Causal Inference Below the Detection Limit: Ancestry-Shifted Assay Censoring in Biomarker Mendelian Randomization

When an instrument cannot measure a biomarker reliably, the reading is not missing at random — it is clamped at a detection limit, or reported as a substitute value like half the limit. Analytical chemists know this well: portable X-ray fluorescence detects only 36 of 92 candidate elements in stream sediments, with reliability collapsing for light elements like aluminum The Application of Portable X-ray Fluorescence (pXRF) for Elemental Analysis of Sediment Samples in the Laboratory and Its Influencing Factors, and trace purines such as adenine and hypoxanthine fall entirely below the limit of quantitation in some plant cultivars UFLC-MS/MS quantification of amino acids and nucleosides in Mume Fructus. Genetic epidemiology, by contrast, pretends biomarkers are clean Gaussian traits. Mendelian Randomization (MR) — which uses genetic variants as natural-experiment instruments to test whether a biomarker causally affects disease — is routinely run on genome-wide association summary statistics built from measurements that were never screened for censoring, and then transported across ancestral populations whose biomarker distributions sit at different distances from the assay's noise floor.

The core claim of this proposal is that these two failures compound. Population differences in baseline nutrition, renal function, and protein binding shift a biomarker distribution toward or away from the physical detection limit, so the same assay censorst different fractions of each ancestry. Censoring is nonlinear: near the limit, the measured signal decays into noise rather than scaling linearly, as the sediment-scanning work shows — water in the sample matrix alone explained 43% of elemental measurement deviations, with accuracy dropping by up to 40% above a 47–52% moisture threshold Application of Corrected Methods for High-Resolution XRF Core Scanning Elements in Lake Sediments. Fed into a linear GWAS, censored measurements attenuate gene–biomarker associations unevenly across the genome and across populations, which corrupts both the relevance of MR instruments and the exclusion restriction (the assumption that instruments act on disease only through the biomarker). The result is that apparent "ancestry-specific biology" in cross-population biomarker MR may in part be a measurement artifact — and nobody has a framework to tell the two apart.

Background and Why This Gap Is Open

Three lines of work stop short of this intersection. The mineral-metabolism MR study of calcific aortic valve stenosis is the closest on the genetics side: it inferred that genetically elevated FGF23 causally increases stenosis risk (discovery odds ratio 3.081, replication 2.280, colocalization PP.H4 = 0.96), while calcium, phosphate, vitamin D, and parathyroid hormone showed no causal effect — but both cohorts were exclusively European, and the authors explicitly flag that transferability to non-European ancestries is unknown Genetic association of serum calcium, phosphate, vitamin D, parathyroid hormone, and FGF23 with the risk of aortic stenosis. It also treats all five biomarkers as fully continuous, with no consideration of assay limits. The 35-biomarker MR study of postmenopausal osteoporosis shares both blind spots, running entirely on UK Biobank and FinnGen with linear assumptions throughout A Mendelian randomization study investigating the causal relationship between 35 blood and urine metabolite biomarkers and postmenopausal osteoporosis. On the portability side, the X-Wing framework quantifies how genetic effects are portable only in specific genomic regions — for mean corpuscular volume, ~1% of the genome carries over 60% of the cross-population genetic covariance — and improves multi-ancestry risk prediction by a median 35.2% in East Asian cohorts Quantifying portable genetic effects and improving cross-ancestry genetic prediction with GWAS summary statistics; but it targets prediction scores, not the validity of causal instruments, and assumes the input traits are well measured. Finally, the work on stable biomarker detection defined the Zero Index Crossing — the rank at which selected features decay into noise — and showed that naive statistics suffer hub confounding Stability of Bivariate GWAS Biomarker Detection; this gives us a usable mathematical notion of a statistical detection limit, but it was developed purely on European WTCCC data and never connected to physical assay limits or ancestry.

Two further papers motivate the design rather than constrain it. The monogenic diabetes study showed that a single biomarker threshold (BMI) derived in one population produces an 80% misdiagnosis rate and a 10-year diagnostic delay in others, with true monogenic prevalence invariant (2.1–3.6%) across ancestries — ethnicity-specific cut-offs doubled the detection rate from 8.8% to 16% and cut the number needed to test from 11 to 6 Precision diagnosis for monogenic diabetes requires ethnicity specific criteria for genetic testing. That is the clinical symptom of exactly the matrix effect we want to model genetically. And the cross-ancestry null MR study of psychiatric disorders and glaucoma demonstrates that consistent nulls across Europeans and East Asians are themselves informative Mendelian randomization study shows no causal relationship between psychiatric disorders and glaucoma in European and East Asian populations — a tool we will use for calibration.

