Is Green-Space Buffering Really Different Across Ancestries? Separating Real Effect Modification From Spatial Artifacts

Many environmental health studies report that green space or nearby water "buffers" people against air pollution or heat. Living near trees or a lake seems to weaken the link between ozone and stroke deaths, or between genetic risk and skin disease. A natural next question is whether this protection works equally well for people of different genetic ancestry. This proposal argues that the standard way of answering that question is likely to produce false findings, and for a specific reason. In most cities, ancestry groups do not live uniformly mixed. They are spread unevenly across the map, often by residential segregation. As a result, three things vary by ancestry for reasons that have nothing to do with biology. Each group's exposure is entangled with smooth, unmeasured geographic factors such as a regional income gradient, and the entanglement is different for each group. Statistical corrections for that entanglement remove different amounts of each group's usable exposure variation. And genetic risk scores built from European data measure risk much less accurately in non-European groups. Each of these can produce an apparent "ancestry difference in buffering" even when none exists, or hide one that does.

We propose an estimator and an evaluation study built around one structural fact: an unmeasured area-level confounder is a property of a place, not of a person's ancestry. It can therefore be estimated once, pooling every resident of every group, and then removed before group-specific buffering effects are estimated. We pair this pooled-field estimator with three per-group diagnostics. We then test it on a semi-synthetic benchmark in which segregation, confounding strength, and genetic-score accuracy can be set independently. Finally, we use it to re-examine a published gene-by-environment buffering finding in a multi-ancestry cohort.

Core Claim

When a spatially smooth exposure modifier is compared across ancestry groups that live in partly separate places, three things can each create or erase apparent effect modification. We call them differential spatial confounding, differential loss of exposure support under deconfounding, and differential polygenic-score reliability. A fourth issue, non-collapsibility of odds ratios across strata with different baseline risk, makes it worse for binary outcomes. Non-collapsibility means that odds ratios can differ between groups with different baseline risk even when the underlying effect is identical.

Our central hypothesis is testable. Under realistic segregation, running a spatial deconfounding method separately within each ancestry stratum will inflate the false-positive rate for "ancestry modifies buffering." It will also give confidence intervals with poor coverage for the between-group difference. Estimating a single shared confounder field from the pooled population, then fitting group-specific buffering slopes on the deconfounded exposure, should restore nominal error rates. Reporting each group's remaining exposure variance should flag the cases where no method can answer the question.

Where This Sits in Prior Work

Several papers motivate the gap. Buffering findings come from studies of greenness moderating ozone and particulate mortality (Wang et al.), ozone-related stroke mortality in Shandong (Zhao et al.), and prenatal ozone and heat effects on congenital heart disease (Li et al.). All of them fit models that assume independent errors in populations treated as uniform. The closest existing work is Chen et al.. That study stratified UK Biobank participants by a polygenic risk score and found that blue-space proximity interacts with genetic susceptibility for psoriasis. It used a European-derived score, ordinary Cox models, and no spatial deconfounding. We treat its result as a target for re-analysis rather than a foundation. Hart et al. found that satellite greenness did not protect against adolescent asthma while nearby accessible parks did. That warns us that the choice of exposure measure is itself a confound. We therefore test both measure types.

Other papers supply the methods. Spatial+ regresses the exposure on spatial basis functions and keeps only the residual before fitting the outcome model. In the Uttar Pradesh simulation of Urdangarin et al. (2022), it recovered a true coefficient of 0.2000 as 0.1861, where a standard conditional autoregressive model gave 0.4603. The multivariate extension in Urdangarin et al. (2023) recovered −0.1432 against a truth of −0.1500. Both papers assume one homogeneous population per area. ROSCE estimates heterogeneous effects under spatial confounding, but its subgroups are geographic regions. Ours are groups of people who share regions. SpaCE provides semi-synthetic spatial confounding datasets with spatially blocked train/test splits, but only at the level of areas. The Spatial Deconfounder learns a substitute confounder from neighboring treatments with a variational autoencoder, and it treats the exposed population as one block. Our pooled-field idea extends what Spatial+ and the Spatial Deconfounder already do. Their confounder estimate is a function of location, and we argue it should be estimated across all strata rather than inside each one.

