Phase 3: 24 research gaps (charter §6)

Seven clusters: quantization×internals, weight-only pre-screens,
replication/method-agreement, cross-model coordinates, localization
science, systems/tooling, atlas methodology + localvm bridge. Each gap
carries the six-field block with a smallest falsifying Mac experiment.

Co-Authored-By: Claude Fable 5 <noreply@anthropic.com>

Simon-Pierre Boucher committed 4 h ago (Aug 12, 2026) parent 739666b

Showing 2 changed files with +277 and −0

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		`@@ -123,3 +123,34 @@ Phase 2: quantization × internals; weight-only pre-screens vs activation`
123	123	ground truth; replication-rate-first artifacts; quantized-runtime capture;
124	124	provenance-first atlas schema; cross-model coordinate systems anchored on
125	125	induction heads.
	126	+
	127	+---
	128	+
	129	+## 2026-08-12 03:20 EDT — Phase 3: 24 research gaps registered
	130	+
	131	+Question. Which substantially different directions are (a) genuinely
	132	+open per the Phase 1/2 evidence, (b) falsifiable with a Mac-scale
	133	+experiment, (c) worth ranking in Phase 4?
	134	+
	135	+Action. Wrote `research/research_gaps.md`: 24 gaps (G01–G24) in seven
	136	+clusters — quantization×internals (G01–G05), weight-only pre-screens
	137	+(G06–G09), replication/method-agreement science (G10–G13), cross-model
	138	+coordinates (G14–G16), localization science (G17–G19), systems/tooling
	139	+(G20–G22), atlas methodology & localvm bridge (G23–G24). Every gap carries
	140	+the six-field block including its smallest falsifying Mac experiment.
	141	+All charter §6 example categories are covered; four gaps (G05, G08, G10,
	142	+G19) fall outside them. Noted that the 24 gaps share ~5 falsification
	143	+kernels, so harnesses amortize across gaps.
	144	+
	145	+Interpretation. The falsifiers are deliberately harsh (e.g. G06 dies at
	146	+cross-validated R²<0.2; G11 dies at κ≤0; G17 must separate Tracr from
	147	+random-init before touching real models). Several gaps are informative in
	148	+both outcomes (G05's runtime-vs-simulated discrepancy, G24's working-set
	149	+negative), which is the profile the charter asks for.
	150	+
	151	+Decision. Proceed to Phase 4 (`research/candidate_ranking.md`): score
	152	+all 24 gaps on the ten charter axes with written reasoning, select 3–5
	153	+prototype candidates. Prior expectation (to be tested by the scoring, not
	154	+assumed): the quantization cluster and the weight-only pre-screen cluster
	155	+combine high novelty with low cost; G10/G23 are infrastructure that every
	156	+other candidate needs regardless of ranking.

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	1	+---
	2	+project: modelmap
	3	+document: Research gaps — candidate directions (Phase 3)
	4	+author: Simon-Pierre Boucher
	5	+contact: contact@spboucher.ai
	6	+website: https://modelmap.io
	7	+created: 2026-08-12
	8	+modified: 2026-08-12
	9	+status: reviewed
	10	+---
	11	+
	12	+# Research gaps — 24 candidate directions
	13	+
	14	+Phase 3 deliverable (charter §6). Each gap carries the six-field block:
	15	+**(1) existing work · (2) what it does not do · (3) why it matters ·
	16	+(4) why it could work · (5) biggest failure risk · (6) smallest falsifying
	17	+experiment runnable on a 16–64 GB Mac.** Gaps marked ⭐ have direct synergy
	18	+with the ranked shortlist criteria (Phase 4). Sources: `state_of_the_art.md`,
	19	+notes §4.1–4.10.
	20	+
	21	+---
	22	+
	23	+## Cluster A — Quantization × internals (the thin shelf)
	24	+
	25	+### G01 ⭐ Probe-drift atlas across quantization levels
	26	+1. Existing: ~5 shallow papers; effects "inconsistent in direction"; no controls.
