Contents
32 — Mapping quantitative traits Part 6 — Quantitative genetics

32 — Mapping quantitative traits

Before this: Ch 14 · Ch 30 · Ch 31 · Time: ~50 min

Statistics needed: S3 Sampling and estimation · S4 Hypothesis testing · S5 Variance and regression · S6 Likelihood and LOD scores

Chapters 30 and 31 treated the genome as an anonymous source of additive variance. That was deliberate: you can predict a selection response without knowing a single locus. This chapter asks the harder question — where are they? — and it is the hinge between quantitative genetics and genomics.

What you'll be able to do

The core idea

You cannot see the locus. You can see markers. makes a marker a noisy proxy for the causal genotype, and — this is the whole chapter — the noise has a closed form. A marker at recombination fraction r from a misclassifies the QTL genotype at rate r, and the resulting of the observed effect is exactly (1 − 2r).

QTL mapping is measurement error in the predictor, with a known error rate. Everything downstream — the confounding of effect with distance, the mixture-model likelihood, the wide confidence intervals, the , and eventually the r² attenuation in — is a consequence of that single fact.

Measurement error in a regressor attenuates the coefficient and inflates the sample size needed to detect it; regression coefficients and what moves them are covered in S5, and this chapter assumes them. Genetics hands you the reliability coefficient for free, as a function of map distance.


1. The one derivation

Take a backcross. Cross two inbred lines, then cross the F1 back to one parent. A with Q/q sits at recombination fraction r from marker M/m. The F1 is MQ/mq; its gametes are:

   parental   M Q      (1 − r)/2
   parental   m q      (1 − r)/2
   recombinant M q     r/2
   recombinant m Q     r/2

Backcross progeny carrying the M allele therefore carry Q with probability (1 − r); those carrying m carry Q with probability r. Let δ = μ_Qq − μ_qq be the QTL's genotypic contrast. Then

E[y | M·] = (1 − r)·μ_Qq +      r·μ_qq
E[y | m·] =      r·μ_Qq + (1 − r)·μ_qq
────────────────────────────────────────
difference = (1 − 2r)·δ

The marker contrast is the QTL contrast shrunk by (1 − 2r). Since variance explained goes as the square of the contrast,

σ²_marker / σ²_QTL = (1 − 2r)²

and the non-centrality of the test — hence the sample size you need — scales as N(1 − 2r)²δ²/σ².

Statistics: the non-centrality parameter, and how it converts into power, are covered in S4 §4.

Under the Haldane map function r = (1 − e^(−2d))/2 with d in Morgans, so 1 − 2r = e^(−2d) exactly. The signal decays exponentially in map distance: the effect estimate by e^(−2d), the variance explained by e^(−4d).

In an F2 the same algebra with three classes (values a, d, −a) gives

ContrastExpectation
E[y|MM] − E[y|mm]2a(1 − 2r)(1 − 2r)
E[y|Mm] − ½(E[y|MM] + E[y|mm])d(1 − 2r)²(1 − 2r)²

Dominance attenuates twice as fast as additivity, because detecting it requires both to be correctly classified. Dominance effects are systematically harder to map, and this is why — not because they are rarer.

2. Designs: buying power and buying resolution separately

Power comes from sample size, effect size, and control of environmental variance. Resolution comes from the number of recombination events that have accumulated between the founders and the individuals you . These are different currencies, and designs buy them differently.

An F2 individual carries the products of two meioses. In a region spanning recombination fraction r, an F2 of N individuals contains roughly 2Nr recombination breakpoints. That number is your positional information. Nothing else is.

DesignRecombination accumulatedPowerResolutionCost
Backcross1 per individualGood; only 2 classes, simpleCoarse (10–30 cM)Cheapest
F22 meioses per individualBest per individual; estimates a and dCoarseCheap, one generation
RIL (recombinant inbred lines)2× (selfing) or 4× (sib-mating) an F2, and homozygous throughoutHigh — genotype once, phenotype k times, so line-mean environmental variance is σ²_E/k~2–4× better than F28+ generations to construct; then reusable forever
NIL (near-isogenic lines)One region segregating on a fixed backgroundVery high for that region — background genetic variance is zeroExcellent, but only where you already lookedNo genome scan; many lines needed
AIL (advanced intercross)t/2 × an F2 after t generations of random intercrossingSame per individual as F2~2/t the interval widtht generations of breeding; needs dense markers to keep up

Two of these deserve the algebra.

