MachineSex/paper/manuscript/si.md

# Supplementary Information — The evolution of sex for artificial intelligence

## Contents

SI Text S1–S4, SI Tables S1–S2, SI Methods M1–M7, SI Statistics, SI Figures S1–S16, and a separate
Appendix 1, *The figures explained* (`figure_legends_for_students.pdf`), which restates every main and
supplementary figure with a plain-language account of the experiment behind it, for readers from biology.

## Reproducibility

Every experiment in this paper is defined by one committed configuration file under `configs/`.
Running it produces three artifacts under `results/<name>/`: the results table (`results.parquet`),
the fully resolved configuration, and a manifest recording content hashes, the master seed, and the
git commit. Each experiment directory also contains a README with the figure legend and the current
status of the experiment's falsifier — the outcome that would refute its claim (see Methods M1) —
plus a figure that regenerates from the parquet file alone. The script `reproduce.sh` re-runs the
entire study from the master seeds, and `REPRODUCING.md` maps every panel of the manuscript to the
configuration and seed behind it.

## SI Text S1. The incompatibility floor: what no alignment can remove

**Setting.** Two models, A and B, are trained on the same input distribution. Their label functions
`f_A` and `f_B` agree everywhere except on a *conflict set* `S`, whose size is its probability mass
`μ(S)`. In the conflict condition of the trained-network speciation experiment, `S` consists of the
cyclically relabelled classes, so `μ(S)` is approximately the configured conflict fraction, up to
class-balance corrections.

A *function-preserving transformation* `T` is any change to a network's weights that leaves its
outputs untouched. For a plain ReLU multilayer perceptron these transformations are exactly the
permutations of hidden units and the positive rescalings of individual units: scaling a unit's
incoming weights up and its outgoing weights down by the same factor does not change what the network
computes. Together they form the *unit symmetry group* of the architecture. By construction `T(B)`
computes the same function as B, that is `T(B)(x) = B(x)` for every input `x`.

**Proposition 1 (endpoint invariance).** Define the *chord* as the straight line connecting the two
endpoint loss values, `(1−α)·L(A) + α·L(B)`. It depends only on the endpoints and is the baseline used
in the definition of the interpolation barrier; it is not the loss along the interpolation path in
weight space. For every function-preserving `T`, the pair `(A, T(B))` has the same endpoint losses as
the pair `(A, B)`, and therefore the same chord. The interpolation path itself is generally not
invariant: the losses along `(1−α)·A + α·T(B)` change with `T`. This is exactly the room an alignment
has to lower a barrier. The proof is immediate from the definition of function-preserving.

*Scope of the alignment guarantee.* The aligner used here is guaranteed to recover a
permuted-and-rescaled copy of a network exactly. That is an important special case, but it does not
prove that the alignment is optimal over the whole symmetry group for independently trained networks.
Consequently the share of the barrier attributed to removable coordinate mismatch is a lower bound,
and the residual share an upper bound, on their true values.

**Proposition 2 (no merged model can serve both parents).** Let `h` be any single classifier; in
particular, any interpolated or merged model, under any alignment. On every input `x ∈ S` the two
parents disagree, `f_A(x) ≠ f_B(x)`, so `h` must disagree with at least one of them. Writing `ε_P(h)`
for `h`'s error rate against parent `P`'s labels,

  `ε_A(h) + ε_B(h) ≥ μ(S)`,  hence  `max(ε_A(h), ε_B(h)) ≥ μ(S)/2`.

When two models' conventions conflict on a set of mass `μ(S)`, any hybrid of the two is wrong on at
least one parent's task at least `μ(S)/2` of the time. This floor is information-theoretic, holding
regardless of the alignment group, the architecture, or the merging operator. In the fitness sense it
is reproductive isolation: beyond a given functional conflict, no recombination operator can produce
an offspring faithful to both lineages.

**What remains empirical, and how the experiment is designed.** Propositions 1 and 2 do not bound the
single-task path barrier: the loss along the interpolation between A and `T(B)`, evaluated on one
parent's task alone. In principle such a path could dip toward one parent's function and yield a low
barrier even under conflict. Whether it does is an empirical question, and it is precisely what the
experiment measures. The measured answer is that it does not. In the conflict condition the barrier is
unchanged by permutation alignment (the `residual` readout) and by alignment modulo the full
permutation-and-positive-rescaling group (the `residual_scale` readout), while the very same aligner
removes almost all of the barrier between independently initialised networks, the positive control.
Work on richer symmetry groups for transformers (83) strengthens the removable side of the
decomposition and is therefore complementary to this result: the more barrier a larger group can
remove for *compatible* models, the sharper the meaning of the barrier that survives for
*incompatible* ones. Proposition 2 caps what any of these methods could ever achieve on the conflict
set.

**Terminology used in the paper.** "Residual (after alignment)" denotes the estimated functional
incompatibility: the part of the merge barrier that remains after the architecture's unit symmetries
have been divided out. For ReLU MLPs I align modulo the full unit symmetry group, so the estimate is
not confounded by symmetries of that architecture class that the aligner might have missed.

## SI Text S2. Emergent versus imposed incompatibility

The conflict condition *imposes* contradiction: the two label maps disagree on `S` by construction,
which pins `μ(S) > 0` and activates Proposition 2. A genuine Bateson–Dobzhansky–Muller
incompatibility is instead *emergent*. Each lineage's substitutions are harmless on their own
background, so the training signals never contradict and `μ(S) = 0`; any incompatibility appears only
when the two lineages are combined.

Two conditions realise this emergent setting. In `disjoint`, the parents are specialists on
complementary classes. In `augment`, they learn divergent input conventions on the same task. Neither
condition contains label conflict, so any barrier that survives alignment cannot be attributed to
label conflict. Such a barrier would be the emergent-speciation signal proper.

Both readings were registered before the run. If the residual barrier grows with divergence, then
model speciation is emergent in real weights, and the trajectory seen in the analytic speciation model
is realised. If the residual stays at the level of the `shared` control, then within this regime
trained networks are more merge-compatible than the biological analogy predicts. The second reading
would bound the analogy, and be a useful design result in its own right: merging is safe
whenever there is no functional conflict.