Research Program

The program has three components. First, a measurement model: write the observed biomarker as a censored transformation of the true value, $y^{\text{obs}} = \max(y, L)$ when the assay reports a floor value, or as $y^{\text{obs}} = y \cdot \mathbf{1}[y > L] + L/\sqrt{2} \cdot \mathbf{1}[y \le L]$ when the lab substitutes the standard fill value, where $L$ is the ancestry- and assay-specific detection limit. The key quantity is the censoring fraction per ancestry, $\pi_a = \Pr(y \le L \mid \text{ancestry } a)$, which differs across populations because the pre-censoring distribution of $y$ differs. The nonlinear clamping means GWAS effect estimates on $y^{\text{obs}}$ are attenuated by an ancestry-specific, non-constant factor, so the same SNP is a weaker instrument in the population whose distribution sits closer to the floor.

Second, an estimator: replace the standard linear GWAS inside the MR pipeline with a censored-normal (Tobit-type) association model that takes $L$ as a known input, producing corrected summary statistics; then run trans-ancestry MR on the corrected statistics, adapting the local-correlation scanning idea from X-Wing Quantifying portable genetic effects... to decide, region by region, whether to pool or keep ancestry-specific instruments. We will also extend the Zero Index Crossing of Bedo et al. Stability of Bivariate GWAS Biomarker Detection into a censoring-aware ZIC: the boundary rank at which instrument selection degrades into noise, now measured as a function of $\pi_a$, so the field gets a practical rule for when a biomarker is simply too censored in a given population to support causal inference at all.

Third, an empirical re-analysis of the mineral-metabolism panel — FGF23, calcium, phosphate, alkaline phosphatase, uric acid, and related circulating markers — across UK Biobank (European), BioBank Japan and China Kadoorie Biobank (East Asian), and PAGE (African and admixed), asking whether the causal links established in Europeans survive censoring-aware correction and cross-ancestry transfer, and whether apparent cross-ancestry discrepancies vanish once measurement is modeled. For FGF23–stenosis specifically, no cross-ancestry estimate of any kind exists — no reported result found on Lacuna for cross-ancestry MR of FGF23 and aortic stenosis — which is precisely the open hole flagged by the original authors.

Proposed Experiments

The simulation study is the engine of the proposal, because only there is ground truth known. We will take real biomarker GWAS from UK Biobank, generate synthetic individual-level data matching each ancestry's allele frequencies, LD structure, and biomarker distribution (parameterized from published biobank summary statistics), then impose detection limits at a range of placements calibrated to reality: from benign ($\pi_a < 1\%$ in every ancestry) to the regime documented analytically, where a fixed instrument leaves most of one group's measurements unquantifiable — as in the trace purines that fell below the limit of quantitation in specific cultivars UFLC-MS/MS quantification..., or the 56 of 92 elements that portable XRF simply cannot see regardless of effort The Application of Portable XRF.... We sweep $\pi_a$ from 0 to 50% and record bias, confidence-interval coverage, and sign-error rate of causal estimates for three pipelines: naive MR on censored statistics, MR on fill-value-imputed data, and our censoring-aware estimator. The decisive readout is a bias curve: if naive and imputed pipelines show bias growing sharply once $\pi_a$ exceeds a threshold in any ancestry while ours stays flat, the compounding claim is established. The moisture-threshold result of Zhang et al. — accuracy loss of up to 40% above a physical threshold that varies by element Application of Corrected Methods... — is the empirical template for expecting exactly this kind of nonlinear breakdown.

The real-data study then applies all pipelines to the mineral biomarkers in the postmenopausal osteoporosis panel A Mendelian randomization study investigating... and the FGF23 panel Genetic association of serum calcium..., re-run per ancestry and pooled. Alkaline phosphatase (reported OR 1.26 in Europeans) and uric acid (OR 0.76) are attractive test cases because East Asian and African biobanks carry the same assays, so any estimate divergence is attributable to distribution position and LD, not assay platform. Where a null is expected — the psychiatric-disorder–glaucoma pairs that were null in both Europeans (e.g., depression OR 1.15, P = 0.20) and East Asians (OR 1.38, P = 0.30) Mendelian randomization study shows no causal relationship... — we verify that censoring correction does not manufacture false positives, which is the type-I calibration check.

A secondary application connects back to the clinical matrix effect: using the BMI-threshold structure of the monogenic diabetes study Precision diagnosis..., we will test whether the detection-rate asymmetry it observed (39% in White versus 11% in South Asian participants under tailored cut-offs) can be reproduced by a censoring model in which the screening biomarker sits closer to its effective floor in one group — a proof of concept that the same mathematics covers diagnostic thresholds and assay floors.

Baselines

The do-nothing reference point is naive two-sample inverse-variance-weighted MR applied directly to the censored summary statistics as published, per ancestry, with the same LD reference panels and the same Bonferroni threshold (0.05/5) used by the mineral-metabolism study Genetic association of serum calcium.... This is what a careful analyst would produce today, and it is the benchmark for quantifying how much censoring actually costs.