RILs decouple power from resolution. Because a RIL is an immortal homozygous genotype, you can phenotype k replicates. The line mean has environmental variance σ²_E/k, so the of the line mean is σ²_G/(σ²_G + σ²_E/k) → 1 as k grows. You buy power without buying a single extra recombination event. Separately, the repeated generations of inbreeding accumulate crossovers: for selfing-derived RILs the observed recombination fraction is R = 2r/(1 + 2r), for sib-mated RILs R = 4r/(1 + 6r) — map expansion factors approaching 2 and 4 for tight .

AILs buy resolution and nothing else. After t generations of random intercrossing from an F2, tightly linked loci recombine at approximately (t/2)·r. Generation 20 gives a tenfold map expansion, so a 20 cM interval becomes 2 cM. Per individual, power is unchanged — you have simply spread the same positional information over a finer grid, which is only useful if you also genotype finely enough to see it.

graph LR F2["F2 / backcross<br/><i>max power per individual</i><br/>2N meioses"] RIL["RILs<br/><i>+ replication</i><br/>2–4× map expansion"] AIL["AIL, gen t<br/><i>t/2 × map expansion</i>"] NIL["NILs<br/><i>background fixed</i><br/>region-specific"] F2 --> RIL --> NIL F2 --> AIL --> NIL NIL --> GENE["candidate gene<br/>+ functional test<br/>Ch 37, Ch 38"]

3. Single-marker analysis, and what it cannot do

Regress on marker , one marker at a time. In a backcross that is a two-sample t-test; in an F2, a one-way ANOVA over three classes, or a regression on the additive code (−1, 0, 1) plus a dominance code. It is valid, it is fast, and it was how mapping was done before 1989.

Its defect is structural, not statistical: the estimate is (1 − 2r)δ, which is one equation in two unknowns. A QTL of effect δ at r = 0.15 and a QTL of effect 0.7δ sitting on top of the marker produce identical data. You cannot report an effect size and you cannot report a position; you can only report that something is near this marker.

Two further costs. Power drops with the square of the , so a QTL sitting midway between sparse markers is detected with (1 − 2r)² of its full signal from either side — with markers 40 cM apart, roughly half. And missing genotype data at a marker simply removes those individuals from that test.

4. Interval mapping: put the QTL between the markers

Lander and Botstein's 1989 move: stop testing markers and start testing positions. Walk a hypothetical along the interval between two flanking markers, at every position z computing the conditional distribution of the unobserved QTL given the observed flanking marker genotypes and the two recombination fractions r₁, r₂ that z implies.

Statistics: likelihood, maximum likelihood, and the likelihood-ratio scale that a reports are covered in S6 §§3–4.

That gives a finite mixture with known, individual-specific mixing weights:

y_i  ~  Σ_g  p_ig(z) · N(μ_g , σ²)

where p_ig(z) = P(QTL genotype g | flanking markers of individual i, position z). The weights are pure genetics — no parameters — and they are what makes z identifiable. Fit by EM:

which is weighted least squares with soft class assignments — the standard normal-mixture EM, except that the mixing proportions are fixed by the map rather than estimated.

At each z compute

LOD(z) = log₁₀ [ L(μ̂₁, μ̂₂, …, σ̂ | QTL at z) / L(μ̂, σ̂ | no QTL) ]

and plot LOD against genome position. The peak estimates location; its height tests existence. Because the mixture is degenerate at a fully informative marker and genuinely mixed between markers, the profile has curvature — which is exactly the positional information single-marker analysis threw away.

Haley–Knott regression replaces the mixture with an ordinary regression of y on E[QTL genotype | markers]. It is a moment approximation to the likelihood: two orders of magnitude faster, peaks in nearly the same place, but it misstates the residual variance and degrades where marker data are sparse or missing. It is what most software does inside a permutation loop.

5. Composite interval mapping and multiple-QTL models

fits one against a null of none, which is wrong in two ways.

Unmodelled QTLs elsewhere inflate σ². Every locus you ignore sits in the residual, lowering power everywhere. Linked QTLs generate ghosts. Two real QTLs flanking an empty interval produce a single spurious peak between them — the mixture model's best one-QTL explanation of a two-QTL reality.

Composite interval mapping (Zeng 1993, 1994; Jansen 1993) fixes both by including selected markers elsewhere in the genome as covariates while scanning. This is ordinary conditioning: cofactors on other absorb background genetic variance; cofactors on the same chromosome block the linked QTL, restoring the ghost peak to two peaks. A window around the test position excludes cofactors that would compete with the QTL being tested and steal its signal.