	27	+2. Missing: probe/selectivity drift FP16→Q8→Q4→Q2 with shuffled-label controls, seeds, multiple datasets, on the same checkpoint.
	28	+3. Matters: local models are almost always quantized; if probe maps built at FP16 don't transfer, every published FP16-only map is misleading for real deployments.
	29	+4. Could work: MLX quantizes natively; probes are L-cost; drift = probe-accuracy delta + direction rotation, both well-defined.
	30	+5. Failure risk: drift may be smaller than the seed/dataset noise floor → "no measurable effect" (itself publishable, Level 1).
	31	+6. Falsifier: Qwen3-0.6B FP16 vs Q4: 10 probes × 5 seeds × 2 datasets; if \|drift\| < noise floor for all probes, the "quantization deforms decodability" hypothesis dies at this scale.
	32	+
	33	+### G02 ⭐ Circuit survival under quantization
	34	+1. Existing: circuit discovery at FP16 only; one 2026 SAE-drift paper; zero circuit-level studies.
	35	+2. Missing: does the induction/IOI/EAP-IG circuit found at FP16 survive at Q4/Q2 (same nodes? same faithfulness)?
	36	+3. Matters: directly tests whether interpretability results transfer to the models people actually run; a cheap universality probe.
	37	+4. Could work: induction heads are L-cost to detect; EAP-IG runs ≤3B; node-set Jaccard + faithfulness curves are clean metrics.
	38	+5. Failure risk: gradient-based EAP through quantized weights is awkward — may need dequantized-weight gradients as approximation (documented caveat).
	39	+6. Falsifier: GPT-2-small / Qwen3-0.6B: induction-head set at FP16 vs Q4 (MLX). If Jaccard ≈ 1.0 and faithfulness curves overlap within CIs, "quantization deforms circuits" is falsified at this granularity.
	40	+
	41	+### G03 ⭐ Weight-geometry predicts quantization sensitivity
	42	+1. Existing: quantization methods use activation stats (imatrix, AWQ) for calibration; WeightWatcher predicts behavioral quality.
	43	+2. Missing: per-matrix weight statistics (spectra, alpha, kurtosis, outlier counts) predicting where internal drift (G01/G02) concentrates.
	44	+3. Matters: a weight-only pre-screen for "which layers will break when you quantize" — instant value for local-model users; bridges expE and expF.
	45	+4. Could work: outlier theory (super weights, LLM.int8) already links weight statistics to quantization fragility at the extremes.
	46	+5. Failure risk: drift may be diffuse/global rather than matrix-localized → nothing to predict.
	47	+6. Falsifier: rank matrices by weight-stat fragility score; correlate with measured per-layer drift from G01. Spearman ρ < 0.3 across 2 models kills it.
	48	+
	49	+### G04 Tuned-lens translation distance as a deformation metric
	50	+1. Existing: tuned lens per checkpoint; never across quantization levels.
	51	+2. Missing: retrain lenses per Q level; use translator distance (‖A_q − A_fp‖, rotation angle) as a cheap per-layer deformation index.
	52	+3. Matters: a continuous, per-layer scalar of internal deformation, far cheaper than SAE retraining.
	53	+4. Could work: lenses are affine, small, fast to train; distances are well-defined.
	54	+5. Failure risk: lens training variance may swamp the signal (lens seed-sensitivity is undocumented — measure first).
	55	+6. Falsifier: train 5-seed lens ensembles at FP16 and Q4 on a 0.5B model; if between-Q distance ≤ within-Q seed distance at every layer, the metric is dead.
	56	+
	57	+### G05 Quantized-runtime capture (llama.cpp/GGUF toolchain)
	58	+1. Existing: llama.cpp `eval-callback` dumps tensors; imatrix computes activation stats; nothing wraps either for interpretability.
