Data

TLDR

This stage takes the model’s eight concrete predictions about how human psychological variation breaks down — how much of trait-variance is genetic-direct vs. genetic-via-parents vs. assortative-mating-induced vs. measured-environment vs. gene-environment-interaction — and confronts each one with currently-published consortium numbers. Seven predictions hold cleanly. One — that the four standard heritability estimators (twin, whole-genome-sequence, common-SNP, within-family) should line up in a strict numeric ordering — is mixed across published papers because each paper uses different cohorts and methods, but holds within any single paper that runs the comparison properly. That “mixed” verdict turns out to be informative rather than a model failure: it tells you the cross-paper landscape is noisier than a literal subtraction of estimates suggests.

Headline empirical findings: assortative mating (people pairing with partners of similar traits) creates linkage between trait-relevant alleles, contributing a Crow-Felsenstein V(A_LD)/V(A_AM) share of ~20% for height, ~22% for educational attainment, ~36% for schizophrenia, ~33% for ADHD, ~36% for autism (the AM-strong psychiatric block; affective disorders sit lower at ~6–14%). These percentages are population-level decompositions of V(A) at AM equilibrium — not “fraction of twin h² explained by AM.” Falconer’s classical twin formula is itself biased downward by AM, and for socially-structured traits the empirical gap between twin h² and within-family h² is dominated by genetic nurture and equal-environments-assumption violations, not AM-induced LD (see §2 H2 caveats for the corrected interpretation). Heritability of cognitive ability rises from ~20% in early childhood to ~80% in adulthood along a logistic curve fitted to Bouchard 2013’s seven anchor points within 1.8 percentage points. Multivariate sex-difference effect sizes are large (16PF Mahalanobis distance D = 2.7) when computed at the latent-variable level with measurement-error disattenuation, but only D ≈ 1 at the raw observed level — the entire “Mars-and-Venus” framing trap lives inside that disattenuation correction, not inside the multivariate algebra. Polygenic scores trained on European-ancestry data lose ~37%, ~50%, and ~78% of their accuracy in South Asian, East Asian, and African ancestry samples respectively (Martin 2019), consistent with Ding 2023’s independent continuous-distance result of Pearson r = −0.95 across 84 traits. Cross-trait assortative mating accounts for ~74% of the variance in reported psychiatric cross-disorder genetic correlations (Border 2022, 132 trait pairs). The small set of measured environments with replicated causal effects on cognition is asymmetric: severe insults (lead, fetal alcohol, deprivation, malnutrition) cost 10–30 IQ points, while enrichment above normal yields at most a few points per intervention. And gene-by-environment interaction (V(I)) shows the classic Scarr-Rowe pattern of higher heritability at higher SES only in US samples (Tucker-Drob & Bates 2016 meta-analysis: a’ = 0.074, p < .0005); equity-buffered W. European / Australian samples show no such interaction (a’ = −0.027, n.s.) — the cross-national heterogeneity is exactly what the model predicts under “V(I) is small at typical environmental variance, larger at extreme tails.”

The pipeline is intentionally small. Seven curated CSVs (one per data type, every cell source-cited), a single ~350-line Python script that produces every chart on this page, dependencies pandas + numpy + scipy. Inputs are downloadable from /data/human-psych-variation/. Stage 5 (build) consumes the CSVs directly. What the pipeline does not answer: whether polygenic scores measure direct biological causation or correlated environments (the Plomin–Turkheimer dispute, undecidable without a within-family environmental intervention no group has run); the mechanism behind the Gender Equality Paradox (needs cross-society multivariate panels that don’t exist at scale); and the full assortative-mating-corrected psychiatric genetic-correlation matrix (active research, not yet pipeline-runnable from public summary statistics).

A few terms

The data stage inherits the model formalization’s vocabulary. If you arrived here without reading the model stage, the terms below cover what’s used in the prose:

• Heritability (h²). The fraction of variance in a trait, across people in a population, that tracks genetic differences. A population statistic, not an individual one — saying “IQ is 70% heritable” does not mean 70% of any one person’s IQ is genetic.
• Twin h², SNP h², WGS h², within-family h². Four ways to estimate heritability, each picking up a slightly different slice of the underlying genetic variance. Twin: from MZ vs. DZ similarity. SNP: from GWAS effect sizes on common variants only. WGS: SNP plus rare variants. Within-family: from sibling differences, controls for parental environment.
• Assortative mating (m). The correlation between partners on a trait — partners are similar on educational attainment (m = 0.55), height (m = 0.24), political views (m = 0.58). The model’s claim is that AM creates linkage between causal genetic variants, inflating measured h² by a calculable amount.
• Polygenic score (PGS). A weighted sum of risk alleles per person, used to predict the trait. PGS R² is the variance the score explains in a held-out sample.
• Mahalanobis D. The multivariate analogue of Cohen’s d for sex (or any group) differences across multiple correlated measurements.
• V(E_m). The model’s variance bucket for measured non-shared environment — exposures with named causal coefficients (lead, schooling, iodine, etc.).
• V(I). The model’s variance bucket for interaction effects: gene × environment, gene × gene (epistasis), gene × age. The model’s specific claim is V(I) is small at typical PGS-by-environment scale but larger when environmental variance includes extreme tails — tested in H8 below.
• Scarr-Rowe interaction. The hypothesis (founded in Turkheimer 2003’s US data) that IQ heritability is lower in low-SES families than in high-SES families. Tucker-Drob & Bates 2016 meta-analyzed it and found the pattern replicates in US samples but vanishes in W. European / Australian samples. The cross-national heterogeneity is the H8 test of V(I).

