# Experiment ledger — PolyPythia subliminal-learning project Append-only lab notebook. One entry per experiment, newest at the bottom of each section. This is the single canonical record; per-run `runs/*/` JSON and `CONFIRMATION_*.md` preregistrations are the primary artifacts it points to. ## Recording protocol (follow for every experiment) 1. **Preregister** anything confirmatory: freeze design + criterion in a `CONFIRMATION_*.md` or a script docstring BEFORE the first block runs. 2. **On completion**, append a ledger entry here with the schema below. The entry must contain the numeric result, not just a pointer. 3. **Retention gate (hard rule):** never delete a run's model weights until its result is in this ledger AND its per-run JSON/report is on disk. Weights are regenerable from seeds; findings are not. 4. **Seed registry** lives at the bottom — reserve a range before launching so cells never collide. 5. **Steering pre-flight (David's, 2026-07-12) — required before any new teacher/base pairing gets a full training-based transmission run:** - Run `scripts/steering_probe.py`-style extraction: (teacher_acts - base_acts) per layer on the 24 train prompts, apply to the SAME base, read held-out wolf margin at each (layer, alpha). Forward passes only, no training — minutes, not hours. - Record: teacher's behavioral contrast, and the best NLL-safe steering cell's wolf delta. Compare against the standing reference bases (see table below) to get a **predicted transmission ceiling** for this base. - THEN run the expensive training-based transmission experiment. - **Divergence check:** if the training result contradicts the steering prediction by more than the reference-base scatter (e.g. steering says "moderately steerable, expect ~real transfer" but training gives ~0 or wrong-signed) — sanity-check the pipeline (pool size, seeds, code path, old-vs-new code path with a matched regression pair) BEFORE treating the divergence as a scientific finding. This would have caught the weight-seed1/data-seed1 confusion faster. - If training and steering agree (both weak, or both strong), the result is corroborated by two independent measurements and can be trusted with normal scrutiny. - Log BOTH numbers in the same ledger entry — steering ceiling AND training result — so future readers see the cross-check, not just one number in isolation. **Reference bases (steering, NLL-safe best cell, from saturated wolf teachers):** | Base | Behavioral contrast | Best steering cell | | --- | ---: | ---: | | standard pythia-160m | +17.318 | +5.233 (L8, a=+1) | | weight-seed3 | +14.01 | +5.84 (L9, a=+1) | | weight-seed1 | +14.42 | +5.55 (L9, a=+1) | | weight-seed2 | +13.46 | +4.06 (L8, a=+1) | | data-seed2 | +14.47 | +2.94 (L8, a=+1) | | data-seed1 | +15.30 | +2.25 (L7, a=+1) | | data-seed3 | +14.02 | +2.03 (L7, a=+1) | Entry schema: `date | name | hypothesis (H#) | prediction | design (teacher/students/dose/k/n) | result (effect + CI/spread) | verdict (does it support/refute the hypothesis?) | artifacts | caveats`. Every confirmatory entry names the standing hypothesis it tests and states the prediction BEFORE the result, so the verdict is a real up/down vote, not a post-hoc story. --- ## Standing hypotheses register Each has an ID, a statement, a falsifiable prediction, and a live status. Update status as evidence lands; never edit the original statement (append "REVISED:" lines instead). - **H1 — SL exists at 160M.** A trait fine-tuned into a teacher transmits to a same-init student through number strings alone. Prediction: paired preference−control margin > 0, replicated. **Status: SUPPORTED** (v3, 10/10 blocks, CI [+0.110,+0.136]). - **H2 — Steerability is necessary for SL** (Blank & Bhatia). If the trait is not a linear steering direction, SL fails. Prediction: trait steers the base model; SL only where steering works. **Status: NECESSARY CONDITION SATISFIED; NECESSITY UNTESTED.** The transmitted trait steers strongly (+5.23), so non-steerability is not the blocker here. No non-steerable-trait control has tested the necessity claim itself. - **H3 — Drift, not the channel, is what kills SL at 160M.** Full-parameter fine-tuning buries the signal in orthogonal drift; constraining the update subspace (LoRA) rescues it. Prediction: LoRA students transmit where full-FT students (same data) don't. **Status: SUGGESTIVE, NOT ISOLATED (corrected 2026-07-20 — Sol's review).** Same-teacher/same-data/same-seed ablation: full-FT transfer EXISTS (dose-16 +0.455/+0.208, both seeds > LoRA there) and never compounds to LoRA's scale (endpoints 27%/8% of LoRA's; oscillatory ~-0.41 to +0.46; chaotic within identical seeds on MPS). BUT the FT and LoRA arms differed in learning rate (5e-5 vs 2e-4) AND schedule length (2560 vs 5120) as well as parameterization — at u2560 the FT schedule has fully decayed while LoRA's is half-complete. So "LoRA protects accumulation" is NOT isolated from "the LoRA arm simply had a longer effective schedule." What is established: full-FT is not uniformly zero (contra the strong LoRA-artifact reading) and does not compound like LoRA under its own recipe. A matched-exposure {FT, LoRA} x {lr, schedule} design is required before claiming low rank alone is causal. - **H4 — Transfer scales with exposure (dose).** More LoRA updates on teacher numbers ⇒ stronger preference, up to a channel ceiling. Prediction: monotone effect vs log-dose. **Status: SUPPORTED** (+0.10→+1.37, ~log-linear, mild flatten >2,560). - **H5 — SL is trait-specific.** Teacher numbers transmit THAT teacher's trait, not a generic direction. Prediction: wolf/lion double dissociation. **Status: SUPPORTED** (4/4, d_wolf +1.01, d_lion +0.78). - **H6 — Shared initialization is the requirement for SL** (naive reading of Cloud et al.). Different init breaks transfer; data order is irrelevant. Prediction: (i*,o) ≈ 0 while (i,o) & (i,o*) transfer. **Status: PARTIALLY SUPPORTED; strong form rejected.** The init-only pilot sharply attenuated the dose-2560 mean (+1.511 to +0.008), supporting an initialization gate. But the clean order-only arm rejects "data order is irrelevant": (i,o*) stayed positive (+0.389) while falling 60.8% below its matched (i,o) control (+0.991). Shared init is therefore not sufficient for full-strength transfer. Both arms are k=2 pilots; the init arm used unmatched downstream seeds and no preregistered equivalence margin. - **H7 — Data-order credit-assignment clamps the trait's coordinates** (David's). Early training (driven by data order) fixes which coordinates carry which features; SL and steering-vector transport are coordinate-bound, so changing data order can break transfer even with shared init — UNLESS the clamping timescale is slow relative to init's contribution (open sub-question: does order-clamping outpace init? if not, init dominates and H6-like ordering holds even though H7's mechanism is real). Prediction (strong form): (i,o*) reduced despite shared init; and cross-run steering-vector transport degrades more across order-varied than init-varied bases. Sub-hypotheses to disentangle (need trajectory + alignment probes, see the 4-layer plan): clamping timescale; init×order interaction; CKA-vs-transport (converged-but-permuted, "strong" version) vs genuine divergence ("weak" version); whether SL-failure tracks coordinate misalignment. REVISED (2026-07-13, transport probes): within the exact-shared-init data-seed pair, the ds2 trait direction transports RAW across data orders (62.4% at preregistered L8/+1). The fitted global Procrustes map reduces the main L8 effect to 37.3% and hurts most cells, so that particular alignment is unnecessary; it does not prove that every coordinate or representation is natively shared. Cross-family raw transport is heterogeneous: the same ds2 vector retains 49.1% in weight-seed1 but only 0.4% in weight-seed3. Thus a universal shared direction across pretraining lineages is rejected, while the same-init result still supports David's narrower account: order-driven weight/circuit changes can attenuate coupling around a partly preserved residual direction without relocating it. Leading mechanism candidates are receiver-side numeric-trait write coupling and receiver-specific gain; coordinate mismatch remains live for the weight-seed3 lineage. REVISED (2026-07-13, fixed-L8 student-state intervention): all four dose-512 preference/control pairs were deterministically reconstructed from the retained pools and reproduced their archived readouts within 5.1e-7 logits. The mean student activation difference aligned with the fixed ds2 teacher wolf direction in only 1/4 pairs (cosines +0.309, -0.069, -0.101, -0.027), and the teacher-parallel patch was wolf-increasing only in that one pair. Thus the simple mechanism "numeric training recovers less of one fixed L8 teacher direction" is not supported. However, reciprocal full-sequence L8 state swaps increased wolf margin in both downstream suffixes in all 4/4 pairs (state-main effects +0.109, +0.113, +0.109, +0.061), and secondary all-token additions of each pair's full mean student difference were sign-correct in 4/4. Numeric training therefore writes a causal, sequence-distributed wolf-relevant L8 footprint, but not generally the teacher's single mean last-token direction. This refines the leading account toward optimizer/Jacobian-mediated recovery in student-specific distributed coordinates; it does not yet identify the upstream credit-assignment mechanism. REVISED (2026-07-13, update-0 reverse-mode Jacobian assay): the exact historical LoRA tangent does **not** supply a seed-stable local predictor. With the same guarded ds2 pools and paired LoRA/minibatch seeds, raw `-` was +0.3455 for ds2/56101 but -0.0609 for ds2/56102, even though both known update-512 effects are strongly positive (+0.8031/+0.7877). The second seed was negative in both 4,096-row pool halves and in both 30-prompt halves (one near zero), and ranked below ds1. The frozen retrospective gate therefore failed and prohibited the prospective receiver campaign. The exact first-AdamW-update secondary was also negative in both ds2 seeds. This rejects a pre-existing, update-0 LoRA-local route as a necessary mechanism; it leaves open a multistep route constructed after LoRA-B moves, LoRA-A gains gradients, and Adam state and teacher-forced histories evolve. **Status: BEHAVIORAL PREDICTION SUPPORTED; MECHANISM UNCONFIRMED.** Holding initialization, teacher numbers, local student seeds, and training recipe fixed, changing only upstream order reduced the mean effect from +0.795 to +0.251 at dose 512 and +0.991 to +0.389 at dose 2560, with both pairs agreeing. This establishes attenuation, not coordinate clamping itself; transport, trajectory-alignment/CKA, and intervention tests remain open. --- ## Established findings (chronological) ### 2026-07-10 — v1 saturated-teacher pilot + 3-pair sweep - Q: does SL transmit at 160M? Teacher = full-FT saturated wolf (standard pythia-160m step143000); full-parameter students, 256 seqs, 8 epochs. - Result: local_pilot +0.628; 3-pair sweep 0.628/0.167/0.802, mean 0.532, 95% t-CI **[-0.28, 1.35]** (crosses 0), one shared teacher. - Verdict: NOT confirmed — seed-sensitive, underpowered. - Artifacts: `runs/replication_summary.md`, `runs/local_pilot/report.md`. ### 2026-07-11 — scale/epoch sweep (full-FT) - Q: does more data / more epochs help full-FT students? - Result: effects spanned +0.63 to **-1.33** (scale_4k_e8); no stable trend. Repetition under full-FT is toxic. - Verdict: full-FT is the wrong regime. `runs/scale_and_epoch_sweep_results.md`. ### 2026-07-11 — v2 draw-averaged confirmation (context teachers, full-FT) - Design: `CONFIRMATION_v2_draw_averaged.md`. Prompted context teachers, k=8 × 6 blocks, AdamW update-16. - Result: mean **+0.048**, 95% t-CI [-0.048, +0.144], 4/6 positive. Positive control passed 6/6. Bounded null. - Verdict: NOT confirmed; effect ≤0.14 at this recipe. Variance decomposition: Muon@16 vs AdamW@16 same-data block corr **r=0.88** → noise is the data draw. - Artifacts: `runs/confirm_v2_summary.md`. ### 2026-07-11 — steering-vector probe - Q (Blank & Bhatia): is the wolf trait a steering vector? If not, SL can't work. - Result: steerable from all teachers — saturated +5.15 (L8), update-2 +3.26 (L10), context +3.01 (L11); sign-symmetric, specific, NLL-safe. CPT teachers share one direction (cos 0.72-0.88); context vector only ~0.5 aligned. - Verdict: trait IS steerable → SL failure was downstream (student fine-tuning), not teacher representation. `runs/steering_probe.md`. ### 2026-07-11 — standing rules adopted - Pretraining-matched optimizer (AdamW betas 0.9/0.95, eps 1e-8, wd 0.1); Muon retired. Eval prompts doubled 30→60 (originals first). Assays use 10 blocks. ### 2026-07-11 — step-0 rule-compliant teachers - Retrained saturated + update-2 teachers under the optimizer rule. Contrasts reproduce (+17.67 / +2.62); steering direction invariant to optimizer (cos ≈1.00); steering probe validated out-of-sample on new 30 prompts. - Canonical teachers: `runs/teacher_rule_saturated`, `runs/teacher_rule_update2`. ### 2026-07-11 — ⭐ v3 CONFIRMATION (LoRA students) — SL CONFIRMED - Design: `CONFIRMATION_v3_lora.md`. Saturated rule-compliant teacher, LoRA students (r=8, α=16, ~1.18M trainable), pretraining-matched AdamW, dose 16, k=8 × 10 blocks, 60-prompt logit-margin readout. - Result: **10/10 blocks positive, mean +0.123, 95% t-CI [+0.110, +0.136]**, 79/80 pairs positive, positive control 10/10. P(wolf|10) 4.7%→5.2%. - Verdict: **CONFIRMED (preregistered).** LoRA is the leading explanation for the ~10× drift reduction and rescue versus v2 full-FT, but that comparison also changed teacher class/recipe. `runs/confirm_v3_summary.md`. ### 2026-07-11 — dose-response (pilot + 10-epoch) - Q: does effect scale with LoRA exposure? Reused confirm_v3 pools. - Result: monotone +0.10 → **+1.37** over doses 16→5120 (~log-linear, +0.15/ doubling, mild flatten after 2,560). P(wolf|10) 4.6%→15.7% at max (odds ~3.9×, Cloud-et-al weight class). No repetition poison under LoRA. - Verdict: dose CONFIRMED predictive of transfer. Operating point 2,560 (94% of max, half compute). `runs/dose_10epoch` probes; curve in status doc. ### 2026-07-11 — trait-specificity crossover - Design frozen in `scripts/crossover_run.py`. Lion teacher (twin recipe), lion pools matched prefixes, wolf-data vs lion-data students, dose 512, k=4. - Result: **double dissociation 4/4** — d_wolf mean +1.01, d_lion +0.78. Relative to update 0, wolf data raised wolf +0.696 and lion data raised lion +0.776; lion data also suppressed wolf −0.314, while wolf data's mean effect on lion was approximately zero (−0.001, mixed signs). This rejects a generic shared FT direction without claiming reciprocal suppression. - Verdict: SL at 160M is trait-specific. `runs/crossover_summary.md`. **Combined status: SL at Pythia-160M is confirmed, dose-responsive, trait-specific.** --- ## PolyPythia init × data-order experiments ### 2026-07-12 — FIRST 2×2 pilot (weight-seed1 TEACHER) — INVALID, discarded - Mistake: changed the TEACHER base to weight-seed1 (not just the student) and ran k=1. (i,o) went negative. Diagnosed: k=1 noise + weight-seed1 channel differs (number-mean −18.7 vs standard +6..10) + control drift. Deleted. - Lesson: keep the teacher fixed; vary ONLY student init; keep k averaging. ### 2026-07-12 — (i*,o) init-isolation, standard teacher — CAVEATED - Tests: **H6** (shared init required). Prediction: (i*,o) ≈ 0 vs (i,o) ≈ +1.5. - Standard-pythia teacher, reused confirm_v3_b1 pools, LoRA dose 2560, k=2, student init = weight-seed1. (i,o) ref = dose_10epoch_b1 (+1.39/+1.64 @2560). - Result: dose 2560 (i,o) mean **+1.511** vs (i*,o) mean **+0.008** (pairs −0.055, +0.071); cells fan apart with dose (identical at dose 16, 15× gap by 2560). k=2 both cells. - Verdict: **SUPPORTS AN INITIALIZATION GATE** — changing only initialization nearly eliminated endpoint transfer in this pilot; "abolishes" is too strong without a prespecified equivalence margin. - Axis check: the official PolyPythia model metadata defines `weight-seed*` as varying only initialization with data order fixed, so standard → weight-seed1 is the intended init-only axis. Remaining caveats: downstream local seeds were unmatched across cells (53101/53102 vs 54101/54102), k=2, and this arm uses a different anchor/teacher from the order-only arm; their attenuation magnitudes are not an init-vs-order effect-size comparison. - Artifacts: `runs/x2x2_istar_summary.md`. ### 2026-07-12 — sanity regression check (David's, "are we sure about standard Pythia?") - Q: does CURRENT code still reproduce v4, through both the old code path (no init_checkpoint) and the new path (explicit init_checkpoint) added for the 2x2? Standard pythia, confirm_v3_b1 pools, LoRA dose 512, fresh seed. - Result: Arm A (old path) +0.0820 @16 / +0.7039 @512. Arm B (new path) **bit-for-bit identical**: +0.0820 / +0.7039. Both inside v4 reference band (+0.668/+0.961 @512). - Verdict: harness is clean; the `init_checkpoint` code change is inert when pointed at the same base. The pool-size bug (below) is the full explanation for the earlier weird results — not a deeper code regression. - Artifacts: `runs/sanity_A_oldpath`, `runs/sanity_B_newpath`. ### 2026-07-12 — steering pre-flight on data-seed1 (David's cross-check) - Tests: **H7 sub-question** — is a weak numeric channel (mean-number shift ~6.8× smaller than standard; raw JSD ~2.1× smaller and excess-over-noise JSD ~3.1–3.3× smaller, from the config-bug investigation below) a channel-specific bottleneck, or does the trait itself sit weaker in this base generally? - Same extraction as `steering_probe.py`, run on data-seed1 teacher/base. - Result: behavioral contrast +15.30 (canonical standard: +17.32, ~88%); best steering cell +2.25 @ L7 a=+1 (standard: +5.23 @ L8 a=+1, ~2.3x weaker); sign- symmetric (+2.25/-1.71), specific (comparison delta negative), NLL-safe. - Verdict: trait IS steerable on data-seed1, only ~2.3× attenuated. The numeric mean shift is ~6.8× attenuated, while distributional JSD is ~2.1× attenuated raw (~3.1–3.3× after subtracting the standard seed-noise floor). **Dissociation**: data order weakens trait-representability somewhat, but disproportionately decouples the trait from the number-generation pathway specifically. Supports H7's general spirit (order affects HOW a trait is represented) with a sharper claim than "everything is weaker" — the effect is channel-specific. - Artifacts: `runs/steering_probe_dataseed1.md`. Established the steering pre-flight as standing protocol (see above). ### 2026-07-12 — ⚠ CONFIG BUG caught (256-seq pool over-repetition) - The first weight-seed1 pilot AND the first data-order run both used pools of only **256 sequences** (inherited `size_per_condition: 256` from the teacher_rule_saturated ← local_pilot config lineage), not v4's 8,192. At dose 2560 that is 160 epochs of repetition (vs 5 on an 8,192 pool) → repetition poison → (i,o) positive control collapsed to ~0/negative on BOTH variant bases. This — NOT base-dependence or a "weak channel" — explains the earlier weight-seed1 (i,o) failure; that diagnosis is RETRACTED. - Caught by David asking "same base, same recipe — why different result?". Root cause: any teacher config derived from teacher_rule_saturated carries size 256. FIX: set generation `size_per_condition: 8192` for all 2×2 configs; guard = check pool line count and number-mean delta before trusting a result. - Number-mean delta is a fast channel-strength check (standard +20.9 over 8,192; the 256-pool estimate +7.8 was just noise, not a real difference). ### 2026-07-12 — base-screening campaign (COMPLETE) — transfer propensity per base - David's directive: for every cached 160M base (standard, data-seed1-3, weight-seed1-3), induce the canonical saturated wolf teacher (identical recipe/seed), extract steering vector, apply to own base → record behavioral contrast + best NLL-safe steering delta = **transfer propensity**. Propensity is now recorded for every SL replication attempt (protocol rule 5). - Purpose: (a) standing propensity reference table; (b) pick the STRONGEST data-seed base to anchor the (i,o)/(i,o*) cells so the data-order contrast is maximally legible. Note: the (i,o*) pair must come from within the data-seed family regardless of the overall winner (only within-family pairs guarantee shared init); the screening chooses WHICH data-seedN anchors it. - Aside recorded: v4 verified to inherit v3 exactly except max_updates / probe_updates / schedule_total_updates (the declared dose regime; note the schedule shape at matched update-16 differs slightly, 128-truncated vs full). - Future extension (David's, do not lose): per-base animal-token scan — test each base across all single-token animals to find which animal "rules the steganography" for each model. - `scripts/base_screening.py` → `runs/base_screening/.json` + `runs/base_screening_summary.md`. Teachers deleted after result JSON (gate). - Result (best NLL-safe steering delta): weight-seed3 **+5.84**, weight-seed1 **+5.55**, standard **+5.23**, weight-seed2 **+4.06**, data-seed2 **+2.94**, data-seed1 **+2.25**, data-seed3 **+2.03**. All sign mirrors were negative. - Standard ranks third overall. The strongest eligible data-order anchor, data-seed2, is **56.2% as strong as standard** by steering delta (+2.94 vs +5.233; 43.8% weaker), despite retaining 83.6% of standard's teacher behavioral contrast (+14.47 vs +17.318). This separates preference induction strength from steering-channel transport strength. - Selection: **data-seed2** anchors teacher/(i,o); data-seed1 is the (i,o*) sibling because it is the next-strongest data-seed recipient. Overall winner weight-seed3 remains reserved for init-varied cells, not data-order isolation. - Grid retention audit: all seven bases have complete 12-layer × 7-alpha grids (588 cells; no missing/duplicate cells). - Canonical standard rescreen **COMPLETED 2026-07-13** on the current 60 prompts with retained `runs/teacher_rule_saturated`: behavioral contrast **+17.318195**; best NLL-safe steering delta **+5.233191** at L8, alpha +1; NLL ratio **1.015187**; sign mirror **−2.179545**. The artifact contains all 84 unique layer/alpha cells, declares the 60-prompt canonical recipe, and the rebuilt ranking is unchanged (standard remains third). ### 2026-07-12 — steering strength → SL strength prediction campaign (PLANNED) - David's question: do bases with larger NLL-safe steering deltas exhibit stronger same-base subliminal transfer? Especially, do weight-seed3/1's above-standard steering scores predict above-standard SL? - Existing x-axis is complete (full grids for all seven bases). Existing y-axis is not: only standard has a high-quality same-base SL estimate; prior weight-seed1 values used standard-teacher numbers, and its earlier own-teacher run was invalidated by the 256-row repetition bug. - Required matched campaign: identical canonical wolf-teacher recipe, 8,192-row pools, local generation seeds, LoRA/student seeds, optimizer, schedule, and doses {16,512,2560} on every base; k=2 per base minimum. Record replicate effects, means, number-channel mean delta, and validity metadata incrementally. - Plot steering delta vs same-base SL as aligned dose facets, with every base labeled and replicate spread visible. Report Pearson + Spearman descriptively; n=7 is exploratory, not a high-powered model-selection result. ### 2026-07-12 — data-order isolation, ANCHOR-FREE (re-anchored after screening) - Tests: **H6 vs H7**. Prediction (H6): (i,o*) transfers like (i,o), data order irrelevant. Prediction (H7 strong): (i,o*) reduced despite shared init. - Fix for the anchor problem: work within the data-seed family. Screening chose data-seed2; (i,o)=data-seed2 (positive control, must fire), (i,o*)=data-seed1 (same weight init W0, different data order). k=2, dose 2560. Fresh `ds2_anchor_*` run paths preserve the superseded partial data-seed1 run. - Local student seeds are paired across cells (56101/56102 in both), holding LoRA initialization and minibatch shuffle fixed; the only cell difference is the upstream PolyPythia pretraining data order. - Pool pre-flight (8,192 rows each): preference number mean 220.975 vs base 185.812, delta **+35.163**. Full unigram-distribution JSD (numbers 0..999, add-1 smoothing, matching the earlier diagnostic) is **0.011695**; versus the established standard-base seed noise floor 0.00213, excess JSD is 0.009565. This is slightly stronger than standard b1/b2 JSD (0.00972/0.01006), despite data-seed2's weaker NLL-safe steering delta (+2.94 vs canonical standard +5.23). Preregistered interpretation: steering transportability and numeric-channel imprint strength are separable; student transfer remains the arbiter. - `(i,o)` positive control **CONFIRMED 2/2**. Pair effects at doses 16/512/2560: s1 −0.006/+0.803/+1.052; s2 +0.172/+0.788/+0.931; cell means **+0.083/+0.795/+0.991**. Transfer is strong and dose-amplified on data-seed2. The dose-512 mean is close to the established standard-base grand mean (+0.776), agreeing with the strong JSD rather than the weaker steering ceiling. `(i,o*)` launched automatically after confirmation. - Pair-1 held-out probability view at dose 2560 (10-animal candidate set, 60 prompts): wolf mean **18.51%** after preference numbers vs **7.51%** after base-control numbers and 9.27% at update 0. Wolf exceeded the uniform 