What a Biobank Must Send: A Minimal Leaky Interface for Cross-Ancestry Mendelian Randomization

Mendelian randomization asks whether a risk factor causes a disease. It uses genetic variants as natural experiments: variants that shift the risk factor at random from birth stand in for a randomized trial. When the variants were discovered in European cohorts and are then used in African, admixed, or East Asian cohorts, the method quietly breaks. The usual reason is linkage disequilibrium (LD), the pattern of which nearby variants tend to be inherited together. That pattern differs between populations, so a variant that tags a causal mutation in Europeans may tag nothing elsewhere. Methods that model LD exist, but they take the LD pattern from public reference panels such as 1000 Genomes. Those panels are small, mostly European, and describe no admixed population exactly. The cohort that actually holds the genotypes knows its own LD. Under current practice it cannot share that information in any standard form, because biobanks exchange only flat files of per-variant summary statistics.

We propose to treat this as an interface design problem, borrowing the "narrow waist" idea from networking. A narrow waist is a small shared layer that lets many upper-layer algorithms run over many lower-layer data sources. Our claim is that a narrow waist for multi-biobank causal inference must be deliberately leaky: alongside effect estimates, it must export a compressed sketch of each cohort's own LD, per-instrument strength, and a sample-overlap statistic. We further claim that a low-rank sketch costing a small fraction of the full LD matrix is enough to restore nominal false-positive rates in admixed cohorts, where reference-panel LD fails. The contribution is a specification of what each cohort must send, plus a measured curve of statistical validity against bytes sent. The software carrying those bytes is secondary.

Core Claim

Two lines of work set up the problem. In the networking line, Towards a Sensor Network Architecture: Lowering the Waistline placed a single-hop abstraction under sensor-network routing. It found that a clean layer must still expose some low-level facts upward, such as link timing and link quality, or the protocols above it perform badly. OmniFed separated a pluggable communication module (gRPC across sites, MPI within a cluster) from the learning algorithm. It was evaluated only on image classification with averaged neural-network weights.

In the genetics line, MR-LDP and GSMR show that valid estimation with correlated variants requires an LD matrix. Both take that matrix from an external panel, and MR-LDP also assumes no sample overlap between exposure and outcome cohorts.

Our hypothesis joins the two lines. In cohorts whose ancestry is poorly matched by the reference panel, the mismatch between panel LD and in-sample LD is the dominant source of excess false positives in LD-aware Mendelian randomization. A rank-$k$ in-sample sketch sent through a standard interface removes most of that excess. Within each LD block of $p$ variants, the cohort sends

$$R \approx U_k \Lambda_k U_k^\top + D,$$

where $R$ is the cohort's $p \times p$ in-sample LD correlation matrix, $U_k$ and $\Lambda_k$ are its top $k$ eigenvectors and eigenvalues, and $D$ is a diagonal correction that keeps unit variances. This costs roughly $pk$ numbers instead of $p^2/2$. The open quantity, and the thing we measure, is how large $k$ must be per ancestry before false-positive rates return to 5%.

Research Program

The interface we would build is small. A participating cohort runs a local module inside its secure enclave. For each exposure–outcome pair, the module emits four things. The first is ancestry-stratified marginal effect estimates and standard errors. The second is the rank-$k$ LD sketch per block. The third is per-instrument F-statistics, which measure how strongly each variant predicts the exposure. The fourth is an overlap statistic: the correlation of z-scores between the exposure and outcome studies at variants believed to have no effect, which estimates how many participants the two studies share.

Two protocol rules come from known failure modes. First, the variants used as instruments are chosen at one node and their effects estimated at another. This is the remedy for the winner's curse documented in Breaking the Winner's Curse in Mendelian Randomization: choosing and estimating on the same sample inflates the selected effects and biases inverse-variance-weighted (IVW) estimates. Where only one sample exists, that paper's rerandomized estimator (RIVW) is run instead. Second, cohorts that are admixed, meaning their members have recent ancestry from several continental populations, send summaries computed within ancestry bins defined by genetic similarity to a 1000 Genomes anchor population. They do not send pooled summaries adjusted with ancestry principal components. This is the summary-level analogue of the calibration in Ancestry Calibration of Polygenic Risk Scores. That paper showed that adding ancestry as a linear covariate next to uncalibrated genetic scores produced spurious associations, such as a significant ancestry term for height that disappeared after calibration.

On the receiving side, unchanged MR-LDP and GSMR estimators read the sketch in place of a panel matrix. The transport layer is OmniFed's communication module, reused rather than redesigned. Its weight-averaging algorithms are not used, because the target quantity is a causal ratio, not a prediction.

The analysis has three parts. The first is the validity–cost curve: false-positive rate and bias as a function of $k$ and bytes per block, for each ancestry. The second is attribution: how much of the excess error comes from LD mismatch, how much from unmodeled overlap, and how much from winner's-curse selection. Each is switched on and off separately. The third is a check that the bin-stratified summaries for admixed cohorts avoid the covariate trap at the summary level, just as calibration did at the individual level.

