52 — From association to mechanism
Before this: Ch 51 — GWAS · Ch 29 — Linkage disequilibrium · Ch 22 — Eukaryotic transcriptional regulation · Time: ~55 min
Statistics needed: S1 Probability · S4 Hypothesis testing · S5 Variance and regression · S6 Likelihood and Bayes
The Catalog holds over a million reported associations. The number for which we can name the causal variant, the gene, the cell type and the direction of effect is a very small fraction of that. This chapter is about the gap, which is where the last two decades of human genetics went.
What you'll be able to do
- Formulate as Bayesian variable selection under near-perfect collinearity, and state what a 95% asserts and what it does not
- Derive the sample size needed to separate two candidate variants from their LD, and use it to explain why multi-ancestry data buys resolution that more of the same ancestry cannot
- Rank nearest-gene, , , and chromatin evidence by what each establishes, and read
colocoutput without the standard misinterpretation - Distinguish the sufficiency claim an tests from the necessity claim a perturbation tests, and say which a clinical interpretation needs
- Give the current explanations for why eQTLs fail to account for most disease loci, including the selection argument
- State the three instrumental-variable assumptions behind , name the untestable one, and read a sensitivity analysis
The core idea
A Manhattan-plot peak is a claim about a region, in one population, at one moment in that population's history. Which base, which gene, which cell, which direction — all of it is recovered afterwards, and each recovery is a separate inference with its own assumptions.
The difficulty is structural. Recombination has shattered into (Ch 29), and within a block every variant is a near-copy of every other: a design matrix whose columns correlate at 0.95 and above, from which you must pick the column carrying the effect. Then work out which of the ten or thirty genes within a megabase it acts on — and roughly 90% of lead variants lie outside protein-coding sequence, so the answer is almost never in the table.
An association identifies a set of variants that are statistically indistinguishable given the recombination history of your sample. Localisation is not a measurement you can improve by collecting more of the same data; it is bounded by how much recombination occurred, in the population you sampled, since the causal arose.
Everything below imports information from outside the association: from populations with different recombination histories, from , from expression, from contact maps, and finally from experiments that perturb the genome and watch.
1. The shape of the problem
One genome-wide-significant peak gives you 50–500 variants whose p-values lie within a few orders of magnitude of each other over 20–200 kb, and three distinct questions:
| Question | What it asks | Where the information comes from |
|---|---|---|
| Which variant? | Which correlated variant carries the effect | Recombination history: sample size, and above all LD contrast |
| Which gene? | Whose activity the variant alters | Expression, chromatin, contact, perturbation |
| Which context? | Which cell type, state and developmental window | Cell-type- and stimulus-resolved assays |
Solving one does not solve the others: you can pin the variant to a single base and have no idea what it does. The third question is the one most analyses skip, because the affordable assay is a bulk tissue from an adult post-mortem donor while the answer may live in a stimulated immune cell or a fetal neuron.
2. Fine-mapping is variable selection under near-perfect collinearity
Write the additive model over the m variants in the region, on standardised :
R is the LD matrix from Ch 29, and it is near-singular, so the OLS solution is numerically meaningless. The marginal statistics you actually have — a reports one regression per variant, not a joint fit — relate to the joint effects by
and inverting that means inverting the ill-conditioned object. Better linear algebra does not help. A sparsity prior does — the assumption that only a handful of variants in the region have non-zero effects.
Put a prior on configurations \gamma (which subset is causal) and on effect sizes, compute each configuration's marginal likelihood, and get a posterior over configurations. Two summaries fall out: the posterior inclusion probability (PIP) of variant j, the total posterior mass of configurations containing j; and the , the smallest set whose PIPs sum to ≥ 0.95.
Statistics: priors, marginal likelihoods and Bayes factors — the machinery this section assumes — are in S6 §5, with §6 on why a credible set is not a confidence interval and §7.4 running this exact PIP calculation on real LD.
The simplest version assumes exactly one causal variant, collapsing the space from 2^m to m. With Wakefield's approximate Bayes factor, prior effect variance W and squared standard error V:
Since V and W barely vary within a region, the PIPs are a softmax over z_j^2/2 — a temperature-scaled softmax of the chi-square statistics, and nothing more.