A further set of papers constrains the design. On cross-ancestry cancer polygenic risk scores shows that European scores shift on the absolute scale across ancestries. Standardizing within each ancestry restores relative stratification: top-decile breast cancer odds ratios were 2.81 in European, 2.88 in African, 2.60 in East Asian, and 2.33 in South Asian participants. We therefore standardize scores within ancestry. The 25(OH)D ancestry-specific score study reports that European weights explained 0.14% of variance in African-ancestry individuals versus 0.31% for ancestry-matched weights. That ratio tells us how much less reliable the score is, and we use it to set noise levels in simulation and to correct interaction estimates. Gorfine et al. show that residual-inclusion and substitution estimators behave differently under logistic non-collapsibility. This is why we compare groups on the marginal risk-difference scale rather than on stratum odds ratios.

Research Program

The estimator has three stages.

In the first stage, we regress the exposure modifier (greenness or blue-space proximity) for all individuals jointly on a shared spatial basis. We use thin-plate splines or eigenvectors of the area adjacency graph, as Spatial+ does, plus individual covariates. This yields one estimated smooth field and individual residuals. The ancestry groups share this field.

In the second stage, we fit the outcome model. It includes group-specific slopes for pollutant × residualized-modifier and polygenic score × residualized-modifier, and a shared spatial term. For binary outcomes, we convert the fitted model into group-specific marginal risk differences by g-computation. G-computation means predicting each person's risk under counterfactual exposure levels and averaging the predictions.

In the third stage, the polygenic interaction for each group is corrected for that group's score reliability by regression calibration, which divides out the attenuation implied by the score's ancestry-specific explained variance.

Alongside the estimates we report three diagnostics per group. The first is the fraction of that group's modifier variance that survives residualization, which we call effective spatial support. The second is the overlap of the group's residential distribution with other groups. The third is the assumed score reliability. When effective support falls below a threshold, we report that the between-group comparison is not identified from the data, instead of reporting a noisy estimate. We consider this refusal as important a product as the estimator itself.

The method assumes that the confounder is shared by place. That assumption fails if, within the same neighborhood, unmeasured confounding differs by ancestry, for example through discrimination in housing quality on the same street. We test this failure mode directly in simulation and do not claim it away.

Baselines

The naive reference is a pooled logistic or Cox model. It contains pollutant × modifier × ancestry interaction terms, coordinates and area deprivation as linear covariates, and no spatial deconfounding. This is the design of most buffering studies and of Chen et al.. A second reference adds a conditional autoregressive random effect, the usual spatial-statistics answer. Urdangarin et al. (2022) reports that this kind of model biases the coefficient upward (0.4603 against a truth of 0.2000 in their high-confounding scenario).

The strongest existing competitor is Spatial+ run separately within each ancestry stratum. This is what a careful analyst would do today with the published tools. In the homogeneous-population setting it is the best-documented method on the file's benchmarks. It reached 0.1861 against a truth of 0.2000 with about 95% coverage in Urdangarin et al. (2022), and SpaCE reports it as the top performer for binary treatments. No reported result was found on Lacuna for Spatial+ on stratified or individual-level multi-group data. We also include the Spatial Deconfounder run per stratum as a learned-confounder competitor. Its paper reports predictive-check p-values near 0.5 on SpaCE but gives no effect-error figures in the file. A further competitor is within-area fixed effects (neighborhood indicators) with group-specific slopes.

All methods receive the same individuals, the same covariates, the same basis families, and the same tuning budget. We use an equal number of basis-dimension choices, selected by the same spatially blocked cross-validation that SpaCE uses. Every method also receives the same within-ancestry score standardization, so that only the deconfounding strategy differs.

Two ablations isolate the key ingredients. The first keeps everything in our estimator but estimates the field within each stratum. This isolates the pooling. The second keeps pooling but drops the reliability correction and the marginal risk-difference scale. This isolates those two corrections.

