Ancestry-Divergent Structural Variants as a Hidden Cause of Cross-Ancestry Instrument Failure

When geneticists want to know whether, say, high body-mass index causes type-2 diabetes without running a trial, they use Mendelian Randomization (MR): genetic variants that influence the exposure act like a natural randomization, because genes are shuffled at conception independently of later environment. The method only works if the variants used as instruments actually track the causal biology in the population being studied. The standard story of why instruments discovered in European cohorts fail in African or admixed cohorts is linear: linkage disequilibrium (LD) — the correlation between nearby DNA letters — decays differently across ancestries, so a "tag" variant stops tagging the causal one. This proposal argues that a second, unmodeled mechanism is at work: ancestry-divergent structural variants — deletions, inversions, and duplications that rearrange large stretches of chromosome — physically rewire the three-dimensional folding of the genome, changing which gene a variant regulates and through which pathway. If a chromosomal inversion common in one ancestry fuses two regulatory domains, an instrument that was valid in Europe can regulate a completely different gene elsewhere, breaking the causal inference in a way that no amount of LD recalibration can fix.

The enabling observation is that rearrangements of this kind are far more common and more population-structured than short-read sequencing acknowledges. Ebert and colleagues assembled 64 haplotype-resolved genomes from 32 globally diverse individuals and found 107,590 structural variants, with 68% completely invisible to short-read sequencing and 63% formed by homology-mediated mechanisms such as non-allelic homologous recombination (<i>De novo</i> assembly of 64 haplotype-resolved human genomes of diverse ancestry and integrated analysis of structural variation; De novo assembly of 64 haplotype-resolved human genomes of diverse ancestry and integrated analysis of structural variation); gnomAD-SV independently cataloged 433,371 sequence-resolved SVs in 14,237 individuals, 54% of non-European ancestry (A structural variation reference for medical and population genetics). Separately, we know these rearrangements matter for regulation in 3D: somatic SVs concentrate at domain boundaries, fuse topologically associating domains (TADs — self-contacting chromatin neighborhoods), and hijack enhancers onto new genes (Structural variation drives enhancer hijacking via 3D genome disruption in ccRCC), and for over 85% of GWAS-associated variants the physically contacted target gene is not the nearest linear gene (HUGIn: Hi-C Unifying Genomic Interrogator). No study has ever put these three facts together for germline variation across ancestries. That is the gap this proposal occupies.

Core Claim

A quantifiable share of cross-ancestry MR and fine-mapping failure is attributable not to linear LD decay but to ancestry-divergent structural variants that disrupt chromatin contact domains. Specifically, when a European-discovered instrument sits in a chromatin domain whose boundary or loop anchors are disrupted by an SV that is differentially frequent in another ancestry, the instrument should show (i) collapsed instrument strength and (ii) clustered horizontal pleiotropy — the instrument affecting the outcome through a pathway other than the exposure. We will build a per-region "rearrangement-differentiation score" from SV breakpoints projected onto 3D contact maps, show that this score predicts instrument failure beyond what linear LD explains, and turn it into a practical filter that improves cross-ancestry instrument selection and causal-effect estimation.

The score itself is simple: for each chromatin domain $r$,

$$D_r = \big| f_{\text{AFR}}(r) - f_{\text{EUR}}(r) \big| \cdot w_r,$$

where $f_{\text{AFR}}(r)$ and $f_{\text{EUR}}(r)$ are the carrier frequencies of boundary-disrupting SVs overlapping domain $r$ in African and European super-populations, and $w_r$ is the predicted contact rewiring — how much of the domain's reference Hi-C contact mass would be redirected if the SV-induced boundary shift occurred, computed with the neoloop boundary-shift logic of Neoloopfinder's framework. The claim is testable by a nested regression: cross-ancestry instrument failure regressed on LD decay alone versus LD decay plus $D_r$. If $D_r$ adds nothing, the idea dies — and that is the decisive check.