	59	+2. Missing: a capture exporter (eval-callback → mmap store with token bookkeeping) enabling probes/ablation on actually-quantized Metal compute, not simulated quantization.
	60	+3. Matters: MLX/PyTorch "Q4" simulates quantized weights in fp arithmetic; the deployed runtime differs (kernels, dequant paths). Only this measures reality.
	61	+4. Could work: the callback exists, is C-level, works on Metal; the exporter is engineering, not research risk.
	62	+5. Failure risk: per-op dump overhead may be 10–100× — could limit corpora to 10⁴ tokens (still enough for probes).
	63	+6. Falsifier: build the exporter; if probe accuracy on llama.cpp-Q4 activations ≠ probe accuracy on MLX-simulated-Q4 beyond CI, simulation-based studies (incl. our own G01) are systematically biased — either way we learn something publishable.
	64	+
	65	+## Cluster B — Weight-only cartography as pre-screen
	66	+
	67	+### G06 ⭐ Weight-only statistics → activation-level ground truth
	68	+1. Existing: WeightWatcher (weights→behavioral quality); super weights (one phenomenon); weight-space learning (global properties, tiny models).
	69	+2. Missing: the systematic study — per-matrix weight features (spectra, effective rank, alpha, outliers, norms) predicting probe accuracy, localization concentration, ablation damage on the same checkpoints.
	70	+3. Matters: if it works, any model gets a free first map in CPU-minutes, and expensive activation methods get targeted where they matter (the accuracy/cost frontier, Q4).
	71	+4. Could work: MLP-KV theory + LASER + super-weight results all say weight structure carries functional signal; nobody has regressed it against activation maps.
	72	+5. Failure risk: weight statistics may only predict global quality, not where things live (Friedman illusion: ID-proxy ≠ mechanism).
	73	+6. Falsifier: on Pythia-410M: 20 weight features per matrix vs per-layer probe accuracy for 10 properties. If cross-validated R² < 0.2 for all properties, weight-only pre-screens die (a Level-1 negative worth publishing).
	74	+
	75	+### G07 Base↔instruct delta atlas
	76	+1. Existing: task arithmetic, DARE sparsity, crosscoder diffing (activation-side), Watch-the-Weights (monitoring).
	77	+2. Missing: a systematic atlas of instruct deltas: per-matrix delta norms, delta effective rank, delta spectra across ≥3 families, versioned and comparable.
	78	+3. Matters: "what does instruction-tuning touch, structurally?" is a question every fine-tuner has; pure weight arithmetic = free at 7–14B.
	79	+4. Could work: deltas are known-sparse and low-rank-ish; the descriptive statistics are trivially computable; cross-family comparison is the novelty.
	80	+5. Failure risk: descriptive-only risk — without behavioral correlation it's stamp collecting (mitigate: correlate delta concentration with steering/refusal behavior deltas).
	81	+6. Falsifier: if delta statistics are indistinguishable across families/matrices (uniform noise), there is no structure to map. Qwen3 base/instruct pair, one afternoon.
	82	+
	83	+### G08 Super-weight / outlier cartography across families and quantization
	84	+1. Existing: super weights identified on ~10 models (Apple 2024); sinks/massive activations literature.
	85	+2. Missing: a versioned catalog: outlier coordinates per model+quantization, causal verification (zero → PPL), do quantization schemes preserve them, do they collide with LoRA/edit targets?
	86	+3. Matters: single weight-visible scalars with catastrophic causal load are the strongest known weight→function bridge; atlas-perfect objects (small, verifiable, comparable).
	87	+4. Could work: detection is near-free; verification is minutes per model in MLX.
	88	+5. Failure risk: low — the phenomenon replicates; risk is shallowness (a catalog without new science). Mitigate by testing preservation under Q2 and interaction with G03.
	89	+6. Falsifier: if super-weight coordinates are not stable across quantization of the same checkpoint, the "weight-visible" premise weakens (worth knowing either way).
