How Much of a Polygenic Score's Fairness Gap Is Linkage Disequilibrium?

Polygenic risk scores (PRS) add up thousands of small genetic effects into one number that estimates disease risk. They work much worse in people of non-European ancestry. European-trained scores keep only 39.4% of their European predictive performance in African-ancestry individuals (Moreno–Grau et al.). A major reason is linkage disequilibrium (LD): nearby genetic variants are inherited together, so a score often puts its weight on "tag" variants that merely travel with the true causal variant. That tag-to-cause correlation is strong in the population where the score was trained and weaker elsewhere, especially in African-ancestry genomes, whose correlated blocks are shorter. When such a score is used to make a yes/no clinical decision, the fairness literature says we cannot have everything. A score cannot be both calibrated within each group (a predicted 10% risk means 10% in every group) and have equal error rates across groups, unless the groups have the same disease prevalence or the score is perfect (On Fairness and Calibration; FACT).

This proposal separates two causes of the error-rate gap that these theorems do not tell apart. The first is a difference in disease prevalence between groups. It is a property of the population, and no model change removes it without deliberately throwing away information. The second is a difference in how informative the score is, caused by LD tagging that fails to carry over. It is a property of the model and can in principle be fixed by better choice of variants. We propose to measure how large each part is for real diseases at real clinical thresholds. We will then test whether fine-mapping (reassigning weight from tag variants to likely causal ones) closes the second part while keeping calibration, which would be the opposite of the standard fix of degrading predictions for the better-served group.

Core Claim

Suppose a score is calibrated within each ancestry group and a fixed risk threshold is applied. The gap in true- and false-positive rates between groups then has two sources. One is prevalence: calibrated classifiers for groups with different prevalence lie on lines of different slope in the error plane, as shown in On Fairness and Calibration. The other is informativeness, which applies even when prevalence is equal. A less informative calibrated score crowds predictions toward the group average, so fewer people cross the threshold, and both sensitivity and false-positive rate fall. In PRS, the informativeness deficit is largely an LD-tagging artifact.

Let $\Delta(s, t)$ be the equalized-odds gap of score $s$ at threshold $t$, defined as the absolute true-positive-rate difference plus the absolute false-positive-rate difference between groups. We define the tagging component as

$$\Delta_{\mathrm{LD}}(t) = \Delta(s_{\mathrm{tag}}, t) - \Delta(s_{\mathrm{oracle}}, t).$$

Here $s_{\mathrm{tag}}$ is the deployed score built on tag variants and recalibrated per group, and $s_{\mathrm{oracle}}$ is a score built on the true causal variants with the same effect sizes, also recalibrated per group. What remains, $\Delta(s_{\mathrm{oracle}}, t)$, is the part that can only come from prevalence differences and imperfect prediction. The oracle score exists only in simulation, so on real data we approximate it with fine-mapped scores and check that approximation against simulation.

The new contribution is not another portability benchmark or another fairness audit. It is this decomposition and a test of whether its reducible part can be reduced without sacrificing calibration.

Positioning Against Prior Work

The closest work motivates this proposal without doing it. Vargas et al. recalibrate PRS against global West African ancestry in 8,841 African American adults. They show large reclassification (33.6% of the top T2D decile) and remove spurious ancestry–height associations. However, they treat calibration only as score standardization and never measure error rates at decision thresholds. We take their calibration as our starting point and ask what error-rate disparity remains after it.

Moreno–Grau et al. quantify the portability gap across 14 diseases and show that ancestry-tailored PRS-CSx scores raise variance explained 1.62-fold in Africans. They frame the gap only as lost accuracy. We ask whether that accuracy gain turns into smaller error-rate gaps, which is not guaranteed: when prevalence differs, a gain in accuracy moves a group along its own calibration line rather than toward the other group's.

Pfohl et al. constrain the design. In 5.8 million EHR patients, forcing equalized odds broke calibration and lowered net benefit at the 7.5% statin threshold, and recalibrating reopened the error gaps. Their features contain no genetic data. We therefore rule out training-time parity penalties as the intended remedy and use them only as a comparison.

The method comes from the fine-mapping and shrinkage literature. PRS-CS supplies joint shrinkage within LD blocks. SuSiE-style credible sets and their small-sample correction (Denault et al.) supply posterior inclusion probabilities, meaning each variant's estimated probability of being causal. KnockoffZoom supplies an alternative, FDR-controlled way to localize causal variants. The observation that silent variants carry association signal purely through tagging (Chen et al.) and the criticism of marginal single-variant testing (de los Campos et al.) explain why tag-based scores should carry over poorly.

Research Program

The first component is a controlled simulation on real genotypes. We take UK Biobank genotypes from European, African, South Asian and East Asian participants, together with 1000 Genomes-style reference LD. We then generate binary phenotypes from a liability model: each person's underlying risk is the sum of causal genetic effects plus noise, and disease occurs above a cutoff. Causal effects are identical across ancestries by construction, so ancestry-specific biology is zero and any portability loss comes from LD and allele frequency.

Three quantities vary independently. The first is the prevalence gap between groups, set through ancestry-specific liability cutoffs. The second is heritability. The third is how causal variants are placed relative to genotyped variants, ranging from typed causal variants to causal variants that are only tagged. On each simulated dataset we fit a European-discovery PRS-CS score and a fine-mapped score that weights variants by posterior inclusion probability. We also compute the oracle score, recalibrate all three per group, and compute $\Delta$, $\Delta_{\mathrm{LD}}$ and the prevalence component across thresholds.