Relaxing the one-variant assumption matters, because allelic heterogeneity is common and a two-signal locus fitted with a one-signal model returns a credible set centred on a compromise variant causal for neither. Stochastic search (FINEMAP and relatives) explores the 2^m space with a shotgun search allowing up to L causal variants, paying for its generality in compute. Sum of single effects (SuSiE) instead decomposes \boldsymbol{\beta} = \sum_{l=1}^{L}\boldsymbol{b}_l with each \boldsymbol{b}_l holding one non-zero entry, fitted variationally as L single-variant fits on residuals. Its pay-off is representational: one credible set per signal, so independent signals appear as separate sets rather than blended, and the number of sets estimates how many there are.
Both have summary-statistics versions taking marginal z-scores plus a reference-panel LD matrix, and that convenience introduces the commonest practical failure: LD mismatch. If the reference R does not match the study sample — wrong population, wrong panel, a meta-analysis of cohorts with different structure — the implied system is inconsistent, and the method resolves the inconsistency by confidently nominating whichever variant explains the discrepancy. PIP 0.99 on the wrong base, no warning. Diagnostics comparing each observed z against the value its neighbours predict exist, and should be run every time.
What a 95% credible set actually asserts
Conditional on the model being right, there is 0.95 that this set contains the causal variant. The conditions are load-bearing and all fail sometimes:
- The causal variant is in the analysed data. A , or one absent from the panel, cannot receive posterior mass; the mass lands on its best tag instead.
- The effect is additive, and the true number of causal variants is within L.
- The LD matrix is correct for this sample, and the prior over which variants are causal (§4) is correct.
Note what it does not say. A variant with PIP 0.2 is not "20% causal", it holds a fifth of the posterior. It is not a frequentist confidence set and carries no guarantee. A singleton set at PIP 0.99 is a statement about a model, not a demonstration; the demonstration is §10.
3. Resolution is a property of LD, not of your method
Statistics: the non-centrality parameter λ, and why power is a function of λ rather than of effect size alone, are covered in S4 §4.
Let the causal variant c explain fraction R^2_c of trait variance, so its non-centrality is \lambda_c = N R^2_c (Ch 32). A candidate t correlated with it at r has \mathbb{E}[z_t^2] = r^2\lambda_c (Ch 29 §5). From the softmax above,
Demand a Bayes factor of at least B and solve for N:
Take B = 20 (so 2\ln B \approx 6) and a strong locus explaining 0.34% of trait variance:
| r^2 with the causal variant | N required to separate |
|---|---|
| 0.90 | 17,500 |
| 0.99 | 175,000 |
| 0.999 | 1,750,000 |
| 1.000 | impossible at any N |
For a median locus explaining 0.02% of variance, multiply every row by 17. The last row is not hyperbole: two variants in perfect LD produce identical columns, and no amount of data distinguishes identical columns. Sample size buys resolution linearly; LD costs it as 1/(1-r^2) — which is why sample sizes grew by two orders of magnitude over the last decade while credible-set sizes shrank by far less.
Why multi-ancestry samples are the efficient fix
r is a population parameter. Two variants in perfect LD in one population may sit at r^2 = 0.6 in another, because the populations have different recombination and demographic histories. Populations of African ancestry have larger long-term effective size and did not pass through the out-of-Africa bottleneck, so their LD blocks are roughly half as long — about 11 kb against 22 kb (Ch 29 §8). Shorter blocks mean sharper r^2 contrasts between neighbours, which is exactly the denominator in the boxed formula. Combining ancestries adds a second : the causal variant is associated in all of them, a tag only where it happens to be correlated. SuSiEx, MESuSiE and MultiSuSiE model per-population effect sizes with shared causal status, differing in how much they let magnitudes vary — a real choice, since the shared-causal-variant assumption fails where a locus has population-specific causal .
Three things must be said plainly. is not race: ancestry is a continuous, measurable property of a genome, estimated from data and varying within any social category, while race is a social classification that varies between countries and over time. The argument above concerns recombination histories and does not transfer to social categories. The advantage is demographic, not qualitative — African-ancestry are more finely shattered because more generations of recombination have acted on a larger population. And the under-representation of non-European samples is a sampling failure with consequences, costing the field resolution it could have had on top of producing that transfer badly (Ch 53). Fixing it means building cohorts with the communities involved, with governance and benefit-sharing attached, not extracting samples because the LD is convenient (Ch 58).
