Mendelian randomization (MR) uses inherited genetic variants as natural experiments. A variant that raises someone's body mass index at conception, and affects disease only through that change, lets us estimate the causal effect of body mass index on disease without a randomized trial. Two assumptions make most MR fragile outside European cohorts. First, the effect is assumed to be a straight line. Second, the variants that serve as instruments were found in European genomes, where their correlation with the true causal mutations can be very different from other populations. We propose to separate these two problems. The causal curve from exposure to outcome is plausibly biology shared across human populations. The link from genotype to exposure is where ancestry actually differs, through linkage disequilibrium (the population-specific pattern of which variants are inherited together). The proposal fits one shared nonlinear causal curve across ancestries, lets the genotype-to-exposure stage be ancestry-specific, and then tests whether the curve itself needs ancestry-specific adjustment.
The mechanism that makes both the curve and the test compact is a trainable rational activation. This is a nonlinearity written as a ratio of two low-degree polynomials whose coefficients are learned. A handful of such coefficients can represent thresholds, plateaus and U-shapes that ordinary polynomials fit poorly. Ancestry-specific effect modification then becomes a small, interpretable change to those coefficients, rather than a separate model per population that small non-European cohorts cannot support. In two sentences, the claim is this: estimate the causal dose–response once, borrowing strength from large European data, while re-learning only the population-specific instrument stage. Then ask, with a few extra shape parameters, whether the curve really differs across ancestries.
Core Claim
We claim that a nonlinear instrumental-variable estimator will recover the causal dose–response curve in small non-European cohorts more accurately than either stratified per-ancestry analysis or naive transport of European estimates. The estimator has three parts: ancestry-specific first-stage features learned from genotypes, a second-stage causal function shared across ancestries, and ancestry-specific deviations confined to the rational coefficients of that second stage. We further claim that the size of the fitted coefficient deviation is a usable test of whether an apparent cross-ancestry discrepancy is genuine effect modification or an artifact of instrument decay. The first claim is about estimation. The second is about separating biology from linkage disequilibrium.
Concretely, for individual $i$ in ancestry group $a$, with genotype instruments $Z_i$, exposure $X_i$ and outcome $Y_i$, we estimate
$$\mathbb{E}\left[\,Y_i - h(X_i;\ \theta + \delta_a)\ \middle|\ Z_i,\ A_i = a\,\right] = 0,$$
where $h$ is a small network whose weights $\theta$ are shared across ancestries. The deviation $\delta_a$ is nonzero only on the numerator and denominator coefficients of its rational activations, and it is shrunk toward zero with a penalty $\lambda\sum_a\lVert\delta_a\rVert^2$. The conditional expectation is estimated with the two-stage feature method described below, using a first-stage feature map $\psi_a(Z)$ that is fit separately per ancestry. Setting $\delta_a = 0$ gives the fully portable model. Letting all of $\theta$ vary by ancestry gives the fully stratified one. Our model sits between them with a few dozen extra parameters per group.
What the Prior Work Supplies and What It Leaves Open
The estimation machinery comes from deep feature instrumental-variable regression. Learning Deep Features in Instrumental Variable Regression (DFIV) learns neural features of both instrument and treatment and solves the two stages in closed form with ridge regression. It beats kernel IV and DeepIV on econometric demand simulations, dSprites and off-policy benchmarks. Optimality and Adaptivity of Deep Neural Features for Instrumental Variable Regression proves that such estimators reach minimax rates over Besov spaces. These are function classes with locally varying smoothness, which is exactly where threshold-like biology lives. It also proves they strictly separate from any linear estimator. Both papers use fixed smooth activations, never touch genetics, and have no notion of multiple populations. We reuse DFIV's two-stage structure. We change the second stage and add the cross-population sharing structure, which is the actual contribution.
The shape family comes from the rational-activation literature. Rational neural networks shows that rational networks need only doubly-logarithmic depth where ReLU networks need logarithmic depth, and gives pole-free initializations. Padé Activation Units supplies the safe form $P(x)/(1+|Q(x)|)$, which cannot blow up on the real line. Rational Neural Networks have Expressivity Advantages proves a parameter-count separation against smooth fixed activations and shows the learned shapes drift toward gated, non-monotone profiles.
The idea of adapting only the activation comes from parameter-efficient tuning. Don't Forget the Nonlinearity (NoRA) freezes weights and tunes rational coefficients, matching full fine-tuning at 0.4% of parameters. Adaptable Adapters reports a low-data GLUE average of 51.28 against 44.87 for a standard adapter with 100 training examples. Those works use activation tuning for predictive transfer in language and vision. We use it for a different purpose: as a structured hypothesis about which part of a causal model is allowed to differ between populations. This matters because a predictive gain says nothing about whether the adapted parameters mean anything. Here they are meant to be read as effect modification.