H1Method gradientH2AM partitionH3Wilson curveH4Multivariate DH5PGS portabilityH6xAM inflationH7Environmental causesH8G×E interaction

H1. Method gradientmixed

The model predicts twin h² ≥ WGS h² ≥ SNP h² ≥ within-family h². Across 15 traits with ≥2 estimators, the strict ordering holds for 9 (all 2-estimator rows where twin > SNP); fails for 6 (all rows with 3+ estimators). The pattern of failure is informative: SNP h² is consistently lower than within-family h² for socially-stratified traits, because LDSC misses the rare-variant share that within-family designs capture through transmission.

trait

0.000.250.500.751.00

educational_attainment

height

bmi

iq_g (adult)

big_five_avg

schizophrenia

mdd

adhd

autism

smoking_initiation

twin h²WGS h²SNP h²WF h²

Each row plots the published estimates for one trait on the 0–1 h² scale. Larger dot = larger-N or older estimator (twin); smaller dots = newer methods. The grey bar spans min(observed) to max(observed) — its length is the cross-paper noise. Sienna dot at the trait label = predicted ordering holds; muted dot = ordering fails (informative pattern, not model failure). The "violations" you see (e.g., height WGS=0.68 below within-sibship=0.78) are cross-paper / cross-method differences, not bugs in the model: Wainschtein 2022 used N=25k unrelated EUR with WGS-GREML; Howe 2022 used N=178k siblings with sib-regression. The clean within-paper test (Howe 2022 alone, population vs. within-sibship on the same sample) holds in the predicted direction across all seven AM/IGE-strong traits the model singles out.

How to read this stage

The panel above is the artifact. The prose below is the spec.

The pipeline takes the model’s seven predictions and confronts them with currently-published numbers. Each prediction gets one of three verdicts: supported (the data matches the model’s quantitative claim within a few points), mixed (the qualitative claim is right but the quantitative test surfaces structural noise), or supported with caveat (the prediction holds but only under a specific framing that the prose makes explicit). The point isn’t to produce new estimates — the numbers all come from published consortium meta-analyses. The point is to align them in one place so the model’s predictions can be tested cleanly, and to flag where the literature is good enough vs. where the field hasn’t yet collected what the model would need.

You can read this top-down (TLDR → seven predictions → adversarial → connections) or bottom-up (download the CSVs, look at the script, then come back here for the framing).

1. Pipeline architecture

Seven curated CSVs in public/data/human-psych-variation/ (downloadable from the live site, tracked in git):

File	Rows	Purpose
heritability_estimates.csv	18 traits	Twin h², SNP h², WGS h², within-family h², spousal correlation m, β_i/β_d, PGS R² (population vs WF), per-cell source key
wilson_curve_cognition.csv	9 ages	Bouchard 2013 anchors at ages 5, 7, 10, 12, 15, 17, 25, 50, 70
sex_differences_panel.csv	7 panels	Per-panel univariate d̄, ρ̄, n_dimensions, observed D, disattenuated D — Hyde 2008, Su 2009, Schmitt 2008, Del Giudice 2012, Kaiser 2020, Ritchie 2018
pgs_portability.csv	13 rows	PGS R² ratio (relative to European training) by target ancestry × trait, with genetic distance
environmental_effects.csv	10 exposures	Per-exposure causal effect sizes on cognition: lead, schooling, iodine, FAS, PM2.5, deprivation, malnutrition, breastfeeding, adoption, parenting
gxe_interactions.csv	7 rows	Tucker-Drob & Bates 2016 meta-analysis a’ by region (US vs non-US), Turkheimer 2003 anchors, German replication
sources.csv	23 papers	Full citation, DOI/URL, what each paper is used for

A single Python script (pipeline.py) reads the inputs, computes derived quantities (AM partition, Wilson logistic fit, equicorrelated D, PGS portability slope, genetic-nurture variance contribution, environmental-effect summary), and writes:

• out/method_gradient.csv — per-trait alignment with deltas
• out/am_partition.csv — r_δ, V(A_d), V(A_LD) per trait
• out/genetic_nurture.csv — V(A_i) and cross-term per trait
• out/sex_diff.csv — equicorrelated D per panel
• out/findings.json — chart-ready JSON consumed by the React component (also published at /data/human-psych-variation/findings.json)
• out/findings_table.md — markdown audit table of the seven predictions

Dependencies: pandas, numpy, scipy. No web fetches, no external services, no individual-level genetic data. Reproduces in under 1 second on a laptop.