**Outcome.** Four replicates, with divergence up to 3,200 steps — up to 6.4× the shared base training
— returned the second reading. The residual barrier was 0.000 at every divergence in both emergent
conditions. Merging moreover *rescued* the `disjoint` specialists, which had forgotten the classes
outside their specialty: at the longest divergence the parents score 0.535 and 0.474 on the full task,
while the merged model holds approximately 0.955 at every divergence tested. This is a sustained
Fisher–Muller rescue at zero barrier. Within this regime, reproductive isolation in real weights
required functional conflict. The same question at language-model scale is answered by the duration
arm of the language-model speciation experiment, which likewise found no isolation from over-training
alone (1 to 12 epochs); whether still longer horizons erode mergeability (cf. 83) remains open.

## SI Text S3. Compatible loci and conflicting alleles in a multigenerational population

**The two kinds of new knowledge.** A *locus* is a position in the genome, and *alleles* are the
alternative versions that can occupy it: one blood-group locus, three alleles A, B and O, of which any
one chromosome carries exactly one. In a model population a locus is a slot for a capability ("how to
answer a two-way question") and alleles are the incompatible conventions that could fill it ("yes/no",
"true/false", "1/2"). A skill that conflicts with nothing a lineage already holds occupies a new locus
and is simply added; a skill that demands a different convention for a question shape the lineage
already answers is a competing allele, and a single model, like a single chromosome, carries one.
Proposition S2 gives the cost: when two parents' conventions disagree on a share `μ(S)` of inputs, any
merged child errs against at least one parent on at least `μ(S)/2` of them. In the six-generation
population a lineage obliged to merge at generation `t` pays that floor against its partner's
conflicting conventions; because the child continues the lineage, the loss is inherited, and the next
generation's conflict adds to it. Under the Latin-square curriculum `μ_t(S)` is zero while partners are
complementary (their skills occupy disjoint loci) and becomes positive once a partner carries a
differently conventioned version of a skill the lineage already holds. Two of the six families —
yes/no questions and two-way pronoun resolution — have the most idiosyncratic conventions and were
measured in calibration at 0.00–0.04 accuracy on every other family, so they carry the largest `μ(S)`
against every partner; the generation at which the curriculum hands them to a lineage's partner fixes
when that lineage's collapse begins.

**Negative controls that isolate convention conflict.** Three alternative explanations of the
obligate arm's collapse were tested directly and refuted. (i) *A destructive skill spreading through
merges.* A single 50/50 merge of two clean single-skill adapters (science questions 0.838 / yes-no
0.000; yes-no 0.800 / science 0.300) scored 0.863 and 0.787, mean 0.825 against 0.550 for the better
parent: one merge is protective, not destructive. (ii) *Geometric dilution of an adapter's signal
under repeated averaging.* Five chained convex merges left the first skill's accuracy unchanged even
though its nominal weight fell to 1/32; but a scaling control showed the adapter alone delivers
nothing at 1/32 (0.000; full effect down to 1/8), so what propagated through the chain was the answer
format supplied by whichever partner carried enough weight, not the skill. Dilution is refuted, and
the transmitted quantity is identified as the convention. (iii) *Continued training on merged
weights.* Merging then training on the incoming family beat merging alone on the tracked skill in four
of five rounds and on the incoming skill in all five, and absorbed the one format shock that dropped
the merge-only chain (0.567 → 0.883). With capacity ruled out by the lifelong-editing benchmark (80)
at three orders of magnitude more content, convention conflict is the mechanism that remains — the one
the framework predicts, and the one single-model studies report (81, 82).

**Neutral and functional variation.** Three adapters trained on the same family, differing only in
seed and data draw, were near-orthogonal in weight space (pairwise cosine +0.006) and disagreed on 24%
of answers, yet merging two of them gave 0.887 against 0.800 for the better one — exactly the fraction
of questions on which either was right (0.887). Decomposing the weight change across seeds, roughly
85% of a LoRA delta is run-specific: shared signal power 6.2 (after correcting the finite-sample mean
for its own noise) against noise power 35. That is why raw weight distance predicted nothing in the
main text's controlled test: most of what it measures is the counterpart of *synonymous substitution*
— sequence change without functional change — which averages out when adapters for the same skill
are combined, while the fraction that conflicts lives in the answer conventions. Averaging same-skill
adapters before crossing them with a different skill improved the cross modestly (0.825 → 0.850) while
leaving each single skill unchanged, the inbred-line pattern: averaging within a line does not improve
the line, it makes it cleaner to cross.

**Attenuation and the effectiveness cliff.** Scaling an adapter's weights down does not degrade its
skill gracefully. Each skill holds full accuracy to a skill-specific fraction (1/8 for science
questions, 1/4 for reading-comprehension spans, 1/2 for commonsense completion, 1/4 for yes/no) and
then loses nearly everything within one further halving. Four of six adapters scored higher when
attenuated (inference 0.40 → 0.68 at 1/4; completion 0.75 → 0.82 at 1/2; spans 0.72 → 0.78 at 1/4;
science 0.87 → 0.92 at 1/8): they were over-trained at full strength — the effect reported for
merging experts (84, 85) — and recoverable here by one scalar per adapter with no retraining (six
separate specialists 0.678 → 0.755). Denoising across seeds does not move the cliff, so the limit is
signal magnitude rather than signal-to-noise. Choosing per-skill merge weights from these solo curves
failed (0.686–0.689 against 0.708 for uniform weights): in a six-way merge a skill's effective
strength is its weight relative to the others — six conventions competing for one output — so raising
one starves the rest.

## SI Text S4. Proof of the blending-inheritance proposition

**Setting.** `K` parents; each independently retains a given rare item with probability `q`, and a
parent that retains it assigns it mass `p`. The child draws `n` samples from a *source distribution*
and keeps the item if at least one draw is that item. Two sources are compared: (A) one parent chosen
uniformly at random; (B) the mean of the `K` parents' distributions.

**Expected mass is conserved.** Let `J ~ Binomial(K, q)` be the number of parents retaining the
item. Under (A) the source mass of the item is `p` with probability `q` and 0 otherwise, so its
expectation is `pq`. Under (B) the source mass is `pJ/K`, whose expectation is `p·E[J]/K = pq`. The
expected number of copies in the child's sample, `n` times the source mass, is therefore `npq` under
both schemes (linearity of expectation).

