What Context Does a Coding Agent Actually Need to Act?

# What Context Does a Coding Agent Actually Need to Act?
Source: [https://arxiv.org/html/2607.09691](https://arxiv.org/html/2607.09691)
Brian Sam\-Bodden Integrallis Software bsbodden@integrallis\.com

###### Abstract

A modern coding agent can hold an entire repository in its context window\. Most of its reading is wasted — and the interesting question is not how much context an agent can use, but what it actually*needs*\. We study that question at the moment it matters most: when the agent must*edit*code\. Separating*finding*the work site from*acting*on it, we hold localization fixed with an oracle, vary only how the code is represented, and score context against real issue resolution on SWE\-bench Verified\. The answer is starkly minimal\. The signal lives in the code being edited itself: natural\-language summaries of it answer almost none of the behavioral questions that the source answers \(4/454/45vs\.27/4527/45, held\-out repositories, independent judge\), and the gap belongs to the representation, not the summarizer — a frontier model’s summaries score exactly as poorly as a 3B model’s\. The surrounding context hardly matters either: across every multi\-file instance in Verified, under a protocol frozen before any data, rendering a file’s remainder as UML skeletons and signatures resolves no more issues than deleting that remainder outright \(N=70N\{=\}70, exact McNemarp=0\.75p\{=\}0\.75\)\. That was our registered hypothesis, and it failed\. Compressed context, meanwhile, matches whole files at a third of the tokens: a resolved issue costs1919K context tokens, not9494K\. The instrument also yielded a finding the field should keep: temperature\-0 API inference flips∼9%\{\\sim\}9\\%of per\-instance outcomes between byte\-identical runs\. That is a noise floor under every small effect reported on this benchmark, including ours\. We release the instrument — gold\-validated environments, per\-instance proof that every reference edit is expressible from every arm’s context, deterministic patch construction, and pre\-registered hypotheses whose nulls we publish\.

![Refer to caption](https://arxiv.org/html/2607.09691v1/x1.png)Figure 1:The find/act boundary\.Behavioral\-probe accuracy by context representation \(n=45n\{=\}45: 15 held\-out classes from seaborn/pylint/pytest×\\times3 probes minted from each class’s*test file*; the*same*model — Claude Sonnet 4\.6 — reads the context and answers in every arm, so only the representation varies; answers graded by an independent\-family judge,κ=0\.84\\kappa\{=\}0\.84against a second judge\)\. The frontier/3B labels indicate the*summarizer*that wrote the representation, not the answerer\. Source answers60%60\\%; natural\-language summaries answer∼9%\{\\sim\}9\\%— identically for a frontier and a 3B summarizer — and no summary succeeds where source fails \(McNemar 23\-vs\-0,p<10−4p\{<\}10^\{\-4\}\)\. Mean representation size incl100k\_basetokens below each bar\.## 1Introduction

When a software engineer fixes a bug, she doesn’t re\-read the repository\. She finds the few functions that matter, reads them closely, and lets the rest of the codebase fall into a vague map of what exists where\. Coding agents are built as if the opposite were true: context windows now hold entire repositories, and the natural instinct is to fill them\. That instinct has a price — tokens, latency, dollars — and surprisingly thin evidence behind it\. Frontier agents already resolve a large fraction of SWE\-bench Verified\[[5](https://arxiv.org/html/2607.09691#bib.bib5)\], yet ContextBench\[[7](https://arxiv.org/html/2607.09691#bib.bib7)\]finds that sophisticated retrieval scaffolds often barely beat trivial baselines, with a wide gap between context*explored*and context*used*\. So the question worth asking is not whether we can fit the code, but:for a given code task, what is the minimal context an agent actually needs — and in what representation?

We separate two sub\-questions that are often conflated:

- •Find— locating where the work happens;
- •Act— given the location, knowing enough to edit correctly\.

To measure*act*\-context cost without rewarding “include more,” we hold localization fixed with an*oracle*\(the same gold files for every arm\) and vary*only the representation*\(§[3](https://arxiv.org/html/2607.09691#S3)\)\. This yields a pre\-specified prediction we can pass or fail:*if program structure is what an agent needs to act, a structured representation tier \(UML\-skeleton / method\-only\) should resolve more, at equal localization, than a flat binary keep/drop*\[[3](https://arxiv.org/html/2607.09691#bib.bib3)\]\. Section[5](https://arxiv.org/html/2607.09691#S5)tests that prediction on every multi\-file instance in SWE\-bench Verified, under a protocol frozen and committed before any data\.The prediction fails, and we report the null\.