The strongest existing competitor is GSMR — Generalized Summary-data-based Mendelian Randomization — which pools multiple correlated instruments while accounting for linkage disequilibrium and sampling variance, and pairs the HEIDI-outlier test to purge pleiotropic instruments and mtCOJO to condition on correlated risk factors Causal associations between risk factors and common diseases inferred from GWAS summary data. It is the strongest competitor because it is the only framework in the file that already handles pleiotropy detection and instrument heterogeneity at scale — it mapped 45 causal links across cohorts of up to 405,072 individuals, including a 3.29-fold type-2-diabetes risk increase per standard deviation of BMI, and its HEIDI-outlier test famously dissolved a spurious LDL–Alzheimer's association by removing 16 pleiotropic SNPs in the APOE region. We will run GSMR under three conditions — on raw censored statistics, on fill-value-imputed statistics, and on our censoring-corrected statistics — with identical instruments, LD panels, and significance thresholds, so that any difference is attributable to the censoring model alone. Beating GSMR means: in simulation, causal-effect bias and sign-error rate strictly lower than GSMR-on-censored-data at matched sample size, with honest coverage; in real data, cross-ancestry estimates whose divergence from European estimates shrinks after correction in the directions the censoring fractions predict.

Two ablations isolate the proposal's ingredients. The first is censoring-aware but single-ancestry: corrected GWAS feeding ordinary per-ancestry MR. This isolates the measurement model and tests whether correction alone recovers most of the benefit. The second is ancestry-aware but censoring-blind: trans-ancestry local-correlation scanning in the X-Wing style Quantifying portable genetic effects... applied to raw statistics. This isolates the multi-ancestry LD modeling and tests whether the portability machinery, applied without measurement correction, mislocalizes portable regions. If the combined pipeline does not beat both ablations somewhere, the compound claim is weakened to whichever ablation wins — and we will say so.

Why Not Just…?

Why not just run MR separately in each ancestry and compare? This is the obvious first move, and it is a partial solution: separate analyses escape cross-ancestry LD mismatch but do nothing about censoring, because the censoring bias lives inside each ancestry's GWAS before any transport happens. Worse, per-ancestry analysis can manufacture spurious ancestry-specific effects precisely when censoring fractions differ, which is the failure mode this proposal targets. The simulation will show this directly: at matched sample size, per-ancestry naive MR on censored statistics should exhibit ancestry-dependent attenuation that correction removes. If it does not — if bias is negligible at realistic censoring fractions — the proposal's premise fails and we will report that honestly.

Why not just impute values below the limit with LOD/2 or LOD/√2? This is standard epidemiological practice and costs almost nothing, so it must be tested as a baseline rather than argued away. The analytical-chemistry evidence says it falls short: near a physical threshold the response is nonlinear, not a constant-offset clamp — water content explained 43% of deviations and accuracy degraded by up to 40% past a threshold Application of Corrected Methods..., and simple count-time and particle-size fixes recovered correlations only for a subset of elements The Application of Portable XRF.... A constant fill value compresses the below-limit mass into a spike that linear models read as a real signal. We expect the imputation baseline to reduce but not remove bias, and to distort significance most when $\pi_a$ is large in one ancestry only; the simulation will settle it quantitatively.

Why not just improve the assays instead of the statistics? Where feasible this dominates — nobody should prefer a correction model to a clean measurement. But it does not address the actual situation: the causal-inference literature runs on existing summary statistics from hundreds of thousands of individuals that cannot be re-measured, and some analytes are near or below physical floors in specific populations no matter the instrument, as the 56 undetectable elements show The Application of Portable XRF.... The realistic choice is between doing inference on censored data blindly or with an explicit measurement model, and the X-Wing result — that we must squeeze portability out of summary statistics we already have Quantifying portable genetic effects... — supports the second path. Where re-measurement is possible, our censoring-fraction estimates tell the field which ancestry–analyte pairs genuinely need it.

Why not just use X-Wing directly? It is the closest methodological threat because it already solves local cross-ancestry portability with summary statistics. But it was built for prediction scores, not for testing the three instrumental-variable assumptions, and it assumes the input traits are measured without floor effects. We borrow its local-scanning machinery for the pooling decision, so the honest test is the second ablation above: if X-Wing-style scanning on raw censored statistics matches our full pipeline, then the censoring model adds nothing and the contribution collapses to a modest extension of existing work. We consider this a real possibility and have designed the ablation to detect exactly it.

Decisive Checks and Closing

Three findings would make the case. In simulation, a bias-versus-censoring-fraction curve showing nonlinear breakdown for naive and imputed pipelines and flat behavior for the corrected one, with the censoring-aware Zero Index Crossing giving a usable rule for when a biomarker supports causal inference in a given population. In real data, cross-ancestry re-analysis of the mineral panel showing which of the European-derived causal links — FGF23 on stenosis at OR 2.280 in replication Genetic association of serum calcium..., or alkaline phosphatase on osteoporosis at OR 1.26 A Mendelian randomization study investigating... — survive correction and transfer, with no false positives manufactured on the psychiatric–glaucoma nulls Mendelian randomization study shows no causal relationship.... And the conceptual deliverable: a demonstration, in the spirit of the monogenic diabetes thresholds Precision diagnosis..., that some apparent ancestry-specific biology in biomarker epidemiology is the sample matrix talking, not the genome.