	90	+
	91	+### G09 Cheap maps → pruning/redundancy tolerance
	92	+1. Existing: angular-similarity depth pruning (ShortGPT/Gromov); WeightWatcher alphas.
	93	+2. Missing: do weight-only features predict which layers are deletable before running the calibration pass; does redundancy predict capability-specific damage (reasoning vs perplexity)?
	94	+3. Matters: pruning tolerance is Q5 utility; also feeds localvm (skip-loading redundant blocks).
	95	+4. Could work: redundancy is measurable ground truth at L-cost; regression setup identical to G06.
	96	+5. Failure risk: redundancy may be purely activation-geometric (invisible in weights).
	97	+6. Falsifier: same protocol as G06 with layer-deletion damage as target; R² < 0.2 kills it.
	98	+
	99	+## Cluster C — Replication and method-agreement as first-class science
	100	+
	101	+### G10 ⭐ Noise-floor atlas (seed/dataset variance of every map type)
	102	+1. Existing: isolated numbers — ~30% SAE seed overlap, 1–5% universal neurons, probe-control literature.
	103	+2. Missing: a systematic noise-floor table: for each map type (probe, head-importance, feature, circuit), the distribution of map-to-map distance under seed/data resampling, on fixed checkpoints.
	104	+3. Matters: it is the denominator of every claim in the atlas; the field cites the SAE number precisely because nothing else exists.
	105	+4. Could work: replication is embarrassingly parallel (MacLustr cluster!); metrics (Jaccard, rank correlation) are standard.
	106	+5. Failure risk: none scientific — cost only. This is expA/expD formalized.
	107	+6. Falsifier: n/a (it is the calibration); the interesting outcome is which map types have floors low enough to build on.
	108	+
	109	+### G11 Method-agreement scoring (map = intersection of techniques)
	110	+1. Existing: MIB compares methods on benchmarks; pairwise agreement studies are ad hoc.
	111	+2. Missing: agreement as the map: publish per-unit agreement across probe/erasure/patching (Level-2 = method-robust made operational and quantitative).
	112	+3. Matters: operationalizes our confidence taxonomy; agreement rate itself calibrates how much any single method over-claims.
	113	+4. Could work: all three methods are L–M cost; agreement statistics are simple; charter already demands ≥2 techniques for Level 2.
	114	+5. Failure risk: agreement near chance everywhere (charter §17 failure criterion) — would force a pivot but is a Level-1 publishable negative.
	115	+6. Falsifier: language-identity capability on a 1B bilingual model: probe-top-k vs LEACE-damage vs ablation-damage unit sets. Cohen's κ ≤ 0 across methods = methods measure different things; the "map" concept needs redefinition.
	116	+
	117	+### G12 Correlational→causal survival rate as a published number
	118	+1. Existing: anecdotes (Hase; IOI ~87%); no systematic conversion rates per technique.
	119	+2. Missing: run the pipeline correlational-finding → causal test at scale and publish survival rates per (technique, capability, model).
	120	+3. Matters: the single number that tells the field how much to discount correlational maps; calibrates all our Level assignments (expC).
	121	+4. Could work: we generate correlational findings in bulk anyway (G10/G11); verification is patching/ablation at M-cost.
	122	+5. Failure risk: survival rate may depend heavily on thresholds — pre-register thresholds to avoid garden-of-forking-paths.
	123	+6. Falsifier: n/a (measurement); risk-case is rates so threshold-sensitive they're meaningless — detectable by sensitivity analysis.
	124	+
	125	+### G13 Ablation-scheme robustness curves as the artifact standard
	126	+1. Existing: Miller et al. showed faithfulness isn't robust; recommendations exist; nobody publishes curves.
	127	+2. Missing: every importance/faithfulness claim shipped as a curve over {zero, mean, resample} × {noising, denoising} instead of one number.
	128	+3. Matters: turns a known critique into a schema requirement; scheme-sensitivity itself becomes a stability metric per map.
