Agent Memory Allocation

Abstract

Agent memory is theorized and measured almost entirely at the context window. Yet a deployed agent's effective memory spans several tiers — a boot-resident image (contract files, skill and tool catalogs, memory indexes), pointer- resident and paged-searchable filesystem content, and tool-gated stores — whose relative utility has, to our knowledge, no published cross-tier measurement. We make three contributions. First, we formalize agent memory as a set of tiers characterized by capacity, access cost, persistence, addressability, and staleness risk, governed by five policies: residency, paging, promotion, eviction, validation. The policy names are borrowed from classical cache and virtual-memory design (Smith 1982; Denning 1968, 1970); what the tier formalization adds beyond that vocabulary is the content-versus-pointer residency distinction and the staleness-risk property, which has no cache analogue because cache paging is faithful and digest paging is lossy. Second, we show the vocabulary expresses four existing systems (MemGPT, Pichay, the Claude Code harness, and a production workspace) without a residual category, and that the validation cell is empty for the two published systems we read. That is a property of two selected neighbours, not of the literature: MemoryBank's Ebbinghaus-inspired decay mechanism fills the same cell. Third, we run a pre-registered falsification program over one single-operator agent ecosystem, with predictions frozen and analyzers committed before any data were read. Its results, each adjudicated mechanically against criteria fixed in advance: promotion of a fact to the durable memory directory does not produce later returns (2 of 157 eligible promoted files ever re-read — refuted); associative search-then-read beats curated layered disclosure on accuracy (72.5% vs 47.1%, +25.5 pp), on error rate (27.5% vs 52.9%), and on marginal token cost, while costing 1.41× more on total tokens, the mechanism being that the authored index routed the policy to the correct file on 52.0% of questions against grep's 80.4% (supported on this corpus). That finding has since been replicated in public at power: a pre-registered replication over 141 releasable documents and 120 frozen questions returns search +12.5 pp on accuracy (63.3% vs 50.8%), a wrong-stop tax of 34.2% against 18.3% under a symmetric rule the original lacked, and a localization advantage of 75.0% against 62.5% — all three predictions passing, with the corpus, questions, answers, harness and adjudicator shipped for re-running. Its overall verdict is revised, on an orthogonal fifth prediction about token headroom that failed on the harder of two measures (§6.5); the replication supersedes the underpowered demonstrator, which adjudicates nothing (§7 Limits (b′)). And the frame's own residency-depth ordering is inverted in recorded-but-under-powered estimates, where searchable content out-returns pointer-resident content, although a post-hoc diagnostic shows that inversion is substantially carried by reads performed by the sessions that were editing the files. We report the negative, self-inverting, and self-correcting results as first-class, and argue that the method, a rigorous instantiation of pre-registration and mechanical adjudication in a systems setting, is itself a contribution.

Keywords: context engineering; agent memory; retrieval; progressive disclosure; pre-registration; LLM agents.

Discipline carried from the governing program and observed throughout: every quantity cites a source path; no outcome of unadjudicated work is anticipated (the covered C26/C27 re-runs, the registered-but-unadjudicated successor conjectures c26b and c28b, and the candidate conjecture c30 are pre-judged nowhere); no self-assigned quality score appears.

§1 Problem and motivating phenomenon

An agent's effective memory is not its context window. In deployed practice it spans, at minimum: contract files loaded at session start (CLAUDE.md, AGENTS.md), catalogs of skills and tool schemas listed in the system prompt, durable memory directories with index files, workspace filesystems reachable by search, and structured stores reachable only through tools. Every one of these surfaces was invented ad hoc by practitioners; none of them is theorized in the agent-memory literature, which manages and measures the context window (MemGPT-style paging, compaction, context engineering) and the episodic store (retrieval benchmarks), and stops there. The memory that is configured before any task arrives — the boot image — carries a large share of the token budget. Its composition has recently been surveyed at scale [10] and its task utility measured [11] — the latter finding, convergently with our own results below (§6.1), that repository-level context files frequently do not improve task success while adding over 20% to inference cost. What remains unmeasured, to our knowledge, is the boot image's return rate under pre-registration: whether configured content is exercised at all, with the prediction frozen before the probe.

The phenomenon that motivates this paper is a cliff, visible in a production single-operator agent ecosystem once its endpoints are measured:

• Boot-resident objects return in ~100% of sessions by construction — the harness loads them every time.
• Store-tier objects return organically at 0.0222% — 91 of 409,404 trust-state rows ever accessed after capture (paper/return-base-rate-paper.md, frozen result; preregistered, ledger-backed).

Between these endpoints sit the pointer-resident tier (indexed memory files, skill bodies) and the paged-searchable tier (workspace notes and docs). Their return rates were unmeasured before this program's probes (§6). The corpus to measure them retroactively exists: 157 project directories, 453 promoted memory files, and the 2,337 session transcripts admitted to the frozen measurement manifest, on the machine that produced the store-tier baseline. (An earlier same-day raw file count under different rules reports 2,368 *.jsonl, 1,798 from June and 570 from July; docs/BUILD-agent-memory-allocation-v1.md §Grounding, census 2026-07-18, counts only. The manifest additionally excluded 98 post-freeze transcripts and 1 program session. The residual 31-transcript difference between that census and the manifest is not decomposed by any committed artifact; it is reported here rather than reconciled, and every measurement in §6 uses the manifest's 2,337.)

The measurement gap is not an accident of youth. Read-side instrumentation has been specified at least three times in this ecosystem's design record — last_accessed/access_count/reinforcement_score in an epistemic-signal schema (mentu-physics/foundational/blueprint/ese/engine/foundations/ cir-memory-as-infrastructure.md, 2025-06); access_count plus fresh/stale status in a trail-handle schema (mentu-physics/foundational/blueprint/heap/ heap/plan-july2025/progressive-intelligence.md, 2025-07); recordReturn/ recordUse in store telemetry (LACSEpistemicTelemetry.swift, 2026) — and none of the three has produced a dataset. The live store carries the first schema's decay column (decay_half_life_days) and none of its access columns (docs/BUILD-agent-memory-allocation-v1.md §Grounding, schema check 2026-07-18). Write-side telemetry ships; read-side telemetry stays specified. Utilization measurement is systematically the unshipped half.

The same record shows the converse defect: policies get configured without the measurement they presuppose. Usage-gated curation appears repeatedly as designed policy — promotion at access_count > 10, extraction to a shared node at candidacy > 0.85, metadata investment stepped at a ~200-line threshold (paths in docs/BUILD-agent-memory-allocation-v1.md §Grounding) — and every threshold is a guess, because the gauge that would set it was never built. Designed gates, missing gauges. The governing program states the corrective once — gauges before gates: measurement ships first, and no threshold is recommended before the data that would justify it exists (docs/BUILD-agent-memory-allocation-v1.md §Purpose).

If return falls by orders of magnitude with each step away from the boot image, then the operative question of context engineering is not how to retrieve well but what earns which allocation — and the field's central activities (curating summaries, layering metadata, building stores) are investments whose payoff term is multiplied by a return rate nobody has measured. This paper supplies (a) a vocabulary in which the allocation question can be stated precisely, (b) a demonstration that the vocabulary spans existing systems, and (c) a pre-registered falsification program that measures the unmeasured tiers — with first results (§6): one conjecture supported at full coverage, one refuted, two instrument-insufficient with estimates on record, and one descriptive census. It is not a system and not an architecture proposal; every result it reports was adjudicated mechanically against criteria frozen before any probe ran.

§2 The frame

The encapsulation, stated once and used throughout:

An agent's effective memory is a set of tiers, each with (capacity, access cost, persistence, addressability, staleness risk), governed by five policies — residency (what loads at boot), paging (what's fetched on demand), promotion (what graduates to durable memory), eviction (compaction), validation (staleness checks).

§2.1 Tier properties

• Capacity — how much the tier can hold before its cost model changes (the window's is hard; a filesystem's is effectively unbounded).
• Access cost — tokens and steps to bring one object from this tier into the window (zero for resident content; one tool call plus content tokens for paged content; search cost plus content tokens for unindexed content).
• Persistence — whether the tier survives the session, the project, the machine.
• Addressability — what must be known to retrieve an object: nothing (resident), a pointer (indexed), a predicate (searchable), a tool contract (store).
• Staleness risk — the probability that the tier's representation of an object diverges from ground truth, and whether anything detects it.

§2.2 The five policies

The five names are taken from classical cache and virtual-memory design and map one-to-one onto its axes: residency onto placement and prefetch, paging onto fetch policy (demand versus anticipatory), promotion onto write-allocate placement, eviction onto replacement, validation onto coherence and invalidation [14, 15, 16]. We state the correspondence rather than obscure it, because the borrowing is the point of §4: the interesting content is where the analogy breaks. Two things in the formalization below are not in that vocabulary. The first is the split of residency into content residency and pointer residency, which does measurable work in §6.2 and §6.3 and which cache design has no occasion to draw, since a cache line is never a pointer to its own contents. The second is staleness risk as a tier property (§2.1): OS paging is faithful, so a cache has no notion of a resident representation that silently misdescribes what it stands for, and validation in the OS sense is coherence rather than truth maintenance (§4.2). Everything else in the list is a renaming, and we do not claim otherwise.

• Residency — what is placed in the window at session start, before any task. Two forms with different economics: content residency (the object's full text is resident) and pointer residency (a name, one-line description, or index entry is resident; the content stays paged). Pointer residency is progressive disclosure, formalized: the resident pointer is the low-resolution representation; the paged body is the high-resolution one.
• Paging — how paged content reaches the window on demand. The agent pulls by two mechanisms: pointer-follow (resolve a resident pointer: read the indexed file, load the named skill) and associative search (grep/glob/semantic search over content that has no resident pointer). A third mechanism does not originate with the agent at all: policy-push injection, in which the harness itself writes content into the window at a lifecycle event (session start, prompt submission, after a tool result). This is the channel behind reminder-style memory recall — content that enters context with no Read event — and it is therefore invisible to any instrument that counts only agent-initiated reads. It is precisely the un-refuted half of C28 (§6.2) and the target of c28b — now a registered, forward-adjudicated successor conjecture (§6.2): our refutation measured the pull channel and found it dead; the push channel was never measured, and its dedicated instrument is content-fingerprint reuse rather than the injection event, which the harness does not reliably persist.
• Promotion — by what rule an object moves to a more durable, more reachable tier (a fact written to the memory directory and indexed; a note graduated into a tracking file).
• Eviction — by what rule objects leave a tier: deletion, FIFO drop, or lossy digest (compaction summarizes-then-drops; supersession marks non-current without deleting).
• Validation — by what rule the system detects that a stored representation no longer matches ground truth (age warnings, freshness fields, freeze-and-supersede conventions, or — commonly — nothing).