This simulation answers three questions. How much of the gap does LD create? Does the part created by LD shrink as fine-mapping gets closer to the oracle? Is the decomposition stable, or does it depend on the threshold?

The second component is an analytic check. Under the Gaussian liability model, sensitivity and false-positive rate at threshold $t$ for a calibrated score depend only on group prevalence and the variance the score explains in that group. We derive the error-plane point for each group in closed form. We then test whether the empirical $\Delta_{\mathrm{LD}}$ is predicted by the attenuation in explained variance alone. If it is, the decomposition reduces to a portability number that practitioners already estimate, which would be a useful and falsifiable simplification.

The third component is real data. We use UK Biobank coronary artery disease and type 2 diabetes, and REGARDS type 2 diabetes if access permits, since that is the Vargas cohort. For each group we report error rates, selection rates, calibration and net benefit under two decision rules:

  • Absolute-risk threshold. A fixed absolute risk cutoff applied to calibrated scores, which preserves calibration.
  • Within-group top decile. Treating the top decile within each group as high-risk, which forces equal selection rates.

Comparing the two rules makes the three-way incompatibility concrete for genomic decisions.

Baselines

The naive reference point is a European-trained PRS-CS-auto score, calibrated per group by the global-ancestry regression of Vargas et al.. This is what a careful clinic would deploy today. The file reports that this calibration raised the top-versus-bottom-decile odds ratio for T2D from 7.97 to 10.77 in REGARDS. We report its error-rate gap directly, because no reported equalized-odds result for PRS was found on Lacuna.

The strongest existing accuracy method is the ancestry-tailored PRS-CSx score, which Moreno–Grau et al. report gives a 1.62-fold gain in variance explained in Africans. It is the main competitor because it attacks the same tagging problem by estimating ancestry-specific effects. It will get the same discovery summary statistics, the same LD panels and the same per-group recalibration. Our fine-mapped score beats it only if it achieves a smaller $\Delta$ at matched calibration error and equal or higher net benefit, with bootstrap intervals that exclude zero difference.

The strongest fairness methods are two approaches that reach parity by force:

  • Reductions. The exponentiated-gradient approach of Agarwal et al., run through Fairlearn with an equalized-odds constraint.
  • Information withholding. The calibration-preserving post-processing of On Fairness and Calibration.

Both take the same score as input and are tuned on the same validation split. They will nearly always win on $\Delta$. The comparison is on the whole triple of $\Delta$, calibration and net benefit. We claim an improvement only if fine-mapping reduces $\Delta$ without the net-benefit loss these methods incur.

The key ablation holds everything fixed except the variant weights. This means the same discovery sample size and a tag-based versus fine-mapped weighting of the same summary statistics, which isolates the LD-localization ingredient from gains that come from more data.

Why not just…?

Why not just calibrate each group, as Vargas et al. do? Calibration is necessary but guarantees unequal error rates whenever prevalence or informativeness differs (On Fairness and Calibration). Their paper never measures error rates, so it cannot say how large the leftover gap is. Our naive baseline is exactly their method, and its measured $\Delta$ is the quantity to be explained.

Why not just enforce equalized odds with a fairness library? Pfohl et al. showed in a large clinical cohort that this breaks calibration and lowers net benefit at a fixed treatment threshold. The reductions approach also returns randomized classifiers (Agarwal et al.). We include it as a baseline so that its cost on genomic scores is measured rather than assumed.

Why not just use PRS-CSx or wait for larger diverse biobanks? This is a real threat. If ancestry-specific effect estimation already removes $\Delta_{\mathrm{LD}}$, fine-mapping adds nothing. The decomposition settles this directly: we compute $\Delta_{\mathrm{LD}}$ for PRS-CSx as well. If that value is near zero, the contribution becomes diagnostic. It would show that the remaining gap is the prevalence component, which no amount of data can remove, and that this component can only be traded against calibration or net benefit. Either outcome changes what "fixing portability" can promise.

Why not just report the AUC gap? AUC averages over all thresholds, but decisions happen at one threshold. The same AUC gap can produce very different error-rate gaps depending on where the threshold sits relative to each group's prevalence. We will show this by comparing AUC gaps with $\Delta(t)$ across thresholds.

Decisive Checks

The first decisive check is in simulation. When causal variants are typed, $\Delta_{\mathrm{LD}}$ should be near zero. It should grow as causal variants become tagged-only, and it should grow faster in African-ancestry genotypes. If it does not grow, LD is not a meaningful driver of fairness gaps, and the proposal's premise fails.

The second is also in simulation. With equal prevalence, the oracle score should show essentially no gap, while the tag-based score should still show one. This separates the informativeness mechanism from the prevalence theorem.

The third is on real UK Biobank data. The fine-mapped score should reduce $\Delta$ relative to the matched tag-based ablation at equal calibration error. The size of that reduction relative to PRS-CSx tells us whether causal localization or ancestry-specific effects matter more.

Throughout, the African-ancestry case counts in UK Biobank are small. We therefore report bootstrap intervals and treat real-data results as confirmation of patterns found in simulation, not as standalone findings.