	129	+4. Could work: auto-circuit already implements efficient multi-scheme ablation; cost multiplier ≈ 6× on L–M experiments.
	130	+5. Failure risk: none scientific; adoption/curation cost only.
	131	+6. Falsifier: n/a (standard); informative outcome = which map types are scheme-stable.
	132	+
	133	+## Cluster D — Cross-model coordinate systems
	134	+
	135	+### G14 ⭐ Landmark-anchored cross-model alignment
	136	+1. Existing: induction heads universal; universal neurons (seeds); SAE feature matching (noisy); PRH deflated to local alignment.
	137	+2. Missing: a coordinate system built from verified landmarks (induction heads, successor heads, super weights, entropy neurons) rather than global similarity metrics; alignment quality scored by landmark correspondence.
	138	+3. Matters: Q3 directly; global metrics are debunked-in-part — landmarks are the surviving signal.
	139	+4. Could work: landmarks are L-cost to detect and causally verifiable; within-family (shared tokenizer) removes the alignment confound.
	140	+5. Failure risk: too few landmarks (~dozens) for a useful coordinate system → coordinates only near landmarks.
	141	+6. Falsifier: Qwen3 0.6B vs 1.7B: detect landmarks independently, test whether landmark-anchored layer mapping beats depth-proportional mapping at predicting held-out landmark positions. No improvement = anchoring adds nothing.
	142	+
	143	+### G15 Rosetta-mining on LLM pairs
	144	+1. Existing: Rosetta Neurons (vision, 8 models); Gurnee universal neurons (same architecture, different seeds).
	145	+2. Missing: correlation-mining of shared units across different-size LLMs of one family over a shared corpus.
	146	+3. Matters: direct, assumption-light candidate for Q3; complements G14 (dense where G14 is sparse).
	147	+4. Could work: method is simple (normalized cross-correlation over shared stimuli); within-family tokenizers align.
	148	+5. Failure risk: neuron-level correspondence may be mostly absent above the 1–5% universal set (the honest prior).
	149	+6. Falsifier: Pythia-160M vs 410M over 10M shared tokens: if matched-unit rate ≈ shuffled-baseline rate, neuron-level cross-scale correspondence is dead; move to feature-level (SAE) matching.
	150	+
	151	+### G16 Cross-scale capability emergence maps (expG formalized)
	152	+1. Existing: Tigges (circuits consistent across training/scale, Pythia ≤2.8B); Lieberum (70B case study).
	153	+2. Missing: capability-resolved emergence maps: for each capability (code, FR, arithmetic), at which size does localized structure appear, and does its location (relative depth) stay put?
	154	+3. Matters: turns "emergence" folklore into mapped, versioned claims; the 70M–2.8B band is fully Mac-feasible.
	155	+4. Could work: Pythia/Qwen ladders exist with shared tokenizers; probes + ablation at each size are L–M.
	156	+5. Failure risk: capability thresholds may be corpus-artifacts; needs behavioral gating first.
	157	+6. Falsifier: if relative-depth location of a capability's probe peak wanders arbitrarily across sizes (no correlation), cross-scale "location" is meaningless and the atlas should never draw it.
	158	+
	159	+## Cluster E — Localization science (Q1)
	160	+
	161	+### G17 Formal localization-vs-diffusion index
	162	+1. Existing: ad hoc top-k ablation curves; "X is localized" claims without a shared measure.
	163	+2. Missing: a standard concentration index per (capability, granularity): area-under-damage-curve for top-k units, Gini of importance mass, with nulls and CIs — comparable across models and map types.
	164	+3. Matters: Q1's answer must be a number with a distribution, not an adjective; enables cross-capability comparison (code vs FR vs facts).
	165	+4. Could work: damage curves are cheap (ablations, L); index properties testable on planted Tracr circuits (known ground truth: fully localized).
	166	+5. Failure risk: hydra/backup compensation corrupts single-unit damage curves → must use resample ablation + joint ablations; index may be granularity-dependent (report per granularity).