**Survival agrees to first order.** Write `f(x) = 1 − (1 − x)^n` for the probability that at least one
of `n` draws hits an item of source mass `x`; `f` is increasing and concave, with `f(x) = nx + O((nx)²)`.
Survival is `E[f(M)]` with `M` the (random) source mass. Under (A), `E[f(M)] = q·f(p)`; under (B),
`E[f(M)] = E[f(pJ/K)]`. When `n·p ≪ 1`, every realised mass satisfies `nM ≤ np ≪ 1`, so `f(M) ≈ nM`
and both expectations reduce to `n·E[M] = npq`: the `1/K` dilution of scheme (B) is cancelled exactly
by the item being present in the mixture whenever any of the `K` parents holds it. (Equivalently, in
this regime the child's copy count is approximately Poisson with mean `nM`, and Poisson thinning by
`1/K` composed with a `K`-fold union preserves the mean.)

**Boundary 1 (common items).** Away from the first-order regime the comparison is settled by
Jensen's inequality. Both schemes give `M` the same mean `pq`; scheme (A) puts all its variance in
the two-point distribution `{0, p}`, and scheme (B) has strictly smaller variance for `K > 1`. Since
`f` is concave, `E[f(M)]` is larger for the less variable `M`, so averaging never lowers expected
survival, and raises it once `np` is not small. The extinction probability `1 − f` is convex, which is
the form in which the main text states this boundary. The proposition is thus a statement about rare
items, where survival is linear in mass; it does not claim averaging is harmful in general.

**Boundary 2 (union operator).** Let the child instead draw from the distribution that assigns each
item the largest mass any parent gives it, renormalised. The item's source mass is then `p` whenever
`J ≥ 1`, an event of probability `1 − (1 − q)^K`, increasing in `K` for every `q ∈ (0, 1)`. Expected
survival `(1 − (1 − q)^K)·f(p)` therefore rises with `K` in every regime, without a first-order
restriction. The operator needs an oracle (a verifier) to say which parent holds each item most
strongly, which is what routing supplies in the language-model tier.

Both statements are confirmed by simulation in Fig. S8, where mean-mixture survival is flat in `K`
and the item-wise maximum rises with it.

## SI Table S1: the claims ledger (status / assumptions / evidence / limits)

| Claim | Status | Key assumptions | Evidence | Known limits |
|---|---|---|---|---|
| Population collapse in the inheritance model is Wright–Fisher drift | Closed form; the diagnosis itself is due to prior work | Knowledge is a categorical distribution; refitting means resampling | Closed forms reproduced to <0.5% | Real learners add a signed, architecture-specific estimator bias (measured) |
| Grounding behaves like immigration, and the critical real-data fraction is far below one | Closed form, plus the sign confirmed empirically | Fresh samples from a fixed, non-drifting truth | Exact `H_eq`; `g*≈0.048`; sign holds in RNN/MLP/VAE and on MNIST | Deepest tail unrescuable at feasible budgets (`m ∼ 1/p`); sharp threshold softens in trained nets |
| "Merge, don't average" conservation | Exact **for the output-mean operator** | Rare-item regime; an oracle/verifier identifies the strongest source | `figS8_multiparent_union` closed form + simulation; neural reproduction | Weight-averaging and routing are empirical cousins, not instances; budgets differ; bridge = the headroom rule |
| Offspring exceed every parent (Fisher–Muller) | Interpretation + empirical | Complementary (decorrelated) parents; verifiable fitness | `figS9_specialist_superparent` (inheritance model); LoRA merges beat the best specialist overall in every seed at 0.5B (5 seeds) and 7B (3 seeds) | LLM tier: 3 lexically-distinct families |
| Outbreeding depression on rugged landscapes; operator design rule | Biological-model result; hypothesis at LLM scale | NK epistasis stands in for skill entanglement | `figS10_rugged_landscapes`, `figS11_directed_recombination`; directed selection rescues | Not yet mapped onto a real task-entanglement measure |
| Optimal mate-pool breadth shrinks with ruggedness | Biological-model result; hypothesis for merging populations | Ring population, local selection | `figS13_mating_breadth` | Phenomenon known to island-model evolutionary computation; the contribution here is the mapping and the diversity/mean decomposition |
| Merge failure decomposes into a coordinate artefact plus a functional residual | Empirical at the trained-network and language-model tiers | Alignment enumerates the architecture's unit symmetries | Full-symmetry residual ≈ 0 for compatible parents versus ≈ the naive barrier under conflict; a cliff in hybrid fitness; function-specific breakdown at the LLM tier | Scoped to aligned linear interpolation; conflict floor is information-theoretic, not genetic |
| Epistasis (not divergence) sets the cliff; snowball onset | Biological-model result; **hypothesis** at the neural tier | BDM incompatibility structure | `fig5_speciation_bdm` | Snowball count ≠ performance cliff without the effect-size link; neural test outstanding |
| Pre-merge functional disagreement predicts merge penalty | Empirical, within a controlled grid (0.5B, 13 conditions × 3 seeds) | Constructed conflict/overlap/duration axes; oracle-potential outcome (pre-registered; ordering sensitive to reference) | Clustered CIs exclude 0; held-out LOCO ρ≈0.4; selected geometry baselines ≈ 0 | Head-to-head predictor differences not individually significant; only selected baselines; generalisation to real task pairs open |
| Confidence weighting improves rank prediction over raw disagreement | Not supported (pre-registered internal prediction) | — | Paired contrast over the same bootstrap resamples: Δ\|ρ\| = −0.021, CI [−0.130, +0.059] | The weighting does sharpen the conflict-versus-compatible level contrast, so it is not useless — only no better as a rank predictor |
| The predictor improves budget-matched operator choice | **Open** | — | Soup-vs-route gap readout noise-dominated at 0.5B | The practical payoff; untested |
| Emergent speciation without label conflict | Not observed (pre-registered) | Shared ancestry; compatible tasks; the divergences tested | Residual 0.000 to 6.4× base training; the merge rescues the specialists | Bounds the hypothesis; longer horizons/distribution shift/capacity pressure untested |
| Grounding, recombination, and diversity preservation make complementary contributions | Biological-model result; hypothesis at LLM scale | Conformity stands in for self-consumption | `fig4_society_ablation` four-arm ablation; each arm fails in a distinct way | General joint necessity is not established; the language-model population (Fig. 4B–C) lacks differential reproduction between lineages |
| Obligate recombination collapses once partners carry conflicting conventions | Empirical (1.5B base, 3 lineages × 6 generations, 3 seeds) | Latin-square curriculum; replay present; linear merge; no culling of lineages | Best lineage 0.269 vs 0.796 never merging; onset at complementarity < 0.8; own-ancestor merge 0.663; three alternative mechanisms refuted (SI Text S3) | Six generations; one base; the arrival order of conflicting families is set by the curriculum |
| A declinable merge reverts the population to asexual accumulation without advance knowledge of when to stop | Empirical (same population, plus two controls, 3 seeds each) | "Keep the parent" scored as one candidate on validation data | Fraction declined 0.44 → 1.00 across generations; finishes 0.792 vs 0.796 never merging. Forced stop after generation 2 finishes 0.793 (veto − stop3 per seed −0.008/−0.006/+0.011). Under a decorrelated curriculum (complementarity 0.00 → 0.70 → 0.00) declines still rise 0.44 → 0.89; pooled partial ρ(declined, complementarity \| generation) = −0.07, CI (−0.21, +0.09); partial ρ with generation +0.31 | The reduction-principle reading (declines track complementarity) is **not supported**; declines track generation, which here confounds adapter age, skill count and the arrival of conflicting conventions. Modifier set by evaluation, not evolved |
| Recombination's net benefit across six generations is an early lead, not a final gain | Empirical (same population); consistent with the inheritance model's speed advantage | Every skill reaches every lineage by the curriculum regardless | +0.08 at generation 0; −0.005 at generation 5 (per-seed −0.03/+0.01/+0.01) | Replay present, so forgetting was not a live pressure; a curriculum that withholds skills from some lineages is untested |