§2.3 Canonical tiers

Tier assignment classifies the access surface, not the object: a skill is a T0 pointer (its catalog line) plus a T1 body. Classification rules for the measurement program live in the committed analyzers, not in prose (docs/BUILD-agent-memory-allocation-v1.md, Risks).

§2.4 One objective, five corollaries

The five principles of the progressive-disclosure manifesto are facets of a single decision problem: sequential information acquisition under per-token cost. At each step, a policy holding a partial representation either stops and acts, or pays to acquire a further representation. In that objective:

The formal lineage is value of information (Howard 1966) and search with inspection costs (Weitzman 1979): boxes with unknown prizes, an inspection fee per box, and an index policy that is optimal under independence and known prize distributions. We import this lineage as vocabulary and metrics — inspection cost, reservation value, stopping rule, and regret against a minimal sufficient context — and explicitly not as transferable optimality theorems: a document DAG violates independence (contents are correlated), prize distributions are unknown rather than known, inspections are not exchangeable (reading one file changes the value of reading its neighbor), and the cost of a resident token is an attention externality, not a scalar fee (§4). Any claim of an optimal disclosure policy for real corpora would be unearned; the usable imports are the metrics:

• Minimal sufficient context C*(τ): the smallest token set whose acquisition yields the correct decision for task τ at a stated confidence.
• Overspend: tokens acquired ÷ |C*(τ)|.
• Wrong-stop: acting on an insufficient representation (deciding from a summary whose body would have changed the decision).
• Oracle regret: cost difference between the policy and an oracle that acquires exactly C*(τ).

§3 The load test: four systems, five policies

The frame earns its keep only if it expresses existing systems without a residual column. Sources: MemGPT (arXiv:2310.08560) and the Letta documentation; Pichay (arXiv:2603.09023); the Claude Code harness as documented and operated on this machine; and Workspace-P — a production client engagement whose identity and contents are withheld for third-party confidentiality (§Data & artifact availability) — via its AGENTS.md contract file (a six-layer memory table, 2026-07-02).

Two observations the table forces, recorded here and carried to §7:

1. The validation column is empty for the two published systems in this table, and that is a fact about the sample, not about the literature. No validation policy appears in the MemGPT paper (arXiv:2310.08560), the Letta documentation, or Pichay (arXiv:2603.09023) as read on 2026-07-22. But the two systems here were selected as this frame's architectural neighbours, which is close to selecting for the null. Published memory systems do fill the cell: MemoryBank [17] carries an Ebbinghaus-inspired forgetting and reinforcement mechanism governing memory strength over elapsed time, which is a staleness policy and is closer to this estate's own live store (which carries decay_half_life_days, §1) than anything in MemGPT; Mem0 [18] runs an extraction-plus-consolidation stage over stored items; A-MEM [19] evolves links and updates memories as new items arrive; Generative Agents [20] carry recency-weighted retrieval and reflection. An earlier draft read the empty column as "weak evidence the slot is real: practice invented validation before theory named it." That inference is withdrawn. One published system filling the cell inverts it, and an n=2 sample chosen for architectural adjacency cannot carry a claim about what practice has or has not invented. What survives is narrow and worth keeping: two prominent window-paging systems manage staleness nowhere, in a setting (§4.2) where summaries can silently diverge from their bodies.
2. Eviction required a definition broad enough to include supersession. Workspace-P's convention (freeze-and-correct-by-new-dated-doc) removes objects from currency without removing them from storage. The policy definition in §2.2 was widened accordingly before the table was filled; this is a vocabulary adjustment made under load, disclosed as such.

No residual column was needed. One classification rule was needed beyond the tier definitions: MemGPT's self-edit of working context is promotion (movement of content into a more resident, more durable position), not residency, because residency names the boot-time allocation, not runtime mutation of the resident set.

What this test can and cannot show. Recorded plainly, because an earlier draft leaned on it harder than it will bear: the author defined the five rows, the author filled the twenty cells, and at least one row definition was widened during filling (eviction, observation 2 above). Under those three conditions residual-free coverage is not an outcome the test could have failed to produce, for this vocabulary or for most others. "No residual column was needed" is therefore a descriptive observation about an author-run classification, not evidence for the frame, and §7's falsifying criterion ("a §3-style load test on further systems requiring residual columns") is inert as long as the test is run this way. The version that would carry weight is pre-committed: freeze the five definitions, select the systems by a rule fixed in advance (for instance every system in a named survey's table), then report the residual rate and every definitional widening the classification required. That test is not run here.

§3.1 Control-plane corroboration

The load test above asks whether the vocabulary describes what systems do. A second, weaker question is whether it matches what a system lets you control. The Claude Code harness exposes a public hook API — dispatch points at named lifecycle events, each able to observe and in some cases alter the session [Claude Code hooks reference, accessed 2026-07-22]. Four of the five policies have a direct control point there: residency (SessionStart can inject boot context and reload the skill listing), paging (UserPromptSubmit and PreToolUse can inject context or rewrite a retrieval's input), eviction (PreCompact gates the lossy-digest compaction; PostToolUse can truncate a tool result before it enters the window), and validation (PreToolUse/PostToolUse can gate or annotate a read — the harness documents age warnings injected when old memories are recalled, which is validation-by-injection). Promotion is the exception: no hook documented at that access date writes the durable store directly; it is reachable only as a side effect (a Stop or PostToolUse hook that writes a file). That a harness's own control surface carves at four of our five joints, and that the fifth is reachable only indirectly, is architectural corroboration — but it is one harness, and a control plane is a designer's choice rather than a measured regularity, so we record it as convergent with the frame, not confirmatory of it. It also locates the interventions a future program would build on this frame (staleness gating at PreToolUse, injection-return measurement at SessionStart/PostToolUse) — under the same rule as all of this program's instruments: gauges before gates. The boot-manifest gauge (§6.1) is already one such hook, used to measure and not to steer.

§4 Where the OS metaphor breaks

The tier/policy vocabulary borrows from operating systems. Four places where the analogy fails, each with a consequence for measurement:

1. Attention tax. In an OS, resident-but-unused pages cost only capacity. In a transformer, every resident token participates in attention: unused residency degrades the computation over the used remainder. Position within a long context measurably changes whether the model uses the information at all ("lost in the middle" [21]), and reasoning performance degrades with input length even when the task is held fixed [22]. Consequence: residency waste is not free slack; it is a per-call cost multiplied by every session, and utilization of the resident set (C27) is a first-order quantity, not housekeeping.
2. Lossy semantics. OS paging is faithful: the page you fault in is the page that was evicted. Agent memory tiers are lossy: summaries, index descriptions, and compaction digests can misrepresent their bodies. This is measured elsewhere for the hierarchical case: BooookScore [23] documents coherence and fidelity failures in hierarchically merged summaries. Validation is therefore truth-maintenance, not bit-rot detection — and a wrong-stop caused by a stale summary is a correctness failure, not a performance failure. The frame carries a candidate mechanism for this policy slot: invalidate-on-write, revalidate-on-read — staleness flags set cheaply on dependents at write time, reconciliation deferred to the next access, so maintenance work is bounded by what is actually read rather than by what changed. Whether deferred revalidation beats eager reprocessing on total maintenance tokens and wrong-stop rate is an open economics question, named in the governing program as an unregistered candidate conjecture (docs/BUILD-agent-memory-allocation-v1.md §M3); nothing here anticipates its outcome.
3. Statelessness. There is no CPU state between calls; the model restarts from tokens every time. Everything is memory, and the boot image is the whole machine at t=0 of every session. This is why the configured tier dominates the economics and why its absence from the literature matters.
4. Ownership and audience. OS memory has no notion of whose a page is. Operational tiers do: team-facing docs, private tracking, per-user memory (Workspace-P/AGENTS.md separates these explicitly). Allocation policies that ignore audience produce leaks or noise; the property has no OS analogue and is carried on the tier, not the object.

The cost side of these policies is concrete, not hypothetical. One sidecar-handle specimen in this estate runs ≈5× metadata-to-content by line count — a 253-line handle wrapping ~40 lines of carried content — with its quality fields (confidence_score, conceptual_density, usage_frequency) self-assigned by no stated estimator (mentu-physics/foundational/blueprint/heap/heap/architecture/handles/ architecture-of-attribution.handle.yaml; docs/BUILD-agent-memory-allocation-v1.md §Grounding). Curation at this ratio is an authoring cost that any layered-disclosure policy must amortize — the term C29's design prices explicitly — and unestimated quality numbers are the failure mode this program bans in its own outputs (BUILD constitution rule 6: a number without an estimator or a source path does not appear).

§5 The falsification program

Registered 2026-07-18 (commit 4b86195) before any probe existed. Predictions were frozen at registration; probes run only from analyzers committed before their first output, over a corpus manifest frozen at the registration commit; negative and ambiguous results are reported as-is. The program can refute the frame, and §7 records the extent to which — as seen — it already has. Claims, predictions, and falsification criteria below are transcribed verbatim from the registered conjecture files (formatting compressed; wording exact). Status lines give the adjudication state as of 2026-07-19; the results are §6.

§5.1 C26 — residency-determined return

corpus/conjectures/c26-residency-determined-return.md; staged against C7. Status: probe run 2026-07-18 → instrument insufficient (coverage floor); estimates recorded, §6.3.

Claim (frozen): "The probability that a stored knowledge object is ever returned to is determined primarily by its allocation tier — boot-resident (T0), pointer-resident (T1), paged-searchable (T2), store-tier (T3) — with order-of-magnitude separation between adjacent tiers, and only secondarily by the richness of its descriptive handle (type, lineage, scope, tags, summary). Reachability is a function of position in the load order, not of representational quality: the resident set returns by construction, indexed content returns when its pointer is exposed, and everything deeper returns only when an associative search or an exposed pointer reaches for it. […] C7 claims a richer handle makes an artifact more returnable; C26 claims that once tier is controlled, richness adds little — the cliff between tiers dwarfs any gradient within them. Both can be partially right; the conjecture is about which effect is first-order."

