53 — Polygenic scores
Before this: Ch 51 — GWAS · Ch 30 — Quantitative traits and variance · Ch 29 — Linkage disequilibrium · Time: ~55 min
Statistics needed: S3 Estimation and error · S5 Variance and regression · S7 High-dimensional data
What you'll be able to do
- Write a as a weighted -dosage sum, and say precisely what each weight estimates
- Explain the two distinct reasons a naive sum over hits fails — LD double-counting and estimation noise — and read clumping+thresholding, LDpred, lassosum and PRS-CS as different priors on the effect-size distribution
- Convert a top-decile relative risk into an absolute risk given a prevalence, and explain why extreme-percentile odds ratios are a rhetorically inflated presentation of the same model
- Distinguish discrimination from calibration, and compute the AUC ceiling that a given liability-scale R^2 implies
- Name each mechanism of cross-ancestry failure, explain why it follows from who was sampled rather than from biology differing between groups, and say why accuracy decays with measured genetic distance rather than with a race label
- Say why the same estimator works far better for dairy cattle than for people
The core idea
Chapter 30 defined an individual's as the sum of the average effects of the it carries: A = \sum_j \alpha_j (X_j - 2p_j). That quantity was a theoretical device — you could estimate its variance from relatives, but not its value for a person, because you could not see the \alpha_j.
(Ch 51) estimates millions of \alpha_j at once. A is the obvious next move: plug the estimates in and evaluate the sum.
The functional form is therefore not a modelling choice. Under an additive model the genetic value is a weighted dosage sum, and there is nothing to design. Everything difficult lives in the weights, and two features of genetics make them hard in a way that ordinary prediction problems are not. The estimates are individually terrible — most are pure noise, and the signal-to-noise ratio per variant is often below 10⁻³. And the predictors are strongly correlated with each other by , while each estimate was obtained from a separate univariate regression that ignored the others. Add them up and you count the same underlying signal once for every marker that tags it.
A polygenic score is not a measurement of a person. It is a prediction from a fitted model, and its accuracy is a property of the training data rather than of the person being scored. The same DNA, scored with weights from two different cohorts, yields two differently reliable predictions. Nothing about the individual changed.
1. The estimator
x_{ij} is the dosage of the effect of variant j in individual i: 0, 1 or 2 for a hard call, or a real number in [0,2] — the posterior expected dosage — when the genotype was imputed (Ch 29). \hat{w}_j is a weight derived from : a regression coefficient for a , a log odds ratio for a disease. Summing log odds ratios rather than odds ratios is what makes the score additive on the scale the logistic model is linear in.
Statistics: logistic regression, the logit scale, and why a coefficient there is a log odds ratio are covered in S5 §7.
Three implementation facts that decide whether the number means anything:
Missing genotypes must be mean-imputed to 2\hat{p}_j, not to zero. Setting them to zero makes the score a function of the assay's failure pattern, which correlates with DNA quality, batch and sometimes ancestry.
The raw sum has no units. It depends on M, on the allele-frequency spectrum of the panel and on the trait's scale. Scores are reported as a z-score or percentile against a reference sample — which means a PRS is a rank statistic until somebody chooses that reference, and the choice of reference is where most of the trouble in §7 enters.
Allele alignment is a real failure mode. The effect allele in the summary statistics must be matched to the effect allele in the target genotypes, on the same strand. A/T and C/G variants are strand-ambiguous — their allele codes are self-complementary — and cannot be resolved from the codes alone; the usual remedies are to match on or to drop them. And because the join is on (CHROM, POS, REF, ALT), an written two valid ways silently fails to match (Ch 41). A sign error on one large-effect variant, or the loss of a few hundred through bad matching, degrades a score with no error message anywhere.
