Which Ancestries Should a Genomic Federation Include? A Factorial Answer

Hospitals and biobanks that cannot legally pool genomes increasingly train shared models through federated learning: each site trains on its own data, and only model updates are combined. The default rule is to let every willing site join, on the theory that more data always helps. That rule is in doubt for genomic prediction across ancestries. In the UK Biobank, adding a 300,000-person European cohort to a 5,000-person African cohort lowered accuracy for African individuals on some blood traits, while the European cohort alone stayed best for height (Optimal strategies for learning multi-ancestry polygenic scores vary across traits). Whether a site helps a target population therefore depends on the trait. It may also depend on which other sites are present and on how the federated optimizer behaves. Nobody has measured this.

We propose to treat site membership as the factors of a designed experiment. For each target ancestry and trait, every other ancestry node is a two-level factor: included or excluded. Two settings of the federated optimizer are crossed with these factors. The first is how much local training each site does between rounds of combining updates. The second is whether the target site is a "straggler," meaning a slow device that can finish only part of its local work. Analyzing this grid the way agronomists analyze crossed fertilizer treatments separates three things: what each site contributes on its own (its "main effect"), what pairs of sites do together beyond the sum of their separate effects (their "interaction"), and how either changes under the kinds of drift and straggling that occur in real federations. The practical output is a cheap, validated rule for choosing a federation per trait and target ancestry. The scientific output is the first estimate of whether cross-ancestry negative transfer comes from single sites, from combinations of sites, or from the training dynamics.

Core Claim

Two failure modes are already documented separately. Pooling across ancestries can hurt a minority population, as Lehman et al. found. Federating across ancestral nodes causes "client drift," where local models wander toward their own data and the combined model shows loss spikes when local work is long (Efficacy of federated learning on genomic data: a study on the UK Biobank and the 1000 Genomes Project). We claim these two effects interact, and that a design varying one factor at a time cannot see the interaction. Kolobkov et al. varied local epochs with the node set held fixed. Lehman et al. varied cohort composition in centralized training. Neither design can say whether a harmful node stays harmful, becomes harmless, or becomes more harmful once optimization dynamics change. Factorial agronomy offers a direct analogy. Zinc sprays look ineffective in single-factor trials, and only crossing them with phosphorus shows that phosphorus suppresses zinc uptake (Shaoxia Wang et al.). Similarly, high salinity cancels the benefit of more light (Christopher Pascual et al.). Our hypothesis is that "the European node hurts African prediction for blood traits" is the same kind of statement: a main effect whose sign depends on other factors.

The claim can fail. Interactions between nodes may turn out to be negligible next to main effects. In that case a cheap additive rule, scoring each node separately, is sufficient, and the right conclusion is that the full factorial is unnecessary. The design is built to tell these two outcomes apart.

Research Program

The data come from the UK Biobank ancestry groups used by Lehman et al.: African, Admixed American, Central/South Asian, East Asian, Middle Eastern, and European. Each group is a separate federated node, so the federation has the extreme statistical heterogeneity of continental silos. For a given target ancestry, the other five nodes give a $2^5 = 32$-cell inclusion grid. The target node is always present, and the cell with every other node excluded is the local-only model. The predictor is federated sparse linear regression in the style of Lassonet, as in Kolobkov et al. We use the same SNP preselection and 20-component federated PCA for ancestry adjustment. All models are scored on held-out individuals from the target ancestry.

Two optimizer factors are crossed with inclusion. Local work per round takes the levels 1 epoch and 32 epochs, the two settings Kolobkov et al. contrasted. The aggregation rule is either plain federated averaging or FedProx. FedProx adds a penalty $\frac{\mu}{2}\|w - w^t\|^2$ that keeps each site's weights $w$ near the current global model $w^t$, and it accepts incomplete local work (Federated Optimization in Heterogeneous Networks). A systems factor makes the target node either a full participant or a straggler that completes only a fraction of its local iterations. This captures a realistic case in which the smallest cohort also has the weakest infrastructure.

The layout is a split-plot design, and this choice follows from how the computation is actually organized. A coalition, meaning a particular set of included nodes, fixes some work that is costly to redo: the federated PCA basis, the SNP preselection, and the initialization. Each coalition is therefore a main plot. The optimizer and straggler settings are cheap to vary on top of a coalition, so they are randomized as subplots within it. This mirrors the structure of Jian J. Duan et al., who assigned transgenic versus conventional corn to large plots and randomized insecticide within them. Duan et al. matter here for a second reason. They showed that single-season comparisons were badly underpowered, with only 22 of 56 reaching 80% power, and that pooling replication fixed this. We take that as a warning. Each main plot is replicated with independent random seeds and train/test splits. Coalition effects are tested against the between-plot error, and optimizer effects against the within-plot error. Treating all runs as independent would make coalition interactions look falsely significant.