4. Functional annotation as a prior
The uniform prior over variants is obviously wrong: open chromatin in a trait-relevant cell type beats a closed heterochromatic desert. So replace it with
where A_{jk} are of variant j and the weights a_k are estimated genome-wide from the enrichment of association signal in each annotation, then applied locally. PAINTOR, fgwas and PolyFun-style approaches do this, and shrink, because the prior breaks ties the likelihood cannot.
Three cautions, all consequences of it being a prior. It cannot create information about which variant is causal, only reweight the survivors — a flat likelihood plus a confident prior returns the prior. It is circular if the annotation came from the same trait. And every PIP is now conditional on the annotation model, so two groups with different annotation stacks report different credible sets from identical summary statistics, both correctly.
5. Variant to gene: the nearest gene is a weak default
The nearest gene is used because it is free and right often enough to feel safe. Estimates of how often range from about a third to about two thirds depending on the benchmark — and the benchmarks are themselves biased, since a gold-standard set is assembled from loci where somebody already found the answer, which over-samples loci where the answer was findable, which over-samples coding and proximal mechanisms. The honest summary: nearest-gene is a strong baseline that good models beat, and it is wrong often enough that building on it unchecked will mislead you at a large minority of loci. The reasons are mechanistic, from Ch 22:
- act over distances up to ~1 Mb and routinely skip intervening genes.
- Their reach is shaped by boundaries as much as by linear distance (Ch 50): boundaries reduce cross-boundary regulation without abolishing it — acute or depletion blurs TADs while changing only modestly and selectively — so contact frequency is a better metric than distance, not a sufficient one.
- Gene density varies by an order of magnitude. At a dense locus "nearest" is near a coin flip; in a the answer may be 800 kb away.
- A variant can sit inside one gene — , 3′ UTR, even a neighbour's coding sequence — and regulate another, which makes the linear actively misleading.
- The effect may not be on expression level at all: , transcript stability, and protein-level effects can leave the transcript count untouched.
Machine-learning integrations — Open Targets' locus-to-gene model is the reference implementation — take distance, output, , chromatin interaction and functional predictions as features and train against a curated gold standard. The output is a calibrated score, which is the right format: a locus-to-gene score is a prioritisation, and prioritisation is what you do before an experiment, not instead of one.
6. eQTLs, and what they can and cannot see
An is a variant whose associates with a gene's expression level. Run Ch 47's pipeline on a few hundred people, normalise, correct for hidden confounders (PEER/ factors, which absorb batch and cell composition), and regress expression on genotype gene by gene.
The operational definition of cis is "within some window of the start site", conventionally 1 Mb; the mechanistic definition is "acting on the same physical copy", testable as -specific expression in heterozygotes and the cleaner claim. Trans is everything else, necessarily through a diffusible intermediate. The asymmetry is structural:
| cis-eQTL | trans-eQTL | |
|---|---|---|
| Tests per gene | ~10⁴ variants in the window | ~10⁷ genome-wide |
| Total tests | ~10⁸ | ~10¹¹ |
| Effect size | Often large — one allele on one | Small: mediated through a chain, each step lossy |
| Detected in | A few hundred samples | Tens of thousands |
| Main artefact | in allele-specific reads | Cell composition — a variant shifting blood cell proportions creates thousands of apparent trans effects |
GTEx is the reference cis resource: on the order of 50 tissue sites from close to a thousand post-mortem donors, the v10 release adding roughly a quarter more samples to the analyses than v8. For trans you need depth in one tissue — a meta-analysis of 31,684 blood samples (eQTLGen 1, Võsa et al. 2021) reports cis-eQTLs for about 88% of tested genes, and, for the ~10,000 trait-associated variants it could afford to test in trans, trans-eQTLs for roughly a third of them — invisible at GTEx sample sizes. Phase 2 extends this to a genome-wide trans scan in a larger sample and is not yet published.
Two things to carry. Tissue specificity is oversold as an explanation: many cis-eQTLs are shared across most tissues, and finding one only in liver may mean it acts only in liver, or that liver had the sample size. Bulk tissue dilutes: a variant acting in 2% of the cells produces roughly 2% of the true effect in bulk, and non-centrality falls by the square of that. Single-cell eQTL studies (Ch 48) attack this directly.