2. Two things break the naive sum
LD double-counting
A regresses the on one variant at a time. The coefficient it reports is therefore a marginal effect, which absorbs the causal effects of everything the variant is correlated with. With standardised ,
where \mathbf{D} is the LD correlation matrix. Concretely: one causal variant, twenty markers tagging it at r = 0.95, and a GWAS that reports twenty near-identical hits.
causal variant ● β = 0.10
tagging markers ○ ○ ○ ○ ○ ○ ○ ○ ○ ○ ○ ○ ○ ○ ○ ○ ○ ○ ○ ○ r ≈ 0.95 to ●
marginal estimates each ≈ 0.95 × 0.10 = 0.095
naive sum over all 20 × 0.095 = 1.90 ← 19× the true genetic contribution
correct answer 0.10
The clean statement of the problem is that the ideal weights are the joint effects, \boldsymbol\beta^{\text{joint}} = \mathbf{D}^{-1}\hat{\boldsymbol\beta}^{\text{marg}}, and you cannot compute that. \mathbf{D} is M \times M with M \sim 10^7; you only have an estimate of it from a reference panel of a few thousand , so it is rank-deficient and appallingly conditioned; and inverting an ill-conditioned matrix against a noisy right-hand side amplifies precisely the noise you are trying to suppress.
Every polygenic-score method is a regularised solution to that linear system. Regularised regression when predictors outnumber samples is covered in S7 §6; this chapter assumes it. What is genetics-specific is that the regulariser has to be chosen from a belief about biology, and that \mathbf{D} is block-diagonal in a useful way — LD decays, so the matrix is banded and can be solved chromosome-block by chromosome-block.
Estimation noise, and selection on it
Write \hat\beta_j = \beta_j + e_j. Two separate problems follow.
Including a variant whose true effect is zero contributes nothing to the signal and \mathrm{Var}(e_j) to the variance of the score. Since the overwhelming majority of variants are null, a genome-wide unshrunken sum is mostly noise. Restricting to significant hits fixes that but discards the enormous number of true effects sitting below — this is the whole reason a p-value threshold is a bias–variance tradeoff, and the reason the optimal threshold is not a property of the trait. It moves with GWAS sample size and with polygenicity, and must be tuned.
And selection makes the surviving estimates biased upward. Conditioning on p < p_T conditions on |\hat\beta| being large, so \mathbb{E}[\hat\beta \mid \text{selected}] > \beta — the (Ch 32). Discovery effect sizes used as weights without shrinkage are systematically too big, and systematically too big for the variants the score leans on hardest.
Statistics: the bias–variance tradeoff, and why a deliberately biased estimator can beat an unbiased one, is in S3 §2; the winner's curse is quantified in S7 §6.
3. Methods are priors on the effect-size distribution
Once you see the problem as regularised regression on summary statistics plus an LD matrix, the zoo collapses. The methods differ in exactly one thing: what they assume the distribution of true effect sizes looks like.
Statistics: priors, posteriors and posterior means are covered in S6 §5, and the sense in which a penalty is a prior in S7 §6.
| Method | Prior on \beta_j | Architecture it assumes | Tuned |
|---|---|---|---|
| Clumping + thresholding (C+T) | point mass at 0 below p_T; no shrinkage above | sparse; LD handled by deleting correlated markers | r^2, window, p_T |
| Infinitesimal / genome-wide ridge | \beta_j \sim \mathcal{N}(0, h^2/M) | every variant has a tiny effect | nothing (h^2 from data) |
| LDpred / LDpred2 | point–normal: \beta_j \sim \mathcal{N}(0, h^2/Mp) w.p. p, else 0 | a fraction p of variants are causal | p (or auto-estimated) |
| lassosum / penalised regression | Laplace (L_1) | sparse, with data-driven selection | \lambda, block shrinkage |
| PRS-CS / continuous shrinkage | global–local scale mixture, heavy-tailed | dense, but with a few large effects | global scale \phi |
| SBayesR / SBayesRC | finite mixture of normals; RC adds | mixed scales, functionally enriched | mixture weights |
Clumping+thresholding deserves respect rather than condescension: it handles LD by keeping the lead variant in each clump (r^2 < 0.1 within a few hundred kb is typical) and dropping the rest, which is a crude but effective answer to double-counting — though the surviving weight is still a marginal effect and still winner's-cursed, so clumping removes the multiple counting without removing the inflation. For genuinely sparse architectures it is hard to beat.