Three assumptions worth naming, because each breaks:

AssumptionWhat breaks when it fails
The cofactor set is fixed and correctIt is chosen by stepwise selection from the same data. The null distribution of the scan is therefore not the null distribution of a fixed-cofactor scan — thresholds must be permuted with cofactor selection inside the loop
One QTL per intervalMultiple linked causal loci are reported as one QTL of intermediate position and inflated effect
Effects are additive across loci is common in crosses. Multiple-QTL models (MQM, MIM) fit k positions plus interaction terms, turning the analysis into model selection over a combinatorial space with penalties calibrated by permutation

6. Thresholds: LOD, and why permutation

A is log₁₀ of a likelihood ratio, not a p-value. Twice the natural-log likelihood ratio is asymptotically χ², so χ² = 2ln(10)·LOD ≈ 4.605·LOD. LOD 3 gives χ²₁ = 13.8, a nominal two-sided p ≈ 2 × 10⁻⁴.

The conventional threshold of 3 comes from Morton (1955) and its justification is Bayesian, not frequentist: for two randomly chosen human loci the prior odds of are roughly 1:50, so a likelihood ratio of 1000:1 yields posterior odds near 20:1 — about a 5% error rate. That argument is specific to the human genome's map length and to a sequential test on single families. It does not transfer to a genome scan in a mouse cross, and it should never be repeated as though it did.

For genome scans the correct object is the null distribution of the maximum LOD over the whole genome, and it is not χ². Under the null the position parameter is unidentified — a regularity failure, not a small-sample problem — so the asymptotics are those of the supremum of a correlated random field, and depend on genome length in Morgans, marker density, cross type and missing-data pattern.

Bonferroni is the wrong correction because adjacent tests are near-. The effective number of independent tests is set by the number of independent recombination intervals — that is, by genome length in Morgans — not by the number of markers. Past roughly one marker per few cM, additional markers add essentially nothing to the multiple-testing burden, and Bonferroni charges you for all of them anyway.

Statistics: Bonferroni, and the idea of an effective number of independent tests, are covered in S7 §2.

Permutation (Churchill & Doerge 1994) is the right answer. Shuffle the vector against the intact matrix, rerun the whole scan, record the maximum LOD. Repeat 1,000 times for a 5% threshold, ~10,000 for a stable 1% tail. What this preserves:

What it assumes: exchangeability of phenotypes under the null. That holds in a designed cross. It fails with population structure or unequal relatedness (outbred panels, AILs, human cohorts), with covariates correlated with genotype, and under selective genotyping — in those cases you must permute within strata, permute residuals, or abandon permutation for a parametric threshold.

For human genome-wide linkage scans, Lander and Kruglyak (1995) gave threshold conventions of roughly LOD 2.2 for "suggestive" and 3.6 for "significant" evidence in sib-pair analysis. Their mouse thresholds move in both directions, which makes the point: 1.9/3.3 for a backcross, lower because the mouse genome is shorter, but 2.8/4.3 for an F2, higher because every position is tested on two parameters rather than one. The exact values depend on design and map density, and the paper's real contribution was insisting that any threshold be justified against the genome-wide null at all.

7. Confidence intervals, and why they are wide

Two standard constructions: the 1-LOD (or 1.5-LOD) support interval — the positions whose LOD is within one unit of the peak — and the nonparametric bootstrap over individuals.

Both come out wide, and the reason is not statistical inefficiency. Positional information comes only from recombination breakpoints that actually occurred near the , and there are very few. In an F2 of N = 200, a 1 cM window contains about 2 × 200 × 0.01 = 4 breakpoints. You cannot localise more finely than the recombination events you observed, and each of those is informative only in proportion to the phenotypic signal it carries.

The standard rule of thumb (Darvasi & Soller 1997) puts the 95% interval at approximately 3000/(N·d²) cM in a backcross and about half that in an F2, where d is the average effect of an substitution — α from Ch 30 §4, which for an additive QTL at frequency ½ is a, that is half the homozygote difference — measured in residual (within-) standard deviations. Read d as the homozygote difference instead and you double it, and since the expression is inverse-square you report an interval four times too narrow. Treat the constant as an order of magnitude; the scaling — inverse in N, inverse in the square of the effect — is the durable part. Halving the effect quadruples the interval.