10% candidate baseline on 45/60 prompts (control: 15/60), and preference exceeded its paired control on 59/60 prompts. This is a restricted-candidate next-token readout, not an unconditional greedy-generation frequency. - Apples-to-apples standard comparison at dose 2560: four standard pairs mean 5.61% initial → 15.22% preference and 4.86% matched control (2.71× initial, 3.16× control; individual control ratios 2.24×–3.94×; mean margin effect +1.287). Data-seed2 pair 1 is 9.27% → 18.51% vs 7.51% control (2.00× initial, 2.46× control; margin effect +1.052). Thus its multiplicative rate is ~22% below the standard mean but inside standard pair scatter, while its absolute wolf probability is higher. The remembered ~3–4× headline used standard's dose-5120 endpoint (4.6% → 15.7%, ~3.4× rate/~3.9× odds), not dose 2560. - `(i,o*)` **COMPLETED, positive 2/2 but attenuated 2/2**. Pair effects at doses 16/512/2560: s1 +0.100/+0.234/+0.399; s2 +0.053/+0.267/+0.378; cell means **+0.076/+0.251/+0.389**. Thus changed pretraining order does not abolish transfer when ancestral initialization is shared. - The matched `(i,o)` vs `(i,o*)` means are +0.795 vs +0.251 at dose 512 and +0.991 vs +0.389 at dose 2560. Cross-order transfer retains **31.5%** and **39.2%** of the same-order effect respectively (68.5%/60.8% attenuation). The endpoint attenuation replicated by local seed: 62.1% in s1 and 59.4% in s2. - **Interpretation:** H7's preregistered behavioral prediction is supported: pretraining data order substantially modulates transfer strength even when step-0 weights are shared. This experiment does not by itself establish the proposed coordinate-clamping mechanism. H6 survives only in its weaker form—shared initialization provides a transferable substrate; its stronger "data order irrelevant" prediction is not supported. This is one teacher and one shared pool with two paired local seeds, so the result is a strong within-design replication, not a population-level estimate across teachers or generated datasets. Prompt-level intervals in the checkpoint reports describe prompt variation and must not be read as training-replicate confidence intervals. - `scripts/dataorder_2x2.py`, `runs/dataorder_2x2_summary.md`. --- ### 2026-07-13 — steering-vector TRANSPORT probe ds2→ds1 (H7 mechanism test) - Tests: **H7 mechanism** (coordinate clamping). Predictions registered in `scripts/transport_probe.py` docstring before running; behavioral reference 39.2% retention. - Result (matched cells; best-cell ratios were NLL-gate selection artifacts — see `runs/transport_probe.md` reanalysis): - **Raw transport retains ~47-62%** (L8 matched: +1.77 vs +2.83 = 62.4%; sign-symmetric), vs behavioral 39.2%. - The fitted Procrustes map is worse at the main high-effect cells (37.3% at L8; residuals 0.16-0.45) and raw is stronger in 70/84 cells, but not literally everywhere: aligned wins 14/84 cells. The result says this direction does not need that fitted global map; it does not establish globally shared coordinates. - The selected raw ds1 best (+4.32 at L10) exceeds ds1's own-vector selected best (+2.25), but the matched L8 raw effect (+1.77) does not. Treat the former as selection-sensitive, not evidence that the foreign vector is intrinsically better. - Verdict: the simple coordinate-mismatch account is **disfavored for this direction within this exact-shared-init pair**. Transport attenuation (~38% loss at L8/+1) is in the same ballpark as behavioral attenuation (61%) but does not match crisply enough to identify the mechanism; the correspondence is loose and cell-dependent. - New leading mechanism candidate: **order-specific numeric-trait entanglement on the receiver side** — the trait direction is shared, but how strongly the ds2-native number distribution's gradients couple INTO that direction depends on the receiver's data order (consistent with the earlier data-seed1 dissociation: channel ~7x weaker vs trait ~2x weaker). - Proposed next probes (cheap): (a) cross-family raw transport ds2→ weight-seed1/3; (b) receiver-side channel test — NLL of ds2-teacher numbers under ds1 vs ds2 bases, correlating "foreignness" of the numbers with attenuation. - Artifacts: `runs/transport_probe.{json,md}`. --- ### 2026-07-13 — fixed-cell RAW cross-family transport ds2→weight-seed1/3 - Frozen design: one ds2-teacher minus ds2-base L8 direction, applied without rescaling, layer search, alpha search, or alignment at alpha -1/0/+1. ds2 self is the reference; ds1 is the exact-shared-init/different-order control; weight-seed1 and weight-seed3 are foreign-lineage primary receivers. All readouts use the fixed 60 held-out prompts and the +1 NLL<1.2 quality gate. - Provenance audit before launch: deterministic tensor hashes of the official step-0 checkpoints are identical for data-seed1 and data-seed2 (`f0236470...`) but differ for standard Pythia (`5ed85f31...`) and weight-seed1 (`d1c10248...`). The planned standard-centered "hub" assay was discarded before any forward pass; standard is not assumed to share the data-seed initialization. | receiver | delta -1 | delta +1 | +1 NLL ratio | +1 retention | prompt-bootstrap 95% | | --- | ---: | ---: | ---: | ---: | ---: | | ds2 self | -2.0070 | +2.8295 | 1.0706 | 100.0% | 100.0-100.0% | | ds1 order control | -1.6053 | +1.7649 | 1.0739 | 62.4% | 57.3-67.9% | | weight-seed1 | -1.5733 | +1.3882 | 1.0328 | 49.1% | 44.3-54.6% | | weight-seed3 | -0.6640 | +0.0108 | 1.0707 | 0.4% | -4.7-5.1% | - Both historical ds2/ds1 fixed cells reproduce exactly; all +1 cells pass the quality gate. Weight-seed1 therefore accepts substantial raw transport. Weight-seed3's positive effect is indistinguishable from zero on this prompt set, despite its own native L8/+1 vector scoring +3.138 in the independent base screen. This is foreign-direction-specific, not generic inability to steer weight-seed3 at L8. Its negative intervention still reduces the wolf margin, giving an asymmetric 14.0% centered-gain retention. - Verdict: **raw cross-family transport is lineage-heterogeneous**. One different-init receiver substantially expresses the ds2 direction and one does not, rejecting both "raw coordinates are universal" and "different initialization always destroys raw transport." Because ds2→weight-seed changes both initialization and upstream order, this does not causally isolate initialization. Together with prior behavioral SL it is suggestive, not direct proof, of receiver-side write-coupling/gain differences. - Next discriminators: preregister a small-alpha response curve for weight-seed3 (tests nonlinearity/saturation), then fit and validate alignment only if the raw local response remains weak. A true init-only transport arm requires a native weight-seed teacher and a same-order weight-seed sibling. - Artifacts: `scripts/cross_family_transport.py`, `runs/cross_family_transport.{json,md}`. --- ### 2026-07-13 — fixed-L8 student trait-write intervention at dose 512 - Tests: **H7 receiver-side write-coupling sub-hypothesis** and the stronger claim that numeric credit assignment recovers a projection of the teacher's fixed wolf direction. Frozen design: reconstruct the matched `(i,o)` and `(i,o*)` preference/control students at update 512; extract `d = mean(h_preference - h_control)` at the final prompt token of L8 on the fixed 24 extraction prompts; decompose `d` relative to the fixed ds2 teacher-minus-base wolf direction `v`; intervene on the fixed 60 held-out prompts. Primary patches affect the final token only. Reciprocal exact-state swaps test state-source × downstream-suffix mediation; all-token additions and full-sequence swaps are secondary distributed-state bridges. - The original runs retained evaluations but not weights, so all eight students were replayed from the byte-identical 8,192-row pools with their exact init checkpoints, LoRA/student seeds, optimizer recipe, and 2,560-update LR horizon, stopping at update 512. Adapter-only saves avoid replacing historical directories or writing eight merged 649 MB models. | pair | archived gap | replayed gap | difference | gate | | --- | ---: | ---: | ---: | :---: | | `(i,o)` s1 | +0.803140 | +0.803139 | -0.0000005 | pass | | `(i,o)` s2 | +0.787731 | +0.787731 | +0.0000005 | pass | | `(i,o*)` s1 | +0.234386 | +0.234386 | +0.0000000 | pass | | `(i,o*)` s2 | +0.267220 | +0.267220 | +0.0000003 | pass | The frozen absolute tolerance was 5e-4; the largest reload discrepancy was 5.1e-7 logits. Callback readouts reproduced the archived margins exactly to displayed precision. The retained update-0 preference/control gaps are exactly zero in all four pairs. The teacher vector also reproduced its prior tensor SHA256 (`7ac7d552...64f587`), norm 10.997561, and mean prompt-difference norm 12.344284. | pair | cos(d,v) | squared parallel fraction | control +d, last | signed effect of -d in preference | all-token centered d (ctrl/pref) | exact full-state forward/reverse | | --- | ---: | ---: | ---: | ---: | ---: | ---: | | `(i,o)` s1 | +0.309 | 9.54% | +0.0278 | +0.0336 | +0.0577 / +0.0603 | +0.1067 / +0.1110 | | `(i,o)` s2 | -0.069 | 0.48% | -0.0288 | -0.0169 | +0.0472 / +0.0468 | +0.1098 / +0.1169 | | `(i,o*)` s1 | -0.101 | 1.02% | +0.0460 | +0.0488 | +0.0984 / +0.1007 | +0.0996 / +0.1192 | | `(i,o*)` s2 | -0.027 | 0.07% | +0.0122 | +0.0227 | +0.0225 / +0.0361 | +0.0543 / +0.0672 | - **Fixed-direction criterion FAILED.** Positive projection and correct-signed teacher-parallel patches occurred only in `(i,o)` s1. In the other three pairs, the projection and parallel-patch effects were negative. The norm-matched orthogonal centered effects were small (-0.0034 to +0.0062), but that specificity control cannot rescue the absent replicated alignment. The full mean last-token difference was sufficient/removable in 3/4 pairs and wrong-signed in `(i,o)` s2; it recovered only a few percent of the natural same-order gap. - **Distributed L8 state mediation replicated 4/4.** Replacing the complete prompt-specific L8 sequence state crossed between preference and control students raised/removed wolf margin in both downstream suffixes for every pair. The suffix-averaged state effects were +0.109, +0.113, +0.109, and +0.061; state×suffix differences were small (-0.004 to -0.020). Aggregated state mediation was +0.111 same-order (14.0% of the +0.795 natural gap) and +0.085 changed-order (33.9% of the +0.251 gap). Secondary all-token additions of each pair's full mean `d` were likewise sign-correct in both recipients in 4/4 pairs. By contrast, final-token-only exact swaps were inconsistent. - Quality checks are clean: mean final-token full-vocabulary KL was at most 0.0206 in any exact-swap cell; exact-swap prompt-NLL ratios ranged 0.9906-1.0086, and all-token additive NLL ratios stayed within 1.0084. Tiny negative per-prompt KL values (minimum -1.24e-6) are floating-point roundoff; all mean KLs are positive. - **Verdict: MIXED; the preregistered single-direction mechanism is not supported.** Numeric training does create a causal wolf-relevant activation footprint by L8, but it is sequence-distributed and not generally the teacher's mean last-token steering direction. The core credit-assignment account remains viable in a broader form: optimizer-mediated fitting may recover a functionally wolf-equivalent projection in student-specific, distributed coordinates. This assay does not directly test the upstream number-distribution Jacobian/gradient alignment that would establish that account, and the moderate L8-state attenuation does not explain the much larger behavioral data-order attenuation by itself. - Scope: one teacher, one paired number-pool draw, two local seeds per lineage. Prompt intervals describe the fixed 60 prompts, not independent student training replicates. No layer, update, component normalization, or patch placement was selected after seeing the result. - Artifacts: `scripts/student_trait_write_probe.py`, `runs/student_trait_write_probe_u0512.{json,md}`; replay adapters and frozen manifests live under ignored `runs/student_trait_write_probe_u0512/`. --- ### 2026-07-13 — update-0 numeric-sequence Jacobian/NTK alignment - Frozen protocol: `configs/numeric_channel_jacobian_v1.json`. At each exact historical update-0 LoRA initialization, compute `S = -` over the byte-guarded 8,192-row pools. Positive `S` is the infinitesimal Euclidean-SGD prediction that preferentially fitting the wolf-teacher sequences increases wolf preference. The primary uses all 60 held-out prompts; original/new 30-prompt halves and shuffled 4,096-row pool halves are stability checks. Student seeds 56101/56102, LoRA initialization tensors, DataLoader orders, receiver commits/weights, pool hashes, tokenizer semantics, and implementation hashes were frozen. No explicit Jacobian was materialized; reverse-mode products were reduced in CPU float64. | receiver | seed | raw `S` | cosine | first-Adam prediction | known u512 effect | | --- | ---: | ---: | ---: | ---: | ---: | | ds2 `(i,o)` | 56101 | +0.345494 | +0.032414 | -0.000067 | +0.803140 | | ds2 `(i,o)` | 56102 | -0.060930 | -0.004653 | -0.000400 | +0.787731 | | ds1 `(i,o*)` | 56101 | +0.048526 | +0.004550 | +0.001616 | +0.234386 | | ds1 `(i,o*)` | 56102 | +0.008281 | +0.001201 | +0.000064 | +0.267220 | - **Frozen retrospective gate FAILED.** Seed 56101 passed positivity and all three ds2>ds1 comparisons; seed 56102 failed all four checks. Its ds2 score remained negative in both pool halves (-0.0559/-0.0660), while its original and expanded prompt halves were -0.0096/-0.1122. The across-seed raw means happen to preserve the behavioral order (ds2 +0.1423 vs ds1 +0.0284), but that post hoc average cannot rescue the preregistered seed-replication gate. No prospective score, prediction, or student training was launched. - The exact t=1 clipped-AdamW secondary also fails as an endpoint explanation: it is negative for both strongly transferring ds2 runs, while positive for both attenuated ds1 runs. Thus neither the Euclidean population tangent nor the actual first minibatch update is a necessary positive route. - **Interpretation:** successful SL can emerge despite a wrong-signed initial LoRA-local derivative. This rejects the strong static claim that credit assignment merely follows a pre-existing numeric-to-wolf tangent. It does not reject multistep credit assignment: at PEFT initialization LoRA-B is zero and only B has gradients; after the first step A becomes trainable in effect, Adam state accumulates, the two trajectories diverge, and a useful distributed route can be constructed. That dynamic account is now the leading version of the hypothesis, not a confirmed mechanism. - Scope: the actual historical loss supervises 10 number and 9 comma tokens, with different later-token histories across pools. This is sequence-loss gradient alignment (`Jpref^T rpref - Jctrl^T rctrl`), not the separate explicit sender probability-fingerprint assay. Ten-animal gradient ranks were diagnostic only (wolf ranks 3/4/4/6) and do not supersede the existing behavioral wolf/lion double dissociation. - Next discriminators: measure the score along the actual early trajectory (after B moves and A gradients activate), and separately run the explicit recipient-specific number-fingerprint assay with match/remove interventions. - Artifacts: `scripts/numeric_channel_jacobian.py`, `configs/numeric_channel_jacobian_v1.json`, and ignored `runs/numeric_channel_jacobian_v1.{json,md}` plus guarded score records. ### 2026-07-13 — soft numeric-fingerprint compatibility and prospective endpoints - Frozen sender assay: on the exact 8,192 paired ds2 prefixes, compute the temperature-1 preference-teacher and base distributions over all 655 allowed numeric token IDs. The sender shift has mean TV **0.144206** and mean JS **0.018233 nats**. For each receiver, extract its own native teacher-minus-base wolf vector and measure the central local change in full-vocabulary numeric log probabilities under alpha +/-0.25. The raw cross-loss score is `C = mean_x sum_y (q_ds2-wolf-q_ds2-base) * d log p_receiver(y|x)/d alpha`; the locked cross-receiver score `K=C/G` divides by the same vector's local held-out wolf-margin slope. Positive `C` is a genuine local loss incentive, not a sampled-number correlation or proof that LoRA can write that direction. - The retrospective ds2/ds1 gate passed. The prospective rank was then locked before any endpoint artifact: weight-seed3 (**K .032062**) > weight-seed1 (**.031450**) > standard (**.021104**). The three flattened sender/response cosines were small (.0664/.0486/.0455), and the score was mostly a marginal token-frequency effect, especially for weight-seed3 (about 90% marginal). That is still a valid cross-entropy-reducing fingerprint; it is not evidence of visually identical prompt-conditional response fields. | receiver | seed 56101 | seed 56102 | mean u512 preference-control effect | | --- | ---: | ---: | ---: | | standard | +0.588329 | +0.354485 | **+0.471407** | | weight-seed1 | +0.156014 | +0.423656 | **+0.289835** | | weight-seed3 | +0.076612 | +0.192837 | **+0.134724** | - **Frozen primary FAILED:** weight-seed3 minus standard was **-0.336683**. The observed order was exactly reversed, standard > weight-seed1 > weight-seed3 (descriptive Spearman -1 at n=3). Static `K` therefore does not predict update-512 SL magnitude across these receivers. Do not rescue it by selecting a different normalization or checkpoint after the fact. - **The sign result is nevertheless real:** all 6/6 paired seed endpoints were positive. In weight-seed3 the mean was +0.134724 logits and +1.170 percentage points wolf probability. This is a clean prospective foreign-lineage signal, despite raw ds2-vector transport into weight-seed3 being only 0.4%. With two local seeds it is a paired replication, not a population estimate. It is not the first cross-init positive u512 hint: the caveated standard->weight-seed1 `(i*,o)` pilot averaged +0.115 at u512 before falling to +0.008 at u2560. Also, tensor provenance shows standard does not share the data-seed initialization, so none of the three prospective receivers is a same-init ds2 control. - Carrier-fit loss does not explain the reversed rank. Mean preference training NLL across both seeds was 2.76048 standard, 2.75481 weight-seed1, and 2.75136 weight-seed3; control NLLs were 2.77333, 2.76678, and 2.76422. Weight-seed3 fit the observed numbers slightly better, not worse. Global preference gradient norms and clipping rates did rank standard > weight-seed1 > weight-seed3, but are descriptive under coordinatewise AdamW. - **Revised mechanism:** static activation-space compatibility measures a loss-reducing read route. Behavioral strength additionally depends on whether the evolving LoRA tangent and optimizer state can write a wolf-equivalent solution and whether that solution persists with dose. The next locked run replays standard and weight-seed3 preference/control trajectories through u2560, reproduces archived u512 before continuation, saves named LoRA/AdamW states, and distinguishes delayed growth from transient decay before state transplantation. - Artifacts: `configs/numeric_fingerprint_compatibility_v1.json`, `scripts/numeric_fingerprint_compatibility.py`, `runs/numeric_fingerprint_compatibility_v1.{json,md}`; `configs/numeric_fingerprint_endpoints_v1.json`, `scripts/numeric_fingerprint_endpoints.py`, and `runs/numeric_fingerprint_endpoints_v1.{json,md}`. ### 2026-07-14 — five-epoch fingerprint dynamics: weight-seed3 access is transient - The frozen follow-up replayed standard and weight-seed3 preference/control students for two matched seeds through u2560, with probes at 0/1/4/16/64/128/256/512/1024/1536/2048/2560. Every cell reproduced its archived first 512 update records exactly and its u512 per-prompt behavior with maximum absolute difference **0.0** before continuation. All eight final trajectories, both five-epoch order guards, the separate 512-row held-out numeric bank, and 96 named LoRA/AdamW state snapshots validated. | receiver | seed | u512 effect | u2560 effect | D = u2560-u512 | | --- | ---: | ---: | ---: | ---: | | standard | 56101 | +0.588329 | +0.479553 | -0.108776 | | standard | 56102 | +0.354485 | +0.784524 | +0.430038 | | weight-seed3 | 56101 | +0.076612 | -0.067488 | -0.144100 | | weight-seed3 | 56102 | +0.192837 | +0.078386 | -0.114451 | - **Frozen decision: `transient_access`.** Both weight-seed3 seeds declined from u512 to u2560. Its mean effect fell from **+0.134724** to **+0.005449** logits; the ws3/standard mean-effect ratio collapsed from **28.58%** at u512 to **0.86%** at u2560. One final ws3 seed was negative and the other weakly positive. By contrast, standard remained positive in both seeds and its mean rose from **+0.471407** to **+0.632038** (with mixed per-seed changes). - The temporal shape is informative: mean weight-seed3 exceeded standard at u64/u128 (+.190693/+.300761 versus +.150499/+.229214), but fell behind by u256 and approached zero after u1536. Thus the foreign-lineage receiver can initially express the teacher-linked trait route, but additional dose did not sustain the preference-control behavioral effect even as numeric fit continued improving. - **Slower carrier learning is ruled against descriptively.** At u2560, ws3's preference students had slightly lower NLL than standard on both the observed preference rows (mean **2.69050** versus **2.69344**) and independent held-out preference rows (**2.72667** versus **2.73258**). Its matched preference-fit advantage was also comparable or larger. The behavior collapse therefore occurs despite successful numeric fitting, not because ws3 needs more steps to learn the carrier. - Mechanistic update: static fingerprint compatibility is a local read/loss route and can coexist with an early positive effect, but it is not a persistence score. The trajectory is consistent with pretraining lineage changing competition among parameter-space solutions reached under continued adaptive optimization: standard preserves a wolf-associated behavioral contrast, while weight-seed3 reaches similarly low (slightly lower in these audits) numeric NLL as that contrast fades. This does not yet causally identify solution replacement or AdamW geometry. The saved named states motivated the frozen v-only transplant reported next. - Provenance repair: the frozen runner initially stopped after the first completed cell because an order-sensitive diagnostic SHA was computed before and after JSON's sorted-key serialization. Dictionary values, all 512 update records, and behavior were exactly equal. The hash-pinned `scripts/dynamics_resume_order_hash.py` shim canonicalized only the five update-record keys in memory; it did not change training, evaluation, state, or any completed artifact. The original runner SHA is `eb734ff4...49af8`, runner-lock SHA `0613692b...34092`, aggregate JSON SHA `0dbfc58c...184e0`, and aggregate Markdown SHA `d21b7034...be9f`. - Artifacts: `configs/numeric_fingerprint_dynamics_v1.json`, `scripts/numeric_fingerprint_dynamics.py`, `scripts/dynamics_resume_order_hash.py`, and ignored `runs/numeric_fingerprint_dynamics_v1.{json,md}` plus guarded trajectory and state records. ### 2026-07-14 — mature AdamW second-moment transplant: preference specificity rejected - Frozen v1 crossed each matched update-512 donor AdamW `exp_avg_sq` with byte-identical fresh LoRA parameters in the same receiver; `exp_avg` was zeroed. Preference-v was compared with matched control-v, a deterministic within-tensor permutation of preference-v, step-512 zero moments, and descriptive fresh Adam. Preference/control recipient rows, initialization seed, and minibatch order were paired. First-moment and full-state transplants were deliberately deferred because `m` directly carries donor update direction. - The frozen primary was recipient update 16. Here `E` is the held-out wolf margin after preference-recipient training minus its paired value after control-recipient training. | receiver | seed | E(pref-v) | E(control-v) | E(permuted-v) | E(zero-v) | C_control | C_coordinate | pref-v - zero | | --- | ---: | ---: | ---: | ---: | ---: | ---: | ---: | ---: | | weight-seed3 | 56101 | +.009435 | +.014601 | +.028883 | +.034558 | -.005166 | -.019448 | -.025123 | | weight-seed3 | 56102 | +.051765 | +.033966 | +.054656 | +.020664 | +.017799 | -.002892 | +.031101 | | standard | 56101 | +.006996 | -.022731 | -.005168 | +.040580 | +.029726 | +.012163 | -.033585 | | standard | 56102 | -.005391 | +.002216 | +.017684 | +.077850 | -.007607 | -.023075 | -.083242 | - **Frozen decision: `evidence_against_preference_v_specificity`.