## SI Table S2: headline quantitative results

Headline quantitative results with sample sizes, uncertainty, and outcome definitions (full
per-experiment tables and falsifier status in the per-experiment documentation).

| Result | Setting / n | Outcome definition | Headline |
|---|---|---|---|
| Closed-form validation | Inheritance model; standing tests | Simulated vs closed-form H-decay, immigration equilibrium, multi-parent union | Agreement < 0.5% |
| Grounding retention | Inheritance model (`fig2_grounding_sweep`); 100 lineages per grounding level | Fraction of equilibrium diversity retained at grounding `g` (operational threshold) | `g ≈ 0.05` retains ≥95% in the tested setting; smooth in `g` |
| MNIST collapse & rescue | Conv-VAE, 4 replicates; frozen oracle (98.5% mode acc.) | Mode support / forward-KL over generations | Dry: 30→1 modes; 10% grounding: 30/30 held |
| Fisher–Muller in LLMs | 5 seeds (0.5B) and 3 seeds (7B), fixed tests | Merged vs best-specialist accuracy (overall; worst family); ±: 95% CI over seeds | 0.5B ties 0.647±0.027 vs 0.592±0.009; 7B soup 0.873±0.004 vs 0.807±0.038 (soup − best +0.066±0.036, 3/3 seeds) |
| Union vs blend (headroom) | 3 seeds (0.5B hard); 3 seeds (7B hard) | Paired per-seed ordering, routing vs weight-average | 0.5B: routing > blend in 3/3 seeds, one catastrophic blend failure avoided. 7B: routing 0.503±0.007 vs soup 0.408±0.021 (+0.094±0.015, 3/3); soup vs best specialist +0.001±0.041 (the seed-1 'soup below best parent' did not replicate). Directed − soup +0.073±0.031 (3/3) |
| Speciation decomposition | MLPs, 3 replicates | LMC error barrier residual after permutation+rescaling alignment | Same-task 0.001; conflict 0.497 (naive 0.502) |
| Emergent isolation | MLPs 4 reps to 6.4× base training; LLM 1→12 epochs | Residual barrier; merged vs parent accuracy | 0.000 everywhere; merge rescues parents (≈0.955 vs ≈0.50) |
| LLM speciation, seeds | 0.5B; 3 training seeds; fixed test prompts | Conflict cliff: merge best-convention accuracy vs parents' own at full conflict. Duration null: merged private-task accuracy, 1 → 12 epochs | Cliff in 3/3 seeds (merge 0.02/0.12/0.16 vs parents 0.23–0.25); merged coherence over the sweep 0.147±0.013 → 0.100±0.082. No isolation in 3/3 (0.760±0.075 → 0.950±0.010) |
| Predictive test | 13 conditions × 3 seeds (0.5B) | Merge penalty vs oracle parent potential (pre-registered; ±: clustered 95% CI) | Functional ρ +0.45/+0.46, CI excl. 0; LOCO ρ ≈ 0.4; geometry n.s.; paired differences n.s. |
| Predictive test, seed sensitivity | Same; per-seed and leave-one-seed-out | Spearman ρ vs merge penalty within each seed alone (n = 13 conditions) | Functional +0.37 to +0.53 in every seed; weight geometry ≈ 0 in every seed; gradient alignment seed-unstable (−0.11 to −0.55) |
| Six-generation population | 1.5B base; 3 lineages × 6 generations; 3 training seeds; fixed tests (60 per family) | Best-lineage accuracy over six families at the final generation (mean of seeds; per-seed contrasts) | Never merge 0.796; declinable merge 0.792 (Δ −0.03/+0.01/+0.01); forced stop after generation 2: 0.793 (declinable − stop −0.008/−0.006/+0.011); obligate merge 0.269 (declinable − obligate +0.57/+0.54/+0.45); own-ancestor merge 0.663; single model 0.802 |
| Conflict-arrival curricula | Conflict-early / conflict-late (boolq + winogrande in generations 1–2 or 5–6); isolated, declinable and obligate arms; 3 seeds each | Decline rate and obligate-arm accuracy per generation; partial Spearman of declines on a conflict-present indicator controlling for generation (seed-clustered bootstrap) | Declines 0.56 → 0.78 (early), 0.44 → 0.89 (late); partial ρ(conflict | generation) −0.09, CI (−0.45, 0.15); ρ(generation | conflict) +0.45; pooled over four curricula −0.04, CI (−0.30, 0.15). Obligate final 0.280 / 0.386 vs isolated 0.796 / 0.781 (3/3 seeds); declinable 0.777 / 0.791 |
| Differential reproduction | Latin square; truncation selection (worst lineage re-founded from the best each generation); isolated and declinable arms; 3 seeds | Final best-lineage accuracy; per-seed contrasts against the unselected arms | Never merge + selection 0.804, declinable + selection 0.793 (declinable − never merge −0.011±0.003, below in 3/3); unselected 0.796 / 0.792; selection − no selection +0.007±0.030 |
| Second base lineage | SmolLM2-1.7B-Instruct; Fisher–Muller 5 seeds, headroom (hard) 3 seeds; fixed tests | Same contrasts as the Qwen rows | Soup − best specialist +0.049±0.022, TIES − best +0.097±0.020 (5/5 each; worst family +0.19 / +0.20). Routing − soup +0.162±0.036 (3/3); soup − best specialist −0.029±0.017 (below in 3/3) |
| Declinable-merge acceptance | Latin-square and decorrelated curricula; 9 merge decisions per generation; 3 seeds each | Fraction of proposed merges declined vs partner complementarity, with generation controlled (partial Spearman, seed-clustered bootstrap CI) | Latin square: 0.44 → 1.00 (raw ρ with complementarity −0.57, n = 18). Decorrelated curriculum (complementarity 0.00, 0.67, 0.70, 0.58, 0.33, 0.00): 0.44 → 0.89. Pooled (n = 36): partial ρ with complementarity −0.07, CI (−0.21, +0.09); partial ρ with generation +0.31 |