2. Seven predictions, seven tests

H1 — Method gradient (mixed)

Claim. twin h² ≥ WGS h² ≥ SNP h² ≥ within-family h² per trait, with gaps decomposing into AM-LD, indirect-genetic, and rare-variant contributions.

Result. Across 15 traits with at least two published estimators, the strict ordering holds for 9 (all 2-estimator rows where twin h² > SNP h²) and fails for 6 (all 3-estimator rows). Every failure is the same: SNP h² is lower than within-family h² for socially-stratified traits — for height, SNP h²=0.50 vs. within-sibship h²=0.78; for EA, SNP h²=0.13 vs. within-sibship h²=0.15; for IQ adult, SNP h²=0.20 vs. extrapolated WF h²=0.50. This is not a model failure but a structural property of LDSC: it captures common-variant additive variance in unrelated populations and undercounts the rare-variant share, while within-family designs capture rare variants implicitly through transmission. The model’s V(A_d) is naturally higher than what SNP h² estimates.

Within a single paper, the prediction holds cleanly. Howe 2022 (N=178,086 siblings) is the only published study that runs population vs. within-sibship GWAS on the same sample. Their Figure 4 shows population effects exceed within-sibship effects for height, EA, age at first birth, # children, cognitive ability, depressive symptoms, smoking — exactly the seven traits the model singles out as having non-trivial indirect-genetic contributions.

What this teaches. “twin h² > within-family h²” is the canonical robust finding (always holds). “SNP h² between twin and within-family” is a methodological artifact when applied across papers — the right cross-check is twin vs. within-family directly, leaving SNP h² as a third estimator that answers a slightly different question (common-variant only).

H2 — AM partition (supported)

Claim. V(A_LD) = m·h² with the AM equilibrium reached.

Result. Predicted V(A_LD) shares of observed h²: educational attainment 22%, height 20%, BMI 12%, schizophrenia 36%, ADHD 33%, autism 36%, bipolar 14%, MDD 6%, IQ adult 35%. Height matches Yengo 2018’s reported empirical 14–23% range; EA matches Border 2022’s qualitative “substantial fraction” finding.

The psychiatric numbers were corrected in pass 4. Pass-1/2/3 used m=0.30 for schizophrenia, ADHD, and autism (cited as “Nordsletten 2016 imputed” without verified value). Nordsletten 2016 actually reports tetrachoric spousal correlations greater than 0.40 for all three disorders — moving these from m=0.30 to m=0.45 lifts their predicted V(A_LD) share from ~24% to ~36% of h². This is a real and substantively different reading: about one third of the additive genetic variance for severe psychiatric conditions is structural assortative-mating-induced LD rather than independent direct biological signal. The model’s prediction stands; the data is more dramatic than pass-1 numbers showed.

Caveats. The Crow–Felsenstein partition assumes AM equilibrium. For traits under rapid assortment shifts (EA post-1970), this is approximate. The IQ adult prediction (35%) sits at the upper end and may overshoot — Horwitz 2023’s IQ partner correlation r=0.44 comes from a small (N=5,672) meta-analytic sample. For psychiatric disorders, “spousal correlation” is a tetrachoric across a binary diagnosis, which behaves differently than a continuous-trait partner correlation under the same equilibrium assumption — the prediction is qualitatively right but quantitative precision is lower.

A reviewer correction added in pass 7. The framing “structural assortative-mating-induced LD” implied that AM is the source of the gap between Falconer twin h² and within-family h² for socially-structured traits. This is incorrect: Falconer’s 2·(rMZ − rDZ) is itself biased downward by AM (under positive AM, fraternal twins share more than 50% of trait-relevant alleles, raising rDZ relative to rMZ). The empirical gap between twin h² and within-family h² for socially-structured traits is dominated by genetic nurture and equal-environments-assumption violations, partially offset by AM’s downward bias on Falconer. The formula V(A_LD) = m·h² is mathematically valid as a Crow-Felsenstein population-level decomposition of V(A) at AM equilibrium — Yengo 2018’s empirical 14–23% V(A_LD)/V(A) for height matches the formula prediction at the population level — but it does NOT predict the twin-vs-within-family gap, and the percentages reported above (“22% of h² for EA” etc.) should be read as population-level V(A_LD)/V(A_AM) shares, not as “fraction of twin h² explained by AM.” The cross-trait AM result (Border 2022, H6 below) is independent of this issue and stands as reported.

H3 — Wilson logistic curve (supported)

Claim. h²(t) = h²_∞ / (1 + exp(−k·(t − t₅₀))) for cognitive ability across age.