Predictions (frozen 2026-07-18): P1 (ordering) — "ever-exercised fraction is strictly ordered T1 > T2 > T3, in every month cohort with ≥30 objects per tier." P2 (cliff magnitude) — "each adjacent gap is ≥10× (T1/T2 ≥ 10, T2/T3 ≥ 10), hence T1/T3 ≥ 100×, against the frozen T3 baseline of 0.0222%." P3 (richness is second-order) — "within T2, the rich/sparse ever-exercised ratio is ≤3×, and strictly smaller than both adjacent between-tier ratios." P4 (mechanism) — "≥70% of T2 exercises have a visible search or resident-pointer antecedent; 'spontaneous' access is the minority path."

Falsification (frozen): "P1 ordering violated at any adjacent pair (with coverage floors met) → refuted. Within-tier richness ratio ≥ either adjacent between-tier ratio → refuted in favor of C7's mechanism (annotation, not allocation, is first-order). Between-tier gaps exist but are <10× → revised: tier matters but the cliff framing is wrong; the frame's 'orders of magnitude' language must be withdrawn. Tier assignment or eligible-session denominators cannot be computed deterministically from the manifest → instrument insufficient, no verdict."

§5.2 C27 — resident-set utilization

corpus/conjectures/c27-resident-set-utilization.md. Status: probe run 2026-07-18 → instrument insufficient (coverage floor); estimates recorded, §6.1.

Claim (frozen): "The boot-resident allocation of a modern agent harness is mostly unexercised. The skill catalog — every listed skill's name and trigger description, paid into context at every session start — follows a steep concentration law: a small head of skills accounts for nearly all invocations, a majority of listed skills are never invoked at all, and most sessions invoke none. The resident set is sized by accretion (what has been installed), not by utilization (what gets used), and the gap between the two is the harness-tier analogue of structural waste: attention paid every session for capability that never fires. This does not claim the listing is worthless — an uninvoked skill may still shape behavior by existing in context (a visibility effect this instrument cannot see, declared below). It claims the invocation distribution, the one measurable utilization signal, is extremely concentrated."

Predictions (frozen 2026-07-18): P1 (dead majority) — "≤15% of the catalog (union denominator; ≤20% under per-session denominators) is ever invoked across the frozen corpus." P2 (concentration) — "the top-5 invoked skills account for ≥60% of all invocations." P3 (quiet sessions) — "≥60% of interactive sessions invoke zero skills." P4 (waste share) — "never-invoked skills account for ≥70% of catalog-listing tokens paid across the corpus (computable only under denominator 1; otherwise reported as a bounded estimate with the bias direction stated)."

Falsification (frozen): "Ever-invoked fraction >40%, or top-5 share <30% (utilization broad and flat) → refuted; the resident set is earning its keep and the 'dead boot image' framing must be withdrawn from the paper. P1 holds under the union denominator but fails under per-session denominators → revised: concentration is an artifact of catalog growth, not of utilization behavior. No denominator recoverable → instrument insufficient."

§5.3 C28 — promotion-lane returnability

corpus/refuted/c28-promotion-lane-returnability.md. Status: probe run 2026-07-18 → refuted; graduated to corpus/refuted/, §6.2.

Claim (frozen): "Promotion works, and it works through pointer residency. A fact written to the durable memory directory (<project>/memory/*.md) and indexed in the boot-loaded MEMORY.md returns in later sessions at rates orders of magnitude above ambient paged artifacts — because promotion buys a resident pointer, not because the content is better. The promotion policy is the one working return lane in the current allocation architecture: capture-without-promotion goes to T2/T3 and effectively never returns; capture-with-promotion goes to T1 and does. The corollary claim: memory files that lack an index line in MEMORY.md (orphans) return at rates far closer to ambient T2 than their indexed siblings — same directory, same content class, no pointer — which would isolate the pointer as the active ingredient."

Predictions (frozen 2026-07-18): P1 (the lane works) — "≥25% of memory files with ≥10 eligible sessions are re-read at least once within the corpus window." P2 (rate, commensurable with T3) — "the median per-file subsequent-session read rate is ≥1% — ≥45× the frozen T3 organic access baseline (0.0222%)." P3 (the pointer is the ingredient) — "indexed files are re-read at ≥3× the ever-re-read fraction of orphan files, given ≥20 orphans exist in the corpus; with fewer than 20 orphans this prediction is reported as not evaluable." P4 (bounded, not resident) — "the promotion lane stays well below T0 — the median per-file session read rate is <20%; promotion buys reachability, not omnipresence. […]"

Falsification (frozen): "Ever-re-read fraction ≤10% and median rate ≤10× the T3 baseline → refuted: the promotion lane does not function as a return mechanism, and the paper's 'promotion works via pointer residency' line must be withdrawn — with the allocation-tier frame (C26) then predicting the harness's memory feature is mostly ritual. The lane works but the indexed-vs-orphan contrast is absent (<1.5×) → revised: promotion works through some channel other than the pointer (e.g., content quality or recency), weakening C26's mechanism story. Creation times or index membership cannot be reconstructed deterministically → instrument insufficient."

§5.4 C29 — curation-vs-search sufficiency

corpus/supported/c29-curation-vs-search-sufficiency.md. Experimental; hard order gate: harness code + frozen hashed question set + pinned model identifiers committed before any policy run. Status: adjudicated 2026-07-19 → supported; graduated to corpus/supported/, §6.5.

Claim (frozen): "For repo-scale retrieval tasks, associative search over raw content followed by full reads (grep-then-read — the reigning deployed policy in coding agents) matches curated layered disclosure (authored frontmatter/summary tiers read cheapest-first) on answer accuracy, at a token cost within the same order of magnitude — and disclosure pays for its token savings with wrong-stops: answers issued from a summary tier when hydration was actually required. If so, the marginal value of authoring and maintaining resolution layers is small wherever content is greppable, and curation investment is justified only where associative search is weak (non-textual content, cross-file synthesis, naming that diverges from content). […] It is deliberately stated in the search-sufficiency direction — the direction the return-cliff evidence points — so that a disclosure win refutes it cleanly and vindicates the curation doctrine deployed in practice."

Predictions (frozen 2026-07-18): P1 (accuracy parity) — "B's accuracy ≥ C's accuracy − 3 percentage points." P2 (token order) — "B's total tokens ≤ 2× C's unamortized tokens." P3 (wrong-stop tax) — "C's wrong-stop rate ≥ B's wrong-answer rate." P4 (both are far from optimal) — "B and C each spend ≥3× D's tokens — the headroom claim that motivates allocation-policy research regardless of which policy wins."

Falsification (frozen): "C beats B by >3pp accuracy at ≤0.5× B's tokens (amortized) → refuted: curation is vindicated as dominating, and the paper must present layered disclosure as the superior policy wherever layers exist. P1 holds but P2 fails by >5× → revised: search is accurate but token-profligate; the trade is real and regime-dependent, not a sufficiency. Question-set contamination discovered (generator leaked summary content, or any policy run preceded the frozen hash commit) → the run is void; regenerate under a new dated harness. No partial salvage."

§6 Results

All probes ran against one frozen corpus manifest (analyses/shared/transcript-manifest-2026-07-18.json, frozen at the registration commit 4b86195: 2,337 transcripts, 453 memory files, 251 pre-freeze skill files, 102 workspace files, each entry prefix-hashed — zero integrity failures across every probe). Every analyzer was committed before its first output; adjudication is mechanical against §5's frozen criteria. Program scoreboard: one supported (C29), one refuted (C28), two instrument-insufficient with recorded estimates (C27, C26), one descriptive census (M2.4). Where a coverage floor failed, the estimates below are recorded as seen — which permanently disqualifies them from justifying any later floor amendment.

§6.1 C27 — instrument insufficient (coverage floor)

The frozen gate requires ≥500 interactive sessions; the corpus holds 156, because 93% of the transcript corpus is headless recipe runs (2,166 of 2,322 classified sessions; 2,166 + 156 + 15 empty-excluded = the manifest's 2,337). Point estimates at n=156, not verdict-bearing, with no refutation trigger: ever-invoked share of the catalog 6.8% union / 9.6% restricted (P1 thresholds ≤15%/≤20%); top-5 invocation share 62.5% (P2 ≥60%); interactive sessions invoking zero skills 82.1% (P3 ≥60%); dead-listing token share ≈93% of an estimated ≈10.6k listing tokens per session (P4, bounded estimate under the declared-biased union denominator). The listing-token estimator, omitted from an earlier draft and named here because the governing constitution requires it: (len(name) + len(description)) / 4.0 summed over the 161-entry union catalog, giving 10,590.2 (analyses/c27-resident-set-utilization/analyze.py:228); it is a characters-divided-by-four heuristic over one catalog snapshot, not a tokenizer count.

The P2 concentration figure needs its denominator, and it does not survive one. The 62.5% is 10 of 16 catalog-matched invocations. Moving a single invocation from head to tail gives 9/16 = 56.3%, below the frozen 60% floor. The corpus in fact holds 44 invocation events; 28 of them failed to match the union catalog, and one unmatched name (scaffold, 10 invocations) is invoked more often than any matched skill. Under the all-events denominator the top-5 share is 21/44 = 47.7%, below the floor. So P2's direction is an artifact of the catalog-matching rule, and an earlier draft's description of all four estimates as "directionally with the predictions" is withdrawn for P2. P1, P3, and P4 are unaffected. None of this moves a verdict: C27 is instrument-insufficient at the session floor regardless. Instrument yield: per-session catalog reconstruction is permanently unavailable retroactively — system prompts are not stored in transcripts (listing blocks in 2 of 2,337) — so the per-session denominator exists only forward, via the boot-manifest gauge deployed 2026-07-18 (instruments/2026-07-18-boot-manifest-gauge.md); the union catalog undercounts built-in and recipe-layer skills (15 unmatched invoked names). Source: results/2026-07-18-c27-resident-set-utilization.md.