## SI Methods: experimental procedures

Every experiment in this paper is one YAML config, one runner invocation, and one artifact triple
(`results.parquet` + the resolved config + a manifest carrying the master seed, git commit, library
versions, and a content hash). The configs named below are the authority on any parameter; this
section gives the scientific reasoning behind the choices. `REPRODUCING.md` maps each manuscript
panel to the config and seed that produced it.

### M1. Design principles

Four rules govern every choice that follows.

*Test each claim at the cheapest tier that can falsify it.* A closed form beats a simulation, a
simulation beats a trained network, and a small network beats a language model, whenever the cheaper
instrument can still return the answer "no". A costlier tier is entered only where it adds a
discriminating test rather than a replication — which is why several cells of the programme (Fig. 1A)
are deliberately empty.

*Match the precision of the claim to the precision of the instrument.* The inheritance model is exact,
so it carries the paper's quantitative statements. Trained systems add optimisation noise and
inductive bias, so at those tiers I claim signs and orderings, never magnitudes.

*Make reality able to refuse.* Every tier has an oracle that is independent of the model being
measured: a fixed true distribution in the inheritance model, a lossless identity code or a frozen
classifier in the neural tier, an exact-match verifier over procedurally generated tasks in the
language-model tier.

*Declare the falsifier before running.* Each experiment states the outcome that would refute the
claim it tests (per-experiment READMEs; SI Table S1). Two pre-registered predictions failed, and are
reported as failures in the main text.

### M2. Replication: what a replicate is, and how many

A replicate means something different at each tier, and conflating the three would misstate what the
error bars cover.

In the inheritance model a replicate is an independent lineage: a fresh random stream driving the same
resolved config, with sub-seeds derived from the master seed by `SeedSequence.spawn`. Because drift
*is* the object of study, the spread across replicates is signal rather than nuisance, and replicate
counts are set so that the confidence interval on the summary statistic is small relative to the
effect being reported.

In the trained-network tier a replicate is an independent lineage including fresh weight
initialisation and data ordering, so it carries optimisation noise on top of drift.

In the language-model tier a replicate is an independent *training* seed evaluated on *fixed* test
sets. Holding the evaluation data constant while varying the training seed isolates training
stochasticity, which is the quantity in doubt; it also means the seed-to-seed spread I report is not
inflated by resampling the benchmark.

Replicate counts, and why each is what it is:

| Experiment | Replicates | Reasoning |
|---|---|---|
| `fig2_grounding_sweep`, `figS5_aimed_grounding`, `figS12_quality_diversity`, `figS3_rebaselining` | 100 lineages | Long horizons (400–600 generations) with drift-dominated variance; 100 lineages put the CI on stationary diversity well inside the effect being resolved |
| `figS8_multiparent_union` | 200 | Outcomes are per-item binary retentions, the highest-variance quantity in the paper |
| `figS9_specialist_superparent` | 40 | The vertical claim; the headline separation, so the most replicated of the genotype experiments |
| `figS10_rugged_landscapes`, `figS11_directed_recombination` | 24 | Landscape sweeps where each point aggregates 200 offspring internally |
| `fig4_society_ablation` | 12 | Four-arm ablation over 80 generations; arms separate by margins far exceeding the CI |
| `fig5_speciation_bdm` | 15 | Each point already averages 500 offspring |
| `figS13_mating_breadth` | 20 | Breadth × ruggedness grid, 60 generations per cell |
| `figS2_kernel_sharpen`, `figS2_kernel_smooth` | 24 | Two-parameter kernel fits against neural reference endpoints |
| `bridge` | 60 | The harness gate: must detect *any* departure from the inheritance model, so the most replicated neural run |
| `figS6_grounding_rnn` | 18 | Nine-point grounding sweep with per-generation network retraining |
| `collapse`, `figS1_architectures` | 5 | Sign-level demonstrations across architectures; each lineage retrains a network 22–25 times |
| recombination | 8 | Operator contrast in trained weights |
| `fig2_mnist_collapse` | 4 | 15 generations × a conv-VAE retrained from scratch each generation; the contrast (30 modes vs 1) is categorical |
| speciation_real, _cliff | 3 | Barrier decomposition; the quantity is a near-deterministic function of the training condition (residual 0.001 vs 0.497) |
| speciation_real_emergent | 4 | A null: replicates are spent on longer divergence horizons rather than more repeats |
| llm_merge_seeds | 5 training seeds | The Fisher–Muller signature, the most-replicated language-model claim |
| llm_moe_hard_seeds, llm_directed_hard_seeds, llm_epistasis(+compat), llm_speciation_add | 3 training seeds | Per-seed orderings reported individually rather than averaged |
| 7B runs (llm_merge_hpc, llm_moe_hard_hpc, llm_directed_hard_hpc) | 3 training seeds | Seeds 2–3 added 2026-09-11 (`hpc/llm_7b_seeds.pbs`, ~33 min per seed on one L40S); per-seed contrasts in `figures/stats_llm_7b_seeds.py` |
| llm_curriculum_v5_{early,late}(_obl) | 3 training seeds each | Conflict-arrival curricula; per-seed contrasts and the pooled partial-correlation test |
| llm_curriculum_v5_cull | 3 training seeds | Differential reproduction; per-seed contrasts against the unselected arms |
| llm_merge_seeds_smol, llm_moe_hard_seeds_smol | 5 and 3 training seeds | Second base lineage; per-seed orderings as for the Qwen runs |
| llm_speciation | 3 training seeds | Conflict cliff and duration null checked seed by seed (`figures/stats_llm_speciation_seeds.py`); seeds 2–3 added 2026-09-12 |
| llm_curriculum_v5, llm_curriculum_v5_veto, llm_curriculum_v5_stop3, llm_curriculum_v5_decor | 3 training seeds | The six-generation population; arm separations (≈0.5) far exceed seed spread (≈0.02), and the declinable-vs-never contrast is reported per seed because its mean is near zero |