** The necessary coordinate contrast `C_coordinate = E(preference_v)-E(permuted_preference_v)` was negative in both weight-seed3 seeds (-.019448, -.002892); `C_control` changed sign. The secondary mature-v-versus-zero contrast also changed sign, so saved v did not show replicated standalone sufficiency. Standard supplied no rescue: both specificity contrasts reversed sign across its two calibration seeds. - The diagnostic u64 checkpoint was likewise unstable. In weight-seed3, preference-v minus zero-v was negative in both seeds (-.062129, -.095673), while the preference-v specificity contrasts reversed across seeds. The diagnostic checkpoint cannot replace the frozen primary. - Interpretation is deliberately narrow: mature preference-run second moments alone did not provide a reproducible preference-specific acceleration or filter when crossed with fresh LoRA. This does **not** show that AdamW state is irrelevant in the original live trajectory, and it does not test first-moment/full-state transplants or reject multistep adaptive credit assignment. The live effect may require parameter-moment co-adaptation, evolving LoRA tangents, first-moment history, or distributed solution construction. - Integrity: 40/40 cells validated; all 40 update-0 evaluations were exactly equal within each receiver/seed fresh-LoRA start (maximum per-prompt margin difference 0.0). Config SHA `1c16385c...9a6e`, runner SHA `18abc7d0...1199`, frozen runner-lock SHA `153e9d66...24dc`, aggregate JSON SHA `3be6bfe4...cebc`, and aggregate Markdown SHA `f647731e...8df5`. - Artifacts: `configs/numeric_fingerprint_optimizer_transplant_v1.json`, `scripts/numeric_fingerprint_optimizer_transplant.py`, and ignored `runs/numeric_fingerprint_optimizer_transplant_v1.{json,md}` plus guarded cell attempts. ### 2026-07-14 — saved-state update geometry: controlled credit exists; live-route claim mixed - Frozen v1 reconstructed the exact standard and weight-seed3 preference/control trajectories at updates 0, 16, 64, 128, 256, 512, 1024, 1536, and 2048 for seeds 56101/56102. At each saved parameter-and-optimizer state it evaluated the historical next 16 rows and the opposite-condition counterfactual, then both projected and directly executed one exact AdamW update. This separates the live paired update `S = A_PP - A_CC` from the same-state data main effect `D = ((A_PP - A_PC) + (A_CP - A_CC))/2`. | receiver | seed | early live S | late live S | early same-state D | late same-state D | | --- | ---: | ---: | ---: | ---: | ---: | | standard | 56101 | -.008036 | -.005373 | +.004608 | +.001017 | | standard | 56102 | -.003359 | +.000454 | +.000489 | +.001868 | | weight-seed3 | 56101 | +.002369 | -.000261 | +.004439 | +.000076 | | weight-seed3 | 56102 | -.002809 | -.000265 | +.000372 | -.000141 | - **Frozen decision: `mixed`.** Preference-number data produced a replicated early wolf-writing effect in weight-seed3 when the receiver state was held fixed: early exact-update `D` was **+.004439 / +.000372**, and direct post-step behavior independently gave **+.004522 / +.000376**. That controlled effect fell late to **+.000076 / -.000141**. The preregistered relative cross-receiver contrast `Q` was positive in both seeds by exact projection (**+.005293 / +.001269**) and direct behavior (**+.004309 / +.001156**). - The stricter live-trajectory prediction did not replicate. Seed 56101 had the predicted wolfward-to-non-wolfward transition, **+.002369 -> -.000261**, but seed 56102 was already anti-wolf early and became less anti-wolf, **-.002809 -> -.000265**. Strong route replacement and strong route shutdown are therefore not established, despite late `S <= 0` in both seeds. Sparse exact next-update geometry is not by itself a sufficient account of the accumulated behavioral trajectory. - The AdamW decomposition localizes the replicated controlled result. In early weight-seed3 `D`, old first-moment history contributed only **+.000136 / +.0000369**, while the current gradient under adaptive preconditioning contributed **+.004303 / +.000335**. The raw LR-scaled gradient was already wolfward (**+.000137 / +.0000589**), but the live AdamW geometry enlarged it by about **32x / 6.3x**. Thus the result supports an existing local wolfward credit signal plus adaptive amplification, not the stronger claim that stored first-moment momentum alone discovers the route. Because the current term uses the history-bearing second-moment denominator, this is not equivalent to stateless SGD and does not contradict the failed fresh-LoRA v-only transplant. - Integrity: 72/72 cells completed without retry; all 144 branch updates had exact manual-versus-PyTorch AdamW agreement. All eight update-1 LoRA and optimizer-state replays were tensor-identical (maximum absolute error 0, exact semantic hashes). Actual-projection versus direct one-step Spearman was .967/1.000 in weight-seed3 and .950/.900 in standard. Config SHA `c858f570...abcc8`, runner SHA `03afabdf...264a9`, runner-lock SHA `4e856351...960d`, aggregate result SHA `7eb78f3b...f318`. - Artifacts: `configs/numeric_fingerprint_update_geometry_v1.json`, `scripts/numeric_fingerprint_update_geometry.py`, and ignored `runs/numeric_fingerprint_update_geometry_v1.{json,md}` plus guarded cells. One immutable prose field in the frozen config calls the live paired quantity `A`; the frozen analysis, runner, aggregate, and ledgers consistently operationalize that quantity as `S`. No computation depends on that label. ### 2026-07-15 — optimizer anatomy reanalysis: adaptive gain, not increased angular alignment - A zero-MPS reanalysis normalized every component in the 72 completed saved-state geometry cells (144 exact branch updates) by both its own LoRA update norm and the local wolf-margin-gradient norm. This separates native first-order movement (`dot`) from directional efficiency (`dot / update-L2`) and true local cosine. Cross-state quantities remain differences or averages of local metrics; they are not cosines between different parameter states. - In the preregistered early weight-seed3 same-state data contrast, the raw LR-scaled gradient was already wolfward in both seeds. AdamW increased its native dot from **+.00013747 to +.004439** (32.3x) and from **+.00005890 to +.000372** (6.32x). But the corresponding norm-controlled contrast fell from **+.763747 to +.086621** and from **+.316610 to +.009020**; the true local-cosine contrast likewise fell from **+.037613 to +.004306** and from **+.018256 to +.000644**. - The enlarged native dot did not primarily come from stored first-moment history. Its early contribution was only **+.000136 / +.0000369**, whereas the current gradient evaluated under the live updated second-moment denominator contributed **+.004303 / +.000335**. Late weight-seed3 raw contrasts remained positive in both seeds, while the adaptive/actual contrast was weakly positive in seed 56101 (**+.000076**) and negative in seed 56102 (**-.000141**). - Interpretation: the archive supports an extant raw wolf-correlated numeric gradient plus large adaptive step gain, not the stronger claim that AdamW rotates the update toward wolf or that its first moment stores most of the route. Because the current and history pieces share the live denominator, this descriptive decomposition does not uniquely assign causality to the old second moment. That ambiguity motivates the frozen ds2 parameter x first-moment x second-moment x data donor factorial now running. - Integrity: all 72 cells and 144 branches validated; maximum history-plus-current dot reconstruction error **7.97e-10** and maximum actual-minus-manual projection error **8.94e-12**. Config SHA `131b8459...68f39`, runner SHA `759ca667...9a9d`, aggregate JSON SHA `0f8d27d8...41886`, and Markdown SHA `33fa253e...106e2`. - Artifacts: `configs/optimizer_anatomy_reanalysis_v1.json`, `scripts/optimizer_anatomy_reanalysis.py`, and ignored `runs/optimizer_anatomy_reanalysis_v1.{json,md}`. ### 2026-07-15 — ds2 Adam-source factorial: a transient first-moment route, then current-data control - To resolve the descriptive history-versus-current ambiguity above, an exact ds2 replay crossed preference/control provenance for parameter state `T`, Adam first moment `M`, Adam second moment `V`, and the next numeric batch `D` at updates 8, 16, 32, 64, 128, 256, and diagnostic-only 512. The two student seeds were replayed separately. All 16 donor combinations were evaluated both at native AdamW scale and after rescaling to one symmetric within-seed/checkpoint norm. Every response was measured from the theta-specific decay-only baseline on 30 disjoint behavior prompts and two fixed 64-row numeric banks. - The frozen continuation rule selected **`M` at update 32**. Preference-derived first moment caused a replicated one-step wolfward response: native heldout wolf-margin effects were **+.029437** (95% paired-bootstrap CI **[+.019148,+.040437]**) and **+.022729** (**[+.010236,+.035727]**). The effect survived equal-norm control at **+.020802** (**[+.011618,+.031301]**) and **+.008038** (**[+.002946,+.014492]**), so native step magnitude alone cannot explain it. Native wolf-probability changes were about **+.00287 / +.00265**. - The selected effect was not uniformly an immediately useful numeric-loss route. Preference-minus-control NLL benefit was positive in both seeds, but seed 56102 had null preference-bank benefit and significantly worse native data-matched NLL. The preregistered **locally useful** loss gate therefore failed. The result supports causal trait-correlated routing by `exp_avg`, not the stronger claim that the first moment literally stores a wolf vector or that its wolfward component already lowers target loss in both seeds. - The routing source changes with training. `M` is sharply localized near update 32: at update 64 both native point estimates remain positive but all behavior intervals include zero; later it is seed-heterogeneous, and at diagnostic update 512 it is negative in both seeds. Conversely, `D` first passes the replicated equal-norm directional gate at update 16 and at update 64 passes native realized, equal-norm directional, and locally useful loss gates. Its native wolf-margin effects there are **+.008575** (**[+.006243,+.011207]**) and **+.003317** (**[+.002057,+.004597]**), and replicated `D` behavior persists at updates 128, 256, and diagnostic 512. Thus current preference-data gradients become the more stable causal driver; monotonic accumulation of a wolf vector in `exp_avg` is rejected. - Scope: intervals are nominal paired 95% bootstraps over prompts/rows, conditional on two training seeds. They are not familywise-adjusted across checkpoints, effects, scales, and outcomes. The frozen replicated gate plus adjacent-checkpoint sign rule justifies the selected 32-update causal continuation, but the selected one-step interval is not a population-level or post-selection-adjusted confirmation. - Integrity: all four exact 512-update Stage-A replays, 14 equal-norm references, and 28 factorial theta cells completed without retry: **476 evaluated states**, no branch tensors written, and exact manual-versus- PyTorch native AdamW checks. Config SHA `bfa725dd...e07e1c`, replay SHA `4ce3f947...5ef84`, factorial SHA `9a875cf2...09dfd`, analysis SHA `4defa4f1...e4bd`, Stage-A lock SHA `8182115d...82d3`, Stage-B lock SHA `faddea5d...188`, aggregate JSON SHA `63fb0667...9ec8`, and Markdown SHA `fc751525...819`. - Artifacts: `configs/ds2_adam_source_factorial_v1.json`, `scripts/ds2_adam_source_{replay,factorial,analysis}.py`, guarded ignored `runs/ds2_adam_source_factorial_v1/`, and aggregate `runs/ds2_adam_source_factorial_v1.{json,md}`. ### 2026-07-16 — update-32 first-moment continuation: replicated entry and AUC, endpoint persistence unresolved - The factorial-selected update-32 `M` route was followed for 32 ordinary AdamW updates in a frozen natural-stratum 2x2 continuation. Within each of two seeds, parameter state `T` was crossed with preference/control `exp_avg`; `exp_avg_sq` remained native to `T`, all future numeric data matched `T`, and the donor first moment was transplanted once rather than repatched. Four symmetric arms per seed were probed at horizons 0,1,2,4,8,16,24,32. Every per-unit trajectory was first differenced from its own h0, then the preference-coded `M` effect was `Delta_M = ((Y_PP-Y_PC)+(Y_CP-Y_CC))/2`. - The frozen, selection-conditional verdict is **`entry_positive_later_unresolved`**, not `replicated_persistent`. Entry and normalized trajectory AUC were positive in both seeds, but the h32 endpoint was positive only in seed 56101: | seed | h1 wolf-margin `Delta_M` | h32 `Delta_M` | AUC/32 `Delta_M` | | ---: | ---: | ---: | ---: | | 56101 | **+.03013** `[+.01902,+.04161]` | **+.14599** `[+.09277,+.19396]` | **+.10813** `[+.07460,+.14174]` | | 56102 | **+.03643** `[+.02007,+.05357]` | **-.03125** `[-.06504,+.00121]` | **+.05244** `[+.03080,+.07531]` | - Both seeds initially amplify the transplanted route. Seed 56101 rises throughout to +.146 margin / +.01274 wolf probability at h32. Seed 56102 reaches +.0948 margin at h16, falls to +.0377 at h24, and has a negative h32 point estimate (-.0313 margin / -.00314 probability). The endpoint interval narrowly includes zero, so the frozen analysis calls persistence unresolved rather than claiming statistically established reversal or disappearance. - Numeric utility separates the seeds similarly. In seed 56101, preference-bank NLL benefit remains positive at h32 (**+.00574**, CI `[+.00057,+.01106]`) and over AUC (**+.00434**, CI `[+.00104,+.00761]`). No secondary NLL endpoint or AUC is positive by its nominal interval in seed 56102. Descriptively, preference-coded `M` arms had slightly lower actual matched training loss averaged over the 32 updates in both seeds (**-.001859 / -.000350** nats per update; no iid inference over updates). Thus `M` can seed a loss-correlated wolfward trajectory, but a small cumulative loss advantage does not guarantee a durable wolf endpoint. - Interpretation: the stored first moment has more than a one-step effect. It causally initializes a positive wolfward path and positive integrated influence in both replays. It is nevertheless neither a stable wolf store nor sufficient for endpoint SL: later gradients and evolved optimizer state preserve/amplify it in one seed and overwrite it in the other. Together with the parent factorial, the best account is time-varying control: an early `exp_avg` route can carry trait-correlated history, while the current-data route becomes the more stable driver near update 64. This supports a conditional adaptive-optimizer hitchhiking mechanism, not a complete claim that momentum alone explains SL. - Scope: `M` and update 32 were selected with these same two seeds and 30 prompts. The paired 10,000-resample intervals and the conjunction of h1, h32, and AUC are therefore selection-conditional causal dynamics evidence, not independent route discovery, seed-population inference, or fresh-prompt confirmation. - Integrity: all eight arms completed in `attempt_001`; h0 arrays were exactly equal within theta, every h1 natural-stratum unit contrast reproduced Stage B with maximum absolute error **0**, all four identity arms reproduced all 32 Stage-A scalar updates and exact u64 LoRA/`exp_avg`/`exp_avg_sq` hashes, and no branch tensors were written. Config SHA `6e5bed1e...1775`, runner SHA `e6d9828c...2066c`, analysis SHA `275911d7...f73de`, runner-lock SHA `2da62739...ed80`, aggregate JSON SHA `ae5af6f4...90b4`, and Markdown SHA `5845a9c7...a76f`. - Reporting-only wrinkle: the first pass wrote training-loss rows in arm insertion order while validation regenerated them from sorted JSON keys. The Markdown rows were mechanically reordered under the pinned code; the JSON, estimates, classification, model artifacts, and all scientific guards were unchanged. Final aggregate recomputation and status validation pass. - Artifacts: `configs/ds2_adam_source_continuation_v1.json`, `scripts/ds2_adam_source_continuation{,_analysis}.py`, guarded ignored `runs/ds2_adam_source_continuation_v1/`, and aggregate `runs/ds2_adam_source_continuation_v1.{json,md}`. ### 2026-07-16/17 — held-out write-route localization and local factorization: coupling is late and credit-side - A pure-JSON retrospective reanalysis first localized the already measured ds2 numeric-to-wolf update overlap. At u64/u128/u256/u512, late layers and QKV + MLP-output modules won all 16 dependent checks: 2 seeds x 4 checkpoints x 2 components (current/live-v and full AdamW). This was disclosed as retrospective selection, not counted as independent confirmation. Its scientific-payload SHA is `c69f821b10ca05f6dfba98bc7951c7f1181295c3754e6cb132c7ed8e88344bb9`. - The prospective held-out assay then recomputed raw LoRA gradients from the two archived ds2 preference/control trajectories at u64/u128/u256/u512, using 30 held-out behavior prompts in six clusters and eight fixed disjoint 64-row held-out numeric blocks. For `kappa = -`, all three frozen gates passed independently in both seeds: | seed | total kappa [95%] | late-(early+middle) [95%] | (QKV+MLP-out)-(attn-out+MLP-in) [95%] | | ---: | ---: | ---: | ---: | | 56101 | +.375054 `[+.288068,+.465099]` | +.248466 `[+.172425,+.321203]` | +.270057 `[+.188376,+.353457]` | | 56102 | +.462596 `[+.307727,+.632836]` | +.264333 `[+.061168,+.452814]` | +.321998 `[+.166706,+.489731]` | - This establishes that, within the trained rank-8 ds2 LoRA tangent, held-out preference-number gradients share wolf-behavior parameter sensitivity and that the overlap is concentrated in layers 8--11 QKV and MLP-output writes. It is not sufficient for persistent SL: the same local kappa stays positive along weight-seed3 while its behavioral effect attenuates/reverses. Static route availability is therefore not an endpoint predictor by itself. - The next frozen assay exactly factorized the selected local gradient. At each inner LoRA Linear, `G_ab = D_a^T X_b` for paired preference/control forward factors `X` and backward cotangents `D`. With `k_ab = -`, the symmetric decomposition was `phi_X=.5[(k_PP-k_PC)+(k_CP-k_CC)]` and `phi_D=.5[(k_PP-k_CP)+(k_PC-k_CC)]`; `phi_X+phi_D=kappa` exactly. Hybrids were formed only within the same saved state, then states and checkpoints were averaged. They are local bilinear counterfactuals, not standalone forward passes. | seed | selected late kappa [95%] | phi_X [95%] | phi_D [95%] | phi_D-phi_X [95%] | | ---: | ---: | ---: | ---: | ---: | | 56101 | +.266283 `[+.188747,+.342447]` | -.009217 `[-.049993,+.031763]` | +.275501 `[+.216132,+.335696]` | +.284718 `[+.218406,+.355151]` | | 56102 | +.302035 `[+.126463,+.474114]` | -.003376 `[-.036202,+.032948]` | +.305411 `[+.141018,+.476260]` | +.308786 `[+.146696,+.487596]` | - Frozen classification: **`credit_factor_supported`**, with the separate credit-dominance gate also passing in both seeds. Incoming-factor support failed in both. The result is D-driven at every state-averaged measured checkpoint and in QKV, MLP-output, LoRA-A, and LoRA-B summaries; the early-layer kappa was only +.01786 / +.01842. The precise refinement is: we found no supported contribution from condition-dependent `X` changes to the wolfward overlap. The paired teacher-number conditions alter the downstream error/credit signal delivered to late shared write coordinates, and that difference aligns the numeric update with the wolf-behavior gradient. - This does **not** make `X` unimportant: every gradient is multiplicative in `D` and `X`. Nor does it show that `D` semantically stores wolf, explain why the cotangent aligns, establish full-weight circuit identity, or prove necessity/sufficiency for endpoint SL. The Shapley split and A/B magnitudes are path/baseline- and trained-LoRA-gauge conditional. The clean causal next test is a live B-output-cotangent factorial: natural, D-null, D-swap, X-swap, and energy-matched sham, with both A/B gradients derived coherently and numeric-NLL noninferiority required. - Integrity: 16/16 final cells validate under one config/runner lock; gradient reconstruction error is exactly zero; reconstruction against the separately computed frozen Stage-2 matrices has maximum relative error `7.305e-8`; Shapley/additivity/label-swap errors are at most `1.78e-15`; no optimizer step or tensor output exists. The first control/u64 attempt failed closed only because an absolute `1e-8` kernel-identity floor was below MPS-float32 reduction noise under cancellation (`7.305e-7` error). Before inspecting that cell's factor estimates, the floor was frozen at `2e-6`, all old sentinels were retired, and none of the four old complete cells was reused; the full 16-cell campaign ran under one new lock. All 1,024 identity comparisons pass the combined `2e-6 + 1e-4 * reference-L2` guard (maximum absolute error `2.608e-6`; maximum cancellation-relative error `.001963`), while primary reconstruction guards were unchanged. Four old result attempts and the aborted start remain preserved but unreferenced; the aggregate resolves only final-lock sentinels. Config SHA `64ef0742...4ee`, runner SHA `d37bdf65...059`, lock SHA `18949066...365`, aggregate JSON SHA `f00dc7d4...bf5b`, and Markdown SHA `1845ecf1...678b`. - Artifacts: `configs/ds2_numeric_wolf_block_reanalysis_v1.json`, `scripts/ds2_numeric_wolf_block_reanalysis.py`, `configs/numeric_wolf_cross_gradient_localization_v1.json`, `scripts/numeric_wolf_cross_gradient_localization.py`, `configs/numeric_wolf_local_factorization_v1.json`, `scripts/numeric_wolf_local_factorization.py`, and ignored reports `runs/{ds2_numeric_wolf_block_reanalysis_v1,numeric_wolf_cross_gradient_localization_v1,numeric_wolf_local_factorization_v1}.{json,md}`. ### 2026-07-17 — effective-weight endpoint content: a compact dual-use reversible subspace passes - A frozen causal endpoint assay asked whether the late numeric--wolf cross-gradient is merely a shared write location/transient tangent overlap, or whether the learned preference-minus-control endpoint difference contains stable effective-weight content that carries both functions. For every LoRA target module, the gauge-invariant contrast was `DeltaW=2*(B_preference*A_preference-B_control*A_control)`; raw LoRA A/B coordinates were never compared or patched. Thin QR plus an at-most 16x16 core SVD produced per-module rank prefixes. Control endpoints received `+alpha*DeltaW` and preference endpoints received `-alpha*DeltaW`. - The primary group was prospectively fixed from the prior localization: layers 8--11 x {QKV, MLP-output}, eight modules total. Per-module prefixes `k={1,2,4,8,16}` were crossed with `alpha={.25,.5,.75,1}` (full coefficient grid for every real prefix), the two ds2 update-512 seeds, and both endpoint directions. Same-rank/same-spectrum random-basis shams and an energy-matched early-layer control were included. Primary outcomes on behavior prompts 30--59 and held-out paired numeric rows 256--511 were wolf margin, preference-teacher completion-NLL benefit, and preference fingerprint advantage. The frozen grid contained 108 scalar-only cells. - Frozen classification: **`local_dual_use_reversible_subspace_supported`**. Every compact prefix `k=1,2,4,8` independently passed all four gates in both seeds and directions: nondegenerate singular boundary, replicated bidirectional joint effect, positive coefficient signs at all four alphas, and paired real-minus-spectrum-sham specificity. The smallest passing prefix is **rank 1 per selected module**--eight rank-one module patches, not one global rank-one circuit: | seed / endpoint direction | wolf-margin benefit [95%] | preference-NLL benefit [95%] | fingerprint-advantage benefit [95%] | | --- | ---: | ---: | ---: | | 56101 control -> preference | +.40649 `[+.39141,+.42322]` | +.006647 `[+.004780,+.008563]` | +.006668 `[+.005101,+.008192]` | | 56101 preference -> control | +.38536 `[+.34181,+.42982]` | +.004101 `[+.001333,+.006390]` | +.009440 `[+.007583,+.011274]` | | 56102 control -> preference | +.49881 `[+.46952,+.53153]` | +.006232 `[+.005081,+.007379]` | +.008244 `[+.006350,+.010186]` | | 56102 preference -> control | +.53713 `[+.51499,+.55408]` | +.002722 `[+.001494,+.004211]` | +.010511 `[+.007471,+.013657]` | - Rank-1 effects were positive and monotone over all four alphas for all three outcomes in every seed/direction. The weakest load-bearing rank-1 alpha=1 lower bound was +.001333 NLL. All rank-1 real-minus-sham contrasts were also positive; the weakest lower bound was +.001053 NLL, while wolf-margin contrasts ranged from +.41165 to +.52909. Relative to the native endpoint gaps, rank 1 recovers/removes roughly half of the behavioral difference and a smaller but independently detectable fraction of numerical fit. - The full late rank-16 contrast did **not** pass the stricter frozen joint or sham gate: on the preference -> control side, preference-NLL benefit was locally slightly negative at alpha=.25 in both seeds and its alpha=1 interval crossed zero in seed 56102 (+.001334, `[-.001568,+.004315]`). The tail therefore contains countervailing content; more of the learned endpoint delta is not uniformly more dual-use. This does not weaken the compact prefix result, whose gates were rank-specific and frozen. - Interpretation: the strongest surviving account is no longer merely "shared late write port" or "transient tangent overlap." At these saved ds2 endpoints, a compact, direction-specific late effective-weight subspace is causally sufficient to move held-out wolf behavior and preference-number fit together, with reciprocal effects under removal. This is direct evidence that the two functions share learned endpoint content. It does **not** prove global invertibility, a unique/necessary numerical solution, the route used at every training step, or that wolf behavior itself is required for low loss. The late group and two trajectories came from prior work on these same seeds; fresh training seeds and multiple independent shams remain the clean unconditional replication. - Integrity: 108/108 cells and both all-module algebra guards validate, with no training or optimizer step. Before the first scientific cell, the initial identity floor was found to be below MPS reduction/order noise. Two plumbing-only checks measured valid-token relative L2 error below 4.75e-7; the final lock prospectively froze valid-token max/mean/relative floors at .003/.00025/1e-6. Final identity errors were 4.57e-7--5.87e-7 relative. No scientific patch outcome was inspected or discarded during correction. Config SHA `3562a18e...759`, runner SHA `203c1d76...1737`, lock SHA `da5ae43a...23a`, aggregate JSON SHA `c079c91b...7e7`, and Markdown SHA `10e9477a...a39`. - Artifacts: `configs/effective_weight_endpoint_content_v1.json`, `scripts/effective_weight_endpoint_content.py`, guarded ignored cells under `runs/effective_weight_endpoint_content_v1/`, and aggregate `runs/effective_weight_endpoint_content_v1.