Ridge with a normal prior is the infinitesimal model made computational: the posterior mean solves (\mathbf{D} + \tfrac{M}{Nh^2}\mathbf{I})^{-1}\hat{\boldsymbol\beta}, so the penalty is set by genetics rather than by cross-validation — polygenicity over sample size times . LDpred generalises it by admitting that not every variant is causal; lassosum swaps the Gaussian prior for a Laplace one and inherits sparsity; PRS-CS abandons hard sparsity entirely and gives each variant its own local scale drawn from a heavy-tailed distribution, so small effects are crushed and large ones pass through almost unshrunk.
Which prior wins is an empirical question about genetic architecture, and the answer differs by trait. Lipids, with large effects at LPA and APOE, and autoimmune disease, with the MHC, reward sparse priors. Height, schizophrenia and educational attainment are hyper-polygenic and reward continuous shrinkage. The best current methods also let the per-variant prior variance depend on — recall from Ch 30 that a locus contributes 2pq\alpha^2, so frequency and effect size are not independent — and on functional annotation, because causal variants concentrate in coding sequence, conserved elements and cell-type-specific open chromatin (Ch 49, Ch 52).
4. Training, tuning, testing — and how R^2 gets inflated
Three disjoint sets of people are required, and the discipline is the ordinary one with one genetics-specific trap in it.
- Discovery — the that produced the summary statistics.
- Tuning — where hyperparameters (p_T, \lambda, p, \phi) are chosen.
- Test — where performance is reported, once.
| Failure | What it does | Why it is easy to miss |
|---|---|---|
| Sample overlap between discovery and target | the score partly memorises the target | biobanks are heavily re-used; overlap is often undocumented |
| Cryptic relatedness across sets | relatives share both and environment | requires an explicit kinship filter, not a name check |
| Tuning on the test set | reports a maximum over hyperparameters as if pre-specified | the tuning step is often not described as one |
| Reporting full-model R^2 | age, sex and PCs carry most of it | a CAD model with age and sex alone reaches a C-statistic near 0.75 |
| Observed-scale R^2 in a case–control sample | depends on the case fraction you chose | two studies of the same score are then incomparable |
Only the incremental R^2 or the incremental C-statistic over a covariates-only model is interpretable, and disease results must be converted to the liability scale before any two of them are compared. The transformation — and the P(1-P) term in it that divides out the study's own case fraction — is at Ch 30 §2.
5. Discrimination, calibration, and the ceiling
For a the metric is incremental R^2, and its ceiling is the SNP h^2_{\text{SNP}} (Ch 31): a score built from common variants cannot explain more variance than common variants tag. Well-powered traits now reach roughly 60–80% of that ceiling in the ancestry they were trained in.
For a disease, use the liability-threshold model. Let S be the standardised score and \rho^2 the fraction of liability variance it explains, so L = \rho S + \sqrt{1-\rho^2}\,U with U \sim \mathcal{N}(0,1) independent. With prevalence K, threshold T = \Phi^{-1}(1-K), i = \varphi(T)/K (mean score-shift in cases) and j = \varphi(T)/(1-K) (in controls),
which is just "probability a case outscores a control" for two normals with the conditional means and variances the threshold model implies.
| \rho^2 (liability) | AUC at K=1\% | K=5\% | K=20\% |
|---|---|---|---|
| 0.02 | 0.607 | 0.586 | 0.570 |
| 0.05 | 0.667 | 0.636 | 0.611 |
| 0.10 | 0.731 | 0.691 | 0.657 |
| 0.20 | 0.815 | 0.766 | 0.722 |
| 0.30 | 0.870 | 0.820 | 0.773 |
Read the table before criticising any published AUC. A score that captured the entire SNP heritability of a disease with h^2_{\text{liability}} = 0.30 and K = 5\% would top out at AUC 0.82. "Only 0.68" is not evidence of a bad method; it is close to the ceiling the biology allows. The interesting question is always the ratio of achieved to attainable.