The motivation comes from genetics. Polygenic risk score portability for common diseases across genetically diverse populations finds that European-trained scores retain only 39.4% of their performance in Africans, 46.6% in East Asians and 51.3% in South Asians. That is direct evidence that the genotype-to-trait stage does not transport. GSMR is the standard summary-data linear MR. Its authors concede that linearity oversimplifies biology at extreme exposures. Its HEIDI-outlier filter removed 16 APOE-region SNPs to eliminate an association. That is the kind of pruning that could also discard valid instruments probing a nonlinear region of the curve. MR-Path shows that instruments cluster into distinct causal mechanisms, for example HDL-C on coronary disease with cluster means near −0.343 and +0.14. However, it models each cluster as linear and does not consider ancestry. The glaucoma study in Mendelian randomization study shows no causal relationship between psychiatric disorders and glaucoma in European and East Asian populations is the typical cross-ancestry design: separate linear analyses per population, compared by eye. Our proposal replaces "compare by eye" with a joint model and an explicit test.
Research Program
The first component is the estimator itself. The first stage maps a panel of candidate instrument SNPs, plus ancestry principal components, to features $\psi_a(Z)$. It is trained per ancestry group, or for admixed individuals as a function of continuous ancestry proportions estimated with Neural ADMIXTURE. Letting it differ is how linkage-disequilibrium mismatch gets absorbed. The second stage $h$ is a narrow network over one exposure, or over a small joint exposure such as LDL, HDL and triglycerides together. It uses safe rational activations of type (3,2) with Zolotarev-style initialization, and it is fit on the pooled data through the shared $\theta$. The group deviations $\delta_a$ are fit with a shrinkage penalty whose strength is chosen by held-out moment-violation loss within each ancestry. The multi-exposure case is where a network is actually needed. For a single exposure, $h$ collapses to essentially one rational function, and we treat that case as a stress test against simpler curve families rather than as the showcase.
The second component is the discrepancy test. We compare three fitted models on held-out target-ancestry data: shared curve, shared curve with rational deviations, and fully stratified curve. From this we form a likelihood-ratio-style statistic on the IV moment loss. We calibrate it by a permutation that shuffles ancestry labels within strata of instrument strength. The interpretive claim to be tested is specific. When a cross-ancestry discrepancy comes from instrument decay, it should be absorbed by $\psi_a$ and leave $\delta_a \approx 0$. When it comes from a real shift in the causal curve, such as a threshold moved to a different exposure value, $\delta_a$ should be nonzero and localized.
The third component is diagnostics for the known fragilities. Rational coefficients can stall in flat regimes, so we track denominator minima and coefficient trajectories across seeds. We also avoid group normalization in $h$, given the degradation reported in Rational Neural Networks have Expressivity Advantages.
Baselines
The naive reference point is linear two-stage least squares and inverse-variance-weighted MR run separately in each ancestry, alongside the European linear estimate transported unchanged to other groups. This is what the glaucoma study and most cross-ancestry MR do. Both variants use the same instrument panel and the same covariates. Beating it means lower integrated squared error of the recovered causal curve in the target ancestry, and correct detection of nonlinearity where the ground truth is nonlinear.
The strongest established linear method is GSMR, run on summary statistics computed from the same individuals, with ancestry-matched linkage-disequilibrium reference matrices and HEIDI-outlier filtering. The reported anchor for the real-data exposure we study is the GSMR estimate that one standard deviation of BMI corresponds to a 3.29-fold increase in type-2 diabetes risk (GSMR), in European data. On real data we do not claim to "beat" this number. We check that our averaged slope in Europeans is consistent with it, and we report where along the exposure range the local slope departs from it.
The strongest nonlinear competitor is DFIV with its original fixed activations, and additionally with GELU. It is run both pooled and stratified, with parameter count, training epochs and hyperparameter search budget matched to our model. We use identical first-stage networks so that only the second stage differs. There is no reported result found on Lacuna for DFIV on genetic or ancestry-stratified data, so this comparison is new ground and must be run by us. Beating it means lower target-ancestry curve error at matched parameters, with the margin growing as the target cohort shrinks.
The key ablations isolate the two ingredients. Replacing the rational activations with fixed ones, while keeping the sharing structure and allowing ancestry-specific output scale and shift, tests whether rationals matter. Replacing the ancestry-specific coefficient deviations with ancestry-specific LoRA-style low-rank weight updates of equal parameter count tests whether deviations should live in the activation. The fully pooled model ($\delta_a=0$) and the fully stratified model bracket the design.
Why not just…?
Why not just run linear MR separately in each ancestry, as the glaucoma study does? Stratified linear MR is honest about ancestry but answers a narrower question. It returns one population-average slope per group, and slopes from different groups are not comparable when the curve is nonlinear and the exposure distributions differ. A population with higher average BMI will show a steeper linear slope under a convex curve, even with identical biology. The semi-synthetic experiments below construct exactly this case: shared curve, shifted exposure distributions. We will show whether stratified linear MR falsely reports ancestry heterogeneity there while the joint model does not.