The asymmetry is deliberate: replicates are cheap exactly where the quantitative claims live, and the
expensive tiers are asked only for the sign of an effect the cheap tier has already quantified. Where
a single run is all there is, the manuscript says so.

### M3. The inheritance-model tier

Knowledge is a distribution over `K` discrete items; reality is a fixed Zipf-tailed distribution
`p*`; one generation resamples `n` draws from the parent, optionally mixes in `m` verified draws from
`p*`, and refits. Implementation: NumPy/SciPy, no GPU, bitwise reproducible.

*Parameter choices.* `K = 500`–`1000` with `zipf_s = 1.1` and half the items designated tail: large
enough that the rare tail contains hundreds of items (so tail statistics are not dominated by a
handful of them) and small enough to sweep densely. `n = 100`–`200` sets drift strength; it is the
population size in the Wright–Fisher correspondence and the distillation sample size in the AI
reading. Horizons of 400–600 generations were chosen so that ungrounded lineages reach fixation and
grounded ones reach stationarity within the run, which the trajectories confirm.

*Sweeps.* The grounding sweep (`fig2_grounding_sweep`) sweeps `g ∈ {0, 0.005, 0.01, 0.02, 0.05, 0.1, 0.2, 0.4}`;
the aimed-grounding experiment (`figS5_aimed_grounding`) contrasts uniform against region-matched
grounding allocation; the multi-parent union experiment (`figS8_multiparent_union`) crosses parent count
`K_T ∈ {1,2,3,5}` with parent correlation `ρ ∈ {0, 0.25, 0.5, 0.75, 1}` and `g ∈ {0, 0.02, 0.05}`; the
selection experiment (`figS12_quality_diversity`) crosses selection mode (none / greedy /
quality-diversity) with novelty weight; the re-baselining experiment (`figS3_rebaselining`) compares
four re-minting arms.

*The correlated-parent construction (`figS8_multiparent_union`).* Parent correlation is constructed directly rather than
obtained by tuning drift, so that `ρ` is not confounded with `n`, `m`, tail size, or generation
count. For each tail item a shared switch `z ~ Bern(ρ)`, a shared retention `s ~ Bern(q)`, and
per-parent `u⁽ᵏ⁾ ~ Bern(q)` give parent `k` retention `s` if `z` else `u⁽ᵏ⁾`. This yields exact
marginal retention `q` and exact pairwise correlation `ρ`, and is exchangeable, so `ρ` is a single
scalar knob.

*Multi-locus experiments* (`figS9_specialist_superparent`, `figS10_rugged_landscapes`,
`figS11_directed_recombination`, `fig4_society_ablation`, `figS13_mating_breadth`). Genotypes are `L = 12` biallelic loci (4096 genotypes —
effectively open-ended relative to the population sizes used), with fitness either additive or a
Kauffman NK landscape whose interaction count `K` tunes ruggedness from 0 to 10. The landscape and directed-recombination experiments breed
from `n_parents = 6` local optima into populations of 200 offspring; the directed one additionally
screens offspring and iterates (5 rounds, keeping 8). The society ablation runs a population of `N = 60` agents for 80
generations at ruggedness `K = 8`, with mutation `μ = 0.03`, 120 offspring per generation, and
selection weighting true fitness against consensus conformity at `g = 0.85`. The mating-breadth experiment sweeps mate-pool
breadth on a ring of `N = 48` against ruggedness.

*Speciation (`fig5_speciation_bdm`).* `L = 20` loci, incompatibility density `ρ ∈ {0.1, 0.25, 0.5}`,
parental divergence swept 0–20 substitutions, 500 offspring per cell at recombination rate 0.5.

*Validation.* Three closed forms are asserted as standing tests to within 0.5%: neutral
heterozygosity decay `E[H_t] = H_0(1 − 1/n)^t`, the exact immigration–drift equilibrium, and the
multi-parent union formula. These run in CI alongside the correctness tests. If they fail, the
science is wrong rather than merely the code.

### M4. The trained-network tier

*Why a synthetic universe.* Measuring collapse requires knowing the true distribution exactly. Each
mode is rendered as a token sequence carrying an identity segment (base-2 digits encoding the mode
index losslessly, so the oracle reads the mode back with zero error) followed by style tokens drawn
uniformly at random. The style segment gives genuine within-mode entropy, so a generative model must
learn a distribution rather than memorise `K` fixed strings, while the identity segment keeps the
measurement noise-free. Mode truth comes from the same `make_true_distribution` used by the
inheritance model, so "mode", "region", and "tail" denote the same objects at both tiers.

*The bridge gate.* Before any trained model is interpreted, a histogram generator is run through the
identical harness; it must reproduce the inheritance model exactly. This separates harness bugs from
model behaviour, and is why the bridge run carries 60 replicates.