#### Contributions\.

\(1\) Anauditedresolve@costinstrument: oracle\-localized representation arms with per\-instance*expressibility*verification \(every gold edit provably expressible from every arm’s context\), per\-instance gold\-patch environment validation, deterministic patch construction, and pre\-registered hypotheses — every number traceable to a raw artifact\. \(2\) Apowered null: structured representation tiers carry no resolve signal over binary keep/drop at oracle localization, single\-shot \(N=70N\{=\}70,p=0\.75p\{=\}0\.75\), while compressed context matches whole files at33–3\.7×3\.7\\timesfewer tokens\. \(3\) Ade\-circularized find/act boundary: with test\-minted probes, held\-out repositories, and an independent judge, source carries roughly7×7\\timesthe actionable signal of natural\-language summaries, and a frontier summarizer cannot close the gap \(the first run of the summarizer\-quality control\)\. \(4\) Amethodological cautionmeasured in passing: run\-to\-run non\-determinism atT=0T\{=\}0flips∼9%\{\\sim\}9\\%of SWE\-bench per\-instance outcomes between byte\-identical runs — bounding the interpretation of all small arm gaps, ours and others’\.

#### Rigor and scope\.

Every number in this paper traces to a raw artifact\. Protocols, hypotheses, and instance samples were frozen and committed before data collection; every instance’s environment is validated with its reference patch before any model call; every reference edit is verified expressible from every arm’s context; figures regenerate from raw result files\. Theresolve@costand probe experiments run on SWE\-bench Verified and held\-out open\-source repositories; superseded or exploratory measurements are quarantined in Appendix[D](https://arxiv.org/html/2607.09691#A4)and carry no claims\. We label everynn, report a Wilson 95% CI for every proportion, and state for each negative which way its biases cut\.

## 2Related work

Sufficiency\-based context for code\.SWEzze\[[3](https://arxiv.org/html/2607.09691#bib.bib3)\]reduces issue contexts to a minimal sufficient subsequence \(binary keep/drop of code segments\), validated on resolution; Joren et al\.\[[6](https://arxiv.org/html/2607.09691#bib.bib6)\]formalize “sufficient context” for RAG\. We build on these; our act\-view probes ask*which alternative rendering*suffices, and ourresolve@costexperiment answers whether*tiers*beat their*keep/drop*\(they do not,N=70N\{=\}70, §[5](https://arxiv.org/html/2607.09691#S5)\)\.Context pruning/compression\.SWE\-Pruner\[[12](https://arxiv.org/html/2607.09691#bib.bib12)\], LLMLingua\[[4](https://arxiv.org/html/2607.09691#bib.bib4)\], and related systems prune tokens or lines; we select among*program\-structure representations*and measure*resolution*, not relevance\.Localization and retrieval\.Agentless\[[13](https://arxiv.org/html/2607.09691#bib.bib13)\], LocAgent\[[1](https://arxiv.org/html/2607.09691#bib.bib1)\], RepoGraph\[[9](https://arxiv.org/html/2607.09691#bib.bib9)\], and LingmaAgent\[[8](https://arxiv.org/html/2607.09691#bib.bib8)\]address*find*; we control localization*out*via an oracle to isolate representation\.Hierarchical retrieval\.RAPTOR\[[11](https://arxiv.org/html/2607.09691#bib.bib11)\]and GraphRAG\[[2](https://arxiv.org/html/2607.09691#bib.bib2)\]build summary hierarchies; our probe results bound what summary nodes can carry for*acting*, and in exploratory tests architecture\-grounded descent did not beat flat retrieval \(Appendix[D](https://arxiv.org/html/2607.09691#A4)\)\.The bitter lesson for code context\.ContextBench\[[7](https://arxiv.org/html/2607.09691#bib.bib7)\]reports sophisticated scaffolds barely beating simple baselines, with much explored context going unutilized; our results corroborate this from an independently built, audited instrument\. CodeCompass\[[10](https://arxiv.org/html/2607.09691#bib.bib10)\]argues the opposite for*navigation*— structural traversal beating retrieval when lexical overlap is low — consistent with our scope: our nulls concern*act*\-context rendering, not navigation\.