8. The Beavis effect

Estimate a 's effect and it is roughly unbiased. Estimate it conditional on having declared it significant and it is not. Writing δ̂ ~ N(δ, σ²_δ̂),

E[δ̂ | δ̂ > c] = δ + σ_δ̂ · λ((c − δ)/σ_δ̂),     λ(x) = φ(x)/(1 − Φ(x))

the inverse Mills ratio. When power is high (c ≪ δ) the correction vanishes. When power is low (c ≫ δ), λ(x) → x and the expression collapses to E[δ̂ | significant] ≈ c: the reported effect is pinned near the detection threshold, almost independently of the truth.

Beavis's simulations put numbers on it: with ~100 progeny, effect estimates are typically about double the true value; with ~500, the inflation is modest; with ~1,000, largely gone.

Three consequences:

You will meet this again, unchanged, in and in construction (Ch 53). It is the same covered in S7 §6, and the same one behind published-effect-size inflation generally.

9. Power versus resolution: the fundamental trade

Cross-based mappingPopulation association mapping
per locus2, by constructionMany, unknown
0.5, by constructionWhatever it is — often rare
EnvironmentControlled, replicableUncontrolled, confounded
Recombination available~2N meioses since the foundersMillions of ancestral meioses
Resolution5–30 cM (Mb-scale, 10²–10³ genes)LD-block scale (kb)
Power per locusVery highVery low
Generalises to natural variationNo — two founders onlyYes

The trade is not a defect of either method. It is the same information appearing in two forms. A cross concentrates all its variance into one contrast at frequency ½ and then has almost no recombination to localise it. A population has spent thousands of generations shattering into kb fragments — perfect localisation — but distributes the causal signal across many rare alleles in an uncontrolled environment.

10. Humans: why linkage stalls on complex traits

Human analysis is mapping in , and for Mendelian disease it worked magnificently: cystic fibrosis, Huntington's, and hundreds of others were localised by tracking co- through families and then sequencing the interval.

It fails for complex traits for two independent reasons.

Effect size. Linkage detects excess sharing among affected relatives, and that signal falls off brutally as the relative risk approaches 1. Risch and Merikangas (1996) made the comparison concrete: for a variant of frequency 0.1 conferring a genotype relative risk of 1.5, an affected-sib-pair linkage study needs about 68,000 sib-pair families, while a family-based association test — the TDT, run on affected singletons and their parents — needs about 2,200 trios. Roughly a thirtyfold difference, and it widens enormously for rarer alleles: at frequency 0.01 the same relative risk demands 4.6 million sib-pair families against about 19,000 trios. That paper is, in retrospect, the design document for .

Recombination supply. A produces only a few dozen crossovers, so a nuclear family offers a few dozen breakpoints total. Affected relatives share -arm-scale segments. Linkage therefore cannot resolve below roughly 10–20 cM no matter how many families you collect — and for a complex trait there is no large pedigree with clean segregation to collect.

Add locus heterogeneity — different families with different causal loci, which averages the linkage signal toward zero — and the method is out of options.

graph TD T{"Trait"} T -->|"rare, large effect,<br/>segregates in families"| L["Linkage / pedigree analysis<br/>→ 10–20 cM interval → sequence it<br/>Ch 54"] T -->|"common, many loci,<br/>each tiny"| A["Association in populations<br/>→ kb-scale LD block<br/>Ch 51"] L --> M["causal gene"] A --> F["fine-mapping + functional follow-up<br/>Ch 52"] F --> M

11. Common variants, polygenicity, and the omnigenic proposal

The common-disease/common-variant hypothesis (Lander 1996; Chakravarti 1999; Reich & Lander 2001) argued that because common diseases are old and human populations passed through a bottleneck and rapid expansion, the contributing to them should themselves be comparatively common and shared across populations. That is a testable population-genetic claim, and it is what justified building fixed genotyping arrays that tag common variation through LD rather than sequencing everyone.

The verdict is a partial vindication with a large correction. Common variants do carry a substantial share of , and arrays did work. But the effect sizes were roughly an order of magnitude smaller than anticipated, so studies powered for odds ratios near 1.5 found nothing and studies of hundreds of thousands of people found thousands of loci with odds ratios near 1.05. "Common" was right; "detectable in a few hundred cases" was badly wrong. Rare variants of larger effect also contribute (Ch 54), so the common-versus-rare framing was a false dichotomy.

What emerged instead is extreme polygenicity: for traits like height, tens of thousands of contributing variants, heritability spread across essentially every roughly in proportion to chromosome length, and enrichment in regulatory regions active in trait-relevant tissues rather than in coding sequence.