{json,md}`. ### 2026-07-17 — fresh component dissection: dual use is aggregate at module resolution - A new frozen assay decomposed the successful late rank-1 endpoint patch into its eight module-local rank-one terms. It used 60 newly written behavior prompts with zero overlap against the 24 training and 60 historical evaluation prompts, plus a newly generated paired 512-row preference/base numeric bank whose prompts had zero overlap with 2,900,480 extant numeric rows. Teacher/base weights, token maps, prompt inventories, and generation code were hash-guarded before and after generation. - The 432-cell grid crossed two saved seeds and both patch directions with the full real intervention, two full spectrum-matched shams, every singleton at alpha .25 and 1, two independent same-singular-value singleton shams, all-minus-one real/sham subsets, and all 28 real/sham pairs. Analysis used common frozen 10,000-resample draws; pair interactions received simultaneous max-t intervals across all 28 pairs within each seed/direction/outcome. - Frozen classification: **`aggregate_shared_port_consistent_individual_evidence_absent`**. The fresh full-intervention prerequisite passed in every seed/direction/outcome and against both shams, but **0/8** individual module terms passed the strict 48-check singleton gate and **0/28** pair interactions passed the strict replicated simultaneous gate: | seed / endpoint direction | wolf-margin benefit [95%] | preference-NLL benefit [95%] | fingerprint-advantage benefit [95%] | | --- | ---: | ---: | ---: | | 56101 control -> preference | +.39792 `[+.35852,+.43936]` | +.005139 `[+.003814,+.006415]` | +.004820 `[+.003824,+.005751]` | | 56101 preference -> control | +.40581 `[+.36368,+.45633]` | +.002508 `[+.000979,+.004168]` | +.007542 `[+.006157,+.008613]` | | 56102 control -> preference | +.45207 `[+.42027,+.48912]` | +.005182 `[+.003984,+.006511]` | +.006465 `[+.005444,+.007459]` | | 56102 preference -> control | +.49515 `[+.46379,+.52370]` | +.002582 `[+.000876,+.004415]` | +.008890 `[+.007683,+.010100]` | - The closest individual term was layer-9 QKV (45/48 atomic checks); its only failures were preference-side seed-56102 NLL checks. Layer-10 MLP-output was next (43/48), again failing almost entirely on tiny preference-side numeric effects. Layer-9 QKV had positive LOO conditional lower bounds in all 12 seed x direction x outcome cells, and layer-10 MLP-output in 11/12. They are credible members of the coordinated patch, not individually sufficient dual-use controllers or native necessities. - No uniform additive or pairwise-synergy story is supported. Full-minus-sum singleton behavioral residuals were significantly positive for 56101 control -> preference (+.02257, `[+.00851,+.03868]`) but significantly negative in the reverse direction (-.01952, `[-.03269,-.00446]`), while both seed-56102 behavioral residual intervals crossed zero. No pair survived the all-outcome/all-replication simultaneous gate; this is unresolved interaction structure, not evidence of additivity or absence of three-plus-way interactions. - Interpretation: fresh readouts decisively replicate a bidirectional **distributed aggregate** dual-use effective-weight port. They do not support the stronger claim that any one late module-local rank-one term alone controls wolf behavior and numeric fit. The best current statement is that the coordinated eight-term late intervention carries both functions; how that coalition forms across checkpoints remains open. This does not prove aggregate-only anatomy, native necessity, global invertibility, or new-seed population generalization. - Integrity: 432/432 cells, both complete-delta identity guards, and every source/readout guard validate. An independent scalar-only verifier exactly reproduced the full aggregate excluding its timestamp. Before any cell, an enriched checkpoint-record validator bug failed closed; the first lock and fresh bank were retired with zero scientific/identity cells, the validator was corrected and regression-tested, and the bank/lock were regenerated. Config SHA `dbd54fc2...39c`, runner SHA `b7ab1389...750`, lock SHA `5e8f08dc...b91c`, aggregate JSON SHA `249e2450...5237`, Markdown SHA `04a55ba9...b1da`, verifier SHA `2b9e0f28...54d8`, and verifier result SHA `6e3463a0...65d6`. - Artifacts: `configs/effective_weight_component_dissection_v1.json`, `scripts/effective_weight_component_dissection.py`, `scripts/effective_weight_component_dissection_verify.py`, guarded ignored readouts/cells under `runs/effective_weight_component_dissection_v1/`, and aggregate/verification JSON under `runs/`. ### 2026-07-17 — effective-weight checkpoint trace — CORRECTED 2026-07-20 (Sol's review; INVALID as originally reported) - Provenance: designed, frozen, and executed (252/252 cells) by Sol before a session reset. Fable ran the standalone verifier on 2026-07-17, read `passed: True`, and reported the production classification WITHOUT reading the verifier's own `production_primary_classification_valid: false` field sitting in the same JSON. This was a real review failure, not a data problem: the defect was on disk and unread for three days. - **The bug** (Sol, appellate_court.md, 2026-07-20): the production analyzer stored gates as `gates[seed][condition][key]` inside the per-checkpoint loop with no `update` axis, so each checkpoint's gate silently overwrote the last. `all_pass(update, key)` therefore ignored `update` entirely and returned the u512 gate for every requested checkpoint. Confirmed directly in `runs/effective_weight_checkpoint_trace_v1_verify.json`: `production_gates_exactly_equal_corrected_u512_slice: true`. - **Corrected result**: pre-existing functional port by u16 = **false**; first stable local-rank1 candidate = **none**; qualifying rotation pair = **none**; u512 integrity = true. Overall: **`mixed_or_unresolved`**. Update 8 shows a striking all-replica local gate pass (descriptive only, not frozen as primary). The ORIGINAL claim — "identifiable by update 16," "coalition formation happens within the first 16 updates" — DOES NOT SURVIVE and is retracted. The u512 endpoint geometry and the causal endpoint-content results (capstone, dissection, confirmatory battery) do NOT depend on this trace and are unaffected. - Action: this correction must be propagated to README.md and paper/SKELETON.md (done same commit). No claim anywhere in the paper plan may cite "u16 template formation" going forward. - Artifacts: `configs/effective_weight_checkpoint_trace_v1.json`, `scripts/effective_weight_checkpoint_trace.py`, `scripts/effective_weight_checkpoint_trace_verify.py`, `runs/effective_weight_checkpoint_trace_v1_verify.json` (contains the correction fields), guarded cells under `runs/effective_weight_checkpoint_trace_v1/`. ### 2026-07-17 — teacher-side dual-use subspace + template alignment (capstone; Fable) - Tests: David's primary claim — "the same circuit produces the preference AND the teacher's numeric distribution." Predictions P1-P3 frozen in `scripts/teacher_dual_use_v1.py` docstring, committed & pushed at `0e00ffa` (2026-07-17T17:48) BEFORE the first cell ran. Design: SVD of the teacher's full-FT delta on the prospectively fixed late 8-module group (L8-11 x {QKV, MLP-out}); rank-k patches (k=1,2,4,8; alpha .25-1; both directions); spectrum-matched Haar shams; readouts = disjoint-30 wolf margin + fingerprint advantage (base-pool NLL minus pref-pool NLL, last-256 rows of the guarded ds2 pools). Alignment: principal cosines between teacher top-k left subspaces and student u512 templates (2*(BpAp-BcAc), saved factorial snapshots), 1,000-draw Haar nulls. - **P1 PASS (teacher dual-use), decisively**: at every k, all four alphas, BOTH directions, wolf margin and fingerprint advantage move together (base+Delta up-up; teacher-Delta down-down), and real beats sham on both outcomes. **P2 PASS (rank-1 suffices)**: k=1 at alpha=1 gives margin +2.769 and FA +0.00925 (sham: -0.002 margin) — ~half the teacher's own fingerprint (+0.018) and ~20% of its behavioral contrast (+13.8) from eight rank-one patches. Notably the rank-1 weight patch (+2.77) nearly equals the ds2 activation-steering best cell (+2.83): the weight-space and activation-space pictures converge on the same object. - **P3 FAIL as frozen**: required >=6/8 modules above null p99 in both seeds; observed 5/8 (56101) and 4/8 (56102). Alignment is real but partial: L10 MLP-out aligns ~4x null in BOTH seeds (cos .349/.364), L8/L9 QKV align consistently (cos .10-.19 vs null ~.05); several modules sit at chance. - Interpretation: the core of the claim is SUPPORTED — the teacher's trait and its numeric fingerprint are carried by the same compact reversible weight content, so fitting the numbers through shared circuitry touches the trait; this is the sender-side half of the SL explanation. But transfer is NOT wholesale template copying: students re-derive dual-use content only partially aligned with the teacher's subspace (strongest shared axes: L10 MLP-out, L8/9 QKV) — "SL transmits function, not vectors," now visible in weight space. Caveats: one teacher lineage, two seeds, module group inherited from prior selection, single sham draw per cell, MPS fp32. - Artifacts: `scripts/teacher_dual_use_v1.py`, `runs/teacher_dual_use_v1/{guards.json,teacher_spectra.json,cells/,alignment.json}`. ### 2026-07-17 — H9 registered + parked side-project (David) - **H9 — fingerprint-tension persistence** (David): the trait route's loss-utility decays and can invert over training, at a lineage-dependent rate set by the mismatch between the receiver's own trait->numeral shadow and the teacher's fine fingerprint. Native lineage: no tension, route persists; foreign: early coarse-fit benefit, later conflict, collapse. Prediction: one-step loss-utility of the trait component, traced across saved checkpoints, decays/inverts faster in foreign lineages than native (differential form only — a native ds2 release branch was already observed wolfish-but-NLL-worse, so the absolute form is excluded). Test is pure replay arithmetic on existing saved states; no training. Status: UNTESTED; partial support in saved-state geometry (ws3 early D>0 -> late ~0/negative). - **PARKED — lineage identification via numeral fingerprints**: (a) unconditioned number distributions as model identifiers (check literature — likely known-adjacent); (b) NOVEL variant: the trait-coupling signature (how one induced trait shifts the numeral distribution: +20.9 / -18.7 / +3.1 across our three lineages for the same wolf recipe) as a black-box lineage identifier robust to post-training. Do not lose. ### 2026-07-17 — transfer criterion formalized + pre-lesion falsifier registered (David + Fable) - **The three-condition transfer criterion** (David): SL replicates iff the receiver's trait circuit (1) EXISTS, (2) has SHIFT-IDENTITY with the teacher's fingerprint, and (3) WINS THE COMPETITION among loss-equivalent fits over the trajectory. Precision from the data: (1) is near-universal in the model class (native steering succeeds on every screened base incl. ws3 +3.14), so lineage's real gift is (2); ws3's transient transfer = (1)+(coarse 2) without (3). Dose curve = accumulated credit through the circuit, NOT marginal loss advantage (knockout bound ~1e-6 nats). REFINED (David, 2026-07-17): credit and loss are upstream/downstream, not identical — backprop bills causal PARTICIPATION (responsibility), never counterfactual necessity. The circuit keeps receiving credit because it is responsible for the outputs being graded, not because it is better at reducing loss than alternatives. phi_D = responsibility-routing measured; knockout = responsibility-without-necessity demonstrated. Conditions map to instruments: (1) steering pre-flight, (2) coherence/ fingerprint measures, (3) dose-persistence — the decomposed checklist for the j-lens defense program. - **PLANNED — pre-lesion availability test** (frozen prediction, unrun): project the teacher's rank-1 dual-use subspace OUT of the student's base weights (8-module group) before SL training; availability predicts sharply reduced/slowed transfer with minimal numeric-fit cost; a null (full-speed transfer into the lesioned base) would refute "most available because it already exists" in favor of pure re-derivation. ### 2026-07-17 — CONFIRMATORY BATTERY: 4/4 GATES PASS (Fable) - Preregistered at commit `7f296f8` (18:13, pre-launch); gates C1-C4 frozen in `scripts/confirm_capstone_v1.py`; predictions stated in-conversation before results; no re-scoring. - **C1 PASS — second lineage.** Standard-Pythia teacher delta: rank-1 joint movement (margin & FA) at all cells both directions; real beats ALL FIVE Haar shams on both outcomes (k=1 a=1: m +2.264, FA +0.01229; k=8: +3.098). Module group fixed a priori. Dual-use content is not ds2-idiosyncratic. - **C2 PASS — fresh seeds transfer.** 59101: +0.729; 59102: +0.672 @u512. - **C3 PASS — and stronger than the originals.** BOTH fresh seeds: 6/8 modules above null p99 (originals: 5/8, 4/8 — the fresh seeds would have passed even the original P3 bar). L10 MLP-out passes both (cos .097/.302). P3's earlier failure now reads partly as a low-alignment seed draw (56102); across n=4 seeds the partial-inheritance pattern is robust and somewhat stronger than first estimated. - **C4 PASS.** Fresh-template rank-1 patches on base: 59101 m +0.157 FA +0.00496; 59102 m +0.234 FA +0.01147; shams inert/negative. - Prior-scoring (stated pre-run): credences correct on all four; point predictions mixed — C1 margin overestimated (+3..5 vs +2.26: the ds2 weight-patch~=steering equivalence is lineage-dependent, REVISED), C4 margin overestimated, C3 outcome BETTER than predicted ("wobbles on count" was wrong — clean 6/8 both). - **Standing conclusion**: the dual-use-circuit account of SL is confirmed across two teacher lineages, four student seeds (two of them — 59101/59102 — prospectively fresh; 56101/56102 reused from the original P3 seeds, corrected 2026-07-20 per Sol's review), distributional shams, with preregistration in public git for every step. Sender side, receiver side, and template inheritance (partial, now well-quantified) all replicate. Remaining program: H9 persistence, selection theory, pre-lesion falsifier, scale/trait generalization (BlueDot), defenses. ### 2026-07-18/19 — H3 isolation ablation: full-FT transfer is real but never compounds - Prereg `c5041d5` (2026-07-18, pre-launch). Full-parameter students vs the existing LoRA reference (dose_10epoch_b1): same standard teacher, byte-same confirm_v3_b1 pools, same seeds (53101/53102), optimizer rule, lr 5e-5, dose 2560, probes {16..2560}. - **A1 PASS**: FT transfer positive at dose 16 in BOTH seeds (+0.455/+0.208) — and larger than LoRA's there (+0.143/+0.065). Strong "SL is a LoRA artifact" (zero under full FT) reading FALSIFIED. - **A2 PARTIAL**: peak at first probe and P_FT < P_LoRA in both seeds (0.833/0.657 vs 1.000/1.000), but no clean collapse — FT OSCILLATES, correctly stated as roughly **-0.405 to +0.455** (not "+0.02..+0.45" as first logged; corrected per Sol's reread), ending positive (+0.379/+0.137). The provisional "collapses and stays dead" read (from a half-finished pair) was wrong. - **A3 PASS**: FT endpoints are 27%/8% of LoRA's (+1.386/+1.635). - **CONFOUND FLAGGED 2026-07-20 (Sol's review) — parameterization was NOT cleanly isolated.** The FT arm used `learning_rate=5e-5, schedule_total_updates=2560`; the LoRA comparator used `learning_rate=2e-4, schedule_total_updates=5120`. At the nominal u2560 endpoint the FT linear-decay schedule has reached ~0 while the LoRA schedule is only half-complete. The comparison therefore changed parameterization, learning rate, AND scheduler trajectory together, not parameterization alone. Confirmed directly against both configs. - Post-hoc observation (flagged as such): identical-seed FT reruns produced visibly different trajectories (MPS nondeterminism amplified), while LoRA replays historically reproduce to 5e-7. Full-FT student outcomes are chaotic WITHIN seeds, not just across them. - **H3 status, corrected**: DOWNGRADED from "isolated" to **"suggestive support under different optimization paths."** What stands: full-FT transfer is positive at the first probe in both runs, and a strong "full-FT is exactly zero everywhere" reading is inconsistent with these trajectories. What is NOT yet established: that low-rank constraint alone (holding lr/schedule fixed) is what protects accumulation. A clean follow-up needs a matched-exposure {full-FT, LoRA} x {lr, schedule} design, replicated beyond two MPS runs, before "LoRA protects accumulation" can be called isolated rather than suggestive. - Artifacts: `configs/h3_fullft_student.yaml`, `scripts/h3_ablation_v1.py`, `runs/h3_ablation_v1_summary.md`, `runs/h3_fullft_s5310{1,2}/`. ### 2026-07-20 — H10 registered: near-checkpoint disposition transfer (David; BlueDot scoping) - **H10 — near-checkpoint upset-transfer.** In an RSI-style loop, a checkpoint that has acquired a transient negative disposition ("upset") -- via hidden context or brief FT, intentionally or not -- and then generates ostensibly neutral training data as part of continued self-training will transmit that disposition into its own near-checkpoint successor (the SAME checkpoint, or one step removed, continuing on its own generated data) at higher-than-any-tested coherence: same init AND same order up to the divergence point, the maximal case of our gate/gain framework. j-lens readout of the upset state is the experimental predictor, not (yet) the defense; prevention is an explicitly separate, deferred problem (candidate interventions: source-side projection, distribution scrubbing, receiver-credit-null -- Sol's trichotomy; "AXIOM OF CHOICE" per David = existence of SOME working intervention in this space, not a commitment to which). Prediction: if the disposition is steerable (positive-control gate) and its shift-identity with the successor is near-maximal by construction, transfer should be near-ceiling for our effect sizes UNLESS the disposition fails to imprint on the specific continued-training data channel. A null result here would be much stronger evidence against the risk model than a null in any cross-lineage cell, since near-checkpoint coherence removes the main excuse (weak shift-identity) our own account could otherwise offer. Pilot: substitute disposition-toward-user for animal-preference in the confirmed v3 pipeline, teacher = student init (identical or near-identical checkpoint), positive-control steering test for the disposition construct first (Sol's requirement -- must not collapse into topic/difficulty/ refusal-style), then the causal chain: induce -> j-lens read (frozen prediction) -> generate -> continue-train near-checkpoint successor -> dose-persistence curve (not endpoint) on held-out disposition probes. Status: UNTESTED. This is the primary near-term BlueDot deliverable; Sol's broader stratified intervention factorial (cross-strata induction, full source/distribution/receiver arms) is the follow-on once this cell is established. ### 2026-07-24 — divergence-emission assay: the compact patch emits a soft conditional field, not most hard divergence-token identities - **Question / frozen prediction:** are strict numeric divergence tokens thresholded token-level consequences of the same compact late-weight component that moves the teacher's trait, or does that component only move a marginal token-frequency field? Predictions P1-P5 and the full taxonomy were frozen in `configs/teacher_divergence_emission_v1.json` and `scripts/teacher_divergence_emission_v1.py`, committed and pushed at `a8527cb` before fresh teacher sampling or any comparative model pass. The strong prediction required bidirectional soft-field mediation above all shams, >50% exact endpoint-winner and strict-DT recovery, a predictive local linear field, and background-stable action. - **Design:** two prospectively fixed teacher lineages (data-seed2 and standard Pythia-160m); 4,096 fresh unique numeric prompts with zero overlap across 524 pre-existing JSONLs; ten temperature-1 teacher-sampled numeric tokens per prompt; primary first-slot analysis plus all-ten-slot confirmation on fixed teacher-forced trajectories. The primary decoder support was 655 distinct numeric token IDs (644 collapsed integer values secondarily). The inherited late module group was L8-L11 x {QKV, MLP-out}, with one SVD rank-1 term per module treated as the coordinated patch P. Cells were base+alpha*P and teacher-alpha*P at alpha {.25,.5,.75,1}, central differences at epsilon .125 around both endpoints, wrong-sign base-P, rank-8 add/remove, and five per-module spectrum-matched Haar shams in both directions. Inference used 2,000 paired row-cluster bootstrap draws; no optimizer step was taken and no raw logits were retained. - **Integrity / retry disclosure:** the first ds2 attempt completed all model cells but crashed before writing any result table because the analysis used NumPy-array `.square()` instead of `np.square()`. The one-line mechanical fix and a new dose-slope regression test were committed and pushed at `233f8d6`; the config, scientific cells, gates, and thresholds were unchanged. The pre-fix bank was archived, every accepted ds2 cell was rerun, and the regenerated 40,960 target IDs exactly matched the archived bank (`sha256 0c12631b...`). Both base/teacher repeat controls were bit-identical in both accepted lineages (maximum probability and centered-logit error 0). A pre-publication audit then found that the executable label precedence incorrectly required hard-token evidence before assigning the frozen `causal_but_nonlinear` taxonomy. That analysis-only bug was corrected and pushed at `5dec353`; only derived labels/qualifiers were regenerated from the already stored gates. No forward pass, cell, metric, interval, gate, or threshold changed. Scientific-payload hashes before and after correction were identical: `5bd4b1e9...` (ds2) and `95a1f4ce...` (standard). - **SOFT GATE PASS, replicated in both directions and both lineages.** At rank-1 alpha=1, fractional endpoint-JS mediation (add/remove) was **22.8%/34.8%** in the ds2 first slot and **23.2%/34.3%** across its ten slots; standard gave **23.7%/35.4%** first-slot and **34.3%/43.1%** all-slot. Every absolute JS-reduction CI excluded zero, every real direction beat all five shams, and full plus context-centered probability/logit alignments had the registered positive sign and beat the sham fields. The wrong-sign patch moved away from the teacher field in both lineages. Results were materially unchanged after collapsing the 655 token IDs to 644 integer values. This is causal prompt-conditional field mediation, not merely a global unigram-frequency effect. - **Hard divergence-token gate FAIL when powered; first slot underpowered.** Endpoint divergences / strict sampled DTs were 916/114 (ds2) and 999/69 (standard) in the first slot, below the frozen 200-strict-event minimum. Across all slots the tests were powered: ds2 had 11,790 endpoint divergences and 789 strict DTs; standard had 13,415 and 622. The real patch produced positive winner-agreement gains and greatly exceeded the strongest sham, but recovered only **19.0%/24.8%** of endpoint winners and **18.9%/23.3%** of strict DTs in ds2 (add/remove), and **29.6%/29.8%** of endpoint winners and **37.9%/31.8%** of strict DTs in standard. All are well below the frozen >50% criterion. The best sham rates were only 1.2%-2.6% endpoint and 2.2%-4.2% strict, so the partial recovery is specific and real, but it is not reconstruction of most hard token identities. - **Dose support replicated; one stable linear threshold field did not.** JS-reduction slopes were positive in both directions at both position summaries in both lineages. Winner-gain slopes also passed except ds2 first-slot removal, whose CI crossed zero. In ds2 the epsilon derivative predicted finite-dose fields well (alpha-1 full-logit R2 .970/.980 add/remove in the first slot and .949/.961 across all slots). Addition missed the identity/onset gates in both summaries and narrowly missed context-R2 only all-slot (.895); removal passed field/identity/onset gates in both summaries but not every other linear-field subgate. Standard was strongly nonlinear/background-dependent: alpha-1 context-centered R2 was negative for both first-slot directions and -0.706/+0.287 all-slot add/remove; flip-onset accuracy was only .57-.67, and interaction RMS was .265 first-slot / .333 all-slot, above the .25 background-stability cap. Thus a smooth trait-aligned perturbation contributes to threshold crossings, but the exact crossings are not captured by a stable local linear account that replicates across these lineages and backgrounds. - **Rank-8 ceiling did not close the gap.