares (2SLS) and MR-Egger show bias "up to 0.3", and the method reduces this to "near zero". The paper also states its own limit: environments must differ enough to identify the split. We treat that limit as a barrier and ask whether a seed lowers it.

Define the environment divergence $D$ as the MMD between the genotype distributions of the training environments. Define the diversity threshold $D^*_\varepsilon$ as the smallest $D$ at which the absolute bias of the causal estimate falls below a tolerance $\varepsilon$. Our central prediction is

$$ D^*_\varepsilon(\text{seeded}) < D^*_\varepsilon(\text{unseeded}), $$

with little loss in the high-divergence regime where the unseeded method already works. The mechanism is plain. When environments barely differ, many different $\hat W/\hat V$ splits satisfy the invariance and independence penalties about equally well. A prior that favors functionally plausible variants breaks that tie in the biologically sensible direction.

Why the Metallurgy Matters Here

The materials literature shapes the design in three concrete ways.

First, it distinguishes two kinds of seed.

We map these onto two genetic priors.

Second, the cladding work that sweeps CeO₂ from 0 to 1.0 wt.% (The Effects of CeO2 Content on the Microstructure and Property of Duplex Stainless Steel Layer Obtained by Plasma Arc Cladding Technology) treats seed loading as a dose. The field also reports that excess particles clump together and start cracks rather than refine grains. That tells us to expect a non-monotone dose-response: too strong a prior should override the data and reintroduce bias whenever the annotations are wrong.

Third, Hierarchical nucleation in deep neural networks shows that class structure in deep networks appears abruptly rather than gradually. It measures this with neighborhood overlap, which asks how often a point's nearest neighbours share its label. In ResNet152 this overlap stays near 0.10 up to layer 142, then jumps to 0.72 within nine layers. We reuse the overlap measure as a training diagnostic. We track the overlap of $\hat W$ with ancestry labels across training, where it should collapse, and its overlap with exposure-relevant variant clusters, where it should rise. We then test whether seeding moves the transition earlier. This is a secondary, descriptive aim. The bias threshold remains the primary claim.

Research Program

The model keeps the base method's architecture and adds one seed term:

$$ \mathcal L = \mathcal L_{\text{rec}} + \lambda_1\,\mathrm{MMD}(\hat W) + \lambda_2\,\mathrm{HSIC}(\hat W,\hat V) + \lambda_3 \sum_j (1-s_j)\,\lVert A_{\cdot j}\rVert_2 . $$

The terms are:

  • $\mathcal L_{\text{rec}}$ is the genotype reconstruction error.
  • $\mathrm{MMD}(\hat W)$ is the cross-environment discrepancy of the instrument part.
  • $\mathrm{HSIC}(\hat W,\hat V)$ is the dependence between the two parts.
  • $A_{\cdot j}$ is the column of first-layer weights connecting variant $j$ to the instrument branch.
  • $s_j\in[0,1]$ is that variant's seed score.

The last term makes it cheap for the instrument branch to use high-scoring variants and expensive to use low-scoring ones. It mirrors how PRISM lowers the regression penalty for biologically aligned variants. $\lambda_3$ is the seed dose. The estimate is then the partialling-out 2SLS from the base paper, with $\hat V$ entered as a covariate.

We build three seed variants: exogenous (annotation-based $s_j$), endogenous (ancestry-matched fine-mapping $s_j$), and a shuffled-seed control. The shuffled control permutes $s_j$ across variants within the locus, which preserves the distribution of scores and destroys their biological meaning. For each variant we trace the full bias-versus-$D$ curve.

Baselines

The naive reference is raw-genotype 2SLS with the top genetic principal components as covariates, run alongside MR-Egger. The base paper reports bias up to 0.3 for this family in the All of Us GLP1R setup. We re-run it on our splits so every method sees the same data.

The strongest existing competitor is the unseeded invariant autoencoder from the base paper, which is the same model with $\lambda_3=0$. It is the only method in the file shown to remove instrument-outcome confounding. For a fair comparison it gets the same architecture, the same environments, and the same hyperparameter search budget over $\lambda_1$ and $\lambda_2$. Seeded models get that budget plus a search over $\lambda_3$ drawn from the same total number of trials. The unseeded model's exact bias numbers are not given in the file; the paper reports only "near zero" in the high-divergence setting. Beating it means a lower $D^*_\varepsilon$, with non-overlapping bootstrap intervals over simulation replicates, and no worse bias or variance at high $D$.