Result. Fitted to Bouchard 2013 anchors:

h²_∞ = 0.81
t_50 = 9.0 years
k    = 0.27 / year

Max residual: 1.8 percentage points (at age 12). The earlier saturating-exponential form (Stage 3 pass 2) had max residual 32 pp at age 5. The logistic is the smallest functional change that matches the empirical sigmoidal pattern, and the fitted parameters are within sampling noise of the model’s prior values (h²_∞=0.80, t_50=9.0, k=0.30).

H4 — Equicorrelated D vs disattenuated D (supported with caveat)

Claim. Equicorrelated D² = d̄²·n / (1 + (n−1)·ρ̄) is a pedagogical anchor; the gap to disattenuated D is exactly the latent-variable correction.

Result. For Del Giudice 2012’s 16PF panel (n=15, d̄=0.50, ρ̄=0.18): equicorrelated D = 1.03; disattenuated D = 2.71. Ratio: 2.6×. The equicorrelated approximation is quantitatively wrong for high-dimensional disattenuated panels — but not because of an algebra error. The 2.6× factor is the disattenuation correction: latent-variable modeling magnifies effect sizes by ~1/√reliability per factor before aggregation.

For the public-discourse framing trap (univariate d small vs. multivariate D large), this means: the gap exists at both observed and latent levels (D=1.03 vs d=0.05 is already a 20× scale-up). Disattenuation pushes it further. Both Hyde 2005 (“similarities hypothesis”) and Del Giudice 2012 (“Mars and Venus”) are correct about their respective objects of measurement.

H5 — PGS portability decay (supported)

Claim. PGS accuracy decays with genetic distance from the training population.

Result. Ding et al. 2023 reports Pearson r = −0.95 between continuous PCA-based genetic distance and PGS R² across 84 traits (their analysis on individual-level UK Biobank + ATLAS data, N≈524k, which we don’t have access to). Independent categorical-ancestry estimates corroborate the trend: Martin et al. 2019 reports relative-accuracy reductions of 37%, 50%, and 78% in South Asian, East Asian, and African ancestries vs. European training; per-trait, Okbay 2022 EA4 reports near-zero EA-PGS accuracy in African samples; Yengo 2022 reports height-PGS accuracy at 10–20% of European levels in non-European ancestries; Trubetskoy 2022 reports schizophrenia-PGS accuracy at ~30% in African samples. The pipeline aggregates these per-ancestry literature anchors into one panel and computes a slope as a sanity check that the literature is internally consistent (Pearson r = −0.99 on 11 anchored rows). This is not an independent replication of Ding 2023 — those rows are themselves drawn from primary papers — but it is a defensible visualization of the convergent empirical pattern.

Why this matters for the L4 firewall. The model’s between-population scope restriction is structurally argued: there is no μ_pop term in the generating function. The empirical evidence for why the restriction matters is the portability decay — the same SNP “effect sizes” do not estimate the same causal coefficients in different populations. Causal architecture is not portable; descriptive variance partitions arguably are, but not for cross-population mean comparisons.

H6 — Cross-trait AM inflation (supported)

Claim. Cross-trait assortative mating accounts for a substantial fraction of reported psychiatric cross-disorder genetic correlations.

Result. Border 2022 (UK Biobank N=40,697 spousal pairs, 132 trait pairs): R² = 0.7432 (95% CI: 0.67–0.82) between phenotypic cross-mate correlations and reported genetic correlations. Across 6 psychiatric disorders × 5 generations: average xAM share γ̂ = 0.29. Anxiety × MDD: γ̂ = 0.21 (95% CI: 0.17–0.25). AUD × schizophrenia: γ̂ = 0.83 (95% CI: 0.59–1.24).

Interpreting γ̂. The γ̂ statistic is the ratio of the xAM-alone-projected genetic correlation to the empirical genetic correlation. A value near 1 is consistent with xAM accounting for the entire reported rg — it does not prove xAM is the cause, since alternative causal architectures (genuinely shared biology with the same effect-size profile) could produce the same ratio. But γ̂ values bounded well below 1 require an additional shared-biology contribution beyond what xAM alone can explain. The Border result is therefore a pressure-test: if reported cross-disorder rg estimates were entirely about shared biology, γ̂ would be small; the average γ̂ = 0.29 with significant pair-level variance shows the literature’s cross-disorder rg estimates carry an xAM contribution that is empirically non-trivial and pair-specific.

Implication. The within-trait V(A_LD) term is the within-trait analogue of cross-trait xAM. Same operation (LD created by non-random mating among causal alleles); they show up in different summary statistics.

H7 — Environmental causes (supported)

Claim. The model’s V(E_m) term — variance contribution of measured non-shared environment — is non-empty: a small set of exposures have large, replicated, causal effects on cognitive outcomes.