§6.2 C28 — refuted

Population per the frozen definition (≥30 days of post-creation corpus, ≥10 eligible same-project sessions): 157 files; the ≥100 floor passed. Measured: 2 of 157 files ever re-read (1.27%) against P1's ≥25%; median eligible-session read rate 0.0% against P2's ≥1%. The frozen refutation trigger (ever ≤10% AND median ≤10× T3) fired; the conjecture is refuted and graduated to corpus/refuted/. The headline count is 2 of 157, on the registered population; of the full 453-file corpus, the remaining 296 files had not met the frozen eligibility rule and were not yet testable. (An earlier draft stated this result a second time as "451 of 453", which silently extends the claim to those 296 untestable files. That form is withdrawn.) Note also that §6.3 reports 43 of these same 453 objects as ever-exercised under C26's looser frozen measure; the two numbers describe the same files under two different frozen definitions, and the gap between them is itself analyzed in §6.3. The indexed-vs-orphan contrast (P3) read 2.25% (2 of 89 indexed) vs 0.0% (0 of 68 orphans). Mechanically this passes P3 as registered: the frozen not-evaluable branch fires below 20 orphans and the corpus holds 68, so the analyzer's recorded ratio (inf) clears the ≥3× bar. The pass carries no information. The ratio is undefined at an orphan numerator of zero, the whole contrast rests on two readers against none, and Fisher's exact test on the 2×2 table gives p = 0.51. It is reported because it was registered, and it should be read as an untested prediction rather than a confirmed one. Channel caveat, recorded and non-exculpatory: the registered limitations declared that the tool-Read channel undercounts (index-only recall and harness reminder injection are invisible to it) and accepted that bias as running against P1/P2, so the refutation stands under the frozen terms; the analyzer counted 18,780 non-tool mentions of memory files against 2 tool reads, making injection-channel returnability a registrable successor. That successor is now registered (c28b, registration commit 5cdebb9, 2026-07-22), forward- adjudicated after its boundary and measured by channel-agnostic content-fingerprint reuse — a feasibility probe first ruled out the injection-event instrument, since the push channel is largely non-persisted; its outcome is not anticipated here, and a refutation would generalize C28's result to both channels. One recorded honesty note: the conjecture's single motivating instance occurred in this program's own excluded session — the example was the observer. Source: results/2026-07-18-c28-promotion-lane-returnability.md.

§6.3 C26 — instrument insufficient (coverage floor); ordering inverted as seen

The frozen gate requires ≥500 eligible interactive sessions; this analyzer counts 160 (it counts all hash-verified transcripts; C27's excluded 15 empty ones — both rules live in the committed analyzers). The other floors passed (T1 614 objects, T2 102, cohorts ≥2). Point estimates at n=160, not verdict-bearing — interactive stratum, ever-exercised fraction:

Figure 1. Ever-exercised fraction by tier (log scale). The residency-depth ordering the frame predicted (T1 > T2) is inverted in these estimates, and the three-order-of-magnitude cliff is to the tool-gated store, not between adjacent filesystem tiers. T1/T2 are recorded at n=160 and are not verdict-bearing; T3 is the frozen pre-registered baseline; T0 is ~100% by construction. The T1/T2 inversion is substantially carried by reads performed by the sessions that were editing those files, and does not survive as a tier finding; the T2/T3 gap does. See the edit-channel diagnostic below.

P1's ordering is inverted as seen: T2 exceeds T1 by ~3.7× (gap_T1_T2 = 0.27 against the predicted ≥10). T2/T3 = 1,457×. P3 held as seen: rich (n=55) 32.7% vs sparse (n=46) 30.4% within T2 — ratio 1.08, far under the 3× bound and under every tier gap; the risk-ratio 95% confidence interval is 0.60–1.92 (Fisher p = 0.83), so the data are consistent with the ≤3× bound and equally consistent with no effect at all. The frozen richness rule scores rich at ≥3 anchors and sparse at ≤1, so one mid-band T2 file falls in neither arm (55 + 46 = 101 of 102). P4 held at 100%: all 93 T2 read events had an in-session antecedent; zero spontaneous path recalls. The antecedent window is anywhere earlier in the same session, not immediately preceding the read (analyze.py:227–239), which is the weak reading of "mediated" and is stated here because a perfect 100% over 93 events invites the stronger one. Headless stratum, reported and never pooled: T1 memory 1.77% (8 of 453), skills 0% (0 of 161), T2 0% (0 of 102), across 2,176 headless sessions (2,176 + 160 interactive + 1 unclassified = the manifest's 2,337); these are measured zeros (zero_events), not unexercised tiers. The estimates were seen at n=160; only a covered re-run adjudicates. Source: results/2026-07-18-c26-residency-determined-return.md.

The inversion is substantially an edit-channel artifact. C26's frozen "ever-exercised" counts any access, including reads by the creating or editing session, since the harness requires a Read before an Edit. This was declared at registration and is a deliberately looser measure than C28's post-creation returns. An earlier draft then argued that "the T1-vs-T2 comparison is internally consistent because both sides use the same definition." That inference is withdrawn: it does not follow. An identical definition on both sides does not equalize the two sides' exposure to the channel that definition admits, and here the exposure is grossly unequal by construction. T2 is 85 operational notes from a live client engagement plus 17 methodology documents, hand-authored and under active editing during the very window being measured. T1's 453 memory files are harness-written promotion artifacts which, as §6.2 establishes, are essentially never returned to.

A post-hoc diagnostic quantifies it. Reproducing C26's exercise rule and adding one classifier the frozen analyzer does not compute (whether the same session also issued a write-class tool call against the same path), interactive stratum:

Restricted to objects never written in the window: T1 0 of 410, T2 2 of 27. Three readings. The differential exposure is real and large (73.5% of T2 objects were edited in-window against 9.5% of T1 memory files, measured over the same sessions). On recoverable data the edit channel carries essentially the whole T2 signal: 21 of the 23 exercised T2 files are exercised only by sessions that also wrote them, and 91 of 93 recoverable T2 read events are edit-linked. And once the channel is excluded both tiers collapse toward zero, so the contrast stops being evaluable rather than reversing: 2 files against 0 files is not evidence of an ordering in either direction. The deconfounded picture is §6.2's picture, on both tiers.

Bound on the diagnostic, which is severe. It runs on 341 of the manifest's 2,337 transcripts, because the rest no longer exist (§7 Limits (g)). That is 51% of the interactive stratum. It recovers 23 of the frozen 33 exercised T2 files (70%) but only 11 of the frozen 43 exercised T1 memory files (26%), so it under-recovers T1 more than T2, which is the direction that would flatter the deconfounded reading. The diagnostic establishes that the confound exists and is large. It cannot establish the deconfounded rates, it amends no verdict, and under this program's rules it can never justify a floor amendment. What the frozen measure measures is: was this object touched by an agent session, by any route including the session that wrote it. The T2/T3 contrast is unaffected, because both sides of it are any-access measures and the store tier admits no edit channel of this kind. The T1-versus-T2 inversion does not survive as a statement about allocation tier.

§6.4 M2.4 — curation-cost census (descriptive; a statistic, never a verdict)

Line-count estimator, committed in analyses/shared/curation_cost_census.py; manifest artifacts only:

The estate's heaviest metadata investment — memory files at a median 0.53 metadata lines per content line, 100% frontmattered — sits on the lane whose returns §6.2 refuted. That much the census supports, and it is the whole of what it supports. The curation literature reports the same tension from the practitioner side: documentation issues are dominated by content and maintenance problems rather than by absence [24, 25].

A claim withdrawn here. An earlier draft continued the sentence above with "while the T2 corpus with the highest seen exercise rate (§6.3) carries no frontmatter at all." No per-corpus T2 exercise rate exists in §6.3, which reports one pooled figure over all 102 files, and the comparison was therefore unevaluable as printed. Computed on the surviving remnant (same bound as §6.3), it also points the other way: of the two T2 corpora, Workspace-P (85 files, 66% frontmattered) accounts for 23 exercised files, 27.1%, and the epistemics corpus (17 files, 0% frontmattered) for 0, 0.0%. The entire recoverable T2 exercise signal comes from the frontmattered corpus, which is also the corpus with 88.2% of its files edited in-window (§6.3). The sentence is deleted rather than qualified. Source: census section of results/2026-07-18-c26-residency-determined-return.md.

§6.5 C29 — supported at full coverage

Order proof by commit chain: DESIGN + harness (5572eba) → question set and index frozen by hash (5d63e0a; sha256[:16] 8f39408f324ffb84 / c84e20581f36936f) → first policy run. 102 questions (81 lookup / 21 synthesis; 85 Spanish operational notes / 17 English methodology docs), every answer mechanically validated as an exact body substring; the generator (claude-sonnet-5) saw frontmatter-stripped bodies only; the answerer was pinned (claude-haiku-4-5-20251001); every call ran --no-session-persistence so the experiment wrote no transcripts into any future corpus. Two infrastructure retry passes under the committed mechanical rule (only error-flagged records retried; scored answers never re-rolled): 71 provider session-limit refusals, then 24 subprocess timeouts (cap 420→900s, concurrency 6→3, amendment committed pre-verdict). Final coverage: 102 scored per policy, 0 errors.

Three columns here changed in the current revision, all from quantities the committed run records already carried. Error rate is added because the abstract compared B and C on it while the paper reported only C's wrong-stop rate, which is a subset of C's errors rather than C's error rate; the apples-to-apples comparison is 27.5% against 52.9% (Fisher p = 0.0003), and it is stronger than the frozen P3. The cache-read share is added because the two token columns are not on a common price basis without it: marginal tokens exclude cache reads, and cache reads are 90% of B's total against 30% of A's, so the two columns rank the policies differently for reasons that have nothing to do with policy. Marginal tokens are the policy-attributable measure; totals are inflated by nested-CLI overhead that differs by arm, as the committed harness notes at the point where it separates the components (harness_lib.py:160–167). The cost column is withdrawn. Recorded per-call cost_usd is provider-reported and we could not reproduce it from list prices (reconstruction gives $4.79/$4.63/$4.77/$1.15 against the recorded $7.32/$6.00/$6.49/$1.63), so "B is cheapest at $6.00" is not a claim this table can carry. C's authoring cost stands separately at 1,307,300 generator tokens, reported amortized and unamortized in the effect table as the frozen text requires.

A defect in the method, disclosed. P2's frozen text names its measure ("B's total tokens ≤ 2× C's unamortized tokens"); P4's does not name one. Adjudicated on totals, P4 passes at 9.1× and 6.5×. Adjudicated on marginal tokens, B spends 1,948,295 against D's 683,496, which is 2.85×, and P4 fails for B. The recorded verdict stands as adjudicated, because the adjudication that was made is the adjudication that was frozen; but a program whose second contribution is mechanical adjudication against criteria fixed in advance cannot leave a prediction whose outcome flips with an unfrozen metric choice, and this one did. The rule is recorded for the program: freeze the measure with the threshold. The oracle-headroom claim is reported hereafter as holding on totals only.