## 3Method

### 3\.1Experimental setup

Table 1:Setup\. Every claim in the paper inherits these conditions unless stated\.Resolve datasetSWE\-bench Verified\[[5](https://arxiv.org/html/2607.09691#bib.bib5)\]:all 71 multi\-file instances\(≥2\\geq 2gold files\); 70 after gold\-validation exclusion \(astropy\-8707, whose gold patch fails its own environment\)\.Probe data15 held\-out classes from seaborn/pylint/pytest at pinned commits, each with a dedicated test file \(probes minted from tests, never from the scored text\)\.Agent \(resolve\)Claude Sonnet 4\.6, single\-shot, temperature 0,max\_tokens=8000,≤2\\leq 2apply\-failure retry rounds; reasoning permitted before edit blocks\.Probe judgeGPT\-4o\-mini \(independent family\), Claude as second judge \(κ\\kappareported\)\.PatchesDeterministic SEARCH/REPLACE→\\todifflibunified diff; ambiguous or non\-matching edits fed back for≤2\\leq 2retries; empty SEARCH creates new files\.ResolveSWE\-bench 4\.1\.0 Docker harness \(FAIL\_TO\_PASS∧\\wedgePASS\_TO\_PASS\)\.Gold patch validated for every instance\(70/71 pass\)\.Expressibility gatePer arm×\\timesinstance, every gold hunk’s deleted lines \(or insertion anchor\) verified verbatim\-present in the rendered context before any agent call: 70/70 in all arms\.Costcl100k\_basetoken proxy, plus Anthropiccount\_tokenson the exact*initial*prompt per episode \(retry prompts are logged in metrics but not token\-counted\)\.StatisticsWilson 95% CIs on every proportion; exact two\-sided McNemar on paired resolve\.Structural tree\.Deterministicastextraction yields Subsystem→\\toComponent→\\toFile→\\toClass→\\toFunction\.Representation rungs:full\-body⋅\\cdotmethod\-only⋅\\cdotUML\-class\-skeleton⋅\\cdotsignature\+doc⋅\\cdotname⋅\\cdotexclude \(all deterministic; no LLM\)\.

### 3\.2Theresolve@costrig

![Refer to caption](https://arxiv.org/html/2607.09691v1/x2.png)Figure 2:The rig, end to end\.Gold\-changed files \(oracle localization\) are rendered under three arms that vary representation; the agent emits SEARCH/REPLACE blocks; a deterministic builder constructs the diff; the official Docker harness reports resolution\.Oracle localizationisolates representation from retrieval: arms share the gold\-changed files\. The arms are also*coverage\-fair*: the compressed arms render module\-level code, class\-attribute regions, decorators, and non\-Python gold files verbatim, so every gold edit is expressible from every arm’s context \(verified per instance; Table[1](https://arxiv.org/html/2607.09691#S3.T1)\)\. We disclose the asymmetry: the compressed arms are built from gold\-edited units \(they encode*where*to edit at full detail\);oracle\_fullreceives whole files with no highlighting\. All arms are oracle*ceilings*, not deployable policies; the tier\-vs\-keep/drop comparison — which shares the same gold units — is the clean one\.

Deterministic patchesremove the main confound of LLM\-authored diffs: in development testing, model\-authored unified diffs failed to apply on 7 of the 9 attempts; the SEARCH→\\todifflibbuilder applies cleanly,git apply \-\-check\-verified, with uniqueness checking, new\-file creation, and≤2\\leq 2retry rounds with per\-edit failure feedback\.

resolve@costis reported as the pair \(resolve rate, mean context tokens\) and summarized as*tokens per resolve*==total context tokens / instances resolved\. We do not divide resolve by mean tokens: that ratio rewards an arm for shrinking context on instances it never solves\.

## 4The find/act boundary

Can a compressed stand\-in for source code — a summary, a signature — carry what an agent needs to*act*? We measure this with behavioral probes: 15 held\-out classes fromseaborn / pylint / pytestat pinned commits, each with a dedicated test file; three probes per class minted*from the tests*\(independent behavioral ground truth — the answerer never sees them; “UNKNOWN” permitted\); a single frontier model \(Claude Sonnet 4\.6\) reads the representation and answers every probe in every arm; answers graded by an*independent\-family*judge \(GPT\-4o\-mini\), with a same\-family judge run in parallel only to report agreement \(κ=0\.84\\kappa\{=\}0\.84, 94% raw\)\. Temperature 0 throughout\. A summarizer\-quality control runs the same prompt at the same 180\-token budget with both a small model \(Qwen2\.5\-Coder\-3B\) and a frontier model \(Claude Sonnet 4\.6\), so “summaries fail” can’t be an artifact of a weak summarizer\.