And then the distinction that most reporting elides:
Discrimination is about the ordering of people; calibration is about the number you tell one person. AUC is invariant to any monotone transformation of the score, so a model can rank flawlessly and still assign 40% risk to people whose true risk is 4%.
Calibration is the property a decision needs — if the model says 12%, do about 12 in 100 go on to develop the disease? It fails independently of discrimination, and it fails first when a score moves to a new setting, because both the baseline risk and the score's own mean and variance shift: different age structure, different prevalence, different ancestry composition. A calibration plot and a decision curve say something an AUC cannot. Absolute risks should be produced by re-estimating the baseline in the target population, never by transporting the discovery model's intercept.
6. From score to risk
The same model gives the risk for an individual directly. Affected means L > T, so
Everything anyone reports about a — decile relative risks, odds ratios per standard deviation, "3× the population average" — is a summary of this one curve. Which summary gets chosen is a rhetorical decision, not a statistical one, and the choices differ by more than an order of magnitude. The worked example does the arithmetic.
Note the shape in advance: \Phi is very flat in the tail, so when K is small, large moves in the score buy modest moves in absolute risk while producing enormous ratios. Rarer disease means bigger relative risks and smaller absolute ones — from the same \rho^2.
7. Portability: the central limitation
A score trained on one population loses accuracy when applied to another, and the loss is large. Prediction accuracy in individuals of African ancestry from European-trained scores runs at roughly a fifth to a half of the accuracy achieved in Europeans, with South Asian and East Asian ancestries falling in between. More informatively, accuracy declines continuously with genetic distance from the training sample — there is no cliff at a population boundary, and measurable decay is detectable even within a single ancestry group, where score performance varies with age, sex and socioeconomic position. That gradient is the signature of a sampling problem, and it is what you would predict.
Four mechanisms, all consequences of the score being fitted to markers in one sample:
| Cause | Mechanism | Effect on the score |
|---|---|---|
| LD differences | the weight was fitted for the tag–causal correlation r in the discovery population; in the target, r differs | the weight is applied to a marker that no longer tracks the causal variant; effects attenuate, and can reverse where LD flips |
| differences | a tag common in the discovery sample is rare or absent in the target | its 2pq contribution collapses toward zero; the score's mean and variance shift, breaking calibration even where ranking survives |
| Effect-size heterogeneity | G{\times}E and ; and \alpha = a + d(q-p) is frequency-dependent by construction (Ch 30) | the estimand itself differs between populations, independent of any measurement problem |
| Environment and trait definition | different exposure distributions, diagnostic thresholds, ascertainment, access to care | the thing being predicted is not the same trait, so even perfect weights mispredict |
A fifth, easily forgotten: residual in the discovery puts a non-causal component into the weights (Ch 51). That component is a property of the discovery cohort's structure and does not transfer — it can transfer with the wrong sign.
Now the framing, because it is routinely got wrong.
This is caused by who was sampled, not by biology differing between groups. African genomes have shorter LD blocks — the has been larger and there was no out-of-Africa bottleneck, so more independent recombination events are represented in any sample (Ch 29) — so a marker chosen for its correlation with a causal variant in Europeans is a worse proxy there. That is a statement about proxies, not about the trait, the causal , or the people. Run the identical pipeline with an African-ancestry discovery cohort and the score works there and degrades in Europeans. The asymmetry lives entirely in the data: European- ancestry participants remain around 90% of everyone ever included in a GWAS, against roughly 16% of the world's population.