Our method beats the strongest competitor if three conditions hold. Under a true null of no ancestry difference in buffering, it must hold the false-positive rate for "ancestry modifies buffering" near 5% where per-stratum Spatial+ exceeds it. It must keep coverage of the between-group difference within a few points of 95% across segregation levels. And it must do this at no worse power when groups are well mixed.

Why not just…?

Why not just run Spatial+ separately within each ancestry group? This is the most direct threat. When groups are well mixed it should do about as well as our estimator, and we expect our simulations to show exactly that. The problem appears with segregation. A small group concentrated in a few neighborhoods has a confounder field that is estimated from few locations. The residualization can then absorb most of that group's exposure variation. Each group's basis also absorbs a differently biased piece of the confounder. Both effects create spurious between-group differences. The segregation sweep in our benchmark settles this question. If per-stratum Spatial+ matches our estimator at realistic segregation levels, the contribution reduces to the diagnostics, and we would say so.

Why not just add neighborhood fixed effects with group-specific slopes? This is a real threat. It is the crudest form of the "the confounder belongs to the place" idea, and it is easy to explain to epidemiologists. It fails in two predictable situations. The first is when the confounder varies smoothly within the fixed-effect units, so that coarse areas leave confounding behind. The second is when areas are made fine enough to remove that confounding, at which point small ancestry groups have almost no within-area exposure variation. The pooled smooth field is meant to sit between these two extremes. We will vary fixed-effect granularity in the benchmark. If some granularity matches our estimator on bias, coverage, and power, we will recommend fixed effects at that granularity plus our support diagnostic.

Why not just use better multi-ancestry polygenic scores and ignore the spatial part? Better scores fix one of the three artifacts and leave the other two untouched. Within-ancestry standardization repairs scale shifts (On cross-ancestry cancer polygenic risk scores). Even so, reliability stays lower where the training GWAS is small (25(OH)D study), and none of this addresses the shared geographic confounding. Our design crosses score reliability with spatial confounding, so the experiments show how much of the spurious difference each source contributes.

Why not just compare stratum-specific odds ratios, as most papers do? Odds ratios are non-collapsible. Groups with different baseline incidence, as is typical for psoriasis or stroke across ancestries, can show different odds ratios with identical underlying effects (Gorfine et al.). We report both scales and count how often they disagree about whether modification is present.

Proposed Experiments

The semi-synthetic benchmark starts from the SpaCE real US grid- and county-level exposures and covariates. We keep its Gaussian Markov random field confounders and spatially blocked splits. Within each spatial unit we simulate individuals with ancestry labels. Group locations are drawn so that a dissimilarity index sweeps from fully mixed to highly segregated. Each individual receives a polygenic score whose reliability in each group is set to match the reported European-to-African transfer ratio (0.14% versus 0.31% explained variance). Outcomes are binary, with true group-specific buffering effects that are either equal (the null) or different by a known margin.

We cross three factors: segregation level, confounding strength (using SpaCE's confounding scores), and score reliability. We also add a scenario in which the confounder truly differs by ancestry within the same place, to measure where our estimator breaks. The metrics are bias and 95% coverage of the between-group difference in marginal buffering risk difference, the false-positive rate under the null, and power under the alternative. We additionally check the single-population case against the Uttar Pradesh and Spanish census scenarios from Urdangarin et al. Pooling with one group should reproduce their Spatial+ estimates (0.1861 and −0.1432), which tests our implementation.

The real-data analysis re-examines the blue-space × polygenic-risk interaction for psoriasis reported by Chen et al.. We use the UK Biobank's European, African, East Asian, and South Asian participants, with satellite greenness and accessible-park measures as parallel exposures following Hart et al.. Non-European groups in this cohort are small and psoriasis is uncommon. The effective-support diagnostic is therefore central: we expect it to say that some between-ancestry comparisons are not identified, and we will report that outcome as a finding.

The decisive checks are three. First, in the simulated null, does per-stratum deconfounding produce apparent ancestry modification that the pooled-field estimator does not? Second, in the European subgroup alone, does the published interaction survive Spatial+-style deconfounding at all? Third, for the remaining groups, does any between-ancestry difference persist after the reliability correction and on the risk-difference scale?