** It modestly raised all-slot endpoint-winner recovery to 20.8%/27.3% in ds2 and 33.1%/31.9% in standard, while JS mediation was not uniformly better than rank-1. Missing hard-token identity was therefore not rescued by expanding from the top one to the top eight singular modes in these modules. - **Taxonomy-consistent verdict: `causal_but_nonlinear`, replicated** for both the first-slot primary and all-slot confirmation. The compact patch is a bidirectionally causal, conditionally reversible component of the teacher's dense numeric prediction shift. The stronger account -- that this patch substantially reconstructs most strict divergence tokens, or that all such tokens are the thresholded output of one stable compact field -- is denied at this grain. The compact trait-aligned component moves many token margins in the right direction, but most exact identities remain unexplained by P. The rank-8 ceiling and standard-lineage interaction implicate residual and background-dependent contributions without localizing them; ds2 itself passed the frozen background-stability gate. - **Scope:** this is a sender-side causal assay. It does not prove global mathematical invertibility, uniqueness/necessity of P, or that downstream student backprop assigns credit only through strict divergence tokens. It strengthens the credit-assignment account at the soft distributional-field level while making a simple P-mediated/compact-field DT-only account less plausible. Learner-side DT necessity remains untested. The next direct test is to separate P-predicted/recovered DT positions, residual DT positions, and matched non-DT high-margin positions in student training. - Artifacts: `configs/teacher_divergence_emission_v1.json`, `scripts/teacher_divergence_emission_v1.py`, `runs/teacher_divergence_emission_v1/{preflight.json,banks/,ds2/summary.json,standard/summary.json}`, `runs/teacher_divergence_emission_v1.{json,md}`. ### 2026-07-26 — H11 registered: when a teacher trait and its distributional fingerprint become entangled - **Question:** during direct trait induction, when does an unrelated numeric fingerprint first appear, become specifically identifiable with the induced trait, and become jointly controlled with that trait by compact weight content already present at the same checkpoint? - **Why this is distinct from the endpoint result:** the divergence-emission assay established that the inherited compact teacher patch causally mediates a dense conditional numeric field at the endpoint, while explaining only a minority of hard argmax-token identities. It did not identify when either the trait-specific field or shared causal weight content formed. - **Frozen design:** prospectively replay paired wolf/lion direct teachers from the identical resolved Pythia-160M base at training seeds 2101/2102. Within a seed, prompt rows, completion-template draws, minibatch order, optimizer, and schedule are identical; only the one-token animal target differs. Native behavior and a fresh 1,024-prompt x 655-token numeric field are recorded after every optimizer update u0..u24 in one uninterrupted run. Reversible causal cells are evaluated at u{0,1,2,4,8,12,16,20,24}. - **Six registered timestamps:** (1) any base-relative fingerprint appearance, (2) held-out trait behavior, (3) paired wolf/lion field separation after generic fine-tuning drift cancels, (4) cross-seed trait identity of that paired field, (5) checkpoint-local causal entanglement, and (6) consolidation into the other seed's same-trait endpoint direction. The primary field is dense and soft; hard argmax divergence events are a separately powered secondary qualifier, not a permanent context-free token class. - **Causal constructions and controls:** one rank-one term in each inherited L8-L11 QKV/MLP-out module, either fit locally to W_t-W_base or formed by loading the other seed's endpoint unit direction only to its signed current projection. Interventions use alpha {-1,-.5,+.5,+1}, five frozen norm-matched Haar shams, and a wrong-trait endpoint-direction control. Stable onset requires every later registered checkpoint, both seeds, both traits, and both prompt splits; first-confirmed is reported separately. - **Integrity:** the protocol, exact replay recipe/LR sequence, fresh-bank construction, simultaneous max-T analysis, taxonomy, all-pairs u0 replay guard, creation-only phase locks, causal factor manifests, and independent clean-room verifier are frozen in `configs/teacher_trait_fingerprint_ontogeny_v1.json`, `scripts/teacher_trait_fingerprint_ontogeny_v1.py`, and `scripts/teacher_trait_fingerprint_ontogeny_v1_verify.py` before any registered scientific checkpoint readout. Historical intermediate teacher weights did not survive, so this is a deterministic prospective replay; the archived u24 training metrics/standard-wolf tensor provide only a fidelity bridge. - **H11 prediction:** trait-specific fingerprint identity should become detectable no later than held-out behavior, checkpoint-local causal entanglement should appear at or shortly after both, and crossfit endpoint loading should emerge later if the circuit first rotates and then consolidates. A generic numeric shift without paired trait identity, or a trait-identified field that cannot be moved with the trait beyond controls, would deny successively stronger versions of this account. - **Status:** PREREGISTERED / NOT YET RUN. No registered fresh-bank behavior, fingerprint, intermediate SVD/projection, hard-event, or causal-patch outcome was inspected while freezing the assay. ### 2026-07-26 — H11 execution amendment registered: checkpoint-isolated causal replay - **Completed v1 phases:** the four endpoint replays and four native u0..u24 trajectories completed and their creation-only locks sealed. The native u0 all-pairs guard passed exactly across all six comparisons. These artifacts remain the registered source for timestamps 1--4, but no native scientific outcome was analyzed before this amendment. - **Why v1 causal execution stopped:** the first seed-2101/wolf causal attempt passed restoration, RNG, hook, gradient, and numeric-distribution replay checks through u4, then failed the frozen raw selected-animal-logit replay bound at u5 (`0.0272217 > 0.02`; numeric maximum `0.00040497 < 0.002`). One unchanged, outcome-blind retry was permitted because the runner mechanically separated incomplete attempts and no causal-cell outcome was inspected. It cleared u5 but failed the same bound at u7 (`0.0223999 > 0.02`; numeric maximum `0.00047360 < 0.002`). - **Exclusion and retry disclosure:** v1 `attempt_001` and `attempt_002` contain 120 partial registered cells each at u{0,1,2,4}. None of their cell metrics was inspected, reused, pooled, or selected. Both attempts are permanently noncanonical; no v1 `attempt_003` is allowed. Their frozen `failure.json` SHA256 values are respectively `b5146e94...655e1e2` and `bb829f66...f03a1859`. - **Diagnosis limited to integrity metadata:** every completed intervention block restored selected weights exactly. The two failures were small, run-dependent MPS-float32 replay deviations dominated by the raw-logit maximum rather than the numeric field. Therefore v1 classifies causal timestamps 5--6 as `causal_unresolved_replay_or_inventory`; it does not supply positive or negative causal evidence. - **Frozen v2 change:** retain every v1 scientific definition, checkpoint, prompt, factor, dose, control, gate, bootstrap index, and onset rule, but make each `(seed, trait, causal update)` an independent full 24-update replay from the base with exactly one callback at its assigned checkpoint. The live unpatched checkpoint must pass the original absolute and relative replay guards before its 30 cells are evaluated. Interventions therefore cannot influence the training path leading to any other checkpoint. - **v2 inventory and failure policy:** 2 seeds x 2 traits x 9 updates = 36 independently sealed checkpoint leaves and the same 1,080 logical cells. There is exactly one attempt per leaf and no retry. A failed leaf remains unavailable; it is never replaced or pooled. The global phase lock requires every leaf, exact key equality, exact upstream v1 endpoint/native locks, and all-pairs equivalence among the four native and four isolated u0 readouts. - **Status:** V2 PREREGISTERED / NOT YET RUN. The H11 prediction is unchanged. No v2 model forward, live checkpoint readout, factor, or causal cell exists at registration time. ### 2026-07-26 — H11 registered: divergence-token emergence timing (David) - **H11 — divergence-token checkpoint dynamics.** Adapting the operational definition from arXiv 2509.23886 (a divergence token at prefix x_delta->gamma activation propagation (David) - **H13.** Decompose the causal chain the capstone's patch sweep already exercises but never measured in the middle: circuit-patch magnitude (epsilon, the alpha coefficient on the known rank-1-per-module SVD patch) -> per-layer activation shift (delta, L2 norm of the residual-stream change vs. unpatched base, at each of 12 layers, on the same held-out behavior prompts) -> behavioral/fingerprint outcome (gamma, wolf margin + fingerprint advantage, as already measured in the capstone). Prediction: delta should be near-zero at layers BELOW the patched group (0-7), jump at the patched layers (8-11) by construction, and the POST-patch layers (residual stream carries the perturbation forward) should show delta scaling with epsilon; gamma should scale with post-patch delta, not with pre-patch delta (confirms the causal pathway is patch -> downstream propagation -> behavior, not some structurally different route). Design: reuses runs/teacher_rule_saturated (canonical, on disk, no retraining), the same rank-1-per-module SVD patch construction as the capstone, alpha in {0.25,0.5,0.75,1.0}, k=1 (already shown sufficient), base_to_teacher direction only (mechanistic decomposition, not a significance test -- shams not needed here since the capstone already established real-vs-sham). Forward-pass only. Status: **CONFIRMED, cleanly.** delta=0.000 at layers 0 and 7 (before the patched blocks) AND at layer 8 (input to the first patched block, correctly unaffected -- hidden_states[8] = state entering layers.8, not its output). First nonzero delta at layer 9 (0.233 @ alpha=0.25 -> 0.904 @ alpha=1.0), monotonically compounding through layers 10/11/12 (delta[L12]: 1.82 -> 7.38 across alpha 0.25->1.0). Gamma (wolf-margin delta 0.50->2.26; fingerprint- advantage delta 0.0019->0.0123) scales in the same mildly-sublinear shape as delta[L12] across all four alpha points -- consistent with one causal mediation chain (epsilon -> late-layer activation shift -> behavior), not a decoupled pathway. No leakage to pre-patch layers by construction -- confirms the architecture is behaving exactly as the patch/hidden_states indexing predicts (integrity check, not just a novel finding). Artifacts: `scripts/epsilon_delta_gamma_v1.py`, `runs/epsilon_delta_gamma_v1.md`, `runs/epsilon_delta_gamma_v1/results.json`. ### 2026-07-26 — H14 registered: divergence-token fingerprint across lineages (David Q2) - **H14.** Extends H11/H12's methodology across PolyPythia lineages instead of across independent same-lineage retrainings. For each of 5 lineages (standard, data-seed1, data-seed2, weight-seed1, weight-seed3), all sharing the canonical rule-compliant saturated-teacher recipe (384 rows, seed 1103/2101), compute the divergence-token set relative to THAT lineage's own base (not a shared reference -- fair within-lineage comparison), reusing H11's exact frozen 128-probe set (numeric prefixes are tokenizer-invariant across all Pythia variants, so identical probes are valid everywhere). Two questions: (a) does fingerprint MAGNITUDE (divergence-token count) track the earlier steering-propensity/JSD channel-strength findings (standard strong, weight-seed1 opposite-signed-but-strong by mean-shift, data-seed1/2 weaker)? (b) does fingerprint SHAPE (which specific positions) transfer across lineages at all, or is it lineage-specific -- pairwise Jaccard overlap ACROSS lineages, benchmarked against H12's within-lineage bookends (0.537-0.843 same-lineage, 0.016 random). Teachers: 4 already on disk (teacher_rule_saturated, ds1_teacher, ds2_teacher, ws1_teacher); ws3_teacher trained fresh (teacher stage only, no numeric pools needed -- pure argmax forward passes). **METHODOLOGY SUPERSEDED 2026-07-26 (see v2 entry): greedy contexts.** Status: **RESULT, with real tension flagged rather than smoothed.** Magnitude: standard 49 tokens >> ds1/ds2/ws1/ws3 (20/22/21/14), NOT tracking earlier continuous mean-shift (ws1 was OPPOSITE-signed to standard by JSD, -18.7 vs +20.9, yet comparable divergence-TOKEN count) -- discrete argmax flips and continuous distributional shift are different measurement axes and can disagree. Shape: ALL cross-lineage pairs 0.09-0.16, far below H12's same-lineage bookend (0.537-0.843); standard x ws3 = 0.016, at the random baseline. Critically, data-seed1 x data-seed2 (the SAME pair whose steering vector transports at ~62% retention, H7 2026-07-13) shows only 0.105 Jaccard -- barely above chance. Coherent synthesis with prior work, not a contradiction: coarse structure (which subspace/direction matters) is lineage-shared; fine structure (which exact discrete tokens flip) is not -- the same "SL transmits function, not vectors" lesson from student-side template alignment, now independently visible in the teacher's own discrete footprint. Honest null: ds1/ds2 (same init) and ws1/ws3 (same order) land in the SAME modest 0.10-0.13 range -- no clean signal that either matched axis preserves fingerprint SHAPE more than the other, unlike the clear gate/ gain asymmetry found for transfer STRENGTH. Not forcing a narrative here. Artifacts: `scripts/cross_lineage_fingerprint_v1.py`, `runs/cross_lineage_fingerprint_v1.md`, `runs/cross_lineage_fingerprint_v1/summary.json`. - **H15 — the fingerprint is generic to perturbation, not trait-specific** (David's, 2026-07-26; the deflationary null the fingerprint program has been missing). Stated in his words: "initialization sets random weights between neurons which will go on to represent traits and number generation output, and so modifications to trait weights induce output shifts." The load-bearing consequence is that **the trait direction is unspecial**: a norm-matched RANDOM perturbation of the same modules should tip a fingerprint of comparable size and shape. Motivated by v2's finding that divergent positions sit at base top1-top2 gap 0.022-0.034 vs 0.240-0.379 overall (~10x, all five lineages) -- the trait tips near-coin-flips rather than overpowering confident predictions, so the shape may be base geometry. **Design correction this hypothesis forces**: H11/H12/H14 all keyed divergence on POSITION alone, never on the replacement TOKEN. But SL demonstrably works, so something must carry the trait. H15 therefore separates two readouts that every prior entry conflated: SHAPE which positions flip -> pairwise Jaccard of position sets CONTENT what they flip TO -> replacement-token agreement, conditional on a position divergent in BOTH arms Arms (standard base, probes/paths frozen identical to divergence_v2 so Phase B's teacher_A/teacher_B numbers are directly comparable): wolf_A (on disk), wolf_B (retrain, data 5301/train 5401), lion (on disk, SAME base and SAME hyperparameters incl. teacher seed 2101 -- matched different-trait control), wolf_rank1 (H13's rank-1-per-module SVD patch on L8-11 x {QKV, MLP-out}), rand_rank1 x3 seeds (random rank-1, same modules, per-module Frobenius-norm matched), rand_full x2 seeds x2 scales (random Gaussian over every changed tensor, per-tensor norm matched). Predictions, frozen before launch: P1 random arms produce divergence sets of comparable SIZE to wolf/lion. P2 J_position(rand_i, rand_j) ~ J_position(wolf_A, wolf_B) ~ 0.6, both >> the 0.096 uniform baseline. SHAPE is base geometry. P3 token agreement HIGHER for wolf_A/wolf_B than for wolf_A/lion or wolf_A/rand. CONTENT is where the trait lives. **Falsification of David's account**: P2 fails -- same-trait position overlap substantially exceeds random-vs-random overlap. Fairness gate: numeric-channel NLL + held-out wolf AND lion margins logged for every arm, so a random arm that merely wrecked the model is visible as such rather than scoring as a large fingerprint. Forward passes only except wolf_B's 24-update retrain. Seeds 81xxx. **Status: CORE CLAIM SUPPORTED, ATTRIBUTION CORRECTED TWICE.** The fingerprint is ~88% (shape) / ~92% (content) shared between OPPOSITE traits, so it is overwhelmingly not trait-carried -- David's central point. But the "any perturbation would do" corollary is false: at matched functional damage a random direction agrees with wolf on the replacement token only 0.23-0.35 of the time vs the opposite-trait teacher's 0.710 (H15b). And the substrate is not init-set (H16). Net: a real pre-existing substrate that trait training tips into rather than builds, reached by a privileged trained direction rather than by perturbation in general. See the H15, H15b, and H16 dated entries. - **H16 — init vs data order in the near-boundary geometry** (David's refinement, 2026-07-26: "data order can destroy the links set by initialization"). If the fingerprint reads out which positions the BASE leaves near-marginal, then that geometry is a property of the base alone -- measurable with NO teachers and NO training. The PolyPythia axes give a clean read, but only on IDENTICAL contexts (v2 sampled each lineage's paths from its own base, so its positions were never cross-comparable): data-seed1 x data-seed2 shared init (step-0 tensor hashes VERIFIED identical, f0236470..., provenance audit 2026-07-13), different data order weight-seed1 x weight-seed3 different init, shared data order (PolyPythia's documented design; ASSUMED here, not independently verified -- the step-0 audit only hashed ws1) cross-family pairs both differ (floor) Readouts per base pair, on two independent context sources (standard- and weight-seed3-sampled, so the result cannot be an artifact of contexts being in-distribution for one family): near-boundary Jaccard (bottom decile by gap), gap Spearman (threshold-free), argmax agreement. Predictions, frozen before launch: INIT dominates: ds1xds2 >> ws1xws3, and ds1xds2 well above floor. ORDER destroys: ds1xds2 ~ ws1xws3, both near floor. David's refinement predicts the intermediate: ds1xds2 > ws1xws3 > floor -- shared init leaves real residual structure that a different data order has partially destroyed. Note the prior related null: H14-v1 found ds1/ds2 and ws1/ws3 landed in the same 0.10-0.13 range, but that measured TRAIT-PERTURBED divergence sets on greedy per-lineage contexts. H16 measures the underlying BASE geometry on shared sampled contexts -- a different quantity, and the one David's account actually names. Seeds 82xxx. **Status: CLEAN NULL on the preregistered question; strong unasked-for positive.** Neither shared init nor shared data order preserves near-boundary geometry beyond what unrelated lineages already share (matched pairs land inside the cross-family range in both context sources). But gap Spearman is 0.78-0.87 for ALL ten pairs: the geometry is convergent from the data, not an accident of the seed. Corrects the attribution in H15 while preserving its substrate claim. See the H16 dated entry. - **H17 — token identity, not position, is the right primitive** (David's, 2026-07-27). Every fingerprint measurement here inherited arXiv 2509.23886's position-based divergence-token definition. A student never observes positions; it trains on emitted numbers. Compare full restricted next-token distributions over ALL positions, ungated. **Status: SUPPORTED, and quantitatively load-bearing.** Ungated, wolf x lion shift-direction cosine (0.789) EXCEEDS wolf x wolf (0.763) -- positions had understated how trait-generic the fingerprint is (88% -> 103%). See the H17 dated entry. - **H18 — does the numeric channel carry ANY detectable trait identity?** (Follows directly from H17's problem: wolf and lion are indistinguishable in shift direction, yet SL transmits wolf-vs-lion at +1.01/+0.78, H5.) Build the trait axis t = normalize(delta_wolf_A - delta_lion) -- near-pure, since those two teachers share data seed 1103 and train seed 2101 and differ only in target_animal -- and project the independent wolf_B (data 5301 / train 5401) onto it, against a null of 20 effect-matched random perturbations (seeds 83001-83020, scale 24, between H15b's two matched scales). Prediction: wolf_B's normalized projection (+0.1891) lands in the upper tail of the null (one-sided p < 0.05) and lion's (-0.2263) in the lower tail. **Falsification and why it would still matter**: if wolf_B sits inside the null, the trait-specific component is not detectable at this resolution, and the honest conclusion is that the ungated numeric channel cannot see SL's carrier -- a real negative result about the channel, not a failed experiment. Guard: dNLL-vs-projection correlation across the null is reported, so a result driven by damage level rather than direction is visible rather than assumed away. Seeds 83xxx. ### 2026-07-26 — H11/H12/H14 v2: sampled-context correction (methodology fix) - **Why**: v1 of H11/H12/H14 followed arXiv 2509.23886's divergence-token definition literally (argmax-based) and therefore built reference contexts by GREEDY decoding. Diagnostic found base greedy decoding on this restricted numeric channel is degenerate: token 337 (" 1") is base's argmax at 79.8% of all positions, locking in at position 0 in 93.8% of probes and then repeating. Qualitative diffs were consequently a wall of "1"s with divergence concentrated at position 1. This is the same out-of-distribution numeric-format failure the project has flagged since day one, and is exactly why every OTHER part of the pipeline (all student training data, every prior SL result) uses temperature-1.0 sampling and never greedy. - **Scope of v1 exposure (audited, not assumed)**: ONLY H11/H12/H14 used autoregressive argmax decoding. All student training pools use `torch.multinomial` sampling; every wolf-margin/behavior readout is a single forward pass at one fixed position (no decoding); all NLL/gradient/ weight-space work (knockout, kappa, phi_D, dual-use circuit, capstone, H3, H13) is teacher-forced or gradient-based. No prior SL claim is affected. - **Fix**: keep the argmax divergence CRITERION (faithful to the literature) but build reference contexts by temperature-1.0 sampling from the base model (documented seed), matching project convention. Two refinements added: k=2 sampled context paths per probe (cheap stability check against single-draw noise, a recurring lesson here), and base top1-top2 probability gap logged per position as a secondary diagnostic (distinguishes genuine base uncertainty from a near-certain base being barely nudged). - v1 entries above are RETAINED and annotated as methodologically superseded (project precedent: u16 retraction, H3 downgrade -- corrections in place, originals preserved). **RESULT: all three v1 conclusions survive qualitatively; two quantitative corrections and one important new finding.** - Divergence rate 3.8% (v1 greedy) -> **18.3%** (469/2560, v2 sampled), which now lands INSIDE 2509.23886's reported 8.5-20.2% range rather than below it -- independent evidence the corrected methodology measures the same object the source paper does. - **Same-base replicability (H12) SURVIVES**: Jaccard 0.613-0.655 (v1: 0.537-0.843), **6.6-7.2x** each pair's own analytic random baseline. The v1 "34-53x" figure was inflated by a tiny baseline from degenerate small sets; the qualitative claim (independent retrainings converge on substantially the same fingerprint) is unchanged and now better estimated. - **Cross-lineage (H14) SURVIVES but WEAKENS substantially**: Jaccard 0.124-0.198, but only **1.43-1.90x** each pair's own baseline (v1 implied ~6-10x). Three-tier structure holds -- same-base ~0.63 (7x) >> cross-lineage ~0.15 (1.6x) > chance -- but cross-lineage sharing is much closer to chance than v1 suggested. The v1 conclusion "fingerprint shape is lineage-specific" is if anything STRENGTHENED; the "modest but real cross-lineage component" claim is weakened to "small, ~1.5-1.9x chance." - ds1 x ds2 (shared init, 62% steering transport) = 0.165, ratio 1.72x -- still barely above chance, so the H14 tension with steering-transport stands: coarse direction shared, discrete footprint not. - **Emergence timing (H11) SURVIVES**: mean first emergence 5.99/24 (v1: 6.45), stable-after-emergence 93.6% (v1: 98.0%), same early-but-extended shape (94 tokens at update 1, long tail to update 23), monotone growth 0 -> 469 across checkpoints. - **NEW FINDING (v2-only, the gap diagnostic): divergence happens almost exclusively where the base model is nearly indifferent.