Two things follow. failure is fixable by recruitment, and by nothing else completely. And because are being proposed to allocate screening and surveillance, deploying them at current accuracy delivers the least reliable predictions to the people already least well served — compounding health inequity rather than being merely neutral about it. That is an argument about deployment, not about the science.
One more distinction, non-negotiable: is a continuous, measurable quantity; race is a social classification. They are not interchangeable, they correlate only loosely, and a portability result reported in terms of the second when it was measured in terms of the first is a scientific error before it is anything else (Ch 28, Ch 58).
What helps. Multi-ancestry GWAS, which is both the fix and the bottleneck. Cross-population Bayesian methods that couple effects across populations under a shared prior while modelling each population's LD separately (PRS-CSx and its relatives; ensemble penalised-regression approaches), which typically recover a substantial fraction of the lost accuracy for under-represented groups without any new recruitment. Statistical to causal variants (Ch 52), because a causal effect transfers better than a tagging correlation does — this is the principled fix. Local-ancestry-aware scoring in admixed individuals, where a single global weight is wrong at each segment. And recalibration of the score's mean and variance as a continuous function of ancestry PCs, which is worth doing while remembering that recalibration fixes calibration, not discrimination: it makes the number honest, not more informative.
8. What it is actually good for
Risk stratification for screening
The realistic clinical use is as one more term in a model that already exists. For breast cancer, a 313-variant score is incorporated into the BOADICEA risk model (delivered through the CanRisk tool) alongside family history, reproductive and hormonal factors, mammographic density, and rare pathogenic variants in BRCA1, BRCA2 and PALB2 (Ch 54); it shifts a meaningful minority of women across a screening or prevention threshold. For coronary artery disease, adding a score to an established clinical equation improves the C-statistic by a small increment — under 0.01 to a few hundredths, depending on model and cohort.
The clinical question is not R^2. It is whether the score moves anyone across a decision boundary where the action changes. A score with a worse AUC that reclassifies 10% of people into a different screening interval is more useful than one with a better AUC that reclassifies nobody. That is what randomised trials of risk-stratified screening are set up to answer, and why "the score is significantly associated" was never the relevant endpoint.
The instructive contrast: genomic selection in agriculture
The same estimator — a marker-weighted sum predicting a — transformed animal and plant breeding. In US dairy cattle, genomic evaluation became official in 2009; bulls could then be selected before progeny testing, the generation interval fell sharply, and the annual rate of genetic gain in Holsteins roughly doubled (Ch 31). Nothing about the statistics is better. Everything about the setting is.
| Livestock / crops | Human clinical prediction | |
|---|---|---|
| Training vs target population | the same closed breed, re-trained every generation | one cohort, applied to everyone |
| LD structure | small N_e → long, stable LD; markers tag well and tag the same way in the target | LD varies continuously with ancestry |
| Environment | controlled, recorded, deliberately uniform | uncontrolled, unmeasured, correlated with |
| What is needed | an accurate ranking of candidates | a calibrated absolute risk for one person |
| Selection | direct, and the response is measured next generation | you can only advise |
| Intensity | extreme — one bull sires enormous numbers of offspring | not applicable |
The method is not the problem. Polygenic prediction is a mature, validated technology. What limits it in humans is that we cannot match the training population to the target, cannot control the environment, and need a calibrated number for an individual rather than a correct ordering of candidates.
Embryo selection
Preimplantation scoring of IVF embryos is sold commercially. The scientific case against expecting much from it is arithmetic, and it starts from a fact about siblings.
Under additivity and equilibrium, the variance of a among full sibs is half its variance in the population — sibs share half their genome in expectation — so the within-family standard deviation is 1/\sqrt{2} = 0.707 population SDs. Selecting the best of n embryos gains \mathbb{E}[\max_n \mathcal{N}(0,1)] \times 0.707 population SDs: 0.82 SD for 5 embryos, 1.09 SD for 10. That is the entire lever, and it is short because the comparison is within a family rather than across the population.