7. Colocalisation: state the question precisely
You have a signal and an signal in the same 200 kb. The question people ask is "do they overlap?" The question that matters is:
Do the two traits share a causal variant, or do they have different causal variants that both happen to sit inside the same LD block?
Naive checks cannot separate these. Testing whether the GWAS lead SNP is a nominally significant eQTL is anti-conservative: LD blocks hold hundreds of correlated variants, expression is a heavily tested , and the chance that some eQTL signal spans the block is not small. You will confidently assign genes that have nothing to do with the trait.
The coloc framework makes the hypotheses explicit, enumerating five mutually exclusive possibilities under a one-causal-variant-per-trait assumption. Posteriors come from summing approximate Bayes factors over single-variant configurations, with priors p_1, p_2 and p_{12} for a variant being causal for trait 1 only, trait 2 only, or both:
| Hypothesis | Interpretation | |
|---|---|---|
| H₀ | No causal variant for either | Region null for both |
| H₁ | Trait 1 only | GWAS signal, no eQTL |
| H₂ | Trait 2 only | eQTL, no GWAS signal |
| H₃ | Distinct causal variants | Both signals real, mechanistically unrelated — LD coincidence |
| H₄ | Shared causal variant | The evidence you wanted |
Reading the output is most of the skill:
- PP4 is the quantity of interest, and PP4/(PP3+PP4) is the conditional statement "given both traits have a signal here, they share it".
- Low PP3 and low PP4 means underpowered, not "no ". If PP0/PP1/PP2 dominates, one trait has no detectable signal. This is the commonest misreading in the literature.
- p_{12} drives the answer. The default 10^{-5} is a guess; report sensitivity to it.
- The one-variant assumption breaks both ways. A locus with two independent GWAS signals, one colocalising, can be pushed toward H3 by the other. Colocalising per SuSiE (coloc + SuSiE), or combining both traits' posteriors (eCAVIAR's CLPP), handles it.
SMR reaches the same question from the other side, estimating the effect of expression on the trait using the eQTL as an instrument (§12) and applying the HEIDI test, which asks whether the GWAS/eQTL effect-size ratio is heterogeneous across the region. It should not be if one variant drives both, so heterogeneity argues for two distinct causal variants.
8. TWAS: a gene-level test that is not a causal test
Train a predictor of a gene's expression from its cis variants in a reference panel, apply the weights to a cohort to get genetically predicted expression, and test that against the trait. With summary statistics only, this reduces to a weighted sum of marginal GWAS z-scores:
The appeal is obvious: it aggregates signal across the window, cuts the testing burden from millions of variants to tens of thousands of genes, and reports in the currency of genes. So is the problem — it is a linear combination of the same GWAS statistics. Two failure modes follow directly. LD confounding: a hit arises whenever the causal variant correlates with variants that happen to receive weight, whether or not the gene mediates anything. Co-regulation: neighbouring genes share regulatory variants, so their weight vectors are correlated and hits arrive in blocks of adjacent genes, with the top-ranked one determined by which prediction model put more weight near the causal variant — a property of the reference panel's size and the gene's cis-, not of biology.
The empirical work is unambiguous: TWAS significance does not imply causality, and at loci with a known answer TWAS frequently ranks a bystander first. Treat it as a that must be followed by and then by perturbation. The same caveat applies to any method imputing a molecular intermediate — the inherits the LD structure it was built on.
9. Physical evidence: contacts, and activity-by-contact
Conformation assays (Ch 50) tell you which regions are near each other in three dimensions. The evidence is weak on its own: contact maps average over millions of cells, resolution is typically coarser than an , and proximity is nearer a necessary condition than a sufficient one — -mates contact each other constantly without regulating each other.
The activity-by-contact model is the idea that makes contact data predictive:
A_E × C_{E,G}
ABC(E, G) = ─────────────────────────────────
Σ over all elements e near G of
A_e × C_{e,G}
A is element activity — in practice the geometric mean of an signal and H3K27ac (Ch 49) — and C is contact frequency. Two measurements, one product, one , essentially no parameters fitted to the target, and it substantially outperforms distance- and correlation-based predictors when benchmarked against perturbations.
The normalisation is the part worth understanding. Dividing by the sum over competing elements encodes that a has finite capacity and enhancers compete for it: a moderate element in a quiet neighbourhood can matter more than a strong one among stronger rivals. That is a mechanistic hypothesis embedded in a scoring function, and it is why the model generalises better than a purely statistical one. Supervised successors — the ENCODE-rE2G family — add features and train directly on CRISPR perturbation outcomes, producing element-to-gene maps across more than a thousand biosamples. The pattern is worth noting: mechanistic prior, then perturbation data, then supervised refinement.
