Borrowing Proximal Bridge Functions Across Ancestries

Observational health records hold millions of treatment decisions, but the patients who received a drug usually differ from those who did not in ways nobody recorded, such as how sick they were before or how often they seek care. Proximal causal inference is a family of methods that corrects for such hidden differences using two kinds of imperfect "proxy" measurements of them. Its main weakness is sample size. The correction requires solving an unstable inverse problem, and estimates become extremely noisy when data are scarce. In genomics-linked biobanks, scarce data is the norm for exactly the groups whose results are least known: non-European ancestry subgroups often number in the hundreds or low thousands, while the European subgroup numbers in the hundreds of thousands.

We propose to estimate a causal effect in a small ancestry group by borrowing only the confounding-correction machinery from the large group, never the effect itself. In proximal inference that machinery is a pair of "bridge functions," learned maps from proxies to outcomes and to treatment. We fit each bridge in the large cohort, learn a penalized correction to it from the small cohort, and plug both into an estimator with a built-in bias correction. Mistakes in what is borrowed then enter the final estimate only as a product of two small errors. We also supply a test of whether the borrowed bridge is valid in the target ancestry. That test checks restrictions that can be observed, unlike the completeness assumptions of proximal inference, which are untestable. The result is a way to report ancestry-specific causal effects with honest confidence intervals at sample sizes where current proximal estimators are unusable. It also separates apparent cross-ancestry differences into a part explained by different population makeup and a part explained by a genuine change in confounding structure.

Core Claim

Proximal identification works as follows. Let $Y$ be the outcome, $A$ the treatment, and $X$ the measured covariates. Let $W$ be outcome-side proxies (related to the hidden confounder and the outcome, but not causing treatment) and $Z$ treatment-side proxies (related to the hidden confounder and treatment, but not directly affecting the outcome). An outcome bridge $h$ solves $\mathbb{E}[Y\mid A,Z,X]=\mathbb{E}[h(W,A,X)\mid A,Z,X]$, and averaging $h(W,a,X)$ gives the mean outcome under treatment $a$, as formalized in Semiparametric Proximal Causal Inference. That paper also derives the proximal doubly robust estimator. This estimator pairs $h$ with a treatment bridge $q$, a proxy-based analogue of inverse propensity weights, and remains consistent if either bridge is right.

Our claim is that in a small target ancestry $t$, the binding constraint is the variance of solving for the bridges, not bias. A large source ancestry $s$ can therefore cut that variance even when its bridges are only approximately right. We write

$$h_t = h_s + \delta_h,\qquad q_t = q_s + \delta_q,$$

where $h_s, q_s$ are fit on the source cohort and the corrections $\delta_h,\delta_q$ are fit on the target cohort under a penalty that shrinks them toward zero. The target effect is then estimated only on target individuals:

$$\hat\psi_t(a)=\frac{1}{n_t}\sum_{i\in t}\Big[\mathbf{1}\{A_i=a\}\,\hat q_t(Z_i,a,X_i)\big(Y_i-\hat h_t(W_i,a,X_i)\big)+\hat h_t(W_i,a,X_i)\Big].$$

Here $n_t$ is the target sample size, and $\hat h_t,\hat q_t$ are cross-fitted, meaning each is estimated on folds that exclude individual $i$. Because this estimator has the Neyman-orthogonal form of the efficient influence function from Pu et al., its bias is bounded by the product of the errors in $\hat h_t$ and $\hat q_t$. That bound is what lets an imperfect borrowed bridge help: a moderately wrong $h_s$ costs second-order bias but can remove first-order variance. The estimand is never pooled across ancestries.

Relation to Prior Work

The motivation comes from two places. On the genetics side, Leveraging the local genetic structure for trans-ancestry association mapping (LOG-TRAM) borrows power from UK Biobank into Biobank Japan only in genome regions where architectures agree, reporting a 49% average gain in effective sample size. It is purely associational and has no confounding bridge. Estimating Trans-Ancestry Genetic Correlation with Unbalanced Data Resources similarly transfers European-estimated weights into small cohorts with error correction, but its target is genetic correlation rather than a treatment effect. We take from both the principle of borrowing structure where it is concordant and checking concordance locally. We apply that principle to the nuisance functions of a causal estimator.