Why not just use DFIV with a wider GELU or ReLU network? This is a fair threat. Fixed activations are universal approximators, and the rational advantage is proven asymptotically (Rational neural networks, Rational Neural Networks have Expressivity Advantages). It has been demonstrated on vision, control and partial differential equations, not on noisy causal curves estimated from weak instruments. Our argument is not raw accuracy on European data. It is that the ancestry-specific part of the model must be tiny to be estimable from a few thousand people. With fixed activations there is no small, shape-changing parameter set to make ancestry-specific; one can only shift or scale. The parameter-matched fixed-activation ablation settles this. If it matches rational deviations in target-ancestry error and in discrepancy detection, we will report that the sharing structure, not the activation family, carries the result.
Why not just fit a spline or fractional polynomial curve with ancestry interaction terms? For a single exposure this is the most serious alternative, and it may work as well. A cubic spline with a few knots and ancestry-by-basis interactions is a transparent competitor with the same "shared curve plus small deviation" logic. We therefore run it as a first-class baseline with degrees of freedom matched to the rational model. We expect rationals to help only where the truth has a sharp threshold or plateau whose location differs by ancestry, since fixed knots cannot move with it, and in the joint multi-exposure setting, where tensor-product splines grow combinatorially. If splines match rationals on single-exposure curves, the paper's claim narrows to the multi-exposure regime and to the sharing design. We state that in advance.
Why not just fine-tune the whole European model, or apply LoRA, on the target cohort? Full fine-tuning on a few thousand target individuals risks overfitting a weak-instrument problem, and it leaves no interpretable record of what changed. LoRA on the second stage is included as an equal-parameter ablation, so the comparison is direct. The evidence that activation-only tuning is competitive in low-data regimes (Adaptable Adapters, Don't Forget the Nonlinearity) comes from language and vision, so it motivates the choice but does not settle it here.
Proposed Experiments
The decisive experiments are semi-synthetic, because real cross-ancestry causal curves have no ground truth. We take real UK Biobank genotypes using the ancestry subsets studied in Polygenic risk score portability for common diseases across genetically diverse populations. That study used 285,000 European individuals for training and 18,000 African, East Asian, South Asian and European individuals for testing, and the real genotypes preserve real linkage-disequilibrium differences. On top of them we simulate a causal SNP set, a tag-SNP instrument panel chosen in Europeans, exposures with unmeasured confounding, and outcomes under known curves.
The simulated curves include linear, saturating, threshold, U-shaped, and threshold-shifted-by-ancestry cases, together with injected horizontal pleiotropy in a subset of variants. We vary the target-ancestry sample size from a few hundred to the full available subset, and we vary instrument strength. Primary metrics are integrated squared error of the recovered curve over the target ancestry's exposure range, error of local slopes at exposure deciles, and bootstrap coverage. For the discrepancy test, we measure false-positive rate on "shared curve, decayed instruments" worlds and power on "shifted curve" worlds. The pre-registered success criterion has two parts. The shared-plus-deviation rational model must beat both stratified DFIV and transported European DFIV in target-ancestry curve error at small target sizes. Its test must keep nominal false-positive rate when only linkage disequilibrium differs, where stratified linear MR is expected to fail.
A secondary synthetic check targets the confusion flagged by GSMR's pruning. Under a saturating curve, we record how many valid instruments HEIDI-outlier removes, and whether our model recovers the plateau using them.
On real data, we apply the method to BMI and type-2 diabetes and to a joint lipid panel and coronary disease, within UK Biobank ancestry subsets. We compare averaged European slopes against the reported GSMR BMI–diabetes estimate, and we compare mechanism structure against MR-Path's two HDL clusters. In the real-data analyses we report whether fitted ancestry deviations are distinguishable from zero after the permutation calibration. We treat the real-data analyses as descriptive, and we will say plainly if non-European sample sizes leave the deviations unidentifiable.
References
- Learning Deep Features in Instrumental Variable Regression
- Optimality and Adaptivity of Deep Neural Features for Instrumental Variable Regression
- Rational neural networks
- Padé Activation Units: End-to-end Learning of Flexible Activation Functions in Deep Networks
- Rational Neural Networks have Expressivity Advantages
- Don't Forget the Nonlinearity: Unlocking Activation Functions in Efficient Fine-Tuning
- Adaptable Adapters
- Polygenic risk score portability for common diseases across genetically diverse populations
- Causal associations between risk factors and common diseases inferred from GWAS summary data
- A latent mixture model for heterogeneous causal mechanisms in Mendelian randomization
- Mendelian randomization study shows no causal relationship between psychiatric disorders and glaucoma in European and East Asian populations
- Neural ADMIXTURE for rapid genomic clustering