10. Sufficiency and necessity are different experiments
At some point you stop scoring and start perturbing. Two families dominate, and confusing their logical claims is the commonest interpretive error in functional follow-up.
test sufficiency. Synthesise both of each candidate element as a short oligonucleotide (150–250 bp), clone each upstream of a minimal and a barcoded reporter, transfect the pool, sequence barcodes in RNA and in input DNA, take the ratio. Thousands to millions of allele pairs at once; variants with reproducible allelic differences are expression-modulating variants. STARR-seq is the same logic with the candidate in the reporter's 3′ UTR so the element is its own barcode. The claim tested is: this 200 bp, removed from chromatin and placed on an episome, drives differently depending on which allele it carries, in this cell type. Real and useful — and not a claim about the endogenous locus.
perturbation of the endogenous element tests necessity. Tile guides across the region and silence it with dCas9–KRAB (CRISPRi), delete it with , or install the specific allele by base or (Ch 38). Read out by FlowFISH, by whole-transcriptome single-cell sequencing (Perturb-seq, CROP-seq), or by a selectable .
| MPRA / STARR-seq | CRISPRi / deletion | Base or prime editing | |
|---|---|---|---|
| Logical claim | Sufficiency of the sequence | Necessity of the element | Necessity of the allele |
| Context | Episomal, out of chromatin | Endogenous | Endogenous |
| Resolution | The exact variant | ~1 kb (KRAB spreads) | Single base |
| Throughput | 10⁴–10⁶ variants | 10³–10⁴ elements | 10¹–10³ edits |
| Main failure | Chromatin-dependent elements score null | Redundant score null | Low efficiency, bystander edits |
The two dissociate constantly, informatively. Sufficient but not necessary: enhancers are frequently redundant, so deleting one changes little. Necessary but not sufficient: an element requiring specific positioning, a , or a long-range contact is inert on a plasmid and essential in situ. Only an experiment installing the specific allele in the correct cell type and state tests the claim a clinical interpretation relies on, which is why prime editing at scale is the direction of travel despite being the lowest-throughput row.
And the context choice is the hard part. A regulatory variant may act only in a stimulated macrophage, only in a beta cell at high glucose, only in a state that exists for three weeks in the second trimester. Screening in an immortalised line expressing none of the relevant is not a negative result; it is a non-experiment. Response- designs — genotyped cells profiled before and after stimulation — exist for exactly this reason, and routinely find variants with no baseline effect and a large post-stimulus one.
11. The missing-regulation problem
Across studies, only about 5–40% of trait associations colocalise with an , depending on trait, tissue panel and threshold. In the most careful test — taking gene–trait pairs where a coding variant already proves which gene is involved, then asking whether the non-coding associations at the same gene are explained by expression — , and regulatory together nominated a candidate target for fewer than 10% of the non-coding variants, and baseline expression explained the association for roughly 8% of the genes.
The regulatory hypothesis for complex traits is almost certainly correct (Ch 00 §3). The eQTL catalogues we have do not demonstrate it. The current explanations, none excluding the others:
| Explanation | The argument | What would fix it |
|---|---|---|
| Wrong cell type | The effect occurs in a minority population within a bulk tissue and is diluted | Single-cell eQTL at donor scale |
| Wrong state | The variant acts only after stimulus, infection, drug or metabolic challenge | Response-eQTL designs |
| Wrong time | The effect is developmental; the trait is set before the sampleable tissue exists | Organoids, fetal atlases, cross-species models |
| Wrong molecular | The effect is on , stability, or protein level, not steady-state mRNA | sQTLs, profiling, pQTLs |
| Trans and network effects | Effects propagate through networks; each link is tiny (Ch 32 §11) | Very large single-tissue cohorts |
| Selection | See below | Rare-variant and burden approaches; better-powered eQTLs in constrained genes |
The selection argument says the mismatch is expected rather than technical. Genes whose dosage matters for a trait are, by that fact, under on expression, so a common variant with a large effect on such a gene would have been removed; what survives at common frequency near constrained genes is small-effect regulatory variation. eQTL studies, meanwhile, most easily find large expression effects, concentrated near the start sites of genes whose expression is not constrained. Comparisons of the two hit sets bear this out: eQTL hits cluster tightly at TSSs and hits do not; genes near GWAS hits are constrained with complex cell-type-specific regulatory landscapes, and genes near eQTLs are the opposite.