On the causal side, Heterogeneous associations between interleukin-6 receptor variants and phenotypes across ancestries (hetFDR) finds many ancestry-heterogeneous associations in the Million Veteran Program but cannot say whether they reflect biology, proxy attenuation, or confounding. Causal associations between risk factors and common diseases inferred from GWAS summary data states plainly that its 45 causal links are untested outside Europeans. Our decomposition step addresses exactly that ambiguity, though for observational exposures rather than genetic instruments.

The methods we reuse are the doubly robust estimator of Pu et al.; the kernel bridge estimators of Proximal Causal Learning with Kernels, whose single-stage moment-restriction objective we adapt into the transportability test; and the orthogonal pseudo-outcome construction of the P-learner in Proximal Causal Learning of Conditional Average Treatment Effects. All three assume one sample from one population with enough data to solve the bridge equations. That is precisely the assumption that fails here.

Two works constrain the design. Demystifying Proximal Causal Inference shows that weak proxies make bridge estimation ill-posed. Borrowing cannot rescue a target in which the proxies are weak for that group, so we must measure proxy strength per ancestry rather than assume it. Robust Mendelian randomization in the presence of residual population stratification, batch effects and horizontal pleiotropy shows that at biobank scale, tiny assumption violations become highly significant false findings. Any small bias in the source bridge will be estimated very precisely and transferred confidently, so the target-side correction and test are essential rather than optional. Finally, On Multi-Cause Approaches to Causal Inference with Unobserved Counfounding rules out the shortcut of pooling many observational associations without structural assumptions. We keep the explicit dual-proxy structure for that reason.

Research Program

The first component is the estimator. Source bridges are fit with scalable approximations, either random-feature or Nyström kernels or flexible sieves, because exact kernel methods scale cubically, as the P-learner paper notes. Target corrections are small-sample kernel problems where exact solutions are cheap. The penalty on $\delta_h,\delta_q$ is selected by the target's own held-out moment violation rather than by source fit. A target that disagrees with the source therefore automatically drifts toward the target-only solution.

The second component is a transportability test. The source outcome bridge is a valid target bridge if and only if $\mathbb{E}[(Y-h_s(W,A,X))\,g(A,Z,X)\mid S=t]=0$ for all test functions $g$. We evaluate the largest such moment over a kernel ball, in the spirit of the moment-restriction estimator of Mastouri et al., and calibrate it by bootstrap on target data. This is a testable restriction, unlike completeness. An analogous test applies to $q_s$.

The third component is a three-way decomposition of the gap between the source effect and the target effect:

  1. The composition part is the change obtained by averaging the unchanged source bridge over the target's distribution of $(W,X)$.
  2. The confounding-structure part is the contribution of $\delta_h$.
  3. The residual part is genuine effect difference given both of the above.

Alongside this, we report a per-ancestry proxy-strength diagnostic: the estimated smallest singular value of the conditional-expectation operator linking $W$ to $Z$. This flags targets where the proxies themselves have weakened. It is the observational analogue of a European tag SNP losing linkage in African genomes.

The theory is a finite-sample error bound. It should show that the variance gain over target-only estimation scales with how small $\delta_h,\delta_q$ are relative to the target's ill-posedness. It should also show that coverage is preserved as long as the product of correction errors shrinks faster than $n_t^{-1/2}$, the usual rate condition for orthogonal estimators.

Baselines

The naive reference is the unadjusted target-only regression of $Y$ on $A$ and $X$, ignoring hidden confounding. The second naive reference simply reports the European proximal estimate for the target group. Together these bracket "do nothing" and "assume generalizability." Both run on the same target samples and are beaten if our estimator has lower root-mean-squared error with nominal coverage.

The most important competitor is target-only proximal doubly robust estimation, following Semiparametric Proximal Causal Inference. It is unbiased under the target's own assumptions and is exactly what an analyst would run today. It uses the same kernel families, the same cross-fitting, and the same hyperparameter search budget as our target-side step. Pu et al. report that in simulation it "maintained low bias (e.g., absolute bias of 0.1), whereas non-robust versions and standard estimators ignoring hidden confounding showed severe bias (up to 64.0)". On small target subsamples we expect its weakness to be variance and interval width, not bias. Beating it means equal coverage with materially narrower intervals. We will report the variance ratio as an effective-sample-size multiplier, with LOG-TRAM's 49% associational gain as a rough reference scale.