Research Program

The program has three components. First, we build the first map of ancestry-divergent, 3D-disruptive germline rearrangements. We start from the 107,590 SVs in the Ebert et al. resource — already phased, already genotyped into 3,202 individuals of the 1000 Genomes Project with PanGenie (<i>De novo</i> assembly of 64 haplotype-resolved human genomes of diverse ancestry and integrated analysis of structural variation; De novo assembly of 64 haplotype-resolved human genomes of diverse ancestry and integrated analysis of structural variation) — and cross-check against gnomAD-SV's 433,371 calls (A structural variation reference for medical and population genetics). Each SV's breakpoints are projected onto reference chromatin contact maps: the HUGIn compendium of 21 tissues at 40 kb resolution (HUGIn: Hi-C Unifying Genomic Interrogator) and the 4D Nucleome loop catalogs of over 140,000 interactions per cell type (An integrated view of the structure and function of the human 4D nucleome). Following the graph formalization of ChromInSight — genomic bins as nodes, Hi-C contacts as edges, epigenomic marks as node features — we represent each SV's effect as an edit to this graph: boundary-node deletion, edge rewiring, or domain fusion, exactly the operations Dong et al. demonstrated oncologically. This yields, for every domain in the genome, both the frequency differential and the predicted contact rewiring that enter $D_r$.

Second, we decompose cross-ancestry instrument failure. We take published European instrument sets for metabolic and cardiovascular risk factors — the GSMR study's instruments for BMI, lipids, and blood pressure (Causal associations between risk factors and common diseases inferred from GWAS summary data) — and evaluate each instrument in African and admixed cohorts from the 1000 Genomes Project (A map of human genome variation from population-scale sequencing) and in the GEUVADIS lymphoblastoid expression data used by the PMR-Egger study (Testing and controlling for horizontal pleiotropy with probabilistic Mendelian randomization in transcriptome-wide association studies). For each instrument we record three failure signatures: $F$-statistic decay (loss of instrument relevance), effect-size heterogeneity, and pleiotropic outliers flagged by HEIDI-outlier (Causal associations between risk factors and common diseases inferred from GWAS summary data). We then ask which failures the linear LD model explains and which only $D_r$ explains.

Third, we convert the diagnosis into a method: a 3D-disruption-aware instrument filter that re-weights or excludes instruments in high-$D_r$ domains before cross-ancestry MR or fine-mapping, and a 3D-constrained target-gene assignment that replaces the nearest-gene or fixed-window heuristic. For validation of target assignment we use a genuine ground truth: the 1,525 SV-eQTLs Ebert et al. identified in diverse-ancestry cell lines, which tell us which genes specific structural variants actually regulate (<i>De novo</i> assembly of 64 haplotype-resolved human genomes of diverse ancestry and integrated analysis of structural variation; De novo assembly of 64 haplotype-resolved human genomes of diverse ancestry and integrated analysis of structural variation).

We must be honest about one structural limitation, because a reviewer will find it anyway: no ancestry-stratified Hi-C maps exist. Every reference contact map available is from a limited set of cell lines and tissues with no population stratification. Our design therefore treats reference topology as shared and models ancestry differences as local perturbations of it. This assumption is itself testable — the SV-eQTL validation tests whether predicted rewiring predicts observed expression changes in the right direction — and the proposal includes a small pilot to probe it directly: Hi-C in a dozen ancestry-diverse lymphoblastoid cell lines from the 1000 Genomes Project, matched in carrier versus non-carrier status at two high-$D_r$ loci. The 40 kb resolution of the tissue compendium also limits breakpoint-level precision, which is why the 4DN loop catalogs and, where available, finer Micro-C data carry the boundary-level analysis.

Proposed Experiments

Experiment 1 builds and characterizes the disruption map. Input: Ebert et al.'s SV calls and PanGenie genotypes, gnomAD-SV, HUGIn and 4DN contact maps. Output: the genome-wide distribution of $D_r$, plus a catalog of predicted TAD fusions and neoloops with ancestry-differentiated carrier frequencies. The key descriptive question is whether high-$D_r$ regions are enriched near regulatory domain boundaries (as Dong et al. found for somatic SVs at TAD boundaries, Structural variation drives enhancer hijacking via 3D genome disruption in ccRCC) and whether African cohorts, with their higher structural diversity, carry systematically more disruptive variants — as both the Ebert and gnomAD-SV resources indicate they should.