The property that makes a gene matter for disease is the property that makes its expression variation rare. eQTL discovery power and complex-trait relevance are anticorrelated by construction — so the gap will narrow with better-resolved eQTL studies, but slowly, and not merely by adding donors to bulk tissue panels.
12. Mendelian randomisation
A different use of the same variants: not "what does this locus do" but "does exposure X cause outcome Y". Observational epidemiology cannot answer that, because of confounding and reverse causation. MR uses as an instrumental variable.
Statistics: confounding, what "controlling for" a covariate actually removes, and the chance / confounding / reverse-causation trichotomy this design exploits are covered in S5 §6 and §8.
With one instrument the estimate is the Wald ratio \hat\beta_{XY} = \hat\beta_{GY}/ \hat\beta_{GX}. With many, the standard estimator is inverse-variance weighting, algebraically a regression of SNP–outcome effects on SNP–exposure effects through the origin. Hold that picture: each point is a variant, the slope is the causal estimate, and every diagnostic question is about the scatter.
| Assumption | Testable? | How it breaks | |
|---|---|---|---|
| IV1 | Relevance — G associated with X | Yes | Weak instruments. In two-sample MR the bias is toward the null; in one-sample MR toward the confounded observational estimate — opposite directions, which is why the designs are not interchangeable |
| IV2 | Independence — G ⫫ confounders of X–Y | Partly | Population structure; assortative mating; dynastic effects, where the parent's genotype acts through the environment they provide. " are randomised at " holds within families and only approximately between them |
| IV3 | Exclusion — G affects Y only through X | No | Horizontal : the variant affects Y by another route |
Pleiotropy is not exotic. Genes are pleiotropic as a rule (Ch 08), and a variant selected for strongly moving a biomarker is exactly the kind likely to move other things. The sensitivity analyses seek robustness under different assumptions: MR-Egger fits a free intercept estimating average directional pleiotropy (valid under the unverifiable InSIDE condition, and underpowered); the weighted median is consistent if half the weight comes from valid instruments, the weighted mode if the largest cluster is; MR-PRESSO detects and removes outlying instruments, which is data-driven and post hoc: it assumes most instruments are valid, and because it selects on the residuals it can manufacture apparent consistency and delete instruments that are valid but merely imprecise — pre-specify the removal rule and report the estimate with and without it; Steiger filtering drops instruments more associated with the outcome than the exposure; and colocalising each instrument with the exposure catches instruments tagging something else.
None of these tests IV3 — each checks that a specific class of violation is absent. The honest reading of an MR paper is: do estimators with different, non-nested assumptions agree? Agreement is the evidence; a single point estimate is not.
Two limits get skipped. MR estimates a lifelong effect — the instrument shifts the exposure from conception, a drug shifts it for five years at 60, and these can differ in magnitude and occasionally in sign. And MR is an observational design, without a trial's warrant. Its record is nonetheless good, and includes its most valuable use: predicting failure. MR of LDL cholesterol on coronary disease predicted benefit, and statin, ezetimibe and PCSK9 trials delivered it with broadly consistent slopes; MR of HDL cholesterol predicted no benefit from raising it, against strong observational evidence, and the trials that raised HDL failed. That asymmetry — MR overturning an observational association, correctly — is what a good instrument is for.
13. What this is all for: genetically supported targets
Drug development is dominated by failure — roughly one in ten programmes entering clinical development reaches approval, and most failures are efficacy failures, which is to say failures of the causal hypothesis. Genetics offers a way to test that hypothesis before spending a decade.
Mechanisms with human genetic support are about 2.6 times more likely to progress from I to approval than those without (Minikel et al., Nature, 2024), refining an earlier estimate of roughly twofold. Two details matter more than the headline. The advantage grows with confidence in the causal gene — it is not "there is a hit nearby", it is "we know which gene", so sections 5–10 are, in commercial terms, how the multiplier is earned. And it is largely unaffected by the variant's effect size or : surprising, then obvious, since a drug perturbs a target far harder than any common does, so a variant with an odds ratio of 1.03 can nominate a target worth hitting. Genetics supplies the target's identity and the direction of the desired perturbation, not a dose–response curve — and no molecule, modality, delivery route or safety profile. It raises a prior. Where the prior is 10%, that is worth a great deal.