The (Boyle, Li & Pritchard 2017) proposes an explanation: gene- within a relevant cell type are sufficiently interconnected that essentially every gene expressed in that tissue perturbs the trait a little, via trans effects propagating to a small number of "core" genes with direct biological roles. On this account most heritability sits in "peripheral" genes with no specific relationship to the trait.

Present this as a hypothesis, because it is one. The principal critique (Wray, Wijmenga, Sullivan, Yang & Visscher 2018) is that the observed polygenicity is already what standard quantitative-genetic models with many loci predict, so no new framework is required; that the core/peripheral distinction has not been shown to be empirically separable; and that a model in which every gene matters is difficult to falsify. The trans-regulatory effects the model requires are individually tiny — consistent with the proposal, and also the reason it is hard to test. What is not in dispute is the polygenicity itself, and its practical consequence: the map from a significant association to a mechanism is many-to-one (Ch 52).

12. G×E, and why it is statistically hard

Fit y = β₀ + β_G·G + β_E·E + β_GE·(G×E) + ε and test β_GE. Four things make this much harder than it looks.

Power. Take a balanced 2×2 design with n per cell. The main-effect contrast has variance σ²/n; the interaction contrast (ȳ₁₁ − ȳ₁₀) − (ȳ₀₁ − ȳ₀₀) has variance 4σ²/n. The standard error is twice as large, so detecting an interaction of a given magnitude needs about four times the sample size of detecting a main effect of that magnitude — and interactions are typically smaller than main effects, not equal.

Measurement error in E. Environments are measured badly — self-reported diet, recalled exposure, "stress". Error in E attenuates β_GE, compounding a power problem that was already 4× worse.

Scale dependence. Interaction is not scale-invariant. A model additive on the log scale shows interaction on the raw scale, and conversely. "There is a " is therefore a statement about a modelling choice unless the scale is independently motivated. This is the most frequently missed point in the literature.

Confounding by gene–environment correlation. If influences behaviour that determines exposure, G and E are not independent and the interaction term absorbs the dependence. Add a search space of (variants × environments) with environments chosen after seeing the data, and you have the conditions that produced the candidate-gene G×E literature — almost none of which replicated.

13. Forward: GWAS is association mapping over historical recombination

Everything in this chapter transfers, with one substitution.

In a cross, the marker is a noisy proxy for the causal locus because of recombination in the one or two meioses since the founders, and the is (1 − 2r)². In a population, the marker is a noisy proxy because of recombination over thousands of generations of shared ancestry, and the attenuation is r²_LD, the squared correlation between the two columns — the same quantity you met in Ch 29. The non-centrality of the marker test is r²_LD times the causal variant's non-centrality. Identical structure, different source of the error.

mapping in a cross
Attenuation(1 − 2r)² = e^(−4d)r²_LD
Recombination~2N meioses~10⁴–10⁵ generations of ancestral meioses
Markers needed10²–10³, one per few cM10⁵–10⁷, one per few kb
ThresholdPermutation, per experimentFixed 5 × 10⁻⁸ ≈ 0.05 / 10⁶ effective tests
Resolution5–30 cMkb, but rarely a single variant
Same, same size, same fix

Permutation is replaced by a universal threshold because LD structure in a given population is stable enough to make the effective number of independent common-variant tests roughly constant within that population (~10⁶), and because permuting a biobank breaks the relatedness and structure that the analysis depends on. It is not constant across populations: S7 §2 prices the difference at about 2×, Ch 51 §5 will do the same for the genome-wide threshold, and the equity consequence is not neutral. Everything else is the same machinery. Chapter 51 picks it up from here.


Common misconceptions

What people thinkWhat's actually true
A significant marker locates the at that markerThe statistic is (1 − 2r)-attenuated. A large effect far away and a small effect nearby give identical data. Single-marker analysis cannot separate them
A QTL is a geneA QTL is an interval. In a typical cross it spans 5–30 cM — often tens of megabases and hundreds of genes — and may contain more than one causal locus
Bonferroni handles the multiple testingAdjacent tests are near-. The effective number of independent tests is set by genome length in Morgans, not by marker count. Bonferroni over-corrects, increasingly so as markers get denser
Adding markers costs you power through multiple testingBeyond roughly one marker per few cM, extra markers barely change the genome-wide null. Permutation prices this correctly and automatically
LOD 3 means p = 0.001LOD is log₁₀ of a likelihood ratio. LOD 3 → χ²₁ = 13.8 → nominal p ≈ 2 × 10⁻⁴. The value 3 comes from a Bayesian prior-odds argument specific to human
A QTL whose effect shrinks on replication was a false positiveThe guarantees that discovery estimates are inflated whenever power is limited. Shrinkage is the expected behaviour of a real locus
failed in humans because the samples were too smallPartly. The deeper problem is that a family supplies a few dozen crossovers. Association exploits millions of ancestral ones — and detects small effects that linkage cannot see at any family count
The explains complex traitsIt is a proposal with a serious identifiability critique. The polygenicity it addresses is measured and real; the core/peripheral mechanism is not established