For heterogeneous effects, the strongest existing method is the P-learner of Proximal Causal Learning of Conditional Average Treatment Effects. It reports a simulated mean squared error of 0.06 against 0.521 for causal forests and 0.049 for an oracle. We run it target-only and with our borrowed bridges, using identical second-stage regressors. No reported result was found on Lacuna for any proximal estimator under a large-source, small-target design. The comparison therefore has to be created here.

Pooling estimates is a further competitor: a fixed-effects meta-analysis combining the target-only and source estimates. It represents what LOG-TRAM-style borrowing would give if applied naively at the effect level.

Two ablations isolate the key ingredients. The first is pooled-with-ancestry-interactions. It fits a single bridge on both cohorts with an ancestry indicator and penalized ancestry-by-proxy interactions, then plugs it into the target-only outcome-bridge estimator without the $q$-weighted correction term. This keeps the borrowing and removes the orthogonality. If it matches our estimator on coverage under shifted bridges, the orthogonal construction is not earning its place. The second ablation is the full method without the target-moment penalty selection, using a fixed shrinkage strength. It tests whether adaptivity is what protects coverage when the source bridge is wrong.

Why not just…?

Why not just run proximal estimation in the target ancestry alone? It is the honest default, and at target sizes in the tens of thousands it may suffice. The weak-proxy analysis in Demystifying Proximal Causal Inference implies that at hundreds to low thousands, the bridge solutions become unstable and intervals become uninformative. Our subsampling experiment measures where that happens. If target-only intervals are already tight at the sizes typical of underrepresented cohorts, the proposal's value shrinks to the decomposition and the test, and we will say so.

Why not just pool all ancestries with ancestry indicators, or reweight the European effect onto the target covariate distribution? Pooling with interactions is a real threat, because it is the obvious way to share structure. That is why it appears as an ablation. Its weakness is that any error in the shared bridge passes straight into the target effect at first order. MR-SENSEMAKR shows that tiny source-side biases are estimated with great confidence at this scale. Covariate reweighting goes further and assumes the confounding correction is identical across ancestries, which is exactly what hetFDR's heterogeneity findings call into question. Our shifted-bridge simulations are designed to break both. If they do not, we report that the simpler pooled estimator is adequate.

Why not just use Mendelian randomization within the target ancestry? Genetic instruments avoid environmental confounding, but European-discovered variants lose strength and can gain pleiotropy in other ancestries. Robust variants trade this for power: PMR-Egger's paper reports competing methods falling to 1–33% power under pleiotropy in Testing and controlling for horizontal pleiotropy. MR also answers a different question, the effect of lifelong genetically shifted exposure, rather than the effect of a treatment as given clinically. We use it as an independent triangulation check rather than as a substitute.

Proposed Experiments

Semi-synthetic study on SUPPORT. The SUPPORT right-heart-catheterization data (5,735 patients) are the standard proximal benchmark used by Pu et al. and the P-learner. We use its real covariates and its established proxy choices to simulate a "source" and a "target" population. The target has a controlled shift of two kinds: in proxy strength, and in the bridge, i.e., confounding structure. Target sizes range from about 200 upward, with the source fixed at full size. We report bias, root-mean-squared error, 95% interval coverage, and interval width. We also report the transportability test's size and power as functions of shift magnitude.

Biobank study with a hidden-confounder design. In multi-ancestry biobanks such as UK Biobank's non-European subsets and the Million Veteran Program, we choose a medication exposure with clinical outcomes, such as metformin and incident cancer, a question also studied by drug-target MR in Evaluating the Impact of Putative Metformin Targets on Cancer Outcomes. We treat a measured confounder, such as an area deprivation index, as hidden, with prior utilization and laboratory measures as proxies. In the Million Veteran Program, the African-ancestry cohort is large (105,838 individuals per hetFDR). The oracle estimate, which adjusts for the withheld confounder on the full African-ancestry cohort, serves as ground truth. We then repeatedly subsample that cohort to small sizes, and our estimator and all baselines are scored against the oracle.

Decisive checks. The method succeeds only if three things hold. Coverage stays within a few points of nominal in every shifted-bridge setting. At target sizes below a few thousand, the variance ratio against target-only estimation is meaningfully above one. The transportability test rejects in the settings where coverage of the pooled ablation collapses.

The method fails, and should be abandoned, in either of two cases. One is that the orthogonal estimator loses coverage whenever the test fails to reject, since this would mean borrowing is silently unsafe. The other is that its gains vanish once the proxy-strength diagnostic shows the target proxies are weak. In that second case the limiting factor is the target data itself, not the target sample size.