Common misconceptions
| What people think | What's actually true |
|---|---|
| The lead SNP is the causal variant | It is the best-correlated genotyped marker. Which block member tops the list is close to sampling noise (Ch 29) |
| A 95% gives each variant a 95% chance of being causal, and is assumption-free because it is data-driven | The set holds 0.95 posterior mass, conditional on a sparsity prior, an effect-size prior, a maximum number of causal variants, and an LD matrix matching the sample. Mismatched reference LD gives confident wrong answers with no error |
| Bigger will eventually resolve loci to single variants | Resolution scales as N(1-r^2). Perfect proxies are indistinguishable at any N. LD contrast, not sample size, is the binding |
| The nearest gene is usually the right gene | Right somewhere between a third and two thirds of the time depending on the benchmark — and benchmarks over-sample loci where the answer was easy to find |
| An at the locus identifies the gene | Only if the two signals share a causal variant. Overlap within an LD block is expected by chance; is the test that distinguishes them |
| Low PP4 means the signals do not colocalise | Only if PP3 is high. Low PP3 and low PP4 means the region is underpowered for one trait — the commonest misreading of coloc output |
| A significant gene is the causal gene | TWAS is a weighted sum of the same GWAS z-scores. LD and co-regulation of neighbouring genes routinely make bystanders significant |
| An -positive variant is validated | MPRA tests whether the sequence is sufficient on an episome. Necessity in native chromatin is a separate experiment, and the two dissociate in both directions |
| No colocalising eQTL means the locus is not regulatory | Most loci have no colocalising eQTL. Wrong cell type, state, time and molecular all cause this — and selection makes the mismatch expected, not merely technical |
| MR is a natural randomised trial, and its sensitivity analyses check the exclusion restriction | MR is observational, rests on three assumptions of which one is untestable, and estimates a lifelong exposure effect. Sensitivity analyses test robustness to particular classes of violation under further assumptions; agreement across non-nested estimators is the evidence |
Worked example: the 1p13.3 LDL-cholesterol locus
One locus, end to end. All coordinates GRCh38.
Step 0 — the association. A of plasma LDL cholesterol in N = 200,000 finds one of its strongest peaks at 1p13.3. Take the lead variant's effect as 0.10 SD per at MAF 0.22 — a round number chosen to keep the arithmetic legible, not the published figure, which is larger (Step 4).
A p-value near 10⁻¹⁵¹ and 0.34% of trait variance — an unusually strong locus, which makes the easy by GWAS standards.
Step 1 — fine-mapping. Five candidates survive. Under the single-causal-variant model the PIPs are a softmax over z^2/2 (§2):
variant z z²/2 Δ = z²/2 − max exp(Δ) PIP
v1 26.20 343.22 0.000 1.000000 0.827
v2 26.14 341.65 −1.570 0.208100 0.172
v3 25.95 336.70 −6.519 0.001473 0.001
v4 24.90 310.01 −33.215 3.7e−15 0.000
v5 22.40 250.88 −92.340 9e−41 0.000
Σ = 1.209573
95% = {v1, v2}, cumulative PIP 0.999.
Cross-check against §3. From z_2/z_1 = 26.14/26.20 the implied correlation is r = 0.9977, so r^2 = 0.9954 and
matching the 1.570 in the table. ✓ Settling it — a Bayes factor of 20 between v1 and v2 — requires
nearly double the cohort, for one of the strongest loci in the trait. Run the same locus at N = 50,000, quartering every z^2, and the credible set becomes {v1, v2, v3} with PIPs 0.534, 0.361, 0.105 — quadrupling the sample removed exactly one variant. Whereas if r^2 between v1 and v2 is 0.72 in an African-ancestry sample, the same separation needs 5.991/(0.28 \times 0.003432) \approx 6{,}200 samples' worth of that contrast.
