Mendelian randomization (MR) asks whether an exposure causes a disease by using inherited DNA variants as natural experiments. Because alleles are dealt out at random at conception, a variant that raises an exposure acts like a coin-flip treatment assignment. In the two-sample version, one study estimates each variant's effect on the exposure, a second study estimates its effect on the disease, and the causal effect is roughly their ratio. A growing share of MR uses molecular exposures, especially gene expression measured by RNA sequencing, with variants near the gene as instruments ("cis-MR"). This note points to a failure mode that the MR toolkit cannot see. RNA reads are counted by aligning them to a single linear reference genome. Reads carrying a non-reference allele, a short insertion or deletion, or sequence missing from the reference align less often. A person's measured expression therefore depends on their genotype even when their true expression does not. That technical association inflates or distorts the variant-to-exposure effect in the first study and leaves the variant-to-disease effect in the second study untouched, so the ratio is biased.
The core proposal is to measure how much of the expression-side signal behind published-style cis-MR instruments is alignment artifact, and to test whether re-quantifying expression against a pangenome graph removes it. A pangenome graph is a reference that encodes many human haplotypes, including structural variants and non-reference insertions, as alternative paths. The test runs against a simpler fix that corrects only single-base alleles. If the graph removes artifact that the simpler fix leaves behind, mainly at loci near insertions, deletions and non-reference sequence, then expression-instrumented MR needs graph-aware quantification. If it does not, the contribution shrinks to an audit and a cheap filter, and we will say so.
Core Claim
The two directions meet at one specific point: the measurement of the exposure, not the genotypes. Consider genotype-side reference bias first. When the same misclassification affects the exposure and outcome GWAS (genome-wide association studies) alike, it shrinks both coefficients by roughly the same factor, and much of it cancels in the ratio. It becomes a problem mainly when the two studies use different references or pipelines. Exposure-side artifact does not cancel. Write $\beta_X$ for the true variant–expression effect, $\delta$ for the alignment-induced association between genotype and measured expression, $\beta_Y = \theta\beta_X$ for the variant–outcome effect, and $\theta$ for the causal effect. The single-instrument Wald ratio then estimates
$$\hat\theta \approx \frac{\theta\,\beta_X}{\beta_X + \delta}.$$
When $\delta$ shares the sign of $\beta_X$, the estimate is attenuated. When $\delta$ opposes $\beta_X$, the estimate is inflated or flips sign. When $\beta_X \approx 0$ and $\delta \neq 0$, a gene with no genetic regulation acquires an apparently strong instrument whose ratio estimate is near zero. That last case can mislead tests that select instruments by first-stage strength.
The artifact is carried by every variant in linkage disequilibrium (LD, the correlation between nearby variants inherited together) with the mis-mapped allele. Two consequences follow. Every correlated instrument carries a $\delta$ of consistent sign, so the bias looks like genuine signal rather than heterogeneity. And cis-MR often has one or a few instruments. Under those conditions, pleiotropy-robust estimators and outlier tests have nothing to work with.
The new claim has two parts. First, $\delta$ is measurable at scale by simulation from known haplotypes. Second, a substantial part of it comes from variant classes that a linear reference cannot represent at all. Wu et al. found that 154 non-reference sequences are in strong LD with 258 GWAS Catalog SNPs and that 565 expression associations sit on such sequences (Human pangenome analysis of sequences missing from the reference genome). Sudmant et al. report that a structural variant is roughly 50 times more likely than a SNP to be an expression-associated variant (An integrated map of structural variation in 2,504 human genomes). Both observations predict that expression signals near these variants mix biology with mapping loss.
Relation to Prior Work
Three papers motivate the proposal. Wu et al. built GraphNRS, a graph containing 45,284 non-reference sequences, which raised RNA read mapping by 1.07%. They used it for association and expression mapping and never asked whether the linear-reference expression signals at those loci were artifacts or how that would affect causal estimates. Sudmant et al. catalogued 68,818 structural variants and showed how they tag GWAS haplotypes, without any instrumental-variable analysis. The Human Pangenome Project documents that roughly 70% of GRCh38 comes from one donor and supplies the diploid assemblies we use as ground truth. Our contribution is to move from "these variants exist and associate" to "here is how much they distort an MR ratio, and here is what fixes it."