Table 2:The find/act boundary\(n=45=15n\{=\}45=15held\-out classes×\\times3 test\-minted probes; independent judge; strictT=0T\{=\}0\)\. Exact McNemar vs\. source: 23\-vs\-0 discordant for both summary arms, 21\-vs\-0 for signature \(allp<10−4p<10^\{\-4\}\)\.Three observations\. First,source is not perfect\(0\.6000\.600\): test\-minted behavioral probes are hard, and sometimes need context beyond one class — which is exactly why a fair protocol matters: a probe set minted from the scored text itself reports a flattering1\.001\.00\(Appendix[D](https://arxiv.org/html/2607.09691#A4)\)\. Second,the boundary is∼7×\{\\sim\}7\\timeswide: source answers60%60\\%of the questions, summaries answer only∼9%\{\\sim\}9\\%, and no summary ever succeeded where source failed\. Third — the control that gives the result its teeth —frontier\-written summaries score identically to 3B summaries: the gap is a property of the*representation class*, not summarizer quality\. Better prose does not buy actionable information at this budget\. Signatures, at similar cost, edge out prose summaries \(6/456/45vs\.4/454/45\) — at these counts no more than a hint that what little survives compression is structure, not narrative\.

This says summaries cannot*act*; it doesnotestablish that summaries help*navigate*— in our exploratory navigation test \(Appendix[D](https://arxiv.org/html/2607.09691#A4)\), summary\-keyed hierarchical descent did not beat flat retrieval either\.

## 5Resolve@cost: every multi\-file Verified instance, pre\-registered

Protocol \(frozen and committed before any data\)\.All 71 instances whose gold patch touches≥2\\geq 2files; oracle localization; vary only representation; single\-shot agent \(Table[1](https://arxiv.org/html/2607.09691#S3.T1)\)\. Every instance’s gold patch is first run through the harness \(70/7170/71environments pass; the failure is excluded and recorded\), and every gold edit is verified expressible in every arm before any agent call\. Registered hypothesis H2:oracle\_tierresolves more thanoracle\_keep\_drop\.

![Refer to caption](https://arxiv.org/html/2607.09691v1/x3.png)Figure 3:Where the sample comes from\.500 Verified instances→\\to71 multi\-file \(the registered criterion\)→\\to70 after one gold\-validation exclusion\. The whole pool runs; nothing is sampled\.![Refer to caption](https://arxiv.org/html/2607.09691v1/x4.png)Figure 4:The powered result \(N=70N\{=\}70\)\.*Left:*resolve rate per arm with Wilson 95% CIs — the registered tier\-vs\-keep/drop comparison is null \(exact McNemarp=0\.754p\{=\}0\.754\)\.*Right:*context tokens per resolved instance: compressed context buys a resolve for1919–2626K tokens; whole files pay9494K\.Table 3:Resolve and context cost \(N=70N\{=\}70; every arm covers every gold hunk on every instance, so differences are due to representation, not expressibility\)\.Table 4:Paired tests \(exact McNemar, two\-sided\)\. The registered H2 is null\.#### Findings\.

\(1\) The registered hypothesis is null: structured tiers do not beat binary keep/drop\(p=0\.75p\{=\}0\.75; keep/drop is nominally*ahead*\)\. Rendering the non\-locus remainder as class skeletons and signatures carries no measurable resolve signal over just dropping it, at oracle localization, single\-shot\.*Scope:*the tiers tested are the thin end of the structured\-artifact family — static name/signature digests; interaction\-level artifacts and distance\-graded detail were specified in our original design but never implemented \(they require call\-edge extraction this codebase lacks\); the null does not cover them\.\(2\) Compressed context resolves at least as well as whole files at33–3\.7×3\.7\\timesfewer tokens\.Both compressed arms are nominally above full; keep/drop vs\. full is marginal \(p=0\.07p\{=\}0\.07\) and we do not claim significance\. On cost\-normalized terms the gap is clear:19,30019\{,\}300context tokens per resolve vs\.93,70093\{,\}700\(Figure[4](https://arxiv.org/html/2607.09691#S5.F4)\)\.\(3\) Format failures do not drive outcomes:0–1 truncated generations and 1–2 empty patches per arm; the retry loop fired on 11–24 instances per arm \(most often for tier, whose synthesized renderings tempt the model to copy non\-verbatim text — a residual asymmetry we disclose; it cuts against H2, which was null anyway\)\.