Step 2 — variant to gene. The fine-mapped variant is rs12740374 (G>T) at chr1:109,274,968 (GRCh38):
chr1 (GRCh38) 109.25 Mb 109.28 Mb 109.31 Mb 109.40 Mb
│ │ │ │
CELSR2 ────────────────────────────► │ │ │
109,249,539 – 109,275,751 (+) │ │ │
▲ │ │ │
rs12740374 │ │ │
109,274,968 │ │ │
(in CELSR2 3′UTR)│ │ │
│◄──── PSRC1 ────┤ │ │
109,284,107 – 109,279,053 (−) │
│◄───── SORT1 ───────────┤
109,397,967 – 109,309,568 (−)
| Gene | Distance to the gene body | Distance to the TSS | Nearest-gene verdict |
|---|---|---|---|
| CELSR2 | 0 bp — the variant is inside its 3′ UTR | 109,274,968 − 109,249,539 = 25,429 bp | winner by gene body |
| PSRC1 | 109,279,053 − 109,274,968 = 4,085 bp | 109,284,107 − 109,274,968 = 9,139 bp | winner by TSS |
| SORT1 | 109,309,568 − 109,274,968 = 34,600 bp | 109,397,967 − 109,274,968 = 122,999 bp | ignored by both |
Note that the two conventions disagree. CELSR2 runs left to right on the + strand, so its TSS sits at the far end from the 3′ UTR the variant lands in: nearest gene body says CELSR2 at distance zero, nearest TSS says PSRC1. This is the textbook case where "the nearest gene" is not one rule but two, and picking between them decides the answer. Both are wrong.
Step 3 — expression evidence, and why it was not enough. Liver data show the variant associated with expression of CELSR2, PSRC1 and SORT1, and confirms a shared causal variant with the LDL-C signal — for all three. This is §8's co-regulation problem in its purest form: three genes sharing a regulatory landscape, no ranking available from expression alone. The eQTL layer narrows twenty candidates to three, then stops. Note also which tissue was needed: run in whole blood — the default because blood is easy to collect — this is one of the strongest cis-eQTLs on record, and it points hard at CELSR2 and PSRC1, the two genes that turn out not to matter, while the hepatic SORT1 regulation that drives the trait is not what blood hands you. The wrong tissue does not return a null. It returns a confident nomination of the wrong gene.
Step 4 — the experiments that decided it. Sufficiency: reporter assays carrying the two alleles show allele-specific activity in hepatocyte lines, and binding experiments show why — the minor (T) allele creates a C/EBP -factor binding site that the major allele lacks. A single base creating a binding site is the textbook mechanism from Ch 22 §6, and no motif scan would have been trusted alone. Necessity: over-express and knock down each of the three candidates in mouse liver and measure plasma lipids — only Sort1 moves LDL cholesterol. That experiment, not a statistic, eliminated CELSR2 and PSRC1. Physiology: hepatic sortilin alters VLDL secretion and thereby plasma LDL. The minor allele creates the site, raises hepatic SORT1, and lowers LDL-C by roughly 5.6 mg/dl per copy (≈0.17 SD; rs629301, Teslovich et al. 2010) — direction consistent at every step.
Step 5 — the chain, and its weakest link.
association (1p13.3, LDL-C)
→ credible set {v1, v2} LD-bounded, model-dependent
→ rs12740374, chr1:109,274,968 (GRCh38) reporter + binding evidence
→ hepatic enhancer, C/EBP site created sufficiency, episomal
→ SORT1, TSS 123 kb away necessity, mouse liver
→ VLDL secretion → plasma LDL-C physiology
→ LDL-C → coronary disease Mendelian randomisation + trials
Each arrow is a different kind of claim, and the chain is exactly as strong as its weakest link. Every link here has direct experimental support, which is why this locus appears in every review — and why it is not typical. For most of the million-plus catalogued associations, the chain stops at the first or second arrow.
Connections
- Back to: Ch 51 supplies the association · Ch 29 supplies r^2, the quantity that bounds resolution · Ch 32 for non-centrality and polygenicity · Ch 22 for what a regulatory variant does mechanistically · Ch 47, Ch 49 and Ch 50 for the measurements · Ch 38 for CRISPRi, base and
- Forward to: Ch 53, where fine-mapped effects improve and the same LD structure causes the failure · Ch 54, where the variant-to-gene problem is usually solved by the coding sequence instead · Ch 55, where functional evidence enters a formal framework and "the evidence is insufficient" becomes a reportable classification · Ch 57 for target discovery downstream · Ch 58 for the governance of the diverse cohorts §3 depends on