*Architectures and training.* The recurrent generator is an embedding (26) → GRU (128 hidden; 192 in
the architecture-generality run) → linear readout, trained each generation from scratch with Adam,
learning rate 2×10⁻³, batch size 256, 25 epochs, and evaluated by sampling 12,000–15,000 sequences.
Feedforward and variational autoencoder generators share the harness. Retraining from scratch each
generation (rather than fine-tuning) makes the generational step a clean refit, matching the
inheritance model's operator.

*MNIST tier.* Dataset: MNIST via torchvision (60,000 training images). Modes are digit class ×
stroke-thickness bin (10 × 3 = 30 modes) with a Zipf frequency profile, so roughly eighteen modes are
rare. The generator is a convolutional variational autoencoder (latent 32, β = 1), retrained from
scratch each generation with Adam, learning rate 10⁻³, batch 256, 30 epochs, on 6,000 images drawn
from the previous generation's own samples, for 15 generations, at `g ∈ {0, 0.1}`. The oracle is a
frozen two-convolution classifier trained once (5 epochs) combined with a deterministic thickness
measure; it reaches 98.5% mode accuracy and its 30 × 30 confusion matrix is recorded in the manifest
as the measurement floor. Build gates: the oracle's accuracy, and generation-0 recovery of all 30
modes.

*Speciation in trained weights.* Two multilayer perceptrons (784–512–512–10, ReLU, no batch
normalisation — batch statistics would break the permutation correspondence the analysis depends on)
are forked from a shared base trained for 500 steps, then trained apart for 100–3,200 further steps
(up to 6.4× the shared base) under SGD at learning rate 0.05, batch 128. Merges are weight averages;
the readout is the linear-mode-connectivity error barrier before and after alignment. Alignment
composes deterministic Re-Basin permutation matching with exact per-unit scale canonicalisation —
the unit symmetry group of this architecture — and is gated by a control that must recover a
permuted-and-rescaled copy exactly. Since the search space is that group rather than all
possible alignments, the removable share is a lower bound and the residual an upper bound.

### M5. The language-model tier

*Base models.* Qwen2.5-Instruct at 0.5B and 7B, open weights under a permissive licence, with the
revision pinned. Using two sizes from one family makes scale the only variable that changes between
the small and large runs; the 0.5B model carries five-seed protocols on the easy families; the 7B
runs are replicated over three training seeds.

*Task families, and why they are procedural.* Three deliberately disjoint families — list
operations, string transformations, and small-integer arithmetic — are generated procedurally from a
seed. Procedural generation buys four things that a standard benchmark cannot: an exact-match
verifier that plays the role of reality (an answer is right or it is not, with no judge model in the
loop); freedom from train/test contamination, since every evaluation item is generated fresh from a
disjoint seed offset; control over family disjointness, which is the precondition for specialists to
be genuinely decorrelated parents; and a difficulty knob. A `hard` variant (multi-step list
operations, Caesar ciphers and letter transforms, multi-step and larger arithmetic) exists because
the easy families saturate a 7B base at ceiling, and saturation removes the headroom in which
recombination operators can differ — a control that proved necessary, since two null results at 7B
turned out to be saturation artefacts rather than scale effects.

*Data splits.* Training, validation, routing-calibration, and test items are drawn from
non-overlapping seed offsets by construction (test from 1000 + family index, routing from 2000 +,
validation from 3000 +, training from the run seed). Test sets are fixed across seeds in the
multi-seed protocols. Selection of merge weights uses validation only; the winners are then reported
on the untouched test split.

*Specialisation.* Each parent is a LoRA adapter (rank 16, α = 32) on the frozen base, applied to all
attention and MLP projection matrices, trained with a manual supervised fine-tuning loop: answer-only
cross-entropy (prompt tokens masked out of the loss), AdamW at 2×10⁻⁴, batch size 8, 3 epochs,
bfloat16, 400–800 training items per family. Low-rank adaptation is the right instrument here for a
structural reason rather than a computational one: it confines each parent's specialisation to an
additive low-rank delta over an identical frozen base, which is what makes weight-space recombination
between parents well defined.

*Recombination operators.* Fusion by uniform weight averaging (soup) and by sign-reconciled,
magnitude-pruned task arithmetic (TIES); union by keeping specialists intact and selecting per input
(oracle routing, and a training-free nearest-centroid router over the base model's own prompt
embeddings) or per module (winner-take-all by delta norm); and directed recombination, which breeds a
population of Dirichlet-weighted merges, scores each on validation, and keeps the fittest.

*Evaluation.* Greedy decoding, exact match after canonicalisation. Alongside overall accuracy I
report worst-family accuracy, because the Fisher–Muller claim is about competence across all
families rather than an average that a single strong specialty can carry.

*The controlled predictive test.* Thirty-nine parent pairs (13 conditions × 3 seeds) span three axes
that are decorrelated by construction: conflict (contradictory conventions on shared prompts, with
private training budgets held fixed), compatible overlap (the same shared prompts under the same
convention — overlap and volume without conflict), and duration (weight divergence with no conflict,
1 to 12 epochs). Six predictors are computed before any merge: confidence-weighted functional
conflict, raw disagreement, gradient alignment at the shared base, LoRA-delta cosine and L2 distance,
and a cross-task performance baseline. Probes are drawn blind to where the conflict lives. The
outcome is the merge penalty against oracle parent potential, pre-registered, and also reported
against best-parent and mean-parent references because the predictor ordering is sensitive to that
choice.