Take the disease of the worked example (K = 5\%, \rho^2 = 0.10) and select the lowest-scoring of five embryos in a family of average risk. Expected risk falls from 4.15% to 2.4% — a 43% relative reduction, an absolute reduction of 1.8 percentage points. The calculation is generous in three ways that all push the true figure down: it uses the population-level \rho^2, whereas within-family predictive power is measurably lower (part of a score's between-family signal is and genetic nurture, neither of which segregates between sibs); it treats the non-score component of liability as independent between siblings when siblings share both and rearing environment; and it assumes five viable, biopsied, genotyped embryos.
Further scientific objections stand on their own: selection is inherently pleiotropic, so moving one score drags every genetically correlated trait with it at a rate set by r_G (Ch 30) and nobody has enumerated what those are; the problem applies inside admixed families; and there is no way to evaluate the outcome for the person who results.
The ethical positions are genuinely contested and worth stating fairly. One holds that prospective parents already choose among embryos on other grounds, so choosing on expected health is at least permissible, and that a small expected benefit is still a benefit. Against that: consent obtained on an overstated premise is not informed; selection embodies a judgement about which lives are worth starting, which is the core of the disability-rights critique; the service is private and expensive and works best for the best-represented ancestries, so it distributes benefit regressively; and the line between disease risk and non-disease traits is not marked anywhere in the method — the same machinery scores height and cognitive test performance. Professional bodies have generally advised against clinical use for polygenic traits pending evidence, and in most jurisdictions the market is lightly regulated. This curriculum does not tell you which position to hold; it insists that the arithmetic above is prior to holding one.
Direct-to-consumer scores
Consumer genomics companies return polygenic reports for common conditions. These are typically research-grade rather than regulator-reviewed as diagnostic devices; they are computed from array genotypes plus ; they are usually trained on European-ancestry data and delivered to everyone; and they are calibrated against the company's own customer base rather than a population with a known prevalence. The defensible reading of such a report is a percentile within that company's reference sample, and nothing more. The 2025 bankruptcy and sale of 23andMe's database to a non-profit is the concrete reminder that a genomic database is an asset that can change hands (Ch 58).
Common misconceptions
| What people think | What's actually true |
|---|---|
| A high PRS means you will get the disease | It shifts a probability. In the worked example the top decile has a 12.8% lifetime risk — 87% of them never develop the disease |
| A PRS is a measurement of the person | It is a prediction from a model fitted to other people. Its accuracy is a property of the training cohort, not of the genome being scored |
| More SNPs is always better | Adding null variants adds variance and no signal. The optimal threshold is a bias–variance tradeoff that moves with sample size |
| Summing all genome-wide significant hits is the natural score | Marginal GWAS effects already contain the effects of everything they tag, so the sum counts each causal signal once per marker. Every method is a regularised fix for this |
| The best method is the most sophisticated one | The best prior is the one matching the trait's architecture. C+T beats Bayesian shrinkage on sparse traits |
| AUC 0.65 means the score is poor | The ceiling is set by . At K=5\% and h^2_l = 0.3, a perfect score reaches 0.82. Achieved-over-attainable is the meaningful ratio |
| A well-discriminating score gives correct risks | Discrimination is rank-invariant; calibration is not. Scores are validated on the first and used as if validated on the second |
| A top-decile odds ratio of 30 means a very large effect | Extreme-percentile odds ratios are chosen to maximise the number. The same model gives 2.6× against the population average |
| failure means the genetics differs between groups | It means the tagging correlations differ, because the score was fitted in one population. It is a consequence of who was recruited and is fixed by recruiting differently |
| Ancestry-specific accuracy justifies reporting scores by race | is continuous and measurable; race is a social classification. Accuracy decays continuously with genetic distance, including within any named group |
| Genomic prediction failed as a technology | It transformed animal breeding. In humans the population is unmatched, the environment uncontrolled, and the required output is a calibrated individual risk |
Worked example: turning a headline relative risk into an absolute one
A disease with lifetime prevalence K = 5\%, and a explaining \rho^2 = 0.10 of variance in liability — near the top of what is currently achieved for common disease.