Experiment 2 is the decomposition. For every European-discovered instrument we fit a regression of cross-ancestry failure indicators on (a) population-specific LD decay around the instrument, using 1000GP and TOPMed-style panels (TOP-LD: A tool to explore linkage disequilibrium with TOPMed whole-genome sequence data), and (b) $D_r$ of the instrument's domain. The decisive statistic is the incremental variance explained by (b) over (a) alone, with a pre-registered expectation: if $D_r$ explains less than 5% of additional failure variance genome-wide, the LD-decay story is sufficient and this proposal's mechanism is not a meaningful driver. We additionally test whether instruments in high-$D_r$ domains show clustered pleiotropy — multiple instruments in the same disrupted domain failing together — which is precisely the pattern that breaks PMR-Egger's equal-effect assumption and that statistical filters cannot distinguish from correlated pleiotropy (Testing and controlling for horizontal pleiotropy with probabilistic Mendelian randomization in transcriptome-wide association studies).

Experiment 3 evaluates the method. On held-out ancestries, we compare three instrument-selection pipelines: unfiltered European instruments; LD-recalibrated instruments (the strongest simple competitor); and our 3D-disruption-aware filter. Metrics are instrument replication rate, calibration of MR causal estimates against within-ancestry estimates, and pleiotropy-outlier recall. For target-gene assignment, we evaluate against the 1,525 SV-eQTLs as ground truth, measuring how often the predicted rewired target matches the observed expression effect. We report the ChromInSight-style graph edit predictions' precision directly; ChromInSight itself achieved an average AUROC of 0.9348 and AUPRC of 0.8225 for predicting double-strand breaks from contact graphs in 22-fold cross-validation (ChromInSight: Revealing DNA Double‐Strand Breaks Through Chromatin Structural Insights With an Interpretable Graph Neural Network Framework), which is the performance level a contact-graph predictive component should be held to, though our task (expression rewiring) is different and we do not expect to match it out of the gate.

Experiment 4 is the pilot validation: Hi-C in carrier/non-carrier lymphoblastoid lines at two loci with the highest $D_r$, testing whether predicted boundary shifts and neoloops are physically present. The somatic precedent is strong — Dong et al. functionally validated an inversion/translocation hijacking an enhancer cluster onto SEMA5B (Structural variation drives enhancer hijacking via 3D genome disruption in ccRCC) — but germline, population-differentiated rearrangements have never been checked this way, and this experiment is where the shared-topology assumption lives or dies.

Baselines

The "do nothing" reference point is the current default practice: take European GWAS instruments and apply them unchanged to non-European cohorts, with target genes assigned by nearest linear gene or a fixed window, as in the proximal mapping used in TWAS (Testing and controlling for horizontal pleiotropy with probabilistic Mendelian randomization in transcriptome-wide association studies). No reported result found on Lacuna for the target-assignment accuracy of nearest-gene mapping; the closest evidence is that it is wrong more than 85% of the time in the loop-based sense reported by HUGIn (HUGIn: Hi-C Unifying Genomic Interrogator). Beating this baseline means anything above it on replication and calibration; it is included because it is what most cross-ancestry analyses actually do.

The strongest competitor on the causal-inference question is GSMR with HEIDI-outlier pleiotropy filtering (Causal associations between risk factors and common diseases inferred from GWAS summary data), the method behind widely cited causal maps such as the 3.29-fold T2D risk increase per standard deviation of BMI, with 45 significant causal associations reported. It is strongest because it is the established machinery for multi-SNP causal inference with LD correction and pleiotropy pruning, and our claim implies it misses a failure mode it was never designed to see: HEIDI-outlier removes pleiotropic instruments statistically but cannot tell why they are pleiotropic or predict which instruments will fail in a specific non-European cohort. We will run GSMR and our 3D-aware variant on identical summary statistics, identical LD panels, and an identical instrument count budget (our filter replaces excluded instruments with the next-strongest unexcluded ones, so instrument strength is matched). Beating GSMR means higher instrument replication rate and better-calibrated causal estimates in held-out ancestries, plus — uniquely available to us — prediction of which instruments will fail before running the target cohort, evaluated by AUROC of failure prediction.

On target-gene assignment, the strongest competitor is loop-based assignment using the HUGIn Fit-Hi-C maps without any ancestry or SV information (HUGIn: Hi-C Unifying Genomic Interrogator). This baseline uses the same 3D contact data we do, so it isolates exactly our new ingredient: the ancestry-divergent SV perturbation layer. It will be run on the same contact maps, same resolution, same SV-eQTL ground truth. Beating it means correctly assigning target genes in rearrangement-differentiated regions where the static reference map points to the wrong gene because the domain was rewired. This ablation is the cleanest test of whether the proposal's core mechanism — rather than merely having Hi-C data — is what helps.

