Giorgio Gilestro
a40ace1821
Analyses (figures/stats_llm_epistasis.py, committed + reproducible): condition-clustered bootstrap CIs (functional measures exclude zero: dis_raw [+0.04,+0.69], conf-weighted [+0.02,+0.68]; gradient alignment [-0.59,-0.06]; geometry straddles zero), PAIRED predictor contrasts (not individually significant — stated), leave-one-condition-out held-out prediction (functional replicates, geometry ~0, performance baseline unstable), three outcome references (ordering sensitive to reference — reported, with the mechanism), between/within-axis decomposition (within-conflict identification impossible by design; the compat axis identifies), and seed-level paired reliability (routing/directed beat soup 3/3 seeds incl. one catastrophic soup failure; CI-width fragility claim withdrawn). Renames and corrections: "decisive experiment" -> "controlled predictive test"; "operational epistasis" -> "confidence-weighted functional conflict (proposed proxy)"; "functional by construction" -> "controls a major source of coordinate mismatch / conflict-associated" (module, configs, READMEs, figures); SI proposition's "chord" defined precisely (endpoint-loss interpolation, invariant) vs the path (not invariant) + no-global-optimality caveat (removable = lower bound, residual = upper); snowball count != performance cliff distinction added; claims table gains four rows (grid finding / weighting NOT supported / functional-vs- all-geometry not established / operator choice open); §1 ladder states the prediction rung as a bounded small-model result. paper/response-to-review-2.md: point-by-point, opening with the bookkeeping correction (E13b/c were in the reviewed draft — revised interpretation, not new results). READMEs rewritten around the four analyses with the chronology (prospective/adaptive/post-hoc) disclosed. 151 tests green. Co-Authored-By: Claude Fable 5 <noreply@anthropic.com> Claude-Session: https://claude.ai/code/session_01BkRLcc18rwT2Lysu6PbG7v
49 lines
3.9 KiB
Markdown
49 lines
3.9 KiB
Markdown
# LLM-tier model speciation — conflict provokes isolation; duration alone does not
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E13 carried into language-model weights (0.5B Qwen, LoRA children of one frozen base — the shared
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base **controls a major source of coordinate mismatch**, allowing a cleaner test of
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conflict-associated merge failure; averaging can still fail for non-conflict reasons — nonlinear
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interaction, scaling, capacity — so failures here are *conflict-associated*, not automatically
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functional). Two knobs, pre-registered readings in the
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configs; figure `llm_speciation.png` (3 panels; panel B from `results/llm_speciation_add/`).
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**Design.** Child A: private family `strings`; child B: private family `arith`; shared **ambiguous
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convention prompts** ("Sort the list […]" — no direction stated) answered *ascending* by A and
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*descending* by B: each convention harmless alone, contradictory jointly (the Bateson–Dobzhansky–
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Muller structure). 50/50 soup merge; exact-match verifier; fixed test sets. **Coherence** of a model =
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max(accuracy under asc grading, under desc grading) on the shared prompts — a coherent parent scores
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under its own convention; a hybrid mixing conventions scores low under both (the `μ(S)/2` floor made
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operational).
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### Finding 1 — function-specific hybrid breakdown (the conflict knob; panel A)
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Once the conventions are trained (`conflict_frac ≥ 0.25`), each parent performs under its own
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convention (~0.20–0.25 — low absolute values: sorting long lists is hard for 0.5B) while the merge's
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coherence sits at **0.02–0.08, below BOTH parents under either grading** — the hybrid loses precisely
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the conflicted function. (At `frac = 0` no one has seen the ambiguous prompts; that point is a
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no-conflict baseline, not part of the cliff.)
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### Finding 2 — the damage does not spread (the de-confounded `add` design; panel B)
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In the original ("replace") sweep, higher conflict fraction mechanically means *less private-family
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training*, so the merge's private-family decline is confounded. The **`add` design**
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(`llm_speciation_add`, 3 seeds) holds each child's private training fixed and adds conflict data on
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top: the merge's private-family accuracy then shows **no trend with conflict** (0.74–0.88, tracking
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parent A's 0.82–0.87 within seed noise at every level). Conflict damage is **localised to the
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conflicted function**; it does not corrupt the disjoint skills — at this scale, hybrid breakdown is
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surgical, not global. Honest rider: 0.5B soup merges carry large *intrinsic* seed variance even at
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zero conflict (sd up to 0.28) — the same averaging-fragility seen in `llm_moe_hard_seeds`.
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### Finding 3 — the duration null: over-specialisation does not erode mergeability (panel C)
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Pure disjoint specialists over-trained from 1 to 12 epochs (no shared data at all): the merged model
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*improves* (0.84 → 0.94 mean-private) and stays **above the best parent at every duration**. The MLP
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tier's "no emergent isolation" null (`speciation_real_emergent`) **generalises to LLM weights** in
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this regime — relevant to the report that averaging prefers under-trained experts (arXiv:2607.11997):
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in our disjoint-family setting, no such over-training penalty appears; the theory's prediction is that
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their effect should trace to *conflicting conventions on shared circuitry*, which the
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`epistasis_predicts` experiment (work order) will test directly.
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**Speciation across all three tiers now reads:** analytic (E12: cliff, epistasis-dependence,
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snowball) → MLP (E13: functional residual survives the full symmetry group; no emergent isolation) →
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LLM (this run: function-specific hybrid breakdown under conflict; no isolation from duration or
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specialisation alone). Isolation must be provoked by functional conflict at every tier tested.
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Falsifiers (not triggered): merge coherence matching the parents (no breakdown), or merged
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private-family accuracy declining with conflict in the `add` design (global corruption).
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