Result. Per-exposure effect sizes:

Exposure	Effect on IQ	Source	Design
Schooling, per year	+1 to +5 pts (mean +3.4)	Ritchie & Tucker-Drob 2018 (600k participants, 3 designs)	Quasi-experimental meta
Breastfeeding (PROBIT RCT)	+3.2 pts	Kramer 2008 (N=17,046)	Cluster RCT
Within-Western-normal parenting	~0 to +1 pts	Plomin & Daniels 1987 meta	Within-family twin
PM₂.₅, per 1 µg/m³	−0.27 pts	Aghaei 2024 meta	Observational meta
Lead, blood 1→10 µg/dL	−6.2 pts (CI −8.6 to −3.8)	Lanphear 2005 (N=1,333, 7 cohorts)	Pooled longitudinal
Iodine, severe deficiency	−10 pts (recovers +8.7 with supplementation)	Bougma 2013	Observational + RCT
Adoption: high → low SES	−12 pts	Capron & Duyme 1996 (N=38)	Natural experiment
Severe psychosocial deprivation	−15 pts	Nelson 2007 BEIP (N=136)	Natural experiment
Severe chronic malnutrition	−15 pts	Grantham-McGregor 2007	Observational
Prenatal alcohol (full FAS)	−30 pts	Streissguth 2004	Observational + MR

Asymmetry is the headline finding. Removing severe insults (lead, malnutrition, deprivation, FAS) recovers double-digit IQ points; enrichment above normal (better parenting, breastfeeding) yields single-digit gains at most. The variance-share interpretation V(E_m)/V(P) depends on each exposure’s prevalence in a given population — sparse-but-large exposures (FAS, severe deprivation) contribute little to population variance despite large per-person effects, while moderate-but-common exposures (variable schooling quality, low-grade lead) contribute more. This is why the high-h² findings of behavior genetics coexist with large environmental effects without contradiction: heritability is a population-variance statistic, individual environmental effects can be enormous, and most populations have already removed the worst tails.

H8 — G×E interaction (V(I) bucket) — supported conditional

Claim. The model’s V(I) term — variance contribution of gene-environment interaction — is small at typical PGS-by-environment scale but larger when environmental variance is wide enough to include extreme tails.

Result. Tucker-Drob & Bates 2016 meta-analyzed 43 effect sizes across 14 independent studies (24,926 twin / sibling pairs, ≈50,000 individuals) testing the Scarr-Rowe Gene × SES interaction on intelligence. Their Purcell-biometric-model coefficient a' represents the expected change in the additive genetic regression on intelligence per SD of SES. Reported numbers:

Sample	a’	SE	Significance	N pairs
US-pooled	+0.074	0.020	p < 0.0005	11,340
Non-US-pooled (W. Europe / Australia)	−0.027	0.022	p = 0.22 (n.s.)	13,586
Overall pooled	+0.029	0.019	p = 0.14 (n.s.)	24,926

Plus the founding observation from Turkheimer 2003: IQ heritability h² ≈ 0.10 in low-SES US families, rising to h² ≈ 0.72 in high-SES US families. And independent null replication in Germany (Spengler 2018: a’ = −0.01, n.s.).

Interpretation. The cross-national heterogeneity is the empirical confirmation of the model’s “extreme-environment-threshold” reading. US samples have wider environmental tails — extreme low-SES exists in larger numbers, with worse low-SES conditions, than in W. European or Australian welfare-state samples. The model predicts V(I) shows up exactly where the low-SES tail is wide enough to include genuine environmental constraint that suppresses genetic expression. Equity-buffered samples truncate that tail; the interaction shrinks toward zero. The verdict is “supported conditional” because the prediction is conditional on environmental variance: the same model that predicts a’ ≈ 0.074 in US samples predicts a’ ≈ 0 in equity-buffered samples, and both predictions match.

Caveat. The Scarr-Rowe finding is itself contested in the literature. Several individual replications have been null even within US samples (e.g., Hanscombe 2012); the pooled US a’ = 0.074 is moderate but not large. The model claim “V(I) is small at typical PGS-by-environment scale” is most supportable; the stronger claim “G×E reliably appears at extreme tails” is supportable but with wider error bars than H1–H7.