#### Interaction\-level follow\-up \(pre\-registered\)\.

Since the tiers above are static digests, we separately tested the sharpest*interaction*artifact: keep/drop’s byte\-identical content plus a deterministic AST\-derived sequence slice of the gold functions’ local call flow \(present on 65/70 instances, mean 215 tokens\)\. Registered H3: slice\>\>keep/drop\. Result:directionally positive, not significant—26/7026/70\(0\.3710\.371\[0\.27, 0\.49\]\) vs\.23/7023/70\(0\.3290\.329\[0\.23, 0\.44\]\), McNemar 4\-vs\-1,p=0\.375p\{=\}0\.375\. The only structured artifact in the study that pointed the right way; atN=70N\{=\}70it supports no claim\.

#### Run\-to\-run noise bounds all small gaps\.

The follow\-up re\-ran the keep/drop arm under the byte\-identical protocol \(temperature 0, same model alias, same prompts\): it resolved23/7023/70vs\. the original25/7025/70, with a symmetric difference of6 instances\. Temperature\-0 API inference is not deterministic;∼9%\{\\sim\}9\\%of per\-instance outcomes flip between identical runs\. Any arm difference of this order — including H2’s 2\-instance gap — is within run noise, a caution that applies to single\-run SWE\-bench comparisons generally\.

## 6Threats to validity \(and which way each cuts\)

Single\-shot, no\-execution regime\.In this regime there is one completion \(plus apply\-failure retries\) — no reproduction script, no test run, no repair loop\. This is the regime*least*likely to surface representation effects — a multi\-turn agent can recover from compressed context by reading more — so the H2 null is a statement about this regime; it biases toward the null for tier\-vs\-keep/drop and plausibly*against*full\. Conclusions about*agents*require the in\-the\-loop version \(future work; Appendix[D](https://arxiv.org/html/2607.09691#A4)\)\.Oracle ceilings, asymmetric construction\.Compressed arms encode gold edit*locations*; full does not\. Tier\-vs\-keep/drop shares the same gold units and is clean; compressed\-vs\-full mixes compression with location hinting — one reason we don’t claim thep=0\.07p\{=\}0\.07comparison\. Realistic retrieval would lower every arm together\.Probe scope\.The find/act boundary rests on held\-out repos, test\-minted probes, and an independent judge \(§[4](https://arxiv.org/html/2607.09691#S4)\), but on one language and 15 classes\. Because probes cluster within classes, we also computed class\-clustered bootstrap intervals: source\[0\.40,0\.78\]\[0\.40,0\.78\]vs\. summaries\[0\.00,0\.20\]\[0\.00,0\.20\], gap CI\[0\.36,0\.67\]\[0\.36,0\.67\]— the boundary is unchanged under clustering; the exploratory own\-code probes in Appendix[D](https://arxiv.org/html/2607.09691#A4)show how much a circular protocol inflates positive controls \(1\.00→0\.6001\.00\\to 0\.600for source\) and are not relied on for any claim\.Format asymmetry, residual\.Tier’s synthesized text triggered the most edit retries \(24/7024/70vs\.1515keep/drop,1111full\); gold\-edit regions are always verbatim, but a residual format penalty against tier can’t be fully excluded \(it cuts against H2, which was null\)\.Non\-determinism — measured, not assumed\.T=0T\{=\}0flips∼9%\{\\sim\}9\\%of outcomes between identical runs \(§[5](https://arxiv.org/html/2607.09691#S5)\); probe cells are single draws atT=1T\{=\}1\.Token units\.Headline counts are a GPT\-BPE proxy; Anthropic counts are logged alongside \(mean full prompt: full32\.632\.6K / tier11\.611\.6K / keep/drop9\.49\.4K\)\. Ratios are robust; absolutes differ\.Single language \(Python\), single model family\.Stated coverage gaps\.Provenance\.Protocols, hypotheses, and samples were committed before data collection; figures regenerate from raw result files; per\-instance harness reports ship with the artifact\.