Step 1 — the threshold. T = \Phi^{-1}(0.95) = 1.6449.
Step 2 — the risk curve. \rho = \sqrt{0.10} = 0.31623 and \sqrt{1-\rho^2} = \sqrt{0.9} = 0.94868, so
Step 3 — check it against the prevalence. For S \sim \mathcal{N}(0,1), \mathbb{E}[\Phi(aS-b)] = \Phi\!\big(-b/\sqrt{1+a^2}\big). Here \sqrt{1+1/9} = 1.0541 and -1.7338/1.0541 = -1.6449, so the average risk is \Phi(-1.6449) = 0.0500. ✓ The curve integrates back to the prevalence.
Step 4 — evaluate it.
| Percentile | s | s/3 - 1.7338 | Absolute risk | vs. median |
|---|---|---|---|---|
| 1st | −2.326 | −2.509 | 0.61% | 0.15× |
| 5th | −1.645 | −2.282 | 1.12% | 0.27× |
| 50th | 0 | −1.734 | 4.15% | 1× |
| 90th | +1.282 | −1.307 | 9.57% | 2.31× |
| 95th | +1.645 | −1.186 | 11.79% | 2.84× |
| 99th | +2.326 | −0.958 | 16.89% | 4.07× |
Averaging the curve over the whole top decile (not just its midpoint) gives a decile risk of 12.75%.
Step 5 — the same model, five headlines. All of these are true statements about the table above:
| Framing | Number |
|---|---|
| Odds ratio, 99th percentile vs 1st percentile | 33.4 |
| Relative risk, 99th percentile vs 1st percentile | 27.9 |
| Relative risk, top decile vs bottom decile | 11.9 |
| Relative risk, top decile vs the other 90% | 3.08 |
| Relative risk, top decile vs population average | 2.55 |
A press release choosing the first has multiplied the last by thirteen without adding any information. Extreme-percentile odds ratios are the most inflated presentation available, because the odds transformation and the extreme comparator both work in the same direction.
Step 6 — what the decision actually needs.
- Top-decile absolute risk 12.75% against a population 5% — an increase of 7.8 percentage points, and 87% of the top decile never develop the disease.
- Fraction of all cases falling in the top decile: 0.1 \times 0.1275 / 0.05 = 25.5\%. Screening only the top decile would miss three quarters of cases. High relative risk in a small group is compatible with most cases arising outside it — the same arithmetic that makes population-wide prevention outperform high-risk targeting for many conditions.
- Bottom decile absolute risk 1.07%, which is not zero, and is not a licence to skip screening.
Step 7 — change only the prevalence. Keep \rho^2 = 0.10 and set K = 0.5\%. Then T = 2.5758, b = 2.7152, and the top-decile risk is 1.75% — a larger relative risk (3.50× the population average, up from 2.55×) attached to a far smaller absolute one. Rarer diseases generate more impressive ratios and less consequential risks. The relative risk is uninterpretable without the baseline, and the conversion is a single multiplication that is almost never printed alongside the headline.
Connections
- Back to: Ch 30 — the a PRS estimates, and the liability-threshold model everything in §5–§6 runs on; Ch 31 — h^2_{\text{SNP}} is the ceiling, and genomic selection is the agricultural sibling; Ch 29 — LD is both what makes tag-based scores possible and what makes them non-portable; Ch 28 — as a continuous, measurable quantity; Ch 51 — where the weights come from and what contaminates them; Ch 41 — variant , without which weights silently fail to match
- Forward to: Ch 52 — to causal variants is the principled fix; Ch 54 — the rare, large-effect end of the same allelic spectrum, where a single variant does what a whole score cannot; Ch 55 — why polygenic risk is not reported as a variant classification; Ch 57 — implementation in health systems; Ch 58 — equity, consent, data stewardship and the embryo-selection debate