Worked example: one interval in an F2 mouse cross

Design. F2, N = 400, from two inbred strains. : fasting glucose (mmol/L). Genotyped at 1,500 markers across a ~1,400 cM genome.

Data at marker M1.

Classnmean
MM989.20
Mm2058.55
mm977.80

Pooled within-class SD = 1.60.

1 — Contrasts. â_obs = (9.20 − 7.80)/2 = 0.70. d̂_obs = 8.55 − (9.20 + 7.80)/2 = 8.55 − 8.50 = 0.05 — negligible, so treat as additive.

2 — Test. SE(ȳ_MM − ȳ_mm) = 1.60 × √(1/98 + 1/97) = 1.60 × √0.020513 = 1.60 × 0.14323 = 0.2292. t = 1.40 / 0.2292 = 6.109, df = 397. So χ² ≈ t² = 37.32, and LOD = 37.32 / 4.605 = 8.10.

3 — Variance explained at the marker. Grand mean = (98×9.20 + 205×8.55 + 97×7.80)/400 = 3410.95/400 = 8.5274. Between SS = 98(0.6726)² + 205(0.0226)² + 97(−0.7274)² = 44.33 + 0.11 + 51.32 = 95.76. Within SS = 397 × 1.60² = 397 × 2.56 = 1016.32. Total SS = 1112.08, so σ²_P = 1112.08/399 = 2.79. PVE at the marker = 95.76 / 1112.08 = 8.6%.

4 — Correct for distance. places the peak 8 cM from M1. Haldane: r = (1 − e^(−0.16))/2 = (1 − 0.85214)/2 = 0.0739, so 1 − 2r = e^(−0.16) = 0.8521.

Check independently: for an additive in an F2, σ²_QTL = a²/2 = 0.822²/2 = 0.337, and 0.337/2.79 = 12.1%. Consistent. An 8 cM displacement understated the effect by 15% and the variance explained by 27%.

5 — Threshold. 1,000 permutations of the phenotype against the intact matrix give a 95th percentile of the genome-wide maximum LOD of 3.4. Observed 8.10 ≫ 3.4: significant.

Compare the alternatives. Bonferroni over 1,500 markers requires nominal p = 3.33 × 10⁻⁵, i.e. z = 4.15, χ² = 17.2, LOD 3.74. Had the same cross been genotyped by sequencing at 50,000 markers, Bonferroni would demand p = 10⁻⁶, z = 4.89, χ² = 23.9, LOD 5.20 — while the permutation threshold would barely move, because the genome is still only ~1,400 cM long and you cannot buy more independent tests than there are independent recombination intervals.

6 — Confidence interval. Residual variance = 2.79 − 0.337 = 2.45, so σ_res = 1.566. The rule of thumb wants the substitution effect — a, not the homozygote difference 2a — so d = 0.822/1.566 = 0.525, and the F2 form gives:

CI ≈ 1500 / (N·d²) = 1500 / (400 × 0.276) = 14 cM

Cross-check with the same paper's other expression, in terms of the variance explained: 530/(N·v) = 530/(400 × 0.119) = 11 cM. Same order — which is all either form claims.

At roughly 2 Mb per cM in mouse, that is ~27 Mb — on the order of 200 genes. This is a large QTL, explaining 12% of the variance in 400 animals, and it still resolves only to a region containing hundreds of candidates. That is the resolution problem, quantified — and 14 cM lands squarely inside the 5–30 cM band that §9 gives for cross-based mapping, which is where a cross of this size belongs.

7 — The Beavis floor. The threshold itself sets a minimum reportable effect. Since χ² ≈ N × PVE for small PVE, the LOD 3.4 threshold corresponds to χ² = 3.4 × 4.605 = 15.66, so PVE ≥ 15.66/400 = 3.9%. A QTL whose true PVE is 3.0% is undetectable on average, and on the occasions it is detected it must be reported at ≥ 3.9% — an unavoidable 30% inflation, built into the design before any data were collected. That is the in one line.

Connections