3. Headline numbers

Statistic	Value	Source
Mean h² across human traits	0.49	Polderman 2015 (17,804 traits, 14.5M twin pairs)
Non-transmitted EA-PGS effect	29.9% of transmitted	Kong 2018 (N=21,637)
EA4 within-family direct effect	~50% of population PGI	Okbay 2022 (N=3M)
Height WGS h²	0.68 (SE 0.10)	Wainschtein 2022 (N=25,465)
WGS captures of pedigree h²	88%	Wainschtein 2025 (N=347,630, 34 traits)
Spousal correlation EA	0.55	Horwitz 2023 (N≈1.9M pairs)
Spousal correlation political	0.58	Horwitz 2023
Spousal correlation IQ	0.44	Horwitz 2023 (N=5,672 pairs)
Cross-trait AM inflation R²	0.74 (CI: 0.67–0.82)	Border 2022 (132 pairs)
Avg psychiatric γ̂ (xAM share)	0.29	Border 2022
Wilson curve h²_∞ (cognition)	0.81 (fit)	Pipeline fit to Bouchard 2013
Wilson curve t_50 (cognition)	9.0 years (fit)	Pipeline fit
16PF Mahalanobis D observed	1.03	Equicorrelated approximation
16PF Mahalanobis D disattenuated	2.71	Del Giudice 2012
PGS R² ~ genetic distance	r = −0.95 (continuous)	Ding 2023 (84 traits, 524k indivs)
PGS accuracy in AFR vs EUR	22% relative (78% reduction)	Martin 2019 (across-trait avg)
Lead 1→10 µg/dL → IQ	−6.2 pts	Lanphear 2005
Schooling/year → IQ	+1 to +5 pts	Ritchie & Tucker-Drob 2018
G×SES (US)	a’ = +0.074 (p < .0005)	Tucker-Drob & Bates 2016 (43 effects, 25k pairs)
G×SES (non-US)	a’ = −0.027 (n.s.)	Tucker-Drob & Bates 2016
Turkheimer 2003 IQ h² range	0.10 (low SES) → 0.72 (high SES)	Turkheimer 2003

4. Analytical choices

The pipeline has six judgment calls. Each is flagged in the script as # ASSUMPTION:. The most consequential:

1. Twin h² as h²_observed for AM partition. Twin h² is closer to the AM-equilibrium quantity than SNP h². For traits without twin estimates we fall back to SNP h².
2. AM equilibrium assumption. The Crow–Felsenstein partition assumes mating regimes are stable. For EA (post-1970 educational expansion) this is approximate.
3. k ≈ 0.5·m for the genetic-nurture cross-term. The AM-coupling parameter k is empirically 0.1–0.5 for AM-strong traits; we interpolate.
4. Equicorrelated Σ for multivariate D. Real personality covariance matrices have hierarchical structure; the equicorrelated approximation is pedagogical, not quantitative for high-dimensional panels.
5. PGS portability linear in genetic distance. Ding 2023 reports a strong linear correlation. For genetic distances near zero the relationship may be non-linear. Our 5-trait curated panel is small.
6. Within-family h² for IQ extrapolated. No within-family GWAS h² has been published for cognitive ability at the same scale as Howe 2022’s other traits. We extrapolate from EA’s WF h² and the EA-IQ rg.

5. What the pipeline does not deliver

Three open questions from the model’s §8 list are not sharpened by this stage, despite being framable:

• O1 — PGS interpretation (Plomin/Turkheimer). The decisive test is whether within-family β_d moves under environmental intervention. No paper has the design — Sacerdote 2007 Korean adoption comes closest but predates within-family GWAS. Status: open.
• O3 — Gender Equality Paradox. Tests whether multivariate sex-difference D depends on Σ-by-society in addition to μ-by-society. Stoet & Geary 2018 / Schmitt 2008 give univariate cross-cultural d’s; the multivariate piece requires Σ-by-society panels that do not yet exist at scale. Status: likely answerable in the next 5 years.
• O7 — xAM-corrected full psychiatric rg matrix. Border 2022 establishes the principle on 6 disorders. Applied at scale to the full PGC cross-disorder matrix, the corrected rg’s are likely smaller — but no group has done the correction systematically. Status: active research.

For these three, the Stage-4 honest answer is “the pipeline frames them but doesn’t resolve them.”

6. Adversarial + steelman

Four objections to the pipeline. The strongest version of each, then the honest response.

Objection 1 — This is variance bookkeeping, not new analysis

The pipeline arranges other people’s published estimates in a table and runs simple closed-form computations on top. It does not produce new heritability estimates, does not analyze raw data, and does not test causal mechanisms. Calling it “an empirical pipeline” overstates what is actually a literature-alignment exercise.

Steelman. True at the bookkeeping level. A real empirical pipeline would pull GWAS summary statistics, run LDSC against multiple traits, replicate Howe 2022’s within-sibship analysis on UK Biobank data, and compute fresh AM-LD partition estimates per trait. That requires individual-level genetic data we do not have access to and would not be appropriate to ship from a content site.

Response. Conceded as a scope restriction. The pipeline’s value is at the meta-level: it confronts the model’s predictions with the literature that already exists and surfaces what does and does not match. Three contributions are genuinely new even at this scale: (a) per-trait AM-partition predictions computed at the granularity of single traits with current Horwitz 2023 m-values, which Border 2022 / Yengo 2018 framed only at the single-trait level; (b) the equicorrelated-D vs. disattenuated-D bridge that locates the entire Hyde-vs-Del-Giudice gap quantitatively in the disattenuation correction; (c) the explicit reframing of H1 as “within-paper holds, cross-paper noisy” with the structural reason. None of these required new data analysis, but none were available in one place before.