*The six-generation population.* Base model Qwen2.5-1.5B (base weights, not the instruction-tuned
variant; 0.006 accuracy on the families untrained). Six public datasets with per-family verifiers:
natural-language inference (MNLI; label), science questions (ARC; letter), commonsense completion
(HellaSwag; letter), reading-comprehension spans (SQuAD; normalised span with aliases), yes/no
questions (BoolQ), and pronoun resolution (WinoGrande; 1/2). Each family's pool is split into disjoint
training, validation, and test items before any sampling, so validation and test never share an item.
Two further curricula, conflict-early and conflict-late, are given as explicit orders: the two families
whose answer conventions conflict (BoolQ yes/no, WinoGrande 1/2) occupy generations 1–2 or 5–6 of
every lineage and the four compatible families fill the remaining generations in rotated orders, so
adapter age and skill count rise one family per generation in both and only the arrival of conflict
differs (`configs/llm/curriculum_v5_{early,late}.yaml`; obligate arms in the `_obl` configs; three
training seeds each; `hpc/llm_curriculum_timing.pbs`). The conflict-timing readout is the partial
Spearman correlation of the per-generation decline rate with an indicator of conflict presence,
controlling for generation, with a seed-clustered percentile bootstrap (`figures/stats_llm_curriculum.py`).
Differential reproduction (`cull: true`) applies truncation selection after each generation's
measurement: the lineage with the lowest all-families accuracy is re-founded from the one with the
highest (adapter, taught families, example budget and ancestry archive are copied; the slot keeps its
curriculum order; ties leave the population unchanged), recorded as `culled` and `cull_source` rows
(`configs/llm/curriculum_v5_cull.yaml`; three training seeds; `hpc/llm_cull.pbs`).
The second base lineage is `HuggingFaceTB/SmolLM2-1.7B-Instruct` (Apache-2.0; Llama architecture),
run through the unchanged `merge_seeds` and `moe_hard_seeds` protocols with its own adapter cache
(`configs/llm/{merge_seeds,moe_hard_seeds}_smol.yaml`; `hpc/llm_smol.pbs`; `figures/stats_llm_smol.py`).
Three lineages take the six families in a cyclic Latin square (each lineage's order is the previous
lineage's shifted by two), which fixes partner complementarity — the fraction of the partner's families
a lineage has not yet seen — at 1.0, 1.0, 0.8, 0.67, 0.33, 0.0 across the six generations. Each
generation a lineage draws 300 new items from its scheduled family and 150 replay items split evenly
across families already seen; the child adapter (rank 16) is initialised from the parent's and trained
for 3 epochs at learning rate 10⁻⁴ (founders from the base at 2×10⁻⁴). Recombination averages two
adapters at each weight in {0.5/0.5, 0.3/0.7, 0.7/0.3}; the winner is chosen on 20 validation items
per family seen and then trains on the generation's new family. In the declinable arm the unchanged
parent is a fourth candidate scored identically. The contemporary partner is the next lineage in the
square; the ancestor partner is the lineage's own adapter three generations earlier; the self-replay
variant draws its replay from the parent's own answers rather than from the datasets. Reporting uses
60 test items per family. Because two of the families are binary, an accuracy threshold at 0.5 is
chance, so the text reports mean accuracy over the families a lineage has been taught and the
trajectory of its first-learned family rather than a count of families above a threshold.

*The composed society.* A population of `N` LoRA agents on a shared frozen base evolves for `G`
non-overlapping generations. Each generation every agent answers a fixed validation pool (verifier
scored) and a fresh conformity pool (whose modal answer defines the population consensus); selection
scores agents by `g·fitness + (1−g)·conformity`; parents are chosen with or without a
quality-diversity term over behavioural distance; offspring are bred by screened recombination; and
each child is a fresh adapter distilled from its source model's own answers, which makes the
inheritance channel literally self-consuming. The verifier enters the loop only where `g > 0`, but is
used for reporting in every arm. The four-arm ablation removes grounded evaluation, recombination,
or diversity preservation in turn.

### M6. Negative controls

The design leans on controls that can remove a result rather than support one, and one of them did.

The compatible-overlap axis was added to the predictive test specifically to expose overlap-and-volume
artefacts, and it did: the initial two-axis grid's best predictor (LoRA-delta cosine, ρ = +0.60)
collapsed to ρ = +0.03 once compatible overlap was present, identifying it as an artefact rather than
a signal. The duration axis supplies divergence without conflict. The emergent-speciation condition
supplies divergence with no conflicting signal anywhere, and returns a null. The budget-controlled
speciation design (`conflict_mode: add`) removes the confound between conflict fraction and private
training budget. The histogram bridge is a harness control. In the inheritance model, `m = 0` arms and
`ρ = 1` (fully correlated parents) are the null conditions against which the corresponding effects
are read. In the six-generation population, three arms are controls — a single model taught the
curriculum alone (no population), the never-merge population (no recombination), and merging with
one's own ancestor (shared conventions, partial complementarity) — and the self-replay variant of the
obligate arm controls the replay channel; SI Text S3 records the three direct tests that refuted
alternative mechanisms for the obligate arm's collapse.

### M7. Statistical procedures

Error bars on replicate means are normal-approximation 95% confidence intervals unless stated
otherwise. For the predictive test, where rows share task-data seeds across conditions and are
therefore not independent, inference uses a condition-clustered bootstrap (13 clusters, 4,000
resamples); predictors are compared by paired contrasts on the same resamples; generalisation is
assessed by leave-one-condition-out prediction; and per-seed and leave-one-seed-out sensitivity are
reported alongside, since three seeds cannot settle seed generalisation on their own. Outcome-
reference sensitivity is reported rather than resolved. Where a difference is not significant at the
sample size available, the manuscript says so rather than reporting the point estimate alone.

## SI Statistics

Output of `figures/stats_llm_epistasis.py` (clustered CIs, paired predictor contrasts, LOCO held-out
prediction, outcome-reference sensitivity, within/between-axis decomposition) — reproduced verbatim at
submission. Chronology of the predictive test (prospective / adaptive / post-hoc) as disclosed in
`results/llm_epistasis/README.md`.

## SI Figures

Sixteen figures are cited from the main text by number. Each is the per-experiment figure
regenerated from the committed results artifact (`figures/plot_*.py`), reproduced here without
re-plotting, so panel titles still carry the experiment's working name. Five of them are
inheritance-model results with no real-model counterpart in this paper, reported here because each
reproduces an established result: blending versus union retention (Fig. S8), the Fisher–Muller
super-parent (Fig. S9), outbreeding depression on rugged landscapes (Fig. S10), directed
recombination (Fig. S11), and the mate-pool breadth optimum (Fig. S13).

*(FIG:s1)*

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*(FIG:s11)*

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*(FIG:s13)*

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*(FIG:s16)*