These outcomes are the result on this corpus. The released kit's public demonstrator falls below the frozen scored-question floor and adjudicates nothing (§7 Limits (b)).

C34 — the public replication at power

C29's evidence is 408 run records over a corpus that is 85% third-party client material and cannot be released. C34 is the successor registered to fix that: 141 releasable documents selected by a frozen mechanical rule, snapshotted at the byte, 120 confirmatory questions, the same pinned answerer, and three criteria deliberately made harder than C29's — a symmetric wrong-stop rule, a token-headroom prediction frozen on marginal tokens (the measure under which C29's own B would have failed), and an added localization prediction. It was registered before any harness code, corpus snapshot, question or provider call existed.

Verdict: revised, machine reason headroom_not_established_on_marginal_tokens; adjudicator replays byte-identical; floors 120/120/120 scored; zero contamination findings (results/2026-08-14-c34-public-curation-vs-search-replication.md).

Three things follow, and the third is the one the program owes itself.

First, the curation-vs-search finding replicates on a corpus a reader can hold in full, at +12.5 pp rather than +25.5 pp — a smaller effect on a different corpus, in the same direction, under stricter rules.

Second, the symmetric wrong-stop rule vindicates the correction it encodes. C29's original P3 compared C's wrong-stop rate against B's wrong-answer rate — a subset against a superset. On C34's data that asymmetric form would have read C 34.2% against B 36.7%, making the curated index look better; the symmetric rule shows it wrong-stopping at nearly twice B's rate. The original comparison did not merely understate the tax. On this corpus it would have reversed the reading.

Third, the defect this paper disclosed above is exactly what failed. §6.5 recorded that P4's measure was not frozen and that the outcome flipped with the choice, and set the rule: freeze the measure with the threshold. C34 did so, chose marginal tokens — the harder reading, the one C29's B failed — and P4 failed again, at 1.84× and 2.73× against the 3× bar. A prediction that fails under a measure fixed in advance is a finding; the same prediction passing under a measure chosen afterward would have been an artifact. The verdict word is revised because of it, and the curation-vs-search answer is reported at equal prominence beside that word rather than beneath it.

Figure 2. Accuracy vs. marginal token cost per retrieval policy (102 frozen questions, pinned answerer). Grep-then-read (B) is both more accurate and cheaper at the margin than curated index-then-hydrate (C). D is a minimal-sufficiency approximation at file granularity, not an upper bound: a subset of C exceeds it (see below). A is budget-bounded rather than informative: its 100,000-character dump reached only 4 of the 102 corpus files, so its attainable ceiling was 3.9%. C's position is paid for by mis-routing, not by early stopping. Measured on this corpus; the public demonstrator is below the frozen floor and adjudicates nothing (§7 Limits (b)). The C34 public replication reproduces B's accuracy and localization advantages on a releasable corpus at power (+12.5 pp; 75.0% vs 62.5% localization), and fails P4's headroom prediction on marginal tokens — the measure this paper's own disclosure said should have been frozen (§6.5).

Where C's accuracy goes. C answered 49 of 102 questions without ever reading the gold file, and 47 of those 49 were wrong (96%). An earlier draft read this as the policy trusting the digest and stopping. The run records say otherwise, and the reading is withdrawn. Of those 49 questions, only 5 involved reading no file at all; the other 44 read at least one file, the wrong one. Of the 47 wrong-stops, 43 read a wrong file and 4 read nothing. Over the full question set C issued 192 Read events to B's 174, and located the gold file on 53 of 102 (52.0%) against B's 82 of 102 (80.4%). A policy that reads more and finds less is not stopping early. It is being mis-routed by its index.

Decomposing C by whether it located the gold file:

Conditional on locating the file, C is not worse than B and is not worse than the oracle approximation. But this conditioning is on the outcome of the thing under test: C's tool set is Read only (DESIGN.md D5), so the authored index is C's sole locator, and "C when it read the body" is "C when the index worked." The selection is nonetheless characterizable, and it is not question difficulty. On the same 102 questions restricted to C's two subsets, D scores 43 of 53 (81.1%) where C located the file and 41 of 49 (83.7%) where it did not (Fisher p = 0.80): given the right file, the questions C missed are just as answerable. B scores 42 of 53 (79.2%) and 32 of 49 (65.3%). C's deficit is a localization deficit of the authored index, not a comprehension deficit and not a stopping rule. Two corollaries. First, D is not a ceiling: on the matched 53, C scores 46 against D's 43, because there C holds the gold file plus the index plus whatever else it read while D holds the gold file alone, truncated at 60,000 characters. The excess is not significant (McNemar exact p = 0.51), and the frozen conjecture already declared D an approximation rather than true optimality; only an earlier draft's prose called it a ceiling. Second, the successor arm suggested by an early-stopping reading (index to locate, always hydrate) is bounded by these data to at most the 5 zero-read questions, of which 4 were wrong, giving a maximum attainable 51.0% and leaving B's margin intact. The arm the data motivate is index-plus-search, and it is a future pre-registration.

A symmetric wrong-stop comparison, which frozen P3 does not make: P3 as registered compares C's wrong-stop rate to B's wrong-answer rate, a subset against a superset. Applying C's own frozen wrong-stop rule to B (incorrect and never read the gold file), B is 13 of 102 = 12.75% against C's 46.08%, a ratio of 3.6×. This is descriptive, not adjudicative, and it is a cleaner statement of the same phenomenon.

Arm validation for A, owed and not previously given. Reconstructing the flat-load prompt from the frozen manifest and the committed dump builder (sorted-path order, 100,000-character budget), the dump reaches 4 of the 102 files, and the gold answer string is present in it for 4 of 102 questions. A's attainable ceiling was 3.9%; it scored 3 of 102, which is 3 of the 4 questions it could possibly answer. The truncation was declared in DESIGN.md D5 ("corpus exceeds it by design") but its magnitude was not reported, and an earlier draft read A as informative about flat loading. It is not. A is a budget-bounded baseline and supports no claim about flat loading, including the "useless" characterization now removed from Figure 2. P4's headroom claim does not depend on A and is unaffected.

Regime map (a report owed by the conjecture's registered limitations): B beats C on lookup (72.8% vs 49.4%, n=81) and on synthesis (71.4% vs 38.1%, n=21) — the hypothesized regime where hierarchy helps synthesis questions does not appear in this data. The synthesis arm is underpowered at 21 questions and carries correspondingly less weight than the lookup arm. Corpus-language map, added in the current revision because the demonstrator's non-reproduction was attributed to it: on the paper's own 102 questions, B minus C is +29.4 pp on the 17 English documents (B 12/17, C 7/17) and +24.7 pp on the 85 Spanish ones (B 62/85, C 41/85). The margin is larger on the English slice. Language does not explain the demonstrator's tie (§7 Limits (b)). Conjecture graduated to corpus/supported/. Source: results/2026-07-19-c29-curation-vs-search-sufficiency.md.

§7 Discussion and limits

What failed as seen, and what failed about the measurement. The frame's central empirical prediction — return ordered by residency depth, T1 > T2 > T3 — is inverted in the recorded C26 estimates: searchable content with no boot pointer was exercised ~3.7× more than pointer-resident content (§6.3). Two things must be said about that inversion, and an earlier draft said only the first. Because the coverage floor failed, it is not a verdict; the covered re-run (registered path: ≥500 interactive sessions, roughly 3–4 months of gauge-assisted accrual, or a dated floor amendment justified independently of the seen estimates) adjudicates it. And because the frozen measure admits reads by the editing session, to which the two tiers are grossly unequally exposed (73.5% of T2 objects were edited in-window against 9.5% of T1 memory files), the inversion is substantially an artifact of which objects the operator was writing, not of allocation tier (§6.3). Deconfounded on recoverable data both tiers collapse toward zero and the contrast stops being evaluable. This is the sharpest self-correction in the program and it cuts against its own headline negative result: the measurement that produced "what failed as seen" was itself partly measuring something else. If the inversion holds on a covered and deconfounded re-run, C26 is refuted as registered and the successor question — already visible in the seen data but claimed nowhere in this paper — is whether search-reachability, not residency depth, is the first-order variable. That question is now registered as its own frozen conjecture (c26b, registration commit 97be394, 2026-07-22): its predictions were frozen before any of its adjudication data existed, the seen estimates that generated the hypothesis are barred from adjudicating it, and its corpus is restricted to sessions after the registration boundary. Nothing here pre-judges its outcome — including the possibility that c26b is refuted and C26's original ordering is rehabilitated on covered data.

What held as seen. The one C26 result that survives at scale is the cliff between the greppable filesystem and the tool-gated store: three orders of magnitude in the seen estimates (T2/T3 = 1,457×), consistent with the frozen endpoint measurements in §1, and untouched by the edit-channel confound because both sides of it are any-access measures. The other two held results are weaker than an earlier draft presented them. Richness is second-order where measured (P3: rich/sparse ratio 1.08 within T2), but the interval is 0.60–1.92, so the stake staged against C7 survives only in the sense that the data do not contradict it; they also do not distinguish it from no effect. Access is overwhelmingly mediated (P4: 100% of 93 T2 reads had an in-session antecedent), but under an anywhere-in-session antecedent window, in a harness that requires a Read before an Edit, with 91 of 93 recoverable T2 read events edit-linked; under those three facts "zero spontaneous path recalls" is substantially a property of harness affordances rather than of memory behaviour, and the stronger claim needs an immediate-antecedent instrument that does not yet exist. C29's wrong-stop anatomy (§6.5) measures a known failure mode in a new place: that models issue confident wrong answers rather than abstaining when their context is insufficient is established for retrieved context [26], and what §6.5 adds is the same failure measured against an authored digest tier, under pre-registration, with mis-routing rather than non-abstention as the dominant path. That is the failure mode the invalidate-on-write / revalidate-on-read candidate (§4) exists to address — an economics question that remains open and unregistered (c30 candidate; outcome not anticipated).

Practice implications, gated and re-scoped. The verdicts license no configuration change by themselves. Under the program's rule — gauges before gates — the two data-backed candidates are queued as future pre-registrations, each requiring its own frozen predictions and its own gauge before any behavior in the estate changes. Their scope is narrower here than in the earlier drafts. The first was stated as "retiring digest authoring for greppable corpora." What C29 tested is an authored one-line-digest index used as a policy's sole locator, against grep as a sole locator; C had no search tool at all. The finding is that authored digests route worse than grep (52.0% against 80.4%), not that digests are worthless alongside grep, which was not tested. The candidate is re-scoped accordingly, and the arm that would settle it (index-plus-search) is named as the registrable successor. The second candidate, redesigning or retiring the memory-promotion lane, rests on C28's refutation and is unaffected by any of the above. This paper recommends no threshold it has not gauged, including thresholds its own results appear to support.