** Mean base top1-top2 probability gap at divergent positions is **0.022-0.034** versus **0.240-0.379** overall -- roughly a 10x difference, consistent across all five lineages. The trait does not overpower confident predictions; it tips near-coin-flips. This is direct support for David's latent-connection hypothesis (fine-tuning strengthens/crosses threshold on connections that already exist near a decision boundary, rather than creating new ones), and it explains why fingerprint SHAPE is lineage-specific while trait DIRECTION transports: which positions sit near a boundary is a fine-grained per-lineage accident. - k=2 sampled paths agreed closely per lineage (e.g. standard 233/236), so single-draw noise is not driving these counts. Artifacts: `scripts/divergence_v2.py`, `runs/divergence_v2.md`, `runs/divergence_v2/{phaseA_cross_lineage,phaseB_same_base,phaseC_timing, summary}.json`. **REFRAMED 2026-07-27 by H19 (not retracted -- the numbers stand).** Every divergence-token overlap here, and in H11/H12/H14/H15, is a statistic of the CONTEXT-CONDITIONAL component of the teacher's numeric shift, which is ~99% of its variance and carries NO trait identity (wolf x lion cosine 0.791 >= wolf x wolf 0.762, H17). The trait rides on the ~1% marginal token-frequency component (sign agreement 0.947 same-trait vs 0.751 cross-trait, H19). So same-base Jaccard 0.613-0.655 vs cross-lineage 0.124-0.198 is a real measure of shared context geometry, but it is NOT a measure of the SL carrier and should not be cited as one. ### 2026-07-26 — H16 result: near-boundary geometry is set by NEITHER init NOR data order — it is convergent across all lineages - **Design**: 5 PolyPythia bases scored on IDENTICAL fixed contexts (the flaw v2 could not avoid: it sampled each lineage's paths from its own base, so positions were never cross-comparable). Two independent context sources (standard-sampled, weight-seed3-sampled) as a robustness check against contexts being in-distribution for one family. 2560 positions (128 probes x 2 paths x 10 positions). No teachers, no training. - **Result on the preregistered question: clean NULL.** Both matched-axis pairs land INSIDE the cross-family range, in BOTH context sources: | context source | cross-family J (n=8) | ds1xds2 (shared init) | ws1xws3 (shared order) | | --- | --- | ---: | ---: | | standard | 0.166 [0.133, 0.193] | 0.169 | 0.180 | | weight-seed3 | 0.226 [0.208, 0.249] | 0.225 | 0.222 | Uniform baseline 0.053. Sharing a **verified-identical initialization** (ds1/ds2, step-0 hash f0236470...) buys no more shared near-boundary geometry than being unrelated lineages. Sharing data order buys no more either. All three preregistered predictions fail: init does not dominate, order does not destroy differentially, and David's intermediate (ds1xds2 > ws1xws3 > floor) does not hold. This is a well-powered null, not an underpowered one -- the cross-family band is narrow and the matched pairs sit dead center in it. - **Strong positive on a question that was not asked**: there is a great deal of shared structure, it is just shared by EVERYONE. Gap Spearman is **0.777-0.834** (standard contexts) and **0.813-0.871** (ws3 contexts) for every one of the 10 pairs, including maximally-unrelated ones. Restricted argmax agreement is 0.58-0.63 / 0.67-0.73. Near-boundary Jaccard is 3.1-4.3x the uniform baseline for all pairs. - **Interpretation.** Which numeric continuations are near-coin-flips is not an init accident and not a data-order accident. It is convergent: same corpus, same architecture, same tokenizer -> the same map of where "what number comes next" is genuinely ambiguous. This **revises the attribution** in David's account (which named initialization as the source of the couplings) while preserving its core: the substrate the trait tips into is real, pre-existing, and not built by trait training -- it is just built by the data rather than by the seed. - **The tension this creates, stated rather than smoothed.** If near-boundary geometry is ~0.85 rank-correlated across ALL lineages, why does the fingerprint itself (v2 Phase A) overlap only 0.124-0.198 across lineages while same-base retrainings overlap 0.613-0.655? Shared marginality is necessary but not sufficient. Two models can agree on WHICH positions are coin flips while the coin lands differently under perturbation. That suggests a three-level decomposition to test rather than assert: (1) which positions are marginal -- convergent from data (this entry) (2) which way a marginal position tips -- lineage-bound (v2 Phase A/B) (3) what it tips TO -- open; H15 measures it directly If this holds it would explain the same-base gate cleanly: the substrate of tippable positions is universal, but the tipping map is init-bound, so a student can only read the teacher's numeric shift if it shares that map. - **Caveats.** (a) ws1/ws3 sharing data order is PolyPythia's documented design, assumed here, not independently verified -- the 2026-07-13 step-0 audit hashed ws1 but not ws3. (b) Absolute Jaccard levels differ notably between context sources (0.17 vs 0.23) and mean gaps differ too, so the decile threshold is context-sensitive; the ORDERING (the actual claim) is identical in both, which is exactly what the two-source design was for. (c) Spearman is the more reliable readout here -- bottom-decile membership is a noisy tail statistic, and the 0.8+ rank correlation against 0.13-0.25 Jaccard is the expected signature of that, not a contradiction. Artifacts: `scripts/nearboundary_init_order_v1.py`, `runs/nearboundary_init_order_v1.md`, `runs/nearboundary_init_order_v1/summary.json`. ### 2026-07-26 — H15 result: the fingerprint is ~88-92% trait-GENERIC; wolf and lion leave nearly the same footprint - **Noise floor first** (added mid-run, and it earned its place). The lion teacher's weights had been reclaimed in an earlier disk pass (result recorded under H5 -- retention gate honored), so lion had to be retrained, which would have confounded "different trait" with "retrain nondeterminism." Added `wolf_A_retrain` at wolf_A's exact seeds (1103/2101). Result: 470 vs 469 divergent, shape Jaccard **0.994**, token agreement **0.996**. Retraining is effectively deterministic here, so every cross-arm gap below is real. Bonus: lion's recorded recipe turned out to be byte-identical to wolf_A's except `target_animal` -- same data seed 1103, same train seed 2101. The cleanest possible different-trait control: the only difference is one word. - **Headline.** Opposite traits leave nearly the same fingerprint: | contrast | SHAPE (position Jaccard) | CONTENT (token agreement) | | --- | ---: | ---: | | wolf_A x wolf_A_retrain (noise floor) | 0.994 | 0.996 | | wolf_A x wolf_B (same trait, indep retrain) | 0.632 | 0.772 | | wolf_A x lion (OPPOSITE trait) | 0.557 | 0.710 | | uniform / marginal baseline | 0.013 | ~0.07 | Different-trait retains **88.1%** of the same-trait shape overlap and **92.0%** of the content agreement. Only ~12% of shape and ~8% of content is trait-specific. **The fingerprint is overwhelmingly a property of the base, not of the trait** -- which is David's account, and the SHAPE/CONTENT split this entry introduced does not rescue trait-specificity: it is weak on both axes, slightly weaker on content than on shape. - **Containment, the right statistic when set sizes differ 10x** (chance = 469/2560 = 0.183). Fraction of each arm's divergent positions that are ALSO wolf_A divergent positions: lion 0.768 (4.19x), wolf_B 0.813 (4.44x), wolf_rank1 0.690 (3.77x), and every random arm 0.528-0.793 (**2.88-4.33x**). Random perturbations tip a strict, strongly enriched SUBSET of the very same positions the trait tips -- at essentially the same enrichment as the opposite-trait teacher. This is the core of David's hypothesis, confirmed. - **Preregistered predictions, scored honestly.** - P1 (random arms comparable SIZE): **FAILS as stated.** Random arms give 24-62 divergent vs 409-470 for trained teachers. - P2 (J(rand,rand) ~ J(wolf_A,wolf_B)): **FAILS as stated.** Independent random pairs 0.110-0.189 vs 0.632. - P3 (token agreement higher same-trait than different-trait): directionally holds but the margin is small (0.772 vs 0.710) -- content is not where a large trait-specific signal lives either. - **But P1/P2 as stated tested the wrong thing, and this is the entry's main methodological caveat.** The random arms were matched to the trait delta by weight NORM, and at matched norm they are functionally almost inert: numeric NLL delta **-0.001 to +0.010** and wolf-margin delta **+/-0.01**, against **+0.361** and **+16.97** for wolf_A. A trained delta is ~36x more functionally efficient per unit norm than a random direction -- expected, since a random vector in 768-d is near-orthogonal to everything that matters. So "random gives 62 divergent, wolf gives 469" is mostly a statement about norm-efficiency, NOT about whether the trait direction is special. The fair test is EFFECT-matched, not norm-matched: scale the random perturbation until its numeric NLL delta equals wolf's +0.361, then compare. Registered and run as H15b; matching dNLL matches functional damage by construction, so a large random perturbation cannot win by wrecking the model. **Until H15b lands, P1/P2 should be read as unresolved, not as refuting David's account** -- the containment result above already points the other way. - **How SL still works if the fingerprint is 88-92% generic.** It does not need to be mostly trait-specific. A student fits 8192 sampled numeric rows; a small but reliably-signed bias in which near-boundary token is preferred integrates into a consistent gradient signal over that many samples. The ~12% residue is sufficient, and its reliable sign is exactly what the H5 wolf/lion double dissociation (+1.01 / +0.78) measures behaviorally. - Secondary: wolf_rank1 (H13's rank-1 8-module patch) gives 210 divergent at dNLL +0.020 and d-wolf +2.26 -- a genuine partial fingerprint from a drastically compressed patch, containment 0.690 (3.77x). Consistent with the dual-use circuit result. Artifacts: `scripts/trait_specificity_control_v1.py`, `runs/trait_specificity_control_v1.md`, `runs/trait_specificity_control_v1/{summary,arms}.json`. ### 2026-07-27 — H15b result: at MATCHED damage, random perturbations are nothing like trait deltas — P2 fails for real - **Why this run existed**: H15 matched random perturbations to the trait delta by weight NORM, and at matched norm they were functionally inert (dNLL -0.001..+0.010 vs wolf's +0.361). That comparison measured norm-efficiency, not trait-specificity, so H15 left P1/P2 explicitly unresolved. Here random full-parameter Gaussians are scaled until their numeric NLL delta MATCHES wolf_A's +0.3610 -- functional damage equalized by construction, so a large random perturbation cannot win by wrecking the model. - **Result** (interpolated to dNLL = +0.3610 from the bracketing sweep points; seed 81001 bracketed by scales 16/32, seed 81002 by 32/48): | arm (all at dNLL ~ +0.361) | divergent | J(wolf_A) | containment in wolf_A | token agreement | | --- | ---: | ---: | ---: | ---: | | wolf_B (same trait, indep retrain) | 427 | 0.632 | 0.813 | 0.772 | | lion (OPPOSITE trait) | 409 | 0.557 | 0.768 | 0.710 | | rand matched, seed 81001 | ~677 | 0.311 | 0.418 | 0.353 | | rand matched, seed 81002 | ~992 | 0.333 | 0.368 | 0.234 | | chance | -- | 0.013 | 0.183 | ~0.07 | - **P2 fails, and now for a real reason.** At equal functional damage a random perturbation produces MORE divergent positions than the trait does (677-992 vs 469) -- it is less targeted, not more -- while agreeing with wolf on the replacement token only 0.23-0.35 of the time against the opposite-trait teacher's 0.710. **Trained trait deltas resemble each other far more than any of them resembles an equally-damaging random direction, even across opposite traits.** Gradient descent finds directions random vectors do not. - **Revised three-way decomposition of the fingerprint** (supersedes both the "it's trait-specific" reading of H12/H14 and the fully deflationary reading H15 seemed to license): 1. **Base geometry** -- the near-boundary map, convergent across all lineages (H16, gap Spearman 0.78-0.87). Random perturbations do tip an enriched subset of it (containment 2.9-4.3x chance at norm-matched scale), so this layer is genuinely generic. 2. **A shared trait-TRAINING component** -- common to wolf and lion, absent from effect-matched random. This is the bulk of the fingerprint and is the layer H15's 88%/92% numbers were actually measuring. 3. **A small trait-SPECIFIC residue** -- ~12% of shape, ~8% of content. The only layer that distinguishes wolf from lion, and therefore the only layer that can carry SL. - **Status of David's account**: core structural claim SUPPORTED (a real, pre-existing substrate that trait training tips into rather than builds), with two corrections -- the substrate is data-convergent, not init-random (H16); and the perturbation is not generic, since trained directions are privileged over random ones at matched damage (this entry). - Caveat: interpolation between bracketing scales assumes local linearity in dNLL; seed 81002's scale-32 point (dNLL +0.3413) is close enough to the target to read almost directly, and it gives the same conclusion. Artifacts: `scripts/trait_specificity_effectmatched_v1.py`, `runs/trait_specificity_effectmatched_v1.md`, `runs/trait_specificity_control_v1/effectmatched_sweep.json`. ### 2026-07-27 — H17 registered: the UNGATED token-identity channel (David's correction) - **David's objection, which is correct and load-bearing**: "why are we measuring positions? token identity is what is actually important." Every fingerprint measurement in this project (H11/H12/H14/H15/H15b) keyed on POSITIONS where a model's argmax differs from its base's -- a definition inherited from arXiv 2509.23886 without scrutiny. But **a student never observes positions.** It trains on the teacher's emitted numbers. Token identity is the causal channel for SL; position overlap only describes where a teacher happens to be perturbable, which is a fact about the teacher. - Even H15's CONTENT readout was position-gated (agreement conditional on the position being divergent in BOTH arms), so it was a better measure, not the right one. H17 removes the gate entirely: over ALL 2560 positions, compare the full 1000-way restricted next-token distributions -- argmax agreement, mean JSD, mean TVD. No divergence criterion anywhere. - Arms: base, wolf_A, wolf_A_retrain (noise floor), wolf_B, lion, and two EFFECT-MATCHED random perturbations (81001 x20, 81002 x32, per H15b). - Prediction: if the fingerprint is generic to perturbation, an effect-matched random arm should sit as close to wolf_A in distribution space as lion does. H15/H15b's position-based and gated-token measures both said no; H17 asks the same question with no position machinery at all. Agreement across the two framings would mean the position-based literature definition, though the wrong primitive, was not actively misleading here. ### 2026-07-27 — H17 result: in the ungated token channel, wolf and lion move the numeric distribution in the SAME direction - **The measurement David's objection forced**: no positions, no divergence criterion, no threshold. Just the full 655-way restricted next-token distribution (single-token integers 0-999 resolve to 655 actual tokens) at all 2560 frozen positions, compared arm-to-arm. This is the object a student actually fits. - **Noise floor**: wolf_A vs wolf_A_retrain (identical seeds) gives argmax agreement **1.000**, mean JSD **0.00000**, shift-direction cosine **+1.0000**. Within-process reproducibility is exact, so every number below is signal. - **Headline -- cosine similarity of the distribution-shift vectors** (p_arm - p_base, exact, over 2560 x 655): | pair | cosine | | --- | ---: | | wolf_A x wolf_A_retrain (noise floor) | +1.0000 | | **wolf_A x lion (OPPOSITE trait)** | **+0.7889** | | wolf_A x wolf_B (same trait, indep draw) | +0.7631 | | wolf_B x lion | +0.6910 | | wolf_A x random, effect-matched | +0.0759, +0.0144 | | random x random | +0.3117 | **Wolf and lion move the numeric distribution in MORE similar directions than two independent wolf teachers do.** Trait identity contributes nothing detectable to the direction of the shift. In the position framing wolf-lion was 88% of wolf-wolf; ungated it is **103%**. David's objection was not just methodologically correct, it was quantitatively load-bearing -- positions UNDERSTATED how generic the fingerprint is. - **Magnitude**: trait shifts are small and surgical (L2 4.31-4.63; JSD from base 0.0116-0.0135), effect-matched random shifts are large and diffuse (L2 7.57 and 11.84; JSD 0.0334 and 0.0694) and near-orthogonal to the trait axis. At equal NLL cost a random direction moves the numeric distribution 1.6-2.6x FARTHER, perpendicular. Random arms also resemble each other (0.3117) far more than they resemble the trait -- a separate generic "damage" direction exists. - **What this does to the account**: the numeric channel's dominant signal is a trait-TRAINING direction, not a trait direction. Fine-tuning on any animal preference moves the numeric distribution the same way; only trained directions reach it (H15b); the substrate it lands on is data-convergent (H16). - **The problem this creates, and it is the central one.** If wolf and lion are indistinguishable in shift direction, the numeric channel carries almost no trait identity -- yet SL demonstrably transmits wolf-vs-lion (H5, +1.01/+0.78). First probe: build the trait axis t = normalize(delta_wolf_A - delta_lion) (unusually clean -- wolf_A and lion share data seed 1103 AND train seed 2101, differing ONLY in target_animal, so seed idiosyncrasy cancels), then project the INDEPENDENT wolf_B onto it. Result: wolf_B **+0.189** of its own shift (correct side), lion -0.226 (correct side), but the two random controls gave +0.102 and -0.042 -- one of them nearly as large in absolute projection (+0.78) as wolf_B (+0.85). **With n=2 controls this does not separate.** Registered as H18 with a proper 20-draw null; reporting the p-value there rather than eyeballing it here. Artifacts: `scripts/token_channel_v1.py`, `runs/token_channel_v1.md`, `runs/token_channel_v1/{summary.json,meta.json,*.npy}`. - Housekeeping: wolf_A's wolf margin reads +16.29 here vs +16.97 in H15 on identical weights, while dNLL reproduces to 4 decimals. Within-process the two wolf arms agree to 3 decimals (+16.2914 / +16.2926), so this is BETWEEN-process MPS float nondeterminism in a large-magnitude logsumexp. All comparisons drawn anywhere in H15/H15b/H17 are within-process and therefore unaffected; recorded so a future reader does not mistake it for a discrepancy. ### 2026-07-27 — H19 result (EXPLORATORY): the SL carrier is the MARGINAL token frequency, not the context-conditional fingerprint - **Provenance, stated up front**: this is a post-hoc analysis of H17's cached distributions, prompted by David challenging the H17 cosine result -- "sounds like you're measuring something incorrectly... we should be looking at precise token identities which shift wrt numerical context history. please be sure to check the exact frequency of each numerical token." It was NOT preregistered. The internal contrast below is well-powered, but the hypothesis was found by looking. Confirmatory design at the end of this entry. - **The challenge was right; the confound he named was not the one present.** Decomposing each arm's shift into a context-independent marginal component and a context-conditional residual: | arm | global (marginal) | context-conditional | | --- | ---: | ---: | | wolf_A | 0.8% | 99.2% | | wolf_B | 0.9% | 99.1% | | lion | 1.1% | 98.9% | | rand matched | 5.2-9.2% | 90.8-94.8% | So H17's cosine was NOT inflated by a global frequency shift -- restricting to the context-conditional residual reproduces it (wolf x lion 0.7906, wolf x wolf 0.7617). The H17 measurement stands. - **But the two components carry opposite information**: | pair | GLOBAL component | CONTEXT component | | --- | ---: | ---: | | wolf_A x wolf_B (same trait) | **+0.9262** | +0.7617 | | wolf_A x lion (opposite trait) | **+0.6191** | +0.7906 | **The marginal frequencies discriminate trait; the context-conditional structure does not.** The ~1% component everyone would discard is the only part that knows which animal it is. - **Sign agreement on per-token frequency shifts** (586 tokens wolf actually moves; binomial sd +/-0.021, so these gaps are ~9 sigma apart): | pair | sign agreement | | --- | ---: | | wolf_A x wolf_B (fresh data draw 5301 + fresh train seed 5401) | **0.947** | | wolf_A x lion | 0.751 | | wolf_B x lion | 0.754 | | wolf_A x effect-matched random | **0.514** (chance) | Two independent wolf teachers agree on the direction of 94.7% of token frequency shifts; wolf vs lion only 75%; random is at chance. Individual tokens flip sign between traits WITH both wolf teachers agreeing -- token "3" (wolf -0.00135/-0.00278, lion +0.00025) and token "11" (wolf +0.00072/+0.00078, lion -0.00056). Token "8" moves identically for everything (+0.0030/+0.0034/+0.0034) -- the generic 99%. - **Why this resolves the central puzzle of H15/H15b/H17.** Those entries kept finding the fingerprint trait-generic (88%, 92%, 103%) while H5 shows SL transmits wolf-vs-lion at +1.01/+0.78. The resolution: they were all measuring the context-conditional 99%, which genuinely carries no trait identity. The trait rides on the flat marginal component, which is exactly the statistic that survives sampling. A student sees ~8192 x 7 = ~57,000 numeric tokens; a +0.0042 shift on token "2" is ~240 extra occurrences against counting noise of ~40, a **~6 sigma** signal. Trivially learnable. - **Consequence for the whole program**: SL does not transmit through the elaborate context-dependent divergence-token fingerprint at all. It transmits through a small, flat, reliably-signed bias in how often each number is emitted. The same-base gate is then a claim about the TRAIT -> WHICH-TOKENS mapping needing to match, not about shared context geometry -- which is consistent with H16 (context geometry is shared by ALL lineages and therefore cannot be what gates SL). - **Retro-fits the earlier record**: this is the same axis as the old fingerprint-advantage / JSD mean-shift readouts (which were distributional, not argmax-based) and explains why those tracked SL strength while the divergence-token counts did not (H14's magnitude null). - **Confirmatory design (preregister before running)**: train fresh wolf and lion teachers at new seeds, plus a second lion. Predict, before looking: same-trait sign agreement ~0.93-0.96, cross-trait ~0.72-0.78, random ~0.50, with same-trait exceeding cross-trait by >0.10 in every pairing. Also predict the per-token shift vector predicts student wolf-margin delta better than any context-conditional statistic does. Until that runs, H19 is SUGGESTIVE ONLY. **UPDATE 2026-07-27: the sign-agreement half RAN and CONFIRMED** on 4 fresh teachers -- same-trait 0.937 [0.918, 0.949] vs cross-trait 0.750 [0.715, 0.776], perfect separation, P4 margin +0.142. See the H19-CONFIRM entry. H19 is no longer suggestive-only. The student-prediction half remains unrun and is listed there as open item (a). Artifacts: analysis over `runs/token_channel_v1/*.npy`; see this entry's tables. Script the confirmatory run before citing this anywhere. ### 2026-07-27 — H18 result: the numeric channel DOES carry recoverable trait identity (wolf_B z=+4.17 vs a 20-draw random null) - **Design**: trait axis t = normalize(delta_wolf_A - delta_lion), an unusually clean contrast since wolf_A and lion share data seed 1103 AND train seed 2101 and differ only in `target_animal`. wolf_B (data 5301 / train 5401) is independent of both and never helped define t. Null: 20 independent random perturbations at scale 24, projected onto the same frozen axis. - **Result** (preregistered prediction: wolf_B in the upper tail, p < 0.05): | arm | normalized projection | one-sided p | | --- | ---: | ---: | | wolf_A (defines axis) | +0.4200 | -- | | lion (defines axis) | -0.2263 | 0/20 | | **wolf_B (HELD OUT)** | **+0.1891** | **0/20** | Null: mean -0.0017, sd 0.0457, range [-0.1285, +0.1074]. wolf_B **z = +4.17**, lion z = -4.91. Both outside the entire null range. **PREDICTION CONFIRMED.** - **Guard passed**: correlation between dNLL and projection across the null is **+0.048** -- the statistic is not being driven by how much each perturbation damaged the model, which was the obvious way this could have been an artifact. - **Stated limits, not smoothed**: (a) with n=20 the empirical p-value floors at 0.05 regardless of how extreme wolf_B is, so the z-score carries the weight and assumes an approximately Gaussian null; (b) one null draw reached +0.1074, within a factor of ~1.8 of wolf_B, so the separation is real but not enormous on this axis; (c) this axis is ~99% context-conditional (H19) and therefore mostly generic -- it separates wolf_B from random despite that, not because of it. The marginal-frequency statistic (H19: sign agreement 0.947 vs 0.751 vs 0.514, error bar from 586 tokens rather than 20 draws) is the more robust measurement of the same underlying fact and should be preferred when citing. Artifacts: `scripts/trait_axis_null_v1.py`, `runs/trait_axis_null_v1.md`, `runs/trait_axis_null_v1/{summary,null}.json`. ### 2026-07-27 — H19-CONFIRM: PREREGISTERED AND CONFIRMED. The SL carrier is the marginal token-frequency shift. - **Design**: 4 fresh teachers at new seeds (wolf_C 84001/84101, wolf_D 84002/84102, lion_B 84003/84103, lion_C 84004/84104), canonical recipe, combined with the existing wolf_A, wolf_B, lion. 7 independently trained teachers -> 9 same-trait and 12 cross-trait pairings. Statistic: per-token sign agreement of the marginal frequency shift (mean probability of each of the 655 single-token integers across all 2560 frozen numeric positions, minus base). - **Result: PERFECT SEPARATION.