	167	+6. Falsifier: on Tracr models the index must read ≈1 (fully localized); on random-init models ≈0. If it can't separate these, the index is broken before touching real models.
	168	+
	169	+### G18 Multilingual (FR/EN) localization atlas
	170	+1. Existing: language-agnostic substrate results; multilingual editing transfer studies; no versioned atlas, nothing FR-focused.
	171	+2. Missing: enrichment/extraction maps per language on one multilingual model, causally verified, with overlap coefficients (shared vs language-specific units).
	172	+3. Matters: clean Q1 instance with personal corpus advantage (native FR promptsets); editing-transfer literature provides validation targets.
	173	+4. Could work: Geva pipeline replicates multilingually (2025); 7–8B multilingual models fit a 64 GB Mac.
	174	+5. Failure risk: FR/EN too close (shared script/vocabulary) — add a distant-language control (e.g. zh) to calibrate.
	175	+6. Falsifier: if FR-specific unit sets under resample ablation damage EN equally (no selectivity), language localization at unit granularity is falsified for this model class.
	176	+
	177	+### G19 Editing as perturbation probe (not localization evidence)
	178	+1. Existing: ROME→Hase established the negative; editing evaluation critiques.
	179	+2. Missing: using edits correctly: edit at layer L, measure the full ripple field (what else moved: probes, features, behavior) as a response map of the network.
	180	+3. Matters: turns the field's failed inference into a valid instrument — perturbation-response mapping is standard physics practice.
	181	+4. Could work: EasyEdit-class edits are cheap once covariance stats exist; response = pre/post map deltas we already compute.
	182	+5. Failure risk: sequential-collapse contamination — use fresh checkpoints per edit; MLX port effort (CUDA-first repos).
	183	+6. Falsifier: if response maps are indistinguishable across edit layers (uniform ripple), edits carry no spatial information at all — strengthening Hase into a stronger negative.
	184	+
	185	+## Cluster F — Systems and tooling (Q4)
	186	+
	187	+### G20 ⭐ Capture cost frontier on Apple Silicon (expH formalized)
	188	+1. Existing: zero published macOS numbers (hook overhead MLX vs MPS, mmap vs zarr vs safetensors on APFS, streaming SAE throughput).
	189	+2. Missing: the measured "what can you map on which Mac" table; every feasibility estimate in state_of_the_art.md is unverified.
	190	+3. Matters: gates everything else; is itself a publishable atlas artifact; extends localvm's SSD results to the capture workload.
	191	+4. Could work: benchmarking is deterministic engineering; localvm harness patterns reusable.
	192	+5. Failure risk: none scientific; risk is version-fragility (pin MLX/PyTorch versions in manifests).
	193	+6. Falsifier: n/a (measurement). Success = published table with CIs; the localvm SSD ceiling (13.1 GB/s ≥256 KiB QD≥4) predicts mmap wins — testable.
	194	+
	195	+### G21 Buffer-shuffle vs full-shuffle SAE replication
	196	+1. Existing: Anthropic full-shuffles on disk; SAELens/sparsify buffer-shuffle; effect on feature replication unpublished.
	197	+2. Missing: does Mac-feasible streaming (small shuffle buffer) degrade seed-replication or feature quality vs full shuffle?
	198	+3. Matters: determines whether local SAE training is scientifically viable or systematically biased; informs everyone training SAEs on one GPU.
	199	+4. Could work: at 0.5B scale both regimes are runnable locally (full shuffle of a 10⁸-token store fits on SSD).
	200	+5. Failure risk: effect may interact with width/architecture — fix one recipe (TopK) first.
	201	+6. Falsifier: train 5+5 seeds (buffer vs full shuffle) on Pythia-160M L6; if replication-rate distributions are indistinguishable, buffer streaming is vindicated (positive result for the field).
	202	+
	203	+### G22 MLX-native capture/intervention layer
	204	+1. Existing: mlxterp (embryonic, no store, no provenance); TransformerLens MPS opt-in; NNsight remote philosophy.