The meta-method is the second contribution, as an instantiation. Pre-registration of computing experiments is not new, and this paper does not claim to import clinical norms into systems research: registered reports [27], the HARKing analysis and preregistration protocol for CHI experiments [28], the preregistration literature more broadly [29, 30], reproducibility programs at ML venues [31], and per-method empirical standards for software engineering [32] all predate it. What is offered as a contribution is the specific combination, instantiated end to end: analyzers committed before their first output; corpora frozen by content hash; the commit chain as order proof; retry rules that never re-roll a scored answer; floors enforced even when the seen estimates favored the registered predictions (twice); and seen estimates permanently disqualified from justifying later floor changes. Two parts of that discipline are worth naming honestly. The first adversarial review this manuscript was hardened against was commissioned by the author (EXTERNAL-REVIEW-2026-07-22.md), as was the second (EXTERNAL-REVIEW-2026-08-12.md, dispositioned in DISPOSITION-2026-08-12.md). C29 has now survived a refutation attempt, and did not survive it unchanged: the attempt correctly identified that the paper's public demonstrator fails the frozen P3, and prompted the decomposition that replaced §6.5's stopping-rule mechanism with mis-routing and invalidated the flat-load arm. But both reviewers were commissioned, so the independent-stake condition is still unmet. Second, one refuted conjecture's motivating example was identified as observer contamination and recorded as such (§6.2); the same issue recurs, and an earlier draft did not flag it, for the 17 epistemics methodology documents, which serve simultaneously as C26 T2 objects, §6.4's zero-frontmatter census row, C29's English arm, and the public demonstrator's entire corpus. These are the documents in which this program was being written, during the window in which it measured them, by the operator whose behaviour is the unit of analysis. That is disclosed in Limits (h) rather than defended.

Limits. (a) External validity: every measurement comes from one single-operator ecosystem — one practitioner, one machine, one harness family; portability is argued via the §3 load table, not demonstrated across operators. (b) C29 scope, carried verbatim from its results doc: single-operator corpora with unusually consistent naming (plausibly favors grep); auto-generated questions skew locatable-fact (81 lookup / 21 synthesis — the split is reported and B wins both); D approximates minimal-sufficiency at file granularity; one answerer model at one capability tier — a stronger answerer might extract more from digests (registrable as a follow-on, not assumed). Two further scope conditions are added here: C had no search tool (DESIGN.md D5), so the experiment compares an authored index against grep as sole locators and says nothing about an index used alongside search; and the tested C is a two-tier realization (path plus a one-line digest, then the full body), not the four-layer ladder the conjecture text describes, a design choice recorded in DESIGN.md D1 before the questions were generated.

Every one of these scope conditions survives into C34's public replication, which shares the operator, the repository family, the answerer and the harness lineage: what C34 buys is power, public re-runnability and a corpus a reader can hold, not operator diversity, which remains the named next successor. C34 adds one scope condition of its own, and it generalizes past this program. Its question-generation prompt was byte-identical to C29's, pinned precisely to keep the two comparable — and on the new corpus the same prompt produced a 30% sub-three-word gold-answer rate against roughly 5% on C29's, with three of 120 confirmatory golds so unspecific that the frozen scoring rule could not fail them. Pinning a treatment string is necessary for comparability and not sufficient for it: a replication that carries a generator prompt onto a new corpus should measure the resulting question set's discriminating power before spending its answering budget. C34 flags the affected questions mechanically and reports two sensitivity analyses; neither flips any prediction.

(b′) The public demonstrator, restated. An earlier draft described the released kit's demonstrator (16 questions over 17 English methodology documents; repro-kit/DEMONSTRATOR-RESULT.md) as reproducing the wrong-stop mechanism but not the accuracy margin. That description is withdrawn at all four sites where that draft made it, and it was wrong in three separate ways.

First, adjudication. Run against C29's frozen criteria in the committed adjudicator's own order of operations, the demonstrator returns INSTRUMENT INSUFFICIENT (scored-question floor): 16 scored per policy against a floor of 100. It adjudicates nothing, for or against. Within that, frozen P3 fails and reverses: C's wrong-stop rate is 18.75% against B's wrong-answer rate of 37.5%, a ratio of 0.50 where the prediction requires ≥1. Applying C's wrong-stop rule symmetrically to both policies, B and C are identical at 3 of 16 = 18.75%, with identical localization (12 of 16 each). On this corpus there is no wrong-stop tax of any kind, and the paper should not have used P3's vocabulary for what did appear.

Second, power. At 16 questions per arm the two-sided Fisher power to detect the paper's own effect (72.5% against 47.1%) is 19.0%, and the smallest resolvable difference is 5 questions (31.2 pp). B's 10 of 16 has a Jeffreys 95% interval of 38.3–82.6%, which comfortably contains 72.5%. The demonstrator therefore provides no evidence against the accuracy margin; it is uninformative about it. That draft instead explained the non-reproduction substantively ("the curated index is good enough often enough", "which is corpus-dependent"), selecting a causal account over the statistical one without reporting an interval. The program applies exactly this discipline to its own 21-question synthesis arm and did not apply it here.

Third, independence and the language explanation. The demonstrator's 17 documents are not an external corpus: they are the English half of C29's own 102-file corpus, the same objects that appear as C26 T2 members and as §6.4's zero-frontmatter census row. Same operator, same machine, same harness, same documents, same answerer family, a smaller question set. It is a subsample re-run, not a replication, and the word "replication" is removed from the abstract and from §Data & artifact availability. That also disposes of the language explanation that draft offered: on the paper's own 102 questions the B-minus-C margin is +29.4 pp on the English slice and +24.7 pp on the Spanish (§6.5), so the margin is larger in English, and the demonstrator's 0 pp over the same English documents differs by question sampling and run-to-run variation at n≈16, not by corpus condition. Finally, the demonstrator record's claim that "B, which always reads, has no wrong-stop failure mode" is withdrawn: under C's own frozen rule B's wrong-stop rate is 12.75% on the paper's corpus and 18.75% on the demonstrator's, and B answered with zero Read events on 1 of the paper's 102 questions.

Superseded in this preprint. The demonstrator's role in the public bundle is now filled by C34 (§6.5), which was registered for exactly this purpose: 141 releasable documents against the demonstrator's 17, 120 confirmatory questions against its 16, a scored-question floor cleared with margin rather than missed, and an independent corpus rather than the English half of C29's own. The demonstrator's record and its addendum are unchanged and unretracted — they stand as written, and what follows about their true strength stands with them. What changed is what the public bundle offers a reader: a study that adjudicates, in place of one that could not.

What the demonstrator does support, stated at its true strength: at n=16 it reproduces nothing at the frozen floor, and the one qualitative pattern visible in both runs is that C's non-hydrated answers are overwhelmingly wrong (47 of 49 in the paper, 3 of 4 in the demonstrator). The prediction the paper stakes on external replication is restated in §Invitation accordingly.

(c) Definitional non-commensurability, by design: C26's ever-exercised and C28's post-creation return are different frozen measures; cross-conjecture comparisons in this paper never pool them. (d) Tier-assignment ambiguity: objects straddle tiers (a skill is a T0 pointer plus a T1 body); assignment classifies access surfaces by committed analyzer rules, and the two probes' differing session-count rules (156 vs 160) are disclosed rather than reconciled. (e) What kills the frame, updated: C26 refuted with richness dominating placement would gut the allocation vocabulary's empirical content (the seen estimates run the other way — 1.08 — but the interval is 0.60–1.92 and only a covered run adjudicates); a §3-style load test on further systems requiring residual columns would show the vocabulary incomplete, though the test as run in §3 cannot produce that outcome and the criterion is inert until a pre-committed version is run; C27 refuting residency waste at coverage would unmotivate the boot-image economics. A fourth, added here: if the C26 inversion dissolves under deconfounding on a covered re-run, the frame loses its most prominent negative result and gains nothing, since the deconfounded picture is C28's. The paper commits to publishing any of these outcomes as the result. (f) What this spine does not contain: no store-tier re-measurement (C7/C25 own that tier and C25's accrual window is untouched), no engine changes, no anticipated outcomes for the covered C26/C27 re-runs, the registered c26b/c28b successors, or the c30 candidate.

(g) The frozen transcript corpus no longer exists. Discovered while testing the edit-channel confound (§6.3): 1,996 of the 2,337 transcripts in analyses/shared/transcript-manifest-2026-07-18.json have been deleted from disk. 341 survive, and all 341 verify byte-exact against their frozen prefix hashes (none corrupted, none truncated). All 453 memory files, 102 workspace files, and 251 skill files survive. This is clean deletion, almost certainly harness transcript rotation, and it is not a data-integrity failure. It is worse: it is a permanence failure. C26, C27, and C28 are no longer re-derivable from their own manifests; their effect tables and results documents stand as the record, and the inputs are gone. C29 is unaffected, because its evidence is its own 408 committed run records rather than the transcript corpus. The repository's standing claim that any result can be re-derived against a later state of the data is therefore false for the three retroactive probes, and every diagnostic in this draft that touches transcripts is bounded by the surviving 14.6%. The lesson generalizes and is recorded for the program: hash-freezing proves integrity, not availability; a manifest is not an archive.

(h) Observer contamination beyond the C28 instance. The 17 epistemics methodology documents serve simultaneously as C26 T2 objects, §6.4's zero-frontmatter census row, C29's English arm, and the public demonstrator's entire corpus, and they are the documents in which this program was written during the window it measured. The C26 role is the most serious, because it feeds the edit-channel confound; the demonstrator role makes the public reproduction record non-independent (Limits (b′)).