Two summary-level methods test whether pleiotropy filtering alone suffices. The first is GSMR with the HEIDI-outlier filter (Causal associations between risk factors and common diseases inferred from GWAS summary data), which multi-SNP-averages instruments and removes pleiotropic outliers; it removed 16 APOE SNPs that were producing a spurious LDL-Alzheimer's association. The second is PMR-Egger (Testing and controlling for horizontal pleiotropy with probabilistic Mendelian randomization in transcriptome-wide association studies), a joint likelihood model that handles correlated instruments. Both assume linear, uniform pleiotropy, which our simulated stratification violates.

The key ablations are the shuffled-seed control and the "seed without autoencoder" baseline described below. The shuffled control isolates whether the benefit comes from biological content or from mere sparsity regularization.

Why not just…?

Why not just use fine-mapped or functional variants directly as instruments in PC-adjusted 2SLS? This is the real threat. The prostate-cancer and PRISM results show that selecting seed variants alone already improves cross-ancestry prediction. If instrument-outcome confounding sits on a different axis from functionality, selection alone would suffice and the autoencoder would add nothing. Our simulations therefore include two regimes. In one, confounding enters through allele-frequency gradients at non-functional tagging variants, where selection alone should work. In the other, confounding runs through the functional variants themselves because their frequency tracks ancestry, where selection cannot help and disentanglement is needed. If selected-variant 2SLS matches the seeded autoencoder in both regimes, we will report that the simpler method is the answer.

Why not just add more principal components or local-ancestry covariates? The base paper shows linear adjustment leaves bias up to 0.3 when confounding enters non-linearly through local linkage disequilibrium. We still include 2SLS with 20 principal components plus local ancestry at the locus, because local ancestry is not tested in the file and may close part of the gap.

Why not just collect more diverse environments for the unseeded autoencoder? When diverse data exist, that is the right answer. The claim here is conditional on limited diversity, and the bias-versus-$D$ curve shows directly how much extra divergence the seed substitutes for. Evaluating Multi-Ancestry Genome-Wide Association Methods shows that pooling diverse individuals raises power substantially. That work is about association discovery, not confounding removal, so it does not settle this question.

Why not just weight instruments by PRISM scores in a standard MR estimator? This is annotation-weighted 2SLS, and we run it as a baseline. It reweights variants but cannot separate a functional variant's causal signal from the ancestry signal it also carries. That separation is exactly what the second simulation regime tests.

Proposed Experiments

The primary benchmark is simulation with HAPGEN2 and Admix-kit genotypes. In these simulations we control:

  • the difference in admixture fraction between environments, which sets $D$;
  • the confounding strength;
  • whether the true causal variants carry high seed scores;
  • annotation accuracy, by corrupting a fraction of $s_j$.

The main result is the bias-versus-$D$ curve for each method, together with coverage of 95% intervals and mean squared error. The second experiment reproduces the semi-synthetic All of Us GLP1R setup with East Asian- and African-ancestry individuals. We subsample ancestry composition to sweep $D$ downward from the published configuration.

Three checks are decisive. First, the seeded curve must sit left of the unseeded curve, and the shuffled-seed curve must not. Second, the dose-response in $\lambda_3$ must show the predicted over-seeding penalty when annotations are corrupted. If it does not, the prior is acting as a hard filter rather than a seed, and selected-variant 2SLS becomes the fairer comparison. Third, the neighborhood-overlap diagnostic should track bias in the simulations, which would make it usable as a label-free model-selection signal.

As an exploratory application, we would re-estimate the European-derived FGF23–aortic stenosis effect (Genetic association of serum calcium, phosphate, vitamin D, parathyroid hormone, and FGF23 with the risk of aortic stenosis, OR 3.081 discovery and 2.280 replication) in non-European All of Us participants, reporting agreement across methods rather than claiming ground truth.