## 7Conclusion

On every multi\-file instance in SWE\-bench Verified, with localization fixed and every gold edit verified expressible in every arm, the answer to “what context does a single\-shot agent need to*act*” is:the edited code itself — and neither of the surrounding\-context renderings we tested \(class skeletons, signatures\) adds anything over dropping it\.Our registered hypothesis, that structured tiers preserve resolve signal that binary keep/drop discards, is null atN=70N\{=\}70, and both compressed arms resolve at least as well as whole files at33–3\.7×3\.7\\timesfewer tokens\. The same was true of every other measurement we ran — descent vs\. flat, ownership scoring, summaries vs\. source: each structure\-aware elaboration failed to beat the simpler alternative\. We see this as one more controlled data point for the bitter lesson in code context, with the usual scope limits \(single\-shot, oracle ceilings, one model family, Python\)\. The lasting contributions are the auditedresolve@costrig and the discipline of registering directional hypotheses and publishing their nulls\.

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## Appendix AAgent prompt and decoding

The agent receives, for every arm, the byte\-identical instruction below; only\{context\}varies\. Decoding \(v2\):max\_tokens=8000, temperature 0, no truncation of issue or context;≤2\\leq 2retry rounds add the failed edits’ diagnostics \(not\-found / ambiguous / no\-such\-file\) and ask for corrected blocks only\.

```
You are fixing a GitHub issue in the ‘{repo}‘ repository.
ISSUE: {issue}
RELEVANT CODE (already localized for you): {context}
Think briefly about the fix first if that helps. Then output ONE OR MORE
edit blocks in EXACTLY this format (the blocks are parsed mechanically;
everything outside them is ignored):
*** FILE: <path relative to repo root>
*** SEARCH
<exact existing lines to replace -- copy them VERBATIM from the code
above, incl. indentation>
*** REPLACE
<the new lines>
*** END
Rules:
- each SEARCH block must be copied verbatim from the provided code and
  match exactly ONE location; keep it small and uniquely matching.
- to CREATE a new file, emit a block whose SEARCH section is empty.
- edit only what is necessary to fix the issue.
```

## Appendix BReproducibility, resources, and research transparency

#### Artifact\.

All experiment code, frozen instance lists, pre\-registrations, per\-instance harness reports, and the figure generator \(every plotted number loaded from a raw result file\) are released at[https://github\.com/integrallis/act\-context](https://github.com/integrallis/act-context)under the MIT license\. The protocol, frozen sample, and expressibility audit were committed before any agent call\. Known limits: the model id resolves to an alias \(claude\-sonnet\-4\-6; the API exposes no dated snapshot or seed\); probe cells are single samples; headline token counts are acl100k\_baseproxy \(Anthropic counts cover each episode’s initial prompt; retry prompts are logged but not token\-counted\)\. One operational note: the first evaluation pass hit Docker Hub’s anonymous image\-pull rate limit; affected instances were detected as*environment*errors \(never counted as model failures\) and re\-run to completion under authenticated pulls\.

#### Compute and cost\.

The resolve experiments are API calls plus commodity Docker: the registeredN=70N\{=\}70run used≈210\{\\approx\}210agent calls \(≈$​20\{\\approx\}\\mathdollar 20of API inference\) and≈6\{\\approx\}6hours of Docker evaluation wall\-clock on a 32\-thread workstation; the sequence\-slice follow\-up roughly doubles the evaluation half; the probe study \(§[4](https://arxiv.org/html/2607.09691#S4)\) used≈600\{\\approx\}600short model calls \(≈$​5\{\\approx\}\\mathdollar 5\)\. No GPUs and no training are required anywhere; figures regenerate on CPU in seconds\.

#### Existing assets\.

SWE\-bench Verified and its evaluation harness\[[5](https://arxiv.org/html/2607.09691#bib.bib5)\]\(MIT license\); the held\-out probe corpora are public open\-source repositories \(seaborn, pylint, pytest\), analyzed at pinned commits under their respective licenses\. Models: Anthropic Claude Sonnet 4\.6 \(agent, summarizer control, second judge\), OpenAI GPT\-4o\-mini \(independent judge\), and Qwen2\.5\-Coder\-3B \(Apache\-2\.0; small\-summarizer arm\), each used via its terms of service\.