Two papers constrain the design. Assessing graph-based read mappers against a baseline approach shows that full graph mappers misalign some reads that carry no variant, and that a carefully tuned linear mapper closes much of the apparent gap. The graph could therefore create new $\delta$ at loci where the linear pipeline was fine. We measure artifacts in both directions rather than assume the graph is cleaner. Ancestry Bias in Genetic Causal Inference attributes the cross-ancestry breakdown of MR to LD and allele-frequency differences. We test whether part of that breakdown is instead a larger $\delta$ in ancestries that diverge more from GRCh38. Sudmant et al. report about 27% more heterozygous deletions in African-ancestry genomes, which makes this plausible.
Two lines of work supply methods. MAGIC (Mediation Analysis with Mendelian Randomization and Efficient Multiple GWAS Integration) corrects selection bias and Gaussian sampling error in summary statistics. It restores 95% confidence-interval coverage where two-step MR and multivariable MR fall to 70–80% in its simulations. Its error model is zero-mean noise, whereas $\delta$ is a systematic, genotype-locked offset. We use MAGIC-style correction as a competitor and show what it cannot absorb. For genotyping on graphs we reuse KAGE (KAGE), which reports SNP F1 of about 0.955 on HG006. We reuse graph alignment tooling from the vg ecosystem as deployed in VG-Pedigree (A complete pedigree-based graph workflow), which reports 4,844 fewer variant errors than BWA-MEM on HG001. We also borrow MR's standard estimators: inverse-variance weighting, weighted median, MR-Egger and MR-PRESSO, as reviewed in Pleiotropy Robust Estimation in Mendelian Randomization.
Research Program
The first component is a ground-truth simulator for null and planted expression effects. We generate personalized diploid transcript sequences from two sources: the 94 HPRC haplotypes, and the 1000 Genomes phased SNP haplotypes with the Sudmant structural-variant callset and GraphNRS non-reference sequences overlaid. We then simulate RNA-seq reads in which true expression is either independent of genotype (null) or has a planted cis effect $\beta_X$. Any association detected under the null is pure $\delta$. Comparing the detected and planted effect gives $\delta$ under the alternative. This yields a per-locus artifact map, stratified by variant class (SNV, indel, structural variant, non-reference sequence), by whether the variant lies inside the quantified transcript or only in LD with it, and by ancestry.
The second component is a set of matched quantification pipelines applied to identical reads: standard linear alignment to GRCh38; linear alignment followed by allele-swap remapping, in which each read is re-aligned with its overlapping alleles flipped and discarded if it maps differently; and graph alignment to an HPRC-plus-GraphNRS graph, with reads projected back to gene coordinates. Each pipeline produces expression-association summary statistics for every gene, both on the simulated cohorts and on the real GEUVADIS RNA-seq that Wu et al. analyzed. GEUVADIS samples belong to 1000 Genomes, so their structural variants are known.
The third component propagates each pipeline's exposure statistics through cis-MR against real outcome GWAS. We hold the outcome data fixed, so any change in $\hat\theta$ comes from the exposure side. The outcomes come from the file: blood pressure from the UK Biobank cohort used by Lin et al. (n = 286,390), BCAC breast cancer used by Zhang et al. (133,384 cases), and FinnGen R10 hepatocellular carcinoma used by Yuan et al.. On real data the truth is unknown. There we report how often conclusions change (sign, significance, and the magnitude of the shift in $\hat\theta$) and check whether the changes concentrate at loci the simulator flags as artifact-prone.
Baselines
The naive reference point is standard practice: expression quantified against linear GRCh38, cis instruments chosen by first-stage F-statistic, inverse-variance weighting. On simulated data its error in $\hat\theta$ sets the bar. Every other method is judged by how much of that error it removes and at what cost in retained instruments.
The strongest competitor is linear alignment with allele-swap remapping, because it targets exactly the single-base allelic mapping loss that probably makes up most of $\delta$. It needs no new reference. It runs on the same reads, same aligner and same compute as the naive pipeline. We found no reported result on Lacuna for allele-swap remapping in an MR setting, so its performance is established here rather than quoted. The graph pipeline beats it only if, on the simulator, it removes a statistically clear additional fraction of null-simulation false associations and of $\hat\theta$ error. That margin must be concentrated at indel, structural-variant and non-reference-sequence loci. The graph must also avoid creating more new artifact at variant-free loci than it removes.
A tuned linear mapper is run as described by Grytten et al.. BWA-MEM is parameterized for accuracy and mapping quality is recalibrated with Minimap2. This tests whether the graph's gain is just better alignment parameters. It gets the same tuning budget as the graph pipeline, namely a parameter sweep on held-out simulated chromosomes.