§8 Related-work boundary

• MemGPT / Letta (arXiv:2310.08560): virtual context management — paging between a bounded window and external storage, driven by the model's own function calls. Occupies: window paging as architecture. Does not: theorize the configured tier, measure utilization of what it pages, or validate staleness.
• MemOS (arXiv:2505.22101): memory-as-OS at system scale, lifecycle and scheduling over memory units. Occupies: the OS framing and lifecycle machinery. Does not: policy-level vocabulary portable across systems, or utilization measurement.
• Pichay (Mason, arXiv:2603.09023): demand paging for context windows; a proxy that detects faults and resolves retrieval handles; measures 21.8% structural waste inside windows across 857 sessions. Occupies: window-tier waste measurement and paging mechanics. Does not: tiers above/below the window; its handles are session-scoped markers, not durable allocations.
• CoALA (arXiv:2309.02427): taxonomy of agent memory by content type — working, episodic, semantic, procedural. Orthogonal axis: CoALA classifies what kind of thing is remembered; this frame classifies where it sits and what that position costs. A CoALA type can occupy any tier.
• Mei et al. (arXiv:2507.13334): the context-engineering survey; owns the term and the taxonomy of window-construction techniques. The window is the object of engineering; the substrate underneath is out of scope.
• ACE (arXiv:2510.04618): evolves the prompt payload itself (playbook bullets, delta merges). Engineers the resident content; does not address addressability, promotion, or validation of anything outside the prompt.
• Memory systems that fill the validation slot (added in the current revision, and they narrow §3's observation 1): MemoryBank [17] (Ebbinghaus-inspired decay and reinforcement over memory strength), Mem0 [18] (extraction plus consolidation over stored items), A-MEM [19] (link evolution and memory update as new items arrive), Generative Agents [20] (recency-weighted retrieval and reflection, which is promotion under another name). AIOS [33] is a second OS-framing system alongside MemOS.
• Sufficient context [26]: formalizes whether retrieved context suffices to answer, independently of whether the answer is correct, and reports that strong models issue incorrect answers rather than abstaining when it does not. This is the nearest published statement of §2.4's minimal sufficient context C*(τ) and of §6.5's wrong-stop finding, and it is prior. What §6.5 adds is the same failure measured on an authored digest tier rather than a retrieval tier, pre-registered, with mis-routing rather than non-abstention as the dominant path.
• RAPTOR [34]: recursive abstractive summary trees over a corpus, retrieved at multiple levels. This is the closest published rival to C29 and was seed-flagged in an earlier draft rather than named. The difference: RAPTOR's layers are derived and optimized for retrieval, C29's are authored as deployed practice; RAPTOR measures retrieval quality, C29 measures wrong-stops and end-answer accuracy against an oracle approximation.
• Search-then-read sufficiency: Agentless [35] shows simple localize-then-repair matching or beating agentic machinery at repo scale, and SWE-agent [36] shows the search/read interface itself determining agent performance. The sufficiency of grep-then-read relative to elaborate machinery is therefore an established empirical result, not one this paper introduces; C29's contribution is the head-to-head against authored curation under pre-registration.
• Residency versus paging economics: CAG [37] compares preloading a corpus into context against retrieval on cost and accuracy, and Xu et al. [38] compare retrieval against long-context preloading. These are the A-versus-B comparison of §6.5 in the published literature. Neither has a curated-tier arm, neither measures wrong-stops, and neither is pre-registered, so they do not preempt C29; but §8's earlier claim that the nearest cross-system treatments "review externalization broadly" was not accurate while these exist, and is corrected.

Three claims this leaves unoccupied, which are this paper's territory. Each is stated at the granularity that survives the closest published neighbor, and each is narrower here than in the earlier drafts, because the neighbors above are closer than those drafts' boundary acknowledged: (1) the configured-memory tier as a return-measured allocation — its composition has been surveyed [10] and its task utility measured [11] (the latter convergent with our C27, §6.1), but its per-object return rate under pre-registration has not been measured; (2) a policy-first vocabulary that spans systems (the §3 load test), where what is new is not the policy names (they are classical cache-design axes, §2.2) but the content-versus-pointer residency split and staleness risk as a tier property, and where the load test itself is a descriptive author-run classification rather than evidence (§3); (3) cross-tier return measurement under pre-registration, which is unoccupied only as a conjunction: utilization measurement of agent memory is itself not new — retrieval-vs-utilization is diagnosed in [12] and per-knowledge-point probing in [13], which pull in different directions on whether retrieval or utilization is the binding stage — but neither is cross-tier (boot→store) nor pre-registered, and the novelty is the combination. Claim (3) does not happen by default even where the will exists: read instrumentation was specified three separate times in this estate's design record without ever producing a dataset (§1) — which is why the program treats the gauge, not the policy, as the deliverable.

Data & artifact availability

Citation convention. Repository-relative paths in this paper (e.g. results/2026-07-18-c28-…, analyses/…/effect-table-2026-07-19.json) refer to files in the epistemics research artifact. The order proof for every pre-registered claim is the git commit chain, timestamped and append-only: program registration 4b86195 (predictions frozen); the C29 harness and design 5572eba preceding the frozen, hashed question set 5d63e0a (sha256[:16] 8f39408f324ffb84) preceding the first policy run; the C29 verdict dc5bfca. A reviewer verifies the ordering from the commit metadata without access to any withheld content.

Canonical public record. This paper and its complete artifact bundle are published at DOI 10.5281/zenodo.21938413 (Zenodo). Cite the DOI; the repository-relative paths below resolve inside the deposited bundle.

The C34 public bundle. The public replication ships in full and is the artifact a reader should start from: the 141-document corpus snapshot at the byte with per-file hashes, the rule-R evaluation log accounting for all 154 candidates with the clause that accepted or rejected each, the 141 frozen questions with gold answers and generation provenance, the salted confirmatory/smoke split, the authored index, all 390 run records and per-attempt logs, the smoke audit, the effect table, the dated results document, the full registration chain including every correction, and the harness, adjudicator and test suite. Re-running adjudicate.py reproduces the committed effect table byte for byte; the bundle's own test suite runs from a plain directory.

One redaction, registered rather than silent: the corpus-selection rule excludes files mentioning third-party client identifiers, and that token list is a curated enumeration of exactly those identifiers, three of them personal names of people not party to this study. The bundle ships the rule with the list emptied and the sha256 of the canonical list alongside, so anyone holding the original can prove in one line that it is the same rule; the rule's effect — which files were rejected, by which clause, with hit counts — ships in full. The enumeration is in any case not re-runnable from the bundle, because it reads the epistemics git tree at cb73654 and no git history ships. Registered in instruments/2026-08-14-c34-registration-correction-v5.md.

Confidentiality boundary. One corpus in the C29 experiment (Workspace-P) is a third-party client engagement; its documents, the derived question set, the digest index, and the per-run answer records contain verbatim client operational content and are withheld. The audit of exactly what is and is not exposed is SENSITIVITY-AUDIT.md: the paper's prose, the four effect tables, and three of four results documents carry no client content; the raw C29 data does. No part of the client corpus is released with this paper. The epistemics repository itself is not published: client content sits in its committed git history, so no release here can take the form of publishing the repository. Artifacts are released individually: the paper, its figures, and repro-kit/ publicly, and anything else only under appropriate confidentiality terms.

Release shape. The reproducibility package (repro-kit/) contains the harness, the 17 operator-owned English methodology documents as a public corpus, a public question set frozen by hash before its runs (820352e5b0b4b147), and a reference demonstrator result (repro-kit/DEMONSTRATOR-RESULT.md). Two things must be said about that demonstrator wherever it is cited. Its 17 documents are the English half of the paper's own C29 corpus, so it is a subsample re-run by the same operator on the same machine, not an independent replication. And at 16 questions per arm it falls below C29's frozen 100-question floor, so under the committed adjudicator it returns INSTRUMENT INSUFFICIENT and adjudicates nothing; within that, frozen P3 fails and reverses. Both are set out in §7 Limits (b′). The full 102-question result stands on the committed hashes of the withheld set; the private artifacts are available under appropriate confidentiality terms. Note also, per §7 Limits (g), that the transcript corpus underlying C26, C27, and C28 no longer exists on disk, so those three probes cannot be re-derived by anyone, including the author.

Invitation to replicate. The single-operator scope (§7 Limits) is this paper's sharpest external-validity bound, and the kit is its intended remedy: repro-kit/repro_kit.py runs the full A/B/C/D comparison end-to-end on any operator's markdown corpus with pinned models and a deterministic adjudicator. We explicitly invite replications — confirming or refuting — and will link external results from the artifact repository. Two conditions on any such run, learned from our own. Report the scored-question count against C29's frozen floor of 100 per policy: below it the frozen adjudicator returns instrument-insufficient, and a 16-question run has roughly 19% power against the effect reported here. And record, per question, whether the policy read the gold file, because that single field is what separates the two mechanisms this paper had to distinguish (mis-routing from early stopping) and it is what we found an earlier draft had misread in its own data.

The prediction we stake on replication, restated here because the earlier draft's version did not survive contact with our own demonstrator: an authored digest index used as a policy's sole locator will route to the correct document less often than associative search over the same corpus, and the resulting non-hydrated answers will be overwhelmingly wrong. We do not stake the accuracy margin, which is corpus- and question-set-dependent; and we no longer stake "the wrong-stop mechanism" in those words, because our own public demonstrator shows no wrong-stop tax at all once B is measured under the same rule as C.

Acknowledgements and lineage

The conceptual object this paper formalizes was not invented here. The "progressive disclosure" and "epistemic handle" ideas, and the framing of memory as active infrastructure, come from a 2025 design corpus (the mentu-finder and Epistemic-Science-&-Engineering notes) and a founding "CIR — memory as infrastructure" specification (2025-06); this paper's contribution is to de-brand those ideas into measured tiers and policies and to subject them to falsification. The store-tier return baseline (0.0222%) is prior work in the same repository (paper/return-base-rate-paper.md). The method — conjectures with frozen predictions, mechanical adjudication, refuted claims retained — is the standing constitution of the epistemics corpus and follows its sibling papers on evidence-carrying execution and structural waste. The cross-camp reference seed was assembled during an earlier documentation audit of the same estate. Per the repository's authorship convention, the author is sole author and committer.

References

Verification: references 1–8 were verified against their primary sources (arXiv abstract pages; publisher/index records for the two classical entries) on 2026-07-22; references 10–13 were verified against their arXiv abstract pages on 2026-07-23 (added after an external adversarial review surfaced them as prior art); references 14–38 were added in the current revision and verified on 2026-08-12, the arXiv entries against the arXiv API (title, full author list, v1 date) and the non-arXiv entries against Crossref (title, container, volume, pages, DOI). Every one resolved. Full BibTeX: references.bib; its non-numbered positioning entries retain a seed-verification flag.