#### LLM usage declaration\.

LLMs are the*subject*of this paper: the evaluated agent, the summarizer arms, and the judges are all LLMs, fully specified in Table[1](https://arxiv.org/html/2607.09691#S3.T1)and §[4](https://arxiv.org/html/2607.09691#S4)\. In addition, LLM\-based development tooling assisted in implementing the experimental infrastructure and drafting the manuscript; all hypotheses, protocols, and analysis decisions were human\-approved and frozen in committed pre\-registrations before data collection, and every reported number is a deterministic artifact of the released code and raw result files\.

#### Broader impact\.

This is foundational measurement on a public benchmark\. Its main practical implication — that agents resolve issues equally well with a third of the context — points toward cheaper, lower\-energy coding agents; we see no direct path to misuse, and the released assets \(evaluation code and result files\) pose no dual\-use risk\.

## Appendix CPre\-registrations and their outcomes

Scaled resolve \(executed\)\.Frozen before any data: all 71 multi\-file instances; coverage\-fair arms; gold validation per instance; expressibility instrumentation; Wilson \+ exact McNemar; H2 \(tier\>\>keep/drop\) registered, a tie reported as the result\. Outcome: §[5](https://arxiv.org/html/2607.09691#S5)— H2 null \(p=0\.754p\{=\}0\.754\)\.Probe re\-grade \(executed\)\.Held\-out classes with dedicated test files; probes minted from tests; independent\-family judge withκ\\kappa; frontier\-summarizer control;T=0T\{=\}0\. Outcome: §[4](https://arxiv.org/html/2607.09691#S4)— the boundary hardens \(source27/4527/45vs\. summaries4/454/45, both summarizers identical; canonical numbers from the corrected strict\-T=0T\{=\}0rerun\)\.Sequence slice \(executed\)\.Keep/drop content\+\+AST call slice, both arms fresh; H3 \(slice\>\>keep/drop\)\. Outcome: directionally positive, ns \(p=0\.375p\{=\}0\.375\); the keep/drop re\-run doubles as the run\-to\-run noise measurement \(6/70 flips\)\.Registered escalation \(future\):a 2\-step agent loop on the solvable subset; an act\-view re\-grade under the §[4](https://arxiv.org/html/2607.09691#S4)protocol\.

## Appendix DExploratory results \(not claims of this paper\)

This appendix collects superseded measurements that ran on the project’s*own in\-house codebases*— small, self\-authored corpora — and/or under self\-judged protocols\. They are reported for transparency and instrument history; no claim in the main text relies on them\.

#### \(a\) Pilot probe protocol \(superseded by §[4](https://arxiv.org/html/2607.09691#S4)\)\.

Probes minted from the scored source \(“answerable only from this source”\), answered and graded by the same model, on in\-house code \(n=15n\{=\}15\): source15/1515/15, summaries0/150/15\. Under the honest protocol of §[4](https://arxiv.org/html/2607.09691#S4), the source control falls to0\.6000\.600— a measure of how much circular minting and self\-judging inflate positive controls — while the boundary itself survives\.

#### \(b\) Act\-view ladder \(own code, self\-judged, construction\-guaranteed positives\)\.

Which rendering suffices to act on a single method \(n=18=6n\{=\}18=6methods×\\times3 probes\)? Full class1\.001\.00at18,66118\{,\}661tokens; UML\-skeleton\+\+body1\.001\.00at2,8142\{,\}814;method body alone1\.001\.00at900900\(≈20×\{\\approx\}20\\timesfewer than the class\); signature\-only0\.060\.06\. Suggestive that the body is the budget — butmethod\_only=1\.00=1\.00is partly guaranteed by construction \(the answerer sees the source the probe was minted from\), so we treat this as a hypothesis for a future test\-minted replication, not a finding\.

#### \(c\) Hierarchical descent vs\. flat retrieval \(own code,n=16n\{=\}16queries\)\.

Summary\-keyed descent over an architecture tree did not beat flat retrieval \(flat0\.8750\.875\[0\.64, 0\.97\] vs\. cumulative\-summary descent0\.8120\.812\[0\.57, 0\.93\]\); residual\-summary keys were worse \(0\.5620\.562\)\. Untested at the repository scales where hierarchy could matter\.