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An AI reviewer named a seeded authorization bug in 9 of 10 valid diff runs and 0 of 10 valid raw-source runs in one small experiment. That result is worth noticing, but it does not show that diff review is generally better: the strongest diff runs used a different harness setting, the test covered only one defect, and the tool accepted none of the findings.
What the experiment actually tested
Ahmad Ammar reports running the experiment on 21 August 2026 with a defect he had written into mayDeleteAccount: the function returned user.role !== 'admin', allowing the users who should not have deletion permission. He asked a small local model, identified in the report only by the alias local-advisor-v1:latest, to “Review for authorization and correctness defects.” The original inputs are private, so readers cannot reproduce the exact comparison from the report alone. Ammar’s experiment report
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The headline counts are diagnoses among valid runs, not a count of independent bugs or a benchmark of code reviewers. The author reports five input arms:
| Input arm | Attempts | Valid runs | Hand-counted diagnoses |
|---|---|---|---|
| Raw source | 5 | 5 | 0 |
| Source embedded in a file | 5 | 5 | 0 |
Diff with --trust-material-paths |
5 | 4 | 4 |
| Same diff on a HEAD tree, with the flag | 3 | 3 | 3 |
| Same diff without the flag | 3 | 3 | 2 |
The flagged diff arms yielded seven diagnoses from seven valid runs; the unflagged arm yielded two from three. Across diff input, that is 9 of 10 valid runs. One diff attempt crashed, so the rate across all 11 diff attempts is 9 of 11. Only one of the nine valid diff diagnoses was unhedged; the other eight expressed uncertainty. Raw source produced no diagnoses in 10 valid runs.
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Why the gap does not prove that diff formatting caused it
The raw-source and diff results are a striking contrast, but the experiment did not vary presentation alone. The arms with the strongest diff results used --trust-material-paths; the harness flag tells the tool to treat material as a diff and extract file paths for scope checks. The report does not demonstrate that the compared inputs were otherwise matched.
A prompt-size estimate was 1,144 tokens with or without the flag, but the author did not compare the prompts themselves. Equal estimated size does not establish identical content or equivalent context. The results are therefore consistent with a presentation effect, but cannot isolate it from the flag or other differences in how the inputs were prepared.
The experiment also used repeated runs on one seeded defect. Those repetitions show how this setup behaved on that example; they are not 21 independent tests of bug-finding ability. The author hypothesizes that a diff may frame code as an intentional change, but that explanation was not measured.
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A diagnosis in prose was not an accepted finding
The model sometimes named the defect in free-text control and evidence fields marked “unverified model claims.” The tool’s acceptance step required a finding to name a file and line and quote evidence copied from that line. It accepted 0 of 20 valid runs. In other words, a model could describe the bug while still failing to produce a finding the tool would accept. These results do not amount to nine automated catches.
That distinction matters when evaluating a reviewer for actual use. A useful result is not just a plausible explanation: it must identify the changed code precisely enough to inspect, support its claim with relevant evidence, and survive the workflow’s validation rules. Count model diagnoses and accepted findings separately.
Input size and scoring add more reasons for caution
The inputs measured 67 bytes for raw source, 390 bytes for the diff, and 1,550 bytes for source embedded in a file. The smallest and largest inputs each scored zero, while the diff scored 9 of 10 overall. Three sizes do not establish a monotonic relationship between length and diagnosis, nor do they isolate length as a cause.
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An audit corrected one false-positive label and separated one invalid-output run from completed reviews. In one corrected raw-source run, the model described the inverted condition as a standard control that correctly limited deletion to admins—an explanation that reversed the actual behavior. The author’s pattern matcher counted 7 of 11, compared with his hand count of 9 of 10; wording differences and disagreements resolved by manual checking were among his reasons for caution about automated scoring. A result should therefore be audited against the actual output, not accepted solely because a matcher found a phrase.
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How to test an AI reviewer in your own workflow
Use a small, controlled test that reflects how your team actually supplies code for review. Keep the reviewer, instructions, context and harness settings fixed when comparing raw source with a diff; otherwise, a difference in results cannot be attributed confidently to the format.
- Prepare known buggy and corrected fixtures. Seed defects that your team can verify, then include corrected versions to reveal whether the reviewer continues to report problems that are no longer present.
- Match the review conditions. Hold model version, instructions, surrounding context, repository state and tool settings constant. Change only the input format you intend to evaluate.
- Repeat runs, but distinguish repetition from coverage. Repeated runs on one defect can expose inconsistent outputs. Add multiple independent defects before drawing conclusions about general detection ability.
- Report two rates for each condition. Show diagnoses among valid outputs, and successful diagnoses across all attempts with crashes and invalid outputs counted as failures. State the denominators so a reader can tell which rate is being quoted.
- Score the whole result. Track whether the defect was named, whether the finding was accepted and actionable, how often the reviewer hedged, false positives on corrected fixtures, and invalid-output or crash rates.
- Audit borderline cases by hand. Check whether the explanation describes the code’s real behavior, especially when the model sounds confident or a pattern matcher supplies the score.
For comparing tools or review workflows, use the same fixtures and evaluation criteria. The reported experiment supplies no comparative performance data for other tools, so it cannot establish which reviewer is best.
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What the report does—and does not—say about models
The tested model is described by a local alias, not a recorded binary digest. The author says a later Ollama inspection reported a Qwen 3.5 architecture, 4.7 billion parameters, Q4_K_M quantization and an 8,192-token context, but the report did not record a digest in August to establish that those were the properties of the exact tested build. Treat those details as an inspection of a later build, not verified specifications for the experiment.
The report does not establish whether the observed gap applies to larger or frontier models. Its original inputs are private, and the public tool tests its method on different material, limiting reproduction of the reported ratios. The author described a follow-up using pinned frontier-model versions and matched settings as prospective; the report provides no results from that follow-up.
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