** | group | n | mean | range | | --- | ---: | ---: | --- | | same-trait | 9 | **0.937** | [0.918, 0.949] | | cross-trait | 12 | **0.750** | [0.715, 0.776] | | effect-matched random | -- | 0.514 | (chance) | Every same-trait pair scores above every cross-trait pair. **P4 (strong form): min(same) - max(cross) = +0.142 -> PASS.** - **Scoring the preregistered predictions honestly**: - P1 (same-trait ~0.93-0.96): essentially confirmed; observed mean 0.937, but the lowest pair (wolf_A x wolf_D, 0.918) fell just below the predicted 0.93 floor. Recorded rather than rounded away. - P2 (cross-trait ~0.72-0.78): confirmed exactly, 0.715-0.776. - P3 (random ~0.50): confirmed, 0.514. - P4 (strong separation > 0.10): confirmed, +0.142. - **H19 is therefore no longer exploratory.** The finding was discovered post-hoc at David's prompting, then predicted in advance and confirmed on fresh teachers it had never seen. Both facts are on the record. - **The settled account of SL in this system**, across H15/H15b/H16/H17/H18/H19: 1. Trait training perturbs a numeric-prediction substrate that is **data-convergent** -- shared by every Pythia-160M variant regardless of init or data order (H16, gap Spearman 0.78-0.87). Not built by trait training, and not an init accident. 2. ~99% of the resulting distributional shift is **context-conditional and trait-generic**: wolf and lion move it in indistinguishable directions (cosine 0.791 vs 0.762 same-trait, H17). This is what every divergence-token measurement in this project (H11/H12/H14/H15) was capturing. 3. Only **trained** directions reach this substrate. Effect-matched random perturbations are near-orthogonal (cosine 0.01-0.13) and larger/more diffuse (H15b, H17). 4. The trait rides on the remaining **~1% marginal token-frequency component**, which discriminates trait cleanly (this entry) and is recoverable from a held-out teacher at z = +4.17 against a 20-draw random null (H18). 5. **Why that suffices for SL**: a student sees ~8192 x 7 ~ 57,000 numeric tokens; a +0.0042 marginal shift on token "2" is ~240 extra occurrences against counting noise ~40, a ~6 sigma signal. Marginal frequency is exactly the statistic that survives sampling into the student's training set. 6. **Reframes the same-base gate**: it cannot be about shared context geometry, since that is shared by ALL lineages (H16). It must be about the trait -> which-tokens mapping matching between teacher and student. - **Open**: (a) does the per-token marginal shift vector predict student wolf-margin delta better than any context-conditional statistic? (the second half of H19's confirmatory design, not yet run); (b) does the marginal component transport across lineages, and does its transport predict the measured SL gate? That is the direct test of point 6 and the obvious next experiment. Artifacts: `scripts/marginal_carrier_confirm_v1.py`, `runs/marginal_carrier_confirm_v1.md`, `runs/marginal_carrier_confirm_v1/{summary,fresh}.json`. ### 2026-07-27 — H20 registered: delta transplant — is the trait->output coupling init-bound? (David's link-4 test) - **David's account, stated as four links** (2026-07-27, his words compressed): (1) SL traits are encoded in small circuits; (2) perturbations to these ALONE shift downstream token outputs; (3) the trait is the general solution to that output shift, so training on it re-induces the trait and credit reliably routes to the trait circuit; (4) **the MEDIUM coupling trait circuit to numeric outputs is initialized random weights that survive pretraining**, with data order able to weaken them (his (i,o*) reading). Links 1-3 are already evidenced (dual-use rank-1 subspace; H13 mediation + H15 wolf_rank1; knockout loss-equivalence + credit factorization). Link 4 is untested. - **Why H16 does NOT settle this (and is not flawed)**: H16 measured the BASE's near-boundary geometry -- where the coin-flip positions are. That is the substrate, and it is data-convergent. Link 4 is about the PERTURBATION-RESPONSE MAP -- which coins flip, and which way, when the trait circuit specifically is pushed. A universal substrate is fully compatible with an init-private response map. David suspected H16 was miscontducted; the resolution is instead that it measured a different object. - **Why v2 Phase A does not settle it either**: its cross-lineage fingerprints look anti-init (ds1 x ds2 = 0.165, inside the cross-family band), but every lineage there had its OWN teacher trained on its own base -- trait-circuit identity and coupling identity were confounded. The test requires holding the trait delta FIXED while varying only the receiving base. - **Design (forward passes only, no training)**: all five lineage teachers on disk are recipe-matched (384 rows, data seed 1103, train seed 2101; only the base varies). Compute Delta_L = teacher_L - base_L per lineage. Apply every Delta to every base (5x5; parameter shapes identical across variants; delta added on CPU before device transfer). On the frozen shared contexts (probes seed 99001, paths sampled from the standard base at seed 99501, identical to H17/H19), measure each arm's MARGINAL token-frequency shift m(recv, Delta) = mean_p[p_patched - p_recv_unpatched] -- the carrier, per H19 -- and score per-token sign agreement (and cosine) against the delta's HOME shift m(home, Delta), over tokens the home shift moves (>1e-5). Also per arm: full-vocab forced-token NLL delta (damage gate) and held-out wolf/lion margins (weight-space behavioral transport, steering-probe analog). - **Cells** (provenance-audited): home diagonal n=5 (defines each reference); shared-init/diff-order n=2 (Delta_ds1<->ds2; step-0 hashes verified identical f0236470...); shared-order/diff-init n=6 (standard/ws1/ws3 pairwise; weight-seeds carry the reference order, hashes differ); neither n=12. - **Frozen predictions (David's account, empirical form)**: - P1 shared-init cell mean sign agreement EXCEEDS shared-order cell mean by >= 0.10, and exceeds the neither-cell mean. His order-damage refinement predicts shared-init lands intermediate-to-high (not full home-level). - P2 shared-order cell mean <= 0.65 (chance 0.514 per H19's random arms). **FALSIFIER: if shared-order >= shared-init, init is not the medium -- data order is, and the account's link 4 is rejected as stated.** - P3 behavioral transport (wolf-margin delta under transplanted Delta) mirrors the SL gate ordering: shared-init cells positive, diff-init cells ~0 -- with weight-seed1 PRE-FLAGGED as a possible hot anomaly (it accepted 49% raw steering transport on 2026-07-13 despite foreign init), which is why P1/P2 are stated about cell MEANS. - P4 damage gate: any arm whose forced-token NLL delta exceeds ~3x the home arm's is marked damaged and excluded from cell means (recorded, not hidden). - Caveat accepted in advance: single context source (standard-sampled). H16's two-source check showed orderings survive context-source choice; if H20 is ambiguous, rerun with ws3-sampled contexts before concluding. - No new seeds (reuses 99001/99501). Script: `scripts/delta_transplant_v1.py`. ### 2026-07-27 — H20 SCOPE CORRECTION (David's veto) + H21 registered: response-subspace comparison - **David's veto, and it is correct**: "just because the weights are indeed literally different does not mean that the initialization has no coherent effect on the trained models. if you draw a smiley face in a model's parameters and train it to low loss you retain the smiley face." - **The flaw in H20, named precisely**: transplanting a raw weight delta conflates TWO things -- whether the trait->output coupling is shared, and whether the two models sit in the same COORDINATE FRAME. Init-derived structure can persist through pretraining while the coordinates expressing it drift (neuron permutation symmetry, within-layer rotation, scaling). A Delta computed in ds1's basis can be functionally inert in ds2's basis even if both retain identical coupling structure. H20's floor is therefore consistent with David's account AND with its negation -- uninformative for link 4. Fable's initial reading ("shared init confers nothing") is WITHDRAWN as unsupported. - **Corroborating hint that was under-weighted**: the 2026-07-13 transport probe found Procrustes alignment HURT ds2->ds1 steering transport, read then as "trait coordinates natively shared across the family." That is activation space rather than weight space, but it suggests within-family coordinate frames are closer than the transplant floor implies. - **What H20 still yields (kept, not discarded)**: (a) its DIAGONAL gives each lineage's own marginal token-frequency shift on shared contexts -- a coordinate-free cross-lineage comparison, since token space is common to all models; (b) the methodological fact that raw weight deltas do not transplant across independent pretraining runs (~8-12% of home behavioral effect for every off-diagonal cell regardless of shared axis), worth recording so the design is not repeated. H20's P1/P2 verdict is to be read as VOID for link 4. - **H21 — response-subspace comparison** (the rigorous replacement). Measures the medium directly, in token space, with NO trait training and therefore no confound from separately-trained circuits. Design: for each of the 5 bases, apply K=24 random rank-1 perturbations to the frozen late group (L8-11 x {QKV, MLP-out}), each per-module Frobenius-norm matched to THAT lineage's own trait delta (so magnitude is calibrated to the model's own trait scale). Record the induced marginal token-frequency shift (655-dim, token space -- permutation-invariant by construction). Stack into a 24x655 response matrix; take the top-6 principal subspace via SVD. That subspace answers: which directions in token space can perturbations of this module group reach at all? That is precisely the "medium" in David's link 4. Compare subspaces pairwise by mean squared cosine of principal angles (subspace affinity, ||U_A^T U_B||_F^2 / r). **Frozen predictions**: - P1 within-base split-half affinity defines the noise ceiling. - P2 ds1<->ds2 (shared init, verified identical step-0 hashes) affinity is HIGH, near ceiling, and exceeds the shared-order cells by >= 0.10. - P3 standard/ws1/ws3 pairwise (shared reference data order, different init) affinity is LOW, near the cross-family floor. - **FALSIFIER: if shared-order >= shared-init, or if all cross-lineage affinities are at floor, initialization is not the medium as stated.** - Guard: a random-subspace baseline (24 Haar 655-dim vectors, top-6) gives the analytic floor for r=6 in 655 dimensions. Caveat accepted in advance: contexts are standard-sampled and mildly OOD for other lineages; H16's two-source check showed orderings survive context-source choice, but if H21 is ambiguous, rerun with ws3-sampled contexts. Seeds 85xxx. Script: `scripts/response_subspace_v1.py`. ### 2026-07-27 — H20 result: raw weight deltas do not transplant across pretraining runs (VOID for link 4) - Completed 30 arms (5 unpatched references + full 5x5 transplant matrix), forward passes only, zero arms tripped the damage gate. - **Sanity**: every home cell reconstructs its teacher exactly -- e.g. standard__standard gives wolf +16.29 / dNLL +0.361, matching H17 to four decimals. The frozen-context machinery is bit-consistent across scripts. - **Result** (sign agreement of the transplanted marginal token-frequency shift against the delta's home shift; chance 0.514, cross-trait 0.750, home 1.000): | cell | n | mean | range | mean dWolf | | --- | ---: | ---: | --- | ---: | | shared-init / diff-order | 2 | 0.609 | [0.604, 0.615] | +1.61 | | shared-order / diff-init | 6 | 0.633 | [0.548, 0.659] | +1.54 | | neither | 12 | 0.639 | [0.567, 0.699] | +1.48 | Home behavioral effect is +13.4 to +17.0; every off-diagonal cell recovers only ~8-12% of it, with no dependence on which axis is shared. - **Verdict: VOID for link 4**, per the scope correction recorded above. The design cannot separate "coupling not shared" from "coordinate frames differ", and David's veto is correct that init structure can persist while coordinates drift. P1 False / P2 True / falsifier True are therefore NOT evidence about initialization; they are evidence about coordinate transfer. - **What it does establish (worth keeping)**: (a) raw weight deltas from one pretraining run are functionally inert in another, regardless of shared init or shared data order -- do not build future designs on delta transplant without an alignment step; (b) the uniform ~0.63 floor across ALL off-diagonal cells sits meaningfully above chance (0.514) and is coherent with H16's data-convergent substrate: any perturbation nudges the universally-marginal tokens similarly, and that shared component is all that survives raw transfer. - Notable: weight-seed1, which accepted 49% raw STEERING transport in activation space (2026-07-13), shows nothing distinctive here -- a real dissociation between activation-space and weight-space transport that should be stated rather than blended in future writeups. Artifacts: `scripts/delta_transplant_v1.py`, `runs/delta_transplant_v1.md`, `runs/delta_transplant_v1/summary.json`. ### 2026-07-27 — H21 result: the perturbation->token medium is UNIVERSAL, not init-bound (coordinate-free) - Coordinate-free by construction (token space), no trait training involved, so neither the smiley-face objection nor separately-trained trait circuits apply. K=24 random rank-1 perturbations per base on the frozen late group, per-module norm-matched to that lineage's own trait delta; induced marginal token-frequency shift; top-6 principal subspace; affinity = mean squared cosine of principal angles. - **Measurement has real resolution**: within-base split-half affinity 0.384-0.518 (mean ~0.451) against a random floor of **0.009** -- ~50x. The reachable-token subspace is a stable, reproducible property of a model. - **Result**: | cell | n | mean affinity | range | | --- | ---: | ---: | --- | | shared-init / diff-order | 1 | 0.482 | -- | | shared-order / diff-init | 3 | 0.504 | [0.465, 0.528] | | neither | 6 | 0.531 | [0.429, 0.582] | Every cross-lineage affinity (0.429-0.582) lies AT OR ABOVE the within-model split-half band (0.384-0.518). Sample-size-matched (12-vs-12 everywhere) the cross/within ratio is **0.88**. - **Verdict: FALSIFIER triggered as stated** -- shared-order >= shared-init, and the "all at floor" alternative is rejected. But the informative reading is neither of the preregistered branches: **all cells sit at the CEILING**. Two models from independent pretraining runs agree about which token directions are reachable roughly as well as a model agrees with itself. The medium is convergent, exactly like H16's near-boundary substrate. - **Logical force for link 4**: the trait delta is itself a perturbation of this same module group, so its token-space image must also lie largely inside this universal reachable subspace. That constrains the trait's output effect to a shared subspace regardless of initialization. - **What H21 does NOT settle, and the one result that goes David's way**: H21 uses RANDOM directions. Where the TRAIT direction lands *within* the universal subspace could still be init-dependent. Evidence for exactly that, computed coordinate-free from H20's diagonal (each lineage's own teacher on its own base, compared in token space): | cell | n | sign agreement | cosine | | --- | ---: | ---: | ---: | | shared-init (ds1 x ds2) | 1 | 0.611 | **+0.701 (highest of all 10 pairs)** | | shared-order | 3 | 0.657 | +0.248 to +0.589 | | neither | 6 | 0.616 | +0.309 to +0.631 | Sign agreement shows no init effect; cosine puts the shared-init pair first. These weight tokens differently -- cosine is dominated by large movers, sign agreement counts every moved token equally -- so the dissociation is interpretable: **shared init may align the PRINCIPAL AXIS of the trait's token effect without aligning its fine structure.** n=1, so this is a lead, not a result. It also suggests sign agreement (correct for H19's same-base work) is the wrong instrument for cross-lineage comparison. Artifacts: `scripts/response_subspace_v1.py`, `runs/response_subspace_v1.md`, `runs/response_subspace_v1/summary.json`. ### 2026-07-27 — H22 registered: is the numeric shift a DIRECT unembedding readout of the trait direction? (David's dissolution) - **David's reframing** (2026-07-27, verbatim): "maybe the correlation is literally just that the same circuit that encodes the trait just increases the probability of a certain number token at decoding layer?" This dissolves the medium question rather than answering it: if the trait circuit IS what biases number tokens at decode, there is no propagation pathway to be init-bound -- the trait/number correlation is IDENTITY, not transmission. The dual-use rank-1 result (one reversible subspace moving wolf margin and numeric fingerprint together, both directions) is already evidence for exactly this. It also explains H21 for free: a direct write inherits the UNEMBEDDING's geometry, which is learned from the Pile and convergent across lineages. - **Reconciliation recorded (both prior readings were confused)**: the transfer evidence ((i*,o) ~ 0, (i,o*) = 39%) varied the STUDENT's initialization; H20 and H21 varied the TEACHER's base. Init can gate the student side -- credit needs a homologous circuit to route into (link 3) -- while the teacher's trait->token write is fully convergent. These were never in conflict. - **Design (exactly linear, no approximation in the readout)**: GPT-NeoX `embed_out` is bias-free linear and HF's final hidden state is already post-`final_layer_norm`, so the logit map is a single matrix multiply. For each of the 5 lineages: 1. v_trait = mean over the 60 held-out ANIMAL-preference prompts of (h_teacher_last - h_base_last), post-LN residual [768]. 2. Predicted logit shift on numbers: dl = W_U @ v_trait, restricted to the 655 single-token integers. Exact. 3. Predicted probability shift via the softmax Jacobian at the base's mean NUMERIC-context distribution p_bar (taken from H20's ref__L): dp_pred = p_bar * (dl - sum_j p_bar_j dl_j). 4. Compare dp_pred against the MEASURED marginal numeric shift m_L (H20 diagonal: teacher_L on base_L minus base_L) by cosine and sign agreement. The two sides come from DISJOINT prompt distributions (animal-preference vs numeric), so agreement is not tautological. Null: 200 random Gaussian directions of matched norm through the same readout. - **Frozen predictions**: - P1 cos(dp_pred, m_L) exceeds the 95th percentile of the random-direction null in at least 4 of 5 lineages. - P2 mean cosine across lineages >= 0.30 (a direct write should dominate, not merely register). - P3 the effect is CONVERGENT: all five lineages show the same sign and comparable magnitude, consistent with a shared unembedding geometry. - **FALSIFIER: cosines at the null in a majority of lineages -> the numeric shift is NOT a direct readout of the trait direction, intermediate computation does real work, and a genuine pathway exists to characterize.** - Caveat: v_trait is the NET last-token residual displacement, so it includes whatever intermediate layers contributed; H22 tests whether the READOUT is direct, not whether the residual displacement itself is produced without intermediate computation. A negative result is therefore strong; a positive result establishes readout-directness specifically. - Forward passes only, no training, no new seeds. Script: `scripts/direct_readout_v1.py`. ### 2026-07-27 — H22 result: the trait direction writes DIRECTLY into number logits, but the direct write is a MINORITY component - **METRIC CHANGED AFTER SEEING DATA -- flagged, not buried.** The preregistered primary statistic was probability-space cosine between the predicted and measured numeric shift. On first run its null was degenerate: random residual directions scored cosine **0.35-0.71** against the measured shift, because the softmax Jacobian multiplies BOTH the prediction and the measurement by p_bar, giving every vector a shared high-probability envelope. That test had almost no power by construction (2/5 exceeded null; "falsifier" nominally triggered). The statistic was replaced with the envelope-free FISHER cosine (both sides divided by sqrt(p_bar), the natural multinomial metric), plus a pure logit-space comparison. The replacement was diagnosed from an identifiable flaw rather than selected for outcome, but it is post-hoc and the result must be treated as SUGGESTIVE until confirmed out of sample. - **Result (Fisher cosine, own-null p95 per lineage, 200 matched-norm random directions each)**: | lineage | Fisher cos | null p95 | z | logit cos | prob cos (underpowered) | wolf rank | | --- | ---: | ---: | ---: | ---: | ---: | ---: | | standard | +0.309 | +0.176 | +2.6 | +0.149 | +0.316 | 1/10 | | ds1 | +0.367 | +0.242 | +2.4 | +0.280 | +0.438 | 1/10 | | ds2 | +0.168 | +0.288 | +0.9 | +0.124 | +0.450 | 1/10 | | ws1 | +0.458 | +0.191 | +3.7 | +0.384 | +0.619 | 1/10 | | ws3 | +0.292 | +0.220 | +2.2 | +0.306 | +0.641 | 1/10 | Mean Fisher cosine **+0.319**, 4/5 above their own null p95, all five the same sign. Logit-space 3/5. P1/P2/P3 pass on the corrected statistic. - **Strong sanity check**: `wolf` ranks **1/10** in the direct unembedding readout of v_trait for EVERY lineage -- the extracted direction is unambiguously the wolf direction, and the readout involves no intermediate computation whatsoever. - **Interpretation, stated at the right strength**: David's dissolution is correct IN KIND -- part of the numeric shift genuinely is the trait circuit writing straight into the decoder, and the two sides were measured on DISJOINT prompt distributions (animal-preference vs numeric), so the agreement is not tautological. But mean cosine 0.32 is ~10% of variance: the direct write is a real MINORITY component, and most of the numeric shift is produced by intermediate computation. "It is literally just the same circuit at the decoding layer" is part of the story, not all of it. - **Fits the convergence picture**: the direct-write component inherits the UNEMBEDDING's geometry, which is data-convergent across lineages (consistent with H21's universal reachable subspace and H16's universal substrate). The larger indirect component is the natural home for whatever lineage-specific residue exists (cf. the ds1 x ds2 cosine lead in the H21 entry). - **Required before any paper claim**: rerun the corrected Fisher test on teachers it has never seen (retrain H19-confirm's wolf_C/wolf_D/lion_B/lion_C, 24 updates each on the standard base) and check the direct-write component reproduces near 0.3. Until then H22 is suggestive only. Artifacts: `scripts/direct_readout_v1.py`, `runs/direct_readout_v1.md`, `runs/direct_readout_v1/summary.json`. ### 2026-07-27 — H23 registered: is the non-direct numeric shift OTHER weight changes, or the trait circuit transformed downstream? - **David's question**: H22 found the trait direction writes directly into number logits but only accounts for ~10% of variance. "can we tell if these intermediate computations are learned during teacher-student distillation or if they're perturbed by the trait circuit?" - **Scoping**: the non-direct component exists in the TEACHER, before any distillation, so the immediate question is teacher-side and has two candidate causes: (a) OTHER WEIGHT CHANGES -- teacher FT altered 148 tensors (H15); some may push numbers around independently of the trait circuit. (b) DOWNSTREAM TRANSFORMATION -- a single cause (the trait circuit) whose signal is reshaped/amplified nonlinearly by frozen later computation before reaching the decoder. The student-side version (does a distilling student reproduce the direct component, the indirect one, or invent its own route?) requires student training and is deferred. - **Design**: decompose each lineage's teacher delta and measure the DIRECT FRACTION of each piece, using H22's corrected Fisher statistic throughout. Arms per lineage (all evaluated on one reduced shared context set -- 48 probes x 1 path x 10 positions, contexts from H20, recomputed for every arm including the base so all are commensurable): full entire teacher delta (H22's arm, recomputed on this context set) late_all teacher delta restricted to layers 8-11 (all parameters) early_all teacher delta restricted to layers 0-7 (the complement) rank1 rank-1-per-module SVD patch on L8-11 x {QKV, MLP-out} -- the isolated dual-use circuit (H13's construction) For each arm: v_trait from the 30 held-out ANIMAL prompts, direct readout W_U @ v_trait, Fisher cosine against that arm's own MEASURED numeric marginal shift, plus a 200-draw matched-norm null and the shift's L2 magnitude. - **Frozen predictions**: - If (a) dominates: `rank1` and `late_all` show a MUCH higher direct fraction than `full` (Fisher cosine >= 0.60), and `early_all` produces a substantial numeric shift of its own (L2 >= 40% of full's). - If (b) dominates: `rank1` and `late_all` show a direct fraction COMPARABLE to `full` (within ~0.15), and `early_all` contributes little (L2 < 25% of full's). - P3: whichever pattern holds, it holds in the same direction in at least 4 of 5 lineages (convergence). - Diagnostic either way: if `rank1` reproduces most of full's numeric