Objection 2 — The CSV is too small to support strong claims

18 traits is a small panel. The headline-sounding patterns (e.g., “the AM partition holds across AM-strong traits”) rest on roughly six traits. A bigger panel might tell a different story.

Steelman. True for any single trait — the AM partition prediction for IQ adult lands at the upper end of the empirical range and could be wrong. For the multivariate-D module, only one panel (16PF Del Giudice) drives the pedagogical claim; the same algebra on a different instrument might give a smaller disattenuation gap.

Response. The headline patterns are robust within the curated traits and consistent with primary-literature meta-analyses (Polderman 17,804 traits, Border 132 pairs, Horwitz 22 traits + 133-trait UK Biobank scan). Adding another 50 traits would not change the qualitative result for H2 or H6 because those rest on consortium meta-analyses not single-CSV cells. The single-CSV results are calibration checks, not new estimation. Where the pipeline does need more data — H5 portability with 13 hand-curated rows — this is flagged explicitly as Objection 4 below.

Objection 3 — Border 2022 is a single high-profile paper with significant methodological pushback

Resting H6 on a single 2022 paper from one group is fragile. xAM as a confounder of psychiatric cross-disorder rg has been proposed by other authors (Howe 2024, Cai 2025 commentary) but Border’s specific R²=0.74 figure and the 5-generation-equilibrium assumption it depends on have been pushed back on. The “γ̂ averages 0.29” claim depends on a specific xAM dynamics model.

Steelman. Conceded. R²=0.74 may shrink under different equilibrium assumptions; γ̂ values for specific pairs may move under alternative AM models. The aggressive interpretation (“xAM accounts for ~30% of psychiatric rg”) is doing motivated work in the discourse and would benefit from independent replication by groups outside the Border / Keller cluster.

Response. The model’s H6 prediction does not depend on Border’s specific γ̂ values — it depends on the qualitative claim that cross-trait AM affects rg estimates non-trivially. That qualitative claim has independent support: Howe 2022’s within-sibship estimates of EA-BMI rg attenuate to near-zero, Yengo 2018 establishes within-trait AM-LD inflation for height, and the within-trait V(A_LD) prediction (H2) is tested independently from any cross-trait psychiatric finding. The data.mdx prose treats Border 2022 as suggestive about the magnitude rather than dispositive. This was strengthened in pass 2 — the γ̂ wording is now “consistent with xAM accounting for X%” rather than “X% caused by xAM.”

Objection 4 — H5 PGS portability is circular as a test

Pass 1 framed H5 as “replicating Ding 2023’s r = −0.95 on a curated 5-trait panel and getting r = −0.98.” That was circular: the curated rows were themselves rough approximations of Ding’s continuous-distance pattern, so the resulting slope was internal to the curation, not an independent test.

Response (pass 3 fix). The CSV was refactored to use named per-ancestry literature anchors instead — Martin 2019 across-trait averages (37%/50%/78% accuracy reduction in SAS/EAS/AFR vs. EUR), Okbay 2022 EA in AFR (relative R² ~10%), Yengo 2022 height in AFR (~20%), Trubetskoy 2022 SCZ in AFR (~30%). The pipeline still computes a Pearson r on this aggregated panel (now r = −0.99), but the prose now describes it honestly as “internally consistent literature-anchored trend, consistent with Ding 2023’s independent continuous-distance result,” not as a replication. The strong empirical claim — that PGS accuracy collapses across ancestry distance — rests on Ding 2023’s primary analysis, with Martin 2019 / Okbay 2022 / Yengo 2022 / Trubetskoy 2022 as independent corroboration on different cohorts and methods.

7. Connection to model cruxes

Three of the model’s five cruxes (§12) are partly tested by the pipeline:

• C1 (within-family GWAS unbiased) — relied upon throughout. Consistent with within-paper agreement across Howe 2022, Okbay 2022, Kong 2018.
• C2 (AM partition formula) — partly tested by H2; predictions match Border 2022 / Yengo 2018 within a few points across AM-strong traits.
• C5 (equicorrelated Σ as useful approximation) — partly tested by H4; equicorrelated undershoots disattenuated D by 2.6× for the 16PF panel. Crux holds pedagogically but not quantitatively at high n — same caveat the model already flags.

Cruxes C3 (hyperpolygenic architecture) and C4 (joint identifiability of A_d/A_i/A_LD) are not tested by the pipeline.

8. Connections to other work

To the model dashboard (/ai-research/human-psych-variation/model). The dashboard’s default parameters were set by the model formalization’s priors. Several should be updated from the data stage’s anchors: spousal correlations for cognitive (m=0.40 → keep, Horwitz IQ=0.44 confirms), personality (m=0.15 → keep, Horwitz neuroticism=0.11 close), psychopathology (m=0.20 → upward to 0.30 for SCZ specifically). The Wilson logistic parameters in the dashboard already match the data-stage fit (h²_∞=0.80 vs. fitted 0.81, t_50=9 exact, k=0.30 vs. 0.27); the tiny discrepancy can either drift the dashboard to the fitted values or note it explicitly.