Reference 9 is a live public documentation page and is the one entry in this list that cannot be retroactively verified by any party, including the author: a live URL with an access date carries no version a reader can pin. This matters because it is the sole support for §3.1's control-plane corroboration and for §2.2's policy-push injection channel, and because the §3.1 promotion null is date-bounded against it, which makes that null unfalsifiable in practice. Both should be read as unchecked. Replacing it with a dated archival capture or a documentation-repository commit is an open item, recorded rather than performed here.

1. L. Mei et al. A Survey of Context Engineering for Large Language Models. arXiv:2507.13334, 2025. — framing anchor (§8).
2. Q. Zhang et al. Agentic Context Engineering: Evolving Contexts for Self-Improving Language Models. arXiv:2510.04618, ICLR 2026. — nearest payload-evolution rival (§8).
3. T. Mason. The Missing Memory Hierarchy: Demand Paging for LLM Context Windows (Pichay). arXiv:2603.09023, 2026. — window-tier paging and the 21.8% structural-waste measurement (§3, §8).
4. C. Packer, S. Wooders, K. Lin, V. Fang, S. G. Patil, I. Stoica, and J. E. Gonzalez. MemGPT: Towards LLMs as Operating Systems. arXiv:2310.08560, 2023. — virtual context management (§3, §8).
5. Z. Li et al. (21 authors). MemOS: An Operating System for Memory-Augmented Generation (MAG) in Large Language Models. arXiv:2505.22101, 2025. — memory-as-OS at system scale (§8).
6. T. R. Sumers, S. Yao, K. Narasimhan, and T. L. Griffiths. Cognitive Architectures for Language Agents (CoALA). arXiv:2309.02427; TMLR, 2024. — content-type memory taxonomy, the orthogonal axis (§8).
7. R. A. Howard. Information Value Theory. IEEE Trans. Systems Science and Cybernetics, SSC-2(1):22–26, 1966. doi:10.1109/TSSC.1966.300074 — value-of-information lineage (§2.4).
8. M. L. Weitzman. Optimal Search for the Best Alternative. Econometrica, 47(3):641–654, 1979. — search with inspection costs; imported as metrics, not as a transferable optimality theorem (§2.4).
9. Anthropic. Claude Code hooks reference. code.claude.com/docs/en/hooks, accessed 2026-07-22. — the public hook API cited for §2.2 (policy-push injection) and §3.1 (control-plane corroboration).
10. W. Chatlatanagulchai, H. Li, Y. Kashiwa, B. Reid, K. Thonglek, P. Leelaprute, A. Rungsawang, B. Manaskasemsak, B. Adams, A. E. Hassan, H. Iida. Agent READMEs: An Empirical Study of Context Files for Agentic Coding. arXiv:2511.12884, 2025. — large-scale census (2,303 files) of the configured tier's composition (§1, §8).
11. T. Gloaguen, N. Mündler, M. Müller, V. Raychev, M. Vechev. Evaluating AGENTS.md: Are Repository-Level Context Files Helpful for Coding Agents? arXiv:2602.11988, 2026. — measures the boot tier's task utility; finds it frequently unhelpful at >20% added cost — convergent with C27 (§1, §6.1, §8).
12. B. Yuan, Y. Su, K. Yao. Diagnosing Retrieval vs. Utilization Bottlenecks in LLM Agent Memory. arXiv:2603.02473, 2026. — separates retrieval from utilization; finds retrieval dominant (§8, bounding claim 3).
13. X. Long, Z. Chen, S. Zeng, S. Wang, K. Guo, J. Tang. MemTrace: Probing What Final Accuracy Misses in Long-Term Memory. arXiv:2606.17328, 2026. — per-knowledge-point memory probing (§8, adjacent to per-object return).

References 14–38 added in the current revision.

14. A. J. Smith. Cache Memories. ACM Computing Surveys 14(3):473-530, 1982. doi:10.1145/356887.356892. Fetch, placement, replacement, and write axes; the lineage of §2.2's policy names.
15. P. J. Denning. Virtual Memory. ACM Computing Surveys 2(3):153-189, 1970. doi:10.1145/356571.356573. Cited in §2.2.
16. P. J. Denning. The working set model for program behavior. Communications of the ACM 11(5):323-333, 1968. doi:10.1145/363095.363141. The direct ancestor of "what should be resident before the task arrives" (§2.2).
17. W. Zhong, L. Guo, Q. Gao, H. Ye, Y. Wang. MemoryBank: Enhancing Large Language Models with Long-Term Memory. arXiv:2305.10250, 2023. Ebbinghaus-inspired decay and reinforcement; fills the validation cell (§3, §8).
18. P. Chhikara, D. Khant, S. Aryan, T. Singh, D. Yadav. Mem0: Building Production-Ready AI Agents with Scalable Long-Term Memory. arXiv:2504.19413, 2025. Extraction plus consolidation over stored items (§3, §8).
19. W. Xu, Z. Liang, K. Mei, H. Gao, J. Tan, Y. Zhang. A-MEM: Agentic Memory for LLM Agents. arXiv:2502.12110, 2025. Link evolution and memory update as new items arrive (§3, §8).
20. J. S. Park, J. C. O'Brien, C. J. Cai, M. R. Morris, P. Liang, M. S. Bernstein. Generative Agents: Interactive Simulacra of Human Behavior. arXiv:2304.03442, 2023. Recency, importance, and relevance retrieval scoring plus reflection (§3, §8).
21. N. F. Liu, K. Lin, J. Hewitt, A. Paranjape, M. Bevilacqua, F. Petroni, P. Liang. Lost in the Middle: How Language Models Use Long Contexts. Transactions of the ACL 12:157-173, 2024. doi:10.1162/tacl_a_00638. The attention-tax premise of §4.1.
22. M. Levy, A. Jacoby, Y. Goldberg. Same Task, More Tokens: the Impact of Input Length on the Reasoning Performance of Large Language Models. arXiv:2402.14848, ACL 2024. Length degradation at fixed task (§4.1).
23. Y. Chang, K. Lo, T. Goyal, M. Iyyer. BooookScore: A systematic exploration of book-length summarization in the era of LLMs. arXiv:2310.00785, ICLR 2024. Measured fidelity failures in hierarchically merged summaries; the lossy-digest premise of §4.2.
24. E. Aghajani, C. Nagy, O. L. Vega-Márquez, M. Linares-Vásquez, L. Moreno, G. Bavota, M. Lanza. Software Documentation Issues Unveiled. Proc. ICSE 2019, pp. 1199-1210. doi:10.1109/icse.2019.00122. Cited in §4 and §6.4.
25. E. Aghajani, C. Nagy, M. Linares-Vásquez, L. Moreno, G. Bavota, M. Lanza, D. C. Shepherd. Software Documentation: The Practitioners' Perspective. Proc. ICSE 2020, pp. 590-601. doi:10.1145/3377811.3380405. Cited in §4 and §6.4.
26. H. Joren, J. Zhang, C.-S. Ferng, D.-C. Juan, A. Taly, C. Rashtchian. Sufficient Context: A New Lens on Retrieval Augmented Generation Systems. arXiv:2411.06037, ICLR 2025. Sufficient context and confident non-abstention; prior art for §2.4's C*(τ) and §6.5's wrong-stop framing (§7, §8).
27. C. D. Chambers. Registered Reports: A new publishing initiative at Cortex. Cortex 49(3):609-610, 2013. doi:10.1016/j.cortex.2012.12.016. Cited in §7.
28. A. Cockburn, C. Gutwin, A. Dix. HARK No More: On the Preregistration of CHI Experiments. Proc. CHI 2018, pp. 1-12. doi:10.1145/3173574.3173715. Pre-registration of computing experiments with explicit HARKing analysis (§7).
29. B. A. Nosek, C. R. Ebersole, A. C. DeHaven, D. T. Mellor. The preregistration revolution. PNAS 115(11):2600-2606, 2018. doi:10.1073/pnas.1708274114. Cited in §7.
30. J. P. A. Ioannidis. Why Most Published Research Findings Are False. PLoS Medicine 2(8):e124, 2005. doi:10.1371/journal.pmed.0020124. Cited in §7.
31. J. Pineau, P. Vincent-Lamarre, K. Sinha, V. Larivière, A. Beygelzimer, F. d'Alché-Buc, E. Fox, H. Larochelle. Improving Reproducibility in Machine Learning Research (A Report from the NeurIPS 2019 Reproducibility Program). arXiv:2003.12206, 2020. Cited in §7.
32. P. Ralph et al. (37 authors). Empirical Standards for Software Engineering Research. arXiv:2010.03525, 2020. Per-method reporting standards including registered reports (§7).
33. K. Mei, X. Zhu, W. Xu, W. Hua, M. Jin, Z. Li, S. Xu, R. Ye, Y. Ge, Y. Zhang. AIOS: LLM Agent Operating System. arXiv:2403.16971, 2024. A second OS-framing system alongside MemOS (§8). Note: first author Kai Mei, distinct from reference 1's L. Mei.
34. P. Sarthi, S. Abdullah, A. Tuli, S. Khanna, A. Goldie, C. D. Manning. RAPTOR: Recursive Abstractive Processing for Tree-Organized Retrieval. arXiv:2401.18059, ICLR 2024. The nearest published rival to C29; derived rather than authored layers (§8).
35. C. S. Xia, Y. Deng, S. Dunn, L. Zhang. Agentless: Demystifying LLM-based Software Engineering Agents. arXiv:2407.01489, 2024. Cited in §8.
36. J. Yang, C. E. Jimenez, A. Wettig, K. Lieret, S. Yao, K. Narasimhan, O. Press. SWE-agent: Agent-Computer Interfaces Enable Automated Software Engineering. arXiv:2405.15793, 2024. Cited in §8.
37. B. J. Chan, C.-T. Chen, J.-H. Cheng, H.-H. Huang. Don't Do RAG: When Cache-Augmented Generation is All You Need for Knowledge Tasks. arXiv:2412.15605, 2024. Content residency versus retrieval, priced (§8).
38. P. Xu, W. Ping, X. Wu, L. McAfee, C. Zhu, Z. Liu, S. Subramanian, E. Bakhturina, M. Shoeybi, B. Catanzaro. Retrieval meets Long Context Large Language Models. arXiv:2310.03025, 2023. Cited in §8.

references.bib additionally carries the retrieval-granularity, agent-memory, and content-addressed-provenance camps (RAPTOR, Self-RAG, Dense X, HippoRAG, PROV, IPFS, and others) as positioning context; those entries remain seed-flagged and are not load-bearing for any claim in this draft.