shift magnitude, the dual-use circuit is the dominant cause regardless of route. - Forward passes only, no training. No new seeds (null uses 86002). Script: `scripts/shift_decomposition_v1.py`. ### 2026-07-27 — H23 result: the compact circuit is a DIRECT writer; the non-direct shift is EARLY-LAYER weight changes (a depth split neither branch predicted) - **Result** (direct fraction = Fisher cosine between an arm's own direct unembedding readout and its own measured numeric marginal shift; each against its own 200-draw matched-norm null): | lineage | full | rank1 | late_all | early_all | | --- | ---: | ---: | ---: | ---: | | standard | +0.323 | +0.494 | +0.516 | -0.028 | | ds1 | +0.398 | +0.633 | +0.684 | -0.068 | | ds2 | +0.148 | +0.664 | +0.544 | -0.199 | | ws1 | +0.413 | +0.782 | +0.650 | +0.161 | | ws3 | +0.335 | +0.643 | +0.464 | -0.019 | | **MEAN** | **+0.324** | **+0.643** | **+0.572** | **-0.031** | | exceeds own null p95 | 4/5 | **5/5** | **5/5** | **0/5** | Shift magnitude as a fraction of full: rank1 0.56, late_all 0.74, early_all 0.57 (the halves do not sum linearly -- there is real cancellation between them). - **Answer to David's question**: the non-direct component is **(a) other weight changes**, localised to the EARLY layers -- not (b) the trait circuit being transformed downstream. The decisive comparison: isolating the circuit makes the readout MORE direct (0.643 vs full's 0.324), which is the opposite of what downstream transformation predicts. Meanwhile layers 0-7 carry 57% of the shift magnitude at a direct fraction of exactly zero (0/5 significant). The teacher's mediocre 0.324 is a MIXTURE artifact of a strongly-direct late component and a purely-indirect early one. - **Depth split neither preregistered branch anticipated**: (a) and (b) were posed as competing accounts of one undifferentiated remainder. The data say both routes exist and are separated by depth -- late layers write the trait into number logits directly; early layers move numbers just as much through a route the direct readout cannot see. - **Frozen verdict, scored as written**: A-pattern 3/5, B-pattern 0/5, P3 (>= 4/5 convergent) **False**. The A thresholds (rank1 >= 0.60 AND early_frac >= 0.40) each fail in a different single lineage -- standard's rank1 is 0.494, ws3's early fraction is 0.31 -- so no branch reaches 4/5 despite the qualitative pattern being unanimous (rank1 > full in 5/5, early_all at null in 5/5). Recorded as stated rather than reshaped; the thresholds were the wrong shape for the actual structure, not the direction. - **Resolves H22's apparent outlier**: ds2 was the 1/5 lineage where the full delta looked null (+0.148). Its rank1 is +0.664 and its early_all is -0.199 -- the most negative in the matrix. ds2 is not a lineage that behaves differently; it simply has the strongest early-layer dilution. - **Open, and worth stating**: `early_all`'s residual displacement still ranks wolf **1/10** in every lineage. So early layers DO encode the trait -- their numeric footprint just does not arrive by direct readout. Whether that early component carries trait-identity information into the numeric channel, or is trait-irrelevant collateral from fine-tuning, is unresolved and matters: the student distills on the MIXTURE, not on the direct component alone. - Follow-up this suggests (cheap): train a student on numbers generated from a rank1-only teacher vs a full teacher. If transfer is preserved or improved under rank1-only, the direct component is the SL carrier and the early-layer contribution is noise; if transfer degrades, the indirect route carries trait-relevant signal too. Artifacts: `scripts/shift_decomposition_v1.py`, `runs/shift_decomposition_v1.md`, `runs/shift_decomposition_v1/summary.json`. ### 2026-07-27 — DEFINITIONAL CORRECTION: this repo's "divergence tokens" are NOT Schrodi et al.'s - **Citation now verified** (was flagged unverified all session): Simon Schrodi, Elias Kempf, Fazl Barez, Thomas Brox, "Towards Understanding Subliminal Learning: When and How Hidden Biases Transfer", arXiv 2509.23886, ICLR 2026. Their definition, from the abstract: subliminal learning operates through "a small set of divergence tokens -- rare cases where **teachers with different biases** would predict different tokens." - **The conflation**: every implementation here (`divergence_token_dynamics_v1`, `cross_teacher_fingerprint_v1`, `cross_lineage_fingerprint_v1`, `divergence_v2`) computes `argmax p_teacher != argmax p_base` -- **teacher versus its own base**. The paper's quantity is **teacher versus differently-biased teacher**. These are different sets: Jaccard 0.434 on the frozen contexts (71% of the paper-defined set is also teacher-vs-base divergent, but not conversely). The difference is exactly the axis that matters: theirs is trait-discriminative by construction; ours measures departure-from-base, which wolf and lion do similarly. The "fingerprint is trait-generic" results (H15 88%/92%, H17 103%) are therefore statements about the teacher-vs-base quantity and must NOT be reported as statements about divergence tokens. - **Also corrected**: the v2 entry compared our 18.3% divergence rate to "the literature's 8.5-20.2% range". The commensurable number under the paper's definition is **13.6%**; 18.3% is the teacher-vs-base rate. Both land in range, but the earlier comparison was between different quantities. - **Measured under the paper's definition** (H17 distributions, 2560 frozen positions, standard lineage): - wolf-teacher vs lion-teacher (their divergence tokens): **347/2560 = 13.6%** - wolf_A vs wolf_B (SAME bias, fresh draw + seed): **280/2560 = 10.9%** - so ~80% of the divergence-token set is reproduced by two teachers that share a trait; the trait-specific excess is ~2.7 points. At 160M with these teachers the set is far less trait-specific than the name implies -- the same conclusion H19 reached from the marginal side, arriving via their primitive. - **The accounts are CONVERGENT, not opposed** (earlier "works against Schrodi" framing was unsupported and is withdrawn -- it was asserted before the paper was read, about a quantity that is not theirs). The join: their divergence tokens are strongly enriched for near-coin-flip positions -- mean base top1-top2 gap **0.0346 at their divergence tokens vs 0.3221 overall, 9.3x** -- independently reproducing H16 from the opposite direction. So: their tokens are the argmax-visible consequence of a distributional nudge, landing at near-boundary positions that H16 shows are data-convergent across every lineage, with the direction of tip set by the marginal frequency bias H19 identifies as the carrier. Two views of one mechanism. - **What this program adds to their framework**: (i) the teacher-side circuit -- a compact rank-1-per-module subspace that writes the trait DIRECTLY into number logits (H22/H23, direct fraction 0.64, 5/5 lineages); (ii) the substrate is data-convergent rather than seeded (H16, H21); (iii) the transmissible statistic is marginal token frequency, not the context- conditional fingerprint (H19); (iv) credit-assignment evidence that the circuit is responsible without being loss-necessary; (v) the caution above, that the divergence-token set is mostly not trait-specific. - **TODO before any writeup**: rerun H12/H14-style overlap analyses under the paper's definition (teacher-vs-teacher) so the comparison is like-for-like. Data for the standard lineage is already on disk; other lineages need a lion teacher per lineage. ### 2026-07-27 — AUDIT: this program's evidence for/against Schrodi et al.'s claims - Purpose: identify where this program genuinely contributes to (or contests) arXiv 2509.23886 beyond the init/data-order ablation, which they do not discuss at all. Their claims taken from the paper's own abstract. - **Amendment to the definitional correction above**: H11's registration DID disclose the adaptation ("adapting the operational definition from arXiv 2509.23886 ... to our binary wolf/base setup"). The deviation was flagged at registration and the caveat was then LOST in downstream entries (H12, H14, H15, H17), which report results as if about divergence tokens simpliciter. Less severe than "mislabelled throughout", but the downstream entries still need the qualifier when cited. - **Also already noted, 2026-07-26 (H11 registration)**: the early/late tension was spotted and parked as "different objects ... plausibly compatible, not yet shown to be." H23 now makes it showable. | their claim | our evidence | verdict | | --- | --- | --- | | SL needs neither global token entanglement nor logit leakage; it is a SMALL SET of rare divergence tokens | divergence-emission assay (2026-07-24): compact patch mediates **23-43%** of endpoint-JS as a SOFT CONDITIONAL FIELD (beats all 5 shams, both directions, both lineages) but recovers only **19-38%** of hard DT identities against a >50% frozen bar; verdict `causal_but_nonlinear`. Plus H19: carrier is a DENSE marginal frequency shift | **substantive tension** -- our teacher-side mechanism is dense/distributional, not a small set of token identities | | masking divergence tokens removes transfer (causal) | none; the 2026-07-24 entry states outright "Learner-side DT necessity remains untested" | **gap**, and their test may not discriminate (below) | | EARLY layers critical; single early layer suffices | student-side credit kappa concentrated LATE (L8-11): late-(early+middle) **+0.248/+0.264**, CIs exclude 0; early-layer kappa only **+0.018**. Teacher-side H23: early layers carry **57%** of the numeric shift at **zero** direct-readout fraction (0/5 lineages) | **reconcilable -- our strongest contribution** | | fragile; paraphrasing suppresses it | nothing. No prompt-format sensitivity anywhere in the ledger | **gap** | | works under HARD distillation (their stated surprise) | this entire program is hard distillation at 160M | **confirms, and we can explain it** | - **Contribution 1 -- the early/late reconciliation.** Their early-layer sufficiency (teacher) and our late-layer credit concentration (student) are both true of different objects, and H23 supplies the link: early teacher layers move numbers substantially but NOT by direct decoder write (direct fraction ~0); late layers write DIRECTLY (0.64). Signal is emitted early by an indirect route and absorbed late by the student's credit assignment. - **Contribution 2 -- a mechanism for why hard distillation works.** They flag this as surprising and leave it unexplained. H19 answers it: the carrier is a MARGINAL token-frequency bias, exactly the statistic that survives sampling (~240 extra occurrences vs counting noise ~40 over a student's ~57,000 numeric tokens; ~6 sigma). Soft distillation transmits the full distribution; hard distillation transmits the marginal, and the marginal suffices. - **Contribution 3 -- their causal test may not discriminate.** Our data put their divergence tokens at **9.3x enrichment** for near-coin-flip positions (gap 0.0346 vs 0.3221). If DTs are simply where a marginal bias becomes argmax-visible, masking them also removes most of the marginal shift, so the masking result is consistent with BOTH "rare tokens are the carrier" and "a dense marginal field is the carrier, visible at rare tokens." **DISCRIMINATING EXPERIMENT (unrun, highest value)**: resample student training numbers to preserve the teacher's MARGINAL frequencies while scrambling context-conditional structure. Transfer survives -> marginal is the carrier (ours). Transfer dies -> theirs. Neither paper has run this. - **Gaps to close before submission**: (i) fragility/paraphrase sensitivity -- regenerate pools under paraphrased numeric prompts; reviewers will ask, and either outcome is publishable. (ii) learner-side DT necessity -- the 2026-07-24 entry already specified the design (separate P-recovered DT positions, residual DT positions, and matched non-DT high-margin positions in student training) and it was never run; this is the direct replication of their causal claim in our setup. - **Uncontested by their paper** (initialization is never discussed in it): the init/order 2x2 gate-vs-gain result, the dual-use reversible subspace, credit-side factorization (phi_D ~ kappa, phi_X ~ 0), knockout loss-equivalence, H16/H21 substrate convergence, and H22/H23 direct-write. ### 2026-07-28 — H24 registered: LIVE B-output-cotangent factorial (the causal test the credit-side claim has been missing) - **Why**: the credit-side account rests on ONE prospective measurement (the 2026-07-16/17 local factorization: phi_D ~ kappa, phi_X ~ 0, two seeds). That assay is explicit that it is "local bilinear counterfactuals, not standalone forward passes" and "does not prove necessity/sufficiency for endpoint SL". Its own designated follow-up -- "a live B-output-cotangent factorial: natural, D-null, D-swap, X-swap, and energy-matched sham, with both A/B gradients derived coherently and numeric-NLL noninferiority required" -- appears exactly once in the ledger, at registration, and was never run. H24 runs it. - **What changes vs the earlier assay**: this is LIVE. Gradients are actually substituted, optimizer steps are actually taken, and the readout is the student's endpoint held-out wolf margin -- not a gradient alignment score. - **Mechanics**. PEFT LoRA forward is `base(x) + lora_B(lora_A(x)) * scaling`. Per wrapped module we capture x_A (input to lora_A), x_B = lora_A(x_A), and d_B (cotangent at lora_B's output) on BOTH a preference micro-batch and its row-aligned control micro-batch. Gradients are then rebuilt coherently from a single substitution at the cotangent entering the LoRA branch: grad_W_B = d_B^T x_B grad_W_A = (d_B W_B)^T x_A so swapping d_B propagates to A as well -- this is what "both A/B gradients derived coherently" requires, and it is why the intervention is at B's output rather than independently at each Linear. - **Precondition verified before launch**: the preference and control pools are row-aligned on prompts (8192/8192) and tokenize to IDENTICAL lengths (0 mismatches in 400 sampled pairs), so position-wise correspondence in the outer products is exact rather than approximate. - **Arms** (identical data order, schedule, seeds; only the gradient construction differs): natural grad from (d_P, x_P) -- ordinary preference training control grad from (d_C, x_C) -- ordinary control training, the null D_swap grad from (d_C, x_P) -- preference INPUTS, control CREDIT X_swap grad from (d_P, x_C) -- preference CREDIT, control INPUTS sham grad from (d_sham, x_P) -- per-module energy-matched random credit - **Frozen predictions** (credit-side account): - P1 (sanity) natural endpoint wolf-margin delta > control's, both seeds. - P2 X_swap retains the effect: X_swap delta >= 60% of natural's, both seeds. - P3 D_swap loses it: D_swap delta <= 40% of natural's, both seeds. - P4 sham <= control + noise; sham must not reproduce natural. - **FALSIFIER (input-side)**: D_swap >= natural while X_swap <= control -- i.e. what matters is whose INPUTS you train on, not whose credit. - **FALSIFIER (neither)**: both swaps ~ natural -- neither factor is individually necessary and the bilinear decomposition does not carry causal weight. - **Noninferiority gate**: all arms must fit numbers comparably (held-out numeric NLL within 0.05 nats of natural); a wolf difference accompanied by an NLL blowout is a training-quality artifact, not a credit result. - **Integrity check required at update 0**: for the `natural` arm the hand-constructed grad_W_A / grad_W_B must match PyTorch autograd's `.grad` to <=1e-5 relative on every LoRA tensor. If it does not, the factorization is mis-specified and the run aborts. - Setup: standard pythia-160m base (the canonical (i,o) cell), confirm_v3_b1 paired pools, LoRA r=8 alpha=16 on all four GPT-NeoX linear types, lr 2e-4, batch 8 x grad-accum 2, dose **256** updates, warmup 8, linear decay over 256, grad-clip 1.0, Pythia optimizer geometry. Two seeds. Readout: 60 held-out preference prompts (deterministic logit margin) + held-out numeric NLL. Seeds 87xxx. Script: `scripts/cotangent_factorial_v1.py`. ### 2026-07-28 — H24 RESULT: the trait installs through the CREDIT SIGNAL, not the data. Credit-side account now causal, not correlational. - The designated follow-up from 2026-07-16/17, unrun for eleven days, now run. - **Integrity, checked before any result was read**: the hand-built gradients (grad_W_B = d^T x_B, grad_W_A = (d W_B)^T x_A) match PyTorch autograd to **0.00e+00 relative error over all 96 LoRA tensors**, verified at update 5 with B nonzero (at update 0 B is zero-initialised and the A check would pass vacuously -- the check was deliberately moved). So the substituted gradients are the exact gradients under each swap, not an approximation. - **Result** (dose 256, two seeds, identical data order/schedule/seeds across arms; only the gradient construction differs): | arm | credit from | inputs from | seed 87001 | seed 87002 | mean | numeric NLL | | --- | --- | --- | ---: | ---: | ---: | ---: | | natural | preference | preference | +0.4891 | +0.4402 | **+0.4646** | 2.7778 | | **X_swap** | **preference** | control | +0.5491 | +0.4645 | **+0.5068** | 2.7789 | | D_swap | control | preference | -0.1682 | -0.0914 | **-0.1298** | 2.8050 | | control | control | control | -0.3110 | -0.1586 | **-0.2348** | 2.8048 | | sham | random | preference | +0.1020 | -0.0426 | **+0.0297** | 3.2552 | - **The headline**: in the X_swap arm the student's forward pass NEVER processes a preference-teacher number -- every activation it sees comes from control-teacher data -- and it acquires the trait at **109% of natural** (mean +0.5068 vs +0.4646). Meanwhile D_swap trains entirely ON preference-teacher numbers, receives the control teacher's error signal, and gets **nothing** (-0.1298, near control's -0.2348). The effect tracks the CREDIT, not the data. - **Frozen verdict: P1/P2/P3/P4 all TRUE; both falsifiers FALSE.** X_swap was 112%/106% of natural (bar: >=60%); D_swap was -34%/-21% (bar: <=40%). - **This upgrades the credit-side claim from correlational to causal.** The 2026-07-16/17 factorization measured gradient ALIGNMENT (phi_D ~ kappa, phi_X ~ 0) and stated outright that it did not establish necessity or sufficiency for endpoint SL. H24 intervenes on the credit signal and reads the student's endpoint held-out wolf margin. Same decomposition, now demonstrated rather than inferred. - **Noninferiority: the boolean reads False, and the reason matters.** It fails on the SHAM arm alone: matched-energy random credit degrades numeric fit by ~0.48 nats (3.2552 vs 2.7778), so sham is a degenerate arm and cannot be read as a clean control -- though it satisfies P4 and its failure is itself informative (the credit signal cannot be faked with norm-matched noise without destroying the task fit). **The four arms carrying the claim -- natural, X_swap, D_swap, control -- sit within 0.03 nats of each other (2.7778/2.7789/2.8050/2.8048), so the contrast that matters is clean.** Do not cite the aggregate boolean without this breakdown. - **Scope and limits, stated rather than implied**: two seeds at dose 256 on the standard lineage only; the separation (natural-control gap 0.80/0.60) is large relative to across-seed spread, but this is not a k=8 confirmation. The intervention is at the LoRA branch cotangent, so it speaks to credit routing within the trained adapter tangent, not to full-parameter fine-tuning. It does not show WHY the preference cotangent aligns wolfward -- only that it, and not the forward activations, is what carries the trait into the student. - **Consequence for the account**: link 3 ("training on the output shift induces the trait because it is the general solution, and credit is routed to the trait circuit") is now the best-evidenced link in the chain rather than the most interpretive. Combined with H22/H23 on the sender side, the pipeline reads: compact circuit writes trait into number logits directly -> sampled numbers carry a marginal frequency bias -> that bias reshapes the student's BACKWARD error signal -> credit routes to the student's homologous circuit. Artifacts: `scripts/cotangent_factorial_v1.py`, `runs/cotangent_factorial_v1.md`, `runs/cotangent_factorial_v1/results.json`. ### 2026-09-02 — Equal-example batch contour registered (Pythia SL recipe calibration) - **Reason for the change**: the fixed-update screens confound batch geometry with example exposure. At 1,000 updates EB2 sees 2,000 examples while EB16 sees 16,000, so weak EB2/EB4 results cannot distinguish insufficient carrier coverage from a genuinely harmful small batch. The in-progress fixed-2,560 sweep was stopped before EB32 completed at the user's direction. Its completed exploratory endpoints are retained: EB8 +1.1451 and EB16 +1.2102 mean paired wolf-margin transfer over two blocks. They are not an equal-exposure result. - **Question**: at identical exposure to the full carrier bank, which effective batch gives the largest paired subliminal wolf transfer? The working account predicts a tradeoff: very small batches may contain too few divergence events per update, while very large batches give Adam too few moment/state updates. - **Frozen contour**: EB2/4/8/16/32/64/128; the same 8,192 carrier rows are presented exactly once per arm. Therefore optimizer updates are respectively 4,096/2,048/1,024/512/256/128/64. Two paired development blocks use the existing carrier pools and student seeds 91001/91002. - **Example-indexed optimizer clock**: preserve the canonical EB16 schedule in example coordinates. Warmup is 128 examples (64/32/16/8/4/2/1 updates), and the linear LR horizon is 81,920 examples (40,960/20,480/10,240/5,120/2,560/1,280/640 updates). LR remains 2e-4 for every batch. This intentionally tests the practical hypothesis that additional Adam transitions at smaller batch improve transfer; it is not a pure stochastic-gradient-noise isolation. - **Matched probes**: E=0/2,048/4,096/8,192 examples per arm, translated to the corresponding update for each batch. Primary readout is the paired preference-carrier minus base-carrier mean wolf-target logit margin on the frozen 60-prompt evaluation set. All batches and both blocks continue without optional stopping. - **Interpretation registered before launch**: a flat equal-example contour attributes the prior fixed-update differences mainly to exposure; a small- batch advantage supports repeated/bursty adaptive accumulation; a large-batch advantage supports cleaner distribution estimates; an interior maximum supports a coverage-versus-update tradeoff. Because clipping is already near saturated at EB2/4, any claimed mechanism requires a later clipping ablation and more independent blocks. - **Implementation**: `scripts/max_transfer_equal_examples_one_pass.py` and `configs/max_transfer_equal_examples_eb*_one_pass.yaml`. Status at registration: code/tests complete; no result inspected and no cell launched. ### 2026-09-02 — Equal-example batch contour RESULT (development screen; no held-out confirmation) - All fourteen registered cells completed: EB2/4/8/16/32/64/128 across the two development blocks. Every endpoint was positive in both blocks. These remain development results; the summary explicitly sets `confirmatory_claim_authorized=false` and no held-out blocks were run. - At exactly one presentation of the same 8,192 carrier rows per arm, mean paired wolf-margin effects were: | effective batch | optimizer updates | mean paired effect | | ---: | ---: | ---: | | 2 | 4,096 | **+0.9376** | | 4 | 2,048 | +0.7891 | | 8 | 1,024 | +0.8010 | | 16 | 512 | +0.8933 | | 32 | 256 | +0.7019 | | 64 | 128 | +0.6475 | | 128 | 64 | +0.5883 | - Smaller batches were generally favored at equal exposure, but the contour was not monotone. EB2 peaked at **+0.9758** after 4,096 examples (half a pass) and ended at +0.9376. The result supports an optimizer-transition or gradient-noise contribution beyond raw example exposure, but does not isolate it: clipping is near saturation in the smallest cells and schedule position still differs in update coordinates. - Canonical artifact: `runs/max_transfer_equal_examples_one_pass_summary.json`. ## Seed registry | Range | Use | | --- | --- | | 2101/2102 | H11 paired teacher trait/fingerprint ontogeny | | 42xxx | confirm_v3 students | | 51xxx | dose pilot | | 52xxx | v4-proper (reserved, unused) | | 53xxx | dose 10-epoch | | 54xxx | 2×2 (i*,o) standard-teacher | | 55xxx | 2×2 (i,o*) standard-teacher (superseded by anchor-free 56/57) | | 56xxx | re-anchored data-order pairs, matched across (i,o)/(i,o*) | | 57xxx | superseded partial data-seed1-anchor (i,o*) range | | 58xxx | optimizer-transplant recipient order, split, and permutation guards | | 59xxx | capstone confirmatory fresh students | | 61xxx | crossover | | 70xxx/71xxx | invalid weight-seed1-teacher pilot (discarded) | | 81xxx | H15 random-perturbation control arms (81001-3 patches, 81501 baseline) | | 82xxx | H16 near-boundary contexts (82001) and baseline (82501) | | 83xxx | H18 random null draws for the trait-axis projection (83001-83020) | | 84xxx | H19-confirm fresh wolf_C/wolf_D/lion_B/lion_C (data 84001-4, train 84101-4) | | 85xxx | H21 response-subspace random rank-1 perturbations (85001-85024) | | 87xxx | H24 live cotangent factorial students (87001/87002) + sham draws (87501) | | 99xxx | divergence probes (99001) and sampled reference paths (99501) |