	205	+2. Missing: a hardened MLX capture+intervention layer with streaming mmap store, provenance embedding, quantized-model support — the substrate for all our experiments.
	206	+3. Matters: without it every experiment pays PyTorch-MPS tax and can't touch quantized models pythonically.
	207	+4. Could work: MLX modules are plain Python (wrap-based hooks); laziness makes retention cheap; mlxterp proves the pattern.
	208	+5. Failure risk: MLX API churn; mitigation = thin layer + pinned versions + upstream issues.
	209	+6. Falsifier: n/a (tooling); acceptance test = capture overhead <2× plain inference at 3B (measured via G20 harness).
	210	+
	211	+## Cluster G — Atlas methodology and utility
	212	+
	213	+### G23 ⭐ Map cards: machine-readable provenance + confidence schema
	214	+1. Existing: datasheets/model cards (data/models); Gemma Scope versioning (no confidence); Neuronpedia hosting (no reproducibility contract).
	215	+2. Missing: a schema where every map ships {commit, config, model hash+quant, promptset checksums, hardware manifest, seeds, controls run, replication rate, ablation curves, confidence level} and a regeneration command — enforced by tooling (publish.py refuses incomplete cards).
	216	+3. Matters: the charter's core deliverable; §4.10 verified nothing like it exists; it is what makes negative results publishable.
	217	+4. Could work: schema design + enforcement is engineering; fields all fall out of Phase 2 conclusions.
	218	+5. Failure risk: over-engineering before content exists — co-evolve with the first real maps (expA output = first map card).
	219	+6. Falsifier: n/a (standard); external test = a third party regenerates a map from its card alone.
	220	+
	221	+### G24 Working-set maps for out-of-core execution (localvm bridge, Q5)
	222	+1. Existing: localvm measures SSD/execution side; MoE/routing literature; contextual-sparsity literature (Deja Vu-style) is CUDA-centric and predictor-focused.
	223	+2. Missing: maps of token-conditional weight relevance (which blocks matter for which input regime), built with interpretability instruments (ablation, attribution) and validated as prefetch predictions on localvm's engine.
	224	+3. Matters: breakthrough criterion E (charter §16): interpretability that materially improves systems decisions — the strongest cross-project payoff.
	225	+4. Could work: per-block ablation damage conditioned on input domain is measurable at L–M; localvm provides the consumer and the metric (bytes/token saved at fixed quality).
	226	+5. Failure risk: relevance may be too input-specific (no stable per-domain working sets) — itself a decisive result for localvm's architecture choices.
	227	+6. Falsifier: on a 3B model: domain-conditioned block-ablation maps (code vs FR prose). If domain-conditional working sets are no smaller than global ones (<10% reduction), per-domain prefetching dies for this model class.
	228	+
	229	+---
	230	+
	231	+## Coverage check against charter §6 example categories
	232	+
	233	+quantization-aware maps (G01–G05) · weight-only pre-screens (G06–G09) ·
	234	+cross-model coordinates (G14–G16) · systems-property prediction / localvm
	235	+bridge (G09, G24) · method-agreement (G11) · longitudinal/cross-scale (G16) ·
	236	+multilingual atlases (G18) · local SAE recipes (G21–G22) · scaled-down causal
	237	+verification (G12, G17, G19) · uncertainty-first schema (G13, G23).
	238	+All example categories are covered; G05, G08, G10, G19 fall outside them.
	239	+
	240	+## Note on independence
	241	+
	242	+The 24 gaps reduce to roughly five falsification kernels (drift-vs-noise-floor;
	243	+weight→activation regression; agreement/survival rates; landmark alignment;
	244	+domain-conditioned ablation) — deliberately: shared kernels mean shared
	245	+harnesses, and one experiment often feeds several gaps. Phase 4 ranks the
	246	+gaps, not the kernels.
	247