On the statistical side we run MR-PRESSO, weighted median, MR-Egger, and a MAGIC-style measurement-error correction on the naive exposure statistics. These test whether downstream estimation can absorb $\delta$ without touching the reads. The reference number is MAGIC's restoration of 95% coverage from 70–80% in its own simulations. We report coverage of these estimators under our artifact simulations. Beating them means our pipeline reaches nominal coverage where they do not.
An ablation isolates the key ingredient. We run the graph pipeline with a graph containing only SNVs and short indels, then with structural variants and non-reference sequences added. If the gap between these two graphs is negligible, non-reference content does not matter, and the allele-swap baseline is effectively the answer.
Why not just…?
Why not just use allele-swap remapping on the linear reference? This is the real threat, and the proposal is designed so it can win. Allele swapping can only correct alleles that exist as alternative bases at reference positions. A read that spans a non-reference insertion has no place to land in either swapped or unswapped form. Deletions and complex structural variants produce partial alignments that swapping does not repair. The 1.07% RNA mapping gain from GraphNRS is a lower bound on what swapping cannot recover, though it does not say how much of that gain falls on expression instruments. The simulator's stratified $\delta$ map settles the question. If residual artifact after swapping is small at structural-variant and non-reference loci, we recommend swapping and drop the graph claim.
Why not just drop any instrument whose LD block overlaps the measured transcript? This filter is cheap and probably removes much of $\delta$. Its cost is that cis instruments for a gene sit, by definition, near that gene, so the filter may leave many genes with no instrument or only weak ones. The filter also cannot see artifacts from non-reference sequences or structural variants that are poorly tagged by SNPs. We report, per pipeline, the fraction of genes still instrumentable at F > 10 and the remaining $\hat\theta$ error. If the filter matches the graph pipeline at acceptable instrument loss, it becomes the recommended practice.
Why not just rely on robust MR estimators or MAGIC? The artifact enters every LD-correlated instrument with a consistent sign. It therefore creates neither heterogeneity for Cochran's Q or MR-PRESSO to flag nor an intercept for MR-Egger to detect. The weighted median helps only if fewer than half the instrument weight is affected, which fails when the gene has one LD block. MAGIC's correction assumes zero-mean error and balanced pleiotropy, and $\delta$ is neither. The coverage experiments above test this directly rather than argue it.
Why not just tune the linear mapper? Tuning improves how reads that can be placed are scored. It cannot place sequence that is absent from the index. The tuned-mapper baseline quantifies how much of $\delta$ is a parameter problem and how much is a missing-sequence problem.
Proposed Experiments
The decisive experiment is the null simulation. Under genotype-independent expression in 2,504 simulated 1000 Genomes individuals, we count genes with an expression association at the usual cis threshold under each pipeline and break the false associations down by variant class and ancestry. Three outcomes would falsify the motivating claim: no excess over the nominal false-positive rate in the naive pipeline, an excess that allele-swap removes completely, or an excess that graph alignment worsens.
Under planted effects we then report three quantities per pipeline: bias and root-mean-square error of $\hat\theta$, confidence-interval coverage, and the fraction of genes with a usable instrument.
On real GEUVADIS data we compute, for each gene, the difference between naive and graph-based exposure effects. We test whether that difference is predicted by the simulator's artifact score, using rank correlation across genes. We then propagate both sets of statistics through cis-MR against the blood pressure, breast cancer and liver cancer outcomes and report how many gene–outcome conclusions change sign or significance.
Finally, the ancestry check splits GEUVADIS by population. It asks whether between-population heterogeneity in $\hat\theta$ shrinks after graph re-quantification. A meaningful shrinkage would show that part of the cross-ancestry instability attributed to LD in Ancestry Bias in Genetic Causal Inference is a reference artifact.
References
- Human pangenome analysis of sequences missing from the reference genome reveals their widespread evolutionary, phenotypic, and functional roles
- An integrated map of structural variation in 2,504 human genomes
- The Human Pangenome Project: a global resource to map genomic diversity
- Assessing graph-based read mappers against a baseline approach highlights strengths and weaknesses of current methods
- Mediation Analysis with Mendelian Randomization and Efficient Multiple GWAS Integration
- KAGE: fast alignment-free graph-based genotyping of SNPs and short indels
- A complete pedigree-based graph workflow for rare candidate variant analysis
- Association between inflammatory proteins and rotator cuff tears: a bidirectional Mendelian randomization study
- The causal associations of circulating amino acids with blood pressure: a Mendelian randomization study
- Complex Role of Circulating Triglycerides in Breast Cancer Onset and Survival: Insights From Two‐Sample Mendelian Randomization Study
- The impact of metabolic syndrome on hepatocellular carcinoma: a mendelian randomization study