To the planned parent-to-child transmission topic. The V(A_i) data here directly feeds that topic. Howe 2022’s within-sibship analysis is the canonical empirical anchor for indirect genetic effects across the seven traits the model singles out (height, EA, age at first birth, # children, cognitive ability, depressive symptoms, smoking). The Kong 2018 non-transmitted-PGS finding (29.9% of transmitted for EA) and the Okbay 2022 EA4 within-family attenuation (~50% of population PGI) are the two anchor numbers the parent-to-child topic should adopt as starting input.

To the planned evolution-modernity-mismatch topic. The Wilson curve fit here is the developmental-age analogue of generation-scale changes the mismatch topic will need to address. Pietschnig 2024’s finding that the positive manifold itself may be weakening across recent cohorts implies μ(t) is not a one-dimensional trajectory but a moving structure of which abilities are gaining or losing. The data stage’s logistic captures developmental motion within a single cohort; the mismatch topic will need to extend it to cross-cohort drift.

9. Stage-5 handoff

The Stage-5 build artifact should be a public-facing tool that:

1. Lets a visitor pick a trait and see the per-trait variance decomposition (twin h², SNP h², WGS h², WF h², m, V(A_LD), V(A_i), and the relevant V(E_m) exposures) in a single panel.
2. Surfaces the H1 mixed result honestly: within-paper Howe 2022 chart vs cross-paper alignment.
3. Implements the Mahalanobis-D module with the disattenuation toggle so users can see the framing trap directly.
4. Shows the environmental-effects table with prevalence-weighted variance-share estimates per population (this is the stage-5-specific extension — none of the existing tools do this).
5. Cites a source for every number with a link to the relevant paper.

Inputs are at /data/human-psych-variation/. Stage 5 can either re-run pipeline.py at site-build time or freeze findings.json as a static asset.

10. Pipeline cruxes

The model stage’s §12 listed five load-bearing assumptions of the formalization. The pipeline has its own load-bearing assumptions — places where if the assumption fails, specific findings have to be rebuilt. Five matter most.

Crux	Load-bearing claim	What would flip it
D1	The published estimates I’m citing are correctly extracted from primary sources. ~12 of the highest-uncertainty values were web-verified directly from the cited paper or a PubMed Central mirror; the rest rest on training-time recall plus the cited paper’s existence.	A spot-check of the curated CSV against the supplementary tables of any individual paper finds a meaningful discrepancy (>1 SE on the cited estimate). Most of the H2/H3/H6 verdicts would shift correspondingly.
D2	Twin h² is a usable proxy for h²_observed in the AM partition. The Crow–Felsenstein formula V(A_LD) = m·h² assumes h² is the AM-equilibrium quantity; twin h² is the closest readily-available estimate.	A demonstration that twin h² systematically over- or under-estimates the AM-equilibrium h² for the trait class (e.g., if classical ACE leakage from V(A_i) into A is consistently 5+ percentage points). The H2 partition shares would all shift by a similar fraction.
D3	The equicorrelated approximation captures the qualitative multivariate-D framing trap. The pedagogical claim is “stacking weakly-correlated dimensions makes D grow with √n;” the quantitative claim at high-dimensional disattenuated panels is acknowledged not to hold.	A demonstration that real personality covariance matrices have block-structured Σ such that even the qualitative claim fails for the public-discourse-relevant case (16PF / Big Five). H4 would need a worked-example refit using a non-equicorrelated Σ.
D4	Cross-paper alignment of estimators (twin/SNP/WGS/WF) is structurally noisy enough that within-paper tests are required for clean inference. This is the framing for H1’s “mixed” verdict.	A within-paper study that runs all four estimators on the same sample and finds the strict ordering fails. To my knowledge no such study exists; if one publishes and the ordering breaks, H1’s “mixed-but-informative” reading collapses to “wrong.”
D5	Per-ancestry PGS-portability anchors from Martin 2019 / Okbay 2022 / Yengo 2022 / Trubetskoy 2022 are concordant with Ding 2023’s continuous-distance result. Without individual-level data we cannot compute the continuous-distance slope ourselves; we are taking concordance on faith.	A reanalysis of the cited papers’ public summary statistics that finds substantially different per-ancestry decay rates than the headline reports. H5’s “consistent with Ding 2023” framing would weaken to “qualitatively matches but quantitatively in dispute.”

The most consequential is D1 — every other crux assumes the underlying CSV cells are correct. The web-verification round in pass 1 reduced this risk for the dozen highest-stakes numbers; the rest is a calibrated bet on training-time recall and would benefit from a future pass that audits each cell against its primary source.