Why not just…?

Why not just use multi-ancestry LD reference panels and re-clump the instruments? This is the approach the field would reach for first, using resources like TOPMed-based LD lookup (TOP-LD: A tool to explore linkage disequilibrium with TOPMed whole-genome sequence data) or the 1000 Genomes Project (A map of human genome variation from population-scale sequencing). It is a real threat and Experiment 3 runs it as the strongest simple baseline with an identical budget — if it matches our filter, the proposal's mechanism is not needed. But two cited results say it should fall short: 68% of the relevant structural variants are invisible to the short-read sequencing that these LD panels are built from (<i>De novo</i> assembly of 64 haplotype-resolved human genomes of diverse ancestry and integrated analysis of structural variation; De novo assembly of 64 haplotype-resolved human genomes of diverse ancestry and integrated analysis of structural variation), so the panels cannot see the rearrangements at all; and linear proximity picks the wrong target gene over 85% of the time (HUGIn: Hi-C Unifying Genomic Interrogator), so even a perfectly recalibrated tag can be aimed at the wrong gene. LD recalibration fixes the tagging problem; it cannot fix the rewiring problem.

Why not just rely on statistical pleiotropy filters like HEIDI-outlier or PMR-Egger? These methods need only summary statistics, which is a genuine practical advantage, and HEIDI-outlier demonstrably works — it removed 16 APOE-region SNPs and abolished a false LDL–Alzheimer's association (Causal associations between risk factors and common diseases inferred from GWAS summary data). But they filter after the fact and rest on distributional assumptions our mechanism violates: PMR-Egger assumes pleiotropic effects are uniformly distributed across variants, whereas SV-driven domain rewiring produces effects clustered in specific disrupted regions (Testing and controlling for horizontal pleiotropy with probabilistic Mendelian randomization in transcriptome-wide association studies; Structural variation drives enhancer hijacking via 3D genome disruption in ccRCC). Their power ceiling under pleiotropy is also documented: PMR-Egger reaches 41% where competitors drop to 1–33%. Our filter is complementary, not a replacement — it predicts failure before estimation and provides a biological reason for it — and Experiment 2's clustered-pleiotropy test would show whether statistical filters systematically mis-classify SV-driven failures.

Why not just do multi-population eQTL colocalization instead of mapping 3D chromatin? Colocalization asks whether the association signal for a trait and for gene expression share the same causal variant, using datasets like the multi-tissue cattle atlas as a template (The enhanced multi-tissue atlas of regulatory effects in cattle). It is cheaper and well established. It falls short here for two documented reasons: bulk expression assays are confounded by shifting cell-type composition across samples — THUNDER showed contact-based features reduce cell-type proportion error by 23–36% relative to standard deconvolution (THUNDER: A reference-free deconvolution method to infer cell type proportions from bulk Hi-C data) — and, more fundamentally, a large fraction of expression variation is driven by the structural variants themselves (1,525 SV-eQTLs in the Ebert resource), which short-read eQTL studies do not genotype. Colocalization can only see effects of variants it has measured; our approach explicitly models the 68% of rearrangements it cannot see.

Closing Decisive Checks

Three results would settle the proposal's fate. The nested-model test in Experiment 2 is the primary one: if the rearrangement-differentiation score adds no significant failure-variance beyond population-specific LD decay, the mechanism is real but negligible, and the proposal should be reported as a negative result with the map released as a resource. The SV-eQTL validation in Experiment 3 is the mechanistic one: if predicted rewired targets do not match observed expression effects in rearrangement-differentiated regions more often than static loop assignment, the shared-topology perturbation model is wrong and ancestry-specific conformation data would be required before any of this works. And the pilot Hi-C in Experiment 4 is the physical one: if carrier and non-carrier lymphoblastoid lines show no detectable boundary differences at high-$D_r$ loci, the predicted disruptions are artifacts of projecting breakpoints onto coarse 40 kb maps, and finer-resolution or ancestry-matched conformation data becomes the necessary first step rather than a refinement. Each check is designed so that its failure is informative rather than ambiguous, and each failure mode points to a concrete, different next project.