Baselines

The naive reference point is current practice. Instruments are selected in European data, pruned to near-independence, and plugged into IVW using the outcome cohort's public summary statistics. Robust Mendelian randomization in the presence of residual population stratification reports that MR-Egger and MR-Mix reach false-positive rates of 46–80% in large simulated samples with slight pleiotropy. That figure sets the scale of failure we expect from the naive pipeline. It is a European-sample result, not a cross-ancestry one.

The strongest competitor is MR-LDP run with the best ancestry-matched 1000 Genomes panel. It already models full LD and pleiotropy, and MR-LDP reports stable 5% Type-I error control under high LD and pleiotropy when the panel matches the study population. We found no reported result on Lacuna for MR-LDP's Type-I error in admixed or African-ancestry cohorts using mismatched reference LD; that number is what we measure.

GSMR with HEIDI-outlier filtering (GSMR) is run as a second LD-aware baseline. HEIDI-outlier is a pleiotropy filter; in that paper it removed 16 pleiotropic variants near APOE in the LDL–Alzheimer's analysis.

For the winner's-curse rule, the comparison is RIVW against IVW. On the published BMI → severe COVID-19 analysis, RIVW gives an odds ratio of 1.60 versus 1.25 for IVW.

The key ablation keeps our interface identical and swaps the in-sample sketch back to panel LD, so any gain is attributable to the leaked information alone. The upper bound is an oracle that runs the same estimator on the full in-sample LD matrix.

All methods share instruments, outcome data, and estimator settings, and each has an equal tuning budget over the pruning threshold or prior hyperparameters. "Beating" the strongest baseline means two things. In admixed cohorts, the sketch must bring Type-I error within Monte Carlo error of 5% where panel-LD MR-LDP is measurably above it. It must do so at $k$ well below $p$, with power no lower than the oracle's minus a small margin.

Why not just…?

Why not just use public summary statistics with an ancestry-matched reference panel? This is the real threat, and the proposal is built to test it. If panel-LD MR-LDP already holds 5% error in REGARDS-like admixed data, the statistical claim fails. What remains would be engineering convenience, and we would report that result rather than argue around it. Our reason to expect mismatch is that admixed LD varies with each individual's ancestry proportions and matches no single 1000 Genomes population. Ancestry Calibration of Polygenic Risk Scores found 33.6–55.0% top-decile reclassification once ancestry was handled properly, which shows how far European-calibrated genetic summaries drift in this population. The panel-versus-sketch ablation settles the question directly.

Why not just pool genotypes centrally? Biobanks such as China Kadoorie Biobank, BioBank Japan, and FinnGen release only summaries; the cross-ancestry study Mendelian randomization study shows no causal relationship between psychiatric disorders and glaucoma worked entirely from such files and had to drop glaucoma subtype analyses in East Asians. We use the pooled analysis as our oracle wherever we can legally run it. The question this proposal answers is how close a cohort can get to the pooled result without pooling.

Why not just run federated learning such as OmniFed's averaging algorithms? Averaging model weights estimates a predictive association, which absorbs confounding. It has no step for choosing valid instruments, testing pleiotropy, or splitting selection from estimation. We reuse OmniFed's transport layer and discard its learning algorithms.

Why not just prune variants hard or add ancestry principal components? MR-LDP shows that pruned IVW and MR-Egger inflate Type-I error under residual LD. Robust Mendelian randomization in the presence of residual population stratification shows that stratification survives adjustment for 20 principal components: the BMI → Townsend deprivation finding has a robustness value below 0.6%, meaning a very weak unmeasured bias would explain it away. Both are included as baselines rather than assumed to fail.

Proposed Experiments

The simulations use real genotypes, so the LD is real. Nodes are built from the UK Biobank European subset (N = 291,274) and the admixed African American REGARDS cohort (N = 8,841); REGARDS genotype access is a dependency of this plan. Synthetic exposures and outcomes are generated with known causal effects, including zero. Pleiotropy is injected at a range of levels, and sample overlap ranges from 0% to 100%. For each configuration we report false-positive rate under no causal effect, bias and coverage under a nonzero effect, and bytes transmitted. These are reported per $k$, comparing panel LD, sketch, and oracle.

The real-data replications use public results with known answers. One is BMI → type 2 diabetes, where GSMR reports a 3.29-fold risk per standard deviation of BMI in Europeans. Others are BMI → diastolic blood pressure, which is robust, and BMI → Townsend deprivation, which is fragile, both from the robustness paper. For the null case we use the psychiatric-disorder → glaucoma pairs, which were null in both European and East Asian data (European depression odds ratio 1.15, 95% CI 0.93–1.42). For East Asian cohorts we can only emulate the panel-LD regime from public summaries, and we state this limit plainly.

Two checks are decisive. The first is whether panel-LD MR-LDP shows excess error in REGARDS-derived simulations at all; if it does not, the core claim is false. The second, if the excess exists, is whether a sketch with $k$ much smaller than $p$ removes it at fixed power. A secondary check asks whether bin-stratified summaries remove the spurious ancestry signals that principal-component adjustment produces. That check uses the height and type 2 diabetes scores from the calibration paper, rebuilt as summary-level instruments.