Several cells will fit the data about equally well. Rather than report one "best coalition," we use Rashomon Partition Sets (Robustly estimating heterogeneity in factorial data using Rashomon Partitions). That method enumerates every interpretable grouping of factorial cells whose posterior is within a set tolerance of the best one, and its authors showed that choosing a single model can hide real subgroup structure. We supply its input from the outcomes of a designed experiment, and the factorial cells are node coalitions. We use the method unchanged, and our grid of a few dozen cells is well within its enumeration limits.

Full 32-cell grids crossed with all subplot levels are run for two anchor traits that bracket the known behavior: height, which is highly polygenic, and mean corpuscular volume (MCV), which is driven by ancestry-specific large-effect loci. Both use African and East Asian targets. For the remaining traits, we run a fractional design that can estimate main effects and two-way interactions. The full grids then serve as ground truth for checking the fractional ones. Causal inference with Mendelian randomization is out of scope. The same design could later ask which nodes keep genetic instruments strong, but we test the idea on prediction first, where ground truth can be measured.

Baselines

The naive reference is include-everyone federated averaging with 1 local epoch, the configuration Kolobkov et al. found stable. They report federated models "nearly indistinguishable" from centralized ones and far better than local ones, but give no per-ancestry $R^2$. No reported result was found on Lacuna for per-ancestry federated accuracy on these UK Biobank groups, so we measure this baseline ourselves. Local-only training on the target node is the second reference point. Centralized pooled LASSO with Lehman et al.'s importance reweighting is the third. They report that the African-only model "significantly outperformed" the European-only model for MCV in African individuals, but the file gives no numeric $R^2$. We therefore reproduce their pipeline and use the reproduced value as the centralized reference.

The strongest competitor is learned per-node aggregation weights. Each node's weight is a continuous parameter tuned on a validation split from the target ancestry, which generalizes Lehman et al.'s reweighting to the federated setting. It is strong because continuous weights include every inclusion pattern as a special case. Leave-one-node-out selection, which removes each node and keeps the removal if accuracy improves, is the standard simpler competitor and is included as well. FedProx with its $\mu$ tuned by grid search is the strongest heterogeneity-aware optimizer. Its reported gain of 22 points of absolute accuracy over federated averaging with 90% stragglers comes from image and text benchmarks, not genomics.

Fairness is enforced by budget. Each selection method gets the same number of complete federated training runs as our fractional design uses, the same seeds, the same validation split, and the same PCA basis for any given coalition. The ablation that isolates our key ingredient is a main-effects-only rule estimated from the same fractional runs. It selects nodes by their additive effects and ignores interactions. If this ablation matches the interaction-aware rule, interactions do not matter in practice. We count our method as beating a competitor if its chosen configuration has a higher target-ancestry $R^2$ than the competitor's choice, by more than the replicate standard error, on traits where negative transfer is present, and if it is not worse on traits where it is absent.

Why not just…?

Why not just let every site join, since federation beats local training? Kolobkov et al. did find that, but their comparison was federation versus isolation. They never compared federation with a well-chosen subset. Lehman et al. show that, centrally, adding European data can lower African accuracy. The include-all cell is one cell of our grid, so the experiment shows directly whether it is ever dominated.

Why not just drop nodes one at a time? Leave-one-out is exactly the procedure that misses antagonism, as the zinc–phosphorus case shows: it can keep two nodes that hurt only in combination, or drop a node that helps only when another node is present. If the full grids show small two-way interactions, leave-one-out is adequate and we will say so. It is a baseline precisely because it might succeed.

Why not just learn continuous node weights on validation data? This is the real threat. It has a conceptual weakness: a 5,000-person validation set from the target ancestry gives a noisy objective over many continuous weights, and without designed replication it cannot tell structure from seed noise. That weakness is an argument, not evidence. If learned weights reach the full-grid best cell within the same budget, the factorial selection rule loses. The design would still keep its scientific value, because it identifies which interactions exist and whether drift changes them. We also test a hybrid in which the factorial main effects initialize the learned weights.

Why not just use random search or Bayesian optimization over everything? These methods find a good configuration but do not decompose why it is good. They cannot say whether negative transfer is a property of a node or of the optimizer. We give them the same budget and compare the accuracy of the configuration each method selects.

Decisive Checks

Three results settle the proposal. First, the full MCV grid with an African target either replicates Lehman et al.'s negative effect of including the European node under federation or fails to. If it replicates, we test whether the effect's size changes significantly between 1 and 32 local epochs, which is the coalition-by-optimizer interaction tested against the correct split-plot error. Second, across both anchor traits and both targets, we compare the variance explained by node-by-node interactions with that explained by main effects. Interactions explaining a negligible share would argue for additive node scoring. Third, configurations selected from the fractional design must fall within one replicate standard error of the full-grid optimum and must beat include-all, leave-one-out, and learned weights at equal budget on the traits with negative transfer. If the third check fails while the first two succeed, the contribution narrows to a measurement result: an explanation of when cross-ancestry federation hurts. That is still useful, but it is not a selection method.