{"id":"23461183-8e20-4d38-91e2-057d0a04751d","arxiv_id":"2608.08266","paper_version":1,"verdict":"CONDITIONAL","confidence":"MODERATE","novelty_score":6.0,"correctness_risk":"medium","formal_verification":"none","parameter_count":0,"one_line_summary":"A systematic study shows that an LLM's internal code-correctness signal depends strongly on extraction configuration and fitting data, and that mutation-isolated bugs do not transfer to ranking real candidates.","lead":"This paper tests whether the hidden \"correctness signal\" that large language models carry inside their internal states is stable, by varying how the signal is extracted and what data is used to extract it. It finds that no single extraction recipe works across benchmarks and models, and that carefully isolating the bug in training pairs does not improve the signal.","discovery_kind":"extension","skeptic_critique":{"model":"deepseek-v4-flash","headline":"RQ2's 'isolating the fault does not help' rests on AST mutations that may not resemble real model mistakes; a transfer test with realistic single-fault pairs is needed.","rationale":"The reader's weakest-assumption analysis identifies the same load-bearing concern I find: RQ2's negative conclusion depends on injected mutations being a valid proxy for the mistakes LLMs make in real code generation. The authors themselves flag this in Section VII, and my reading of Tables V and VI confirms that the M-Only direction's high in-isolation accuracy only validates learnability within the mutation distribution, not representativeness of the test distribution. The MC confound control addresses surface-form variation but not the deeper mismatch between a direction fit on 'solution vs. mutated copy' and a test set of independently generated failing attempts. A concrete transfer experiment with LLM-injected or semantically realistic single-fault pairs would directly resolve the ambiguity: it holds the protocol fixed and swaps only the source of the incorrect programs. If transfer stays low, the conclusion is robust; if it recovers, the paper's headline overreaches. Since the paper already acknowledges this threat and a CONDITIONAL verdict is appropriate, I do not propose changing the reader's verdict.","tokens_in":25460,"tokens_out":3717,"duration_ms":39272,"concrete_test":"Construct a fitting set from realistic single-fault pairs on BigCodeBench, e.g., the LLM-injected semantic-error pairs of Kassem et al. [58] or by prompting a strong LLM to introduce one semantic error per canonical solution and keeping only pairs whose mutant fails the native test suite. Then run the exact Section III-F/Section V transfer protocol: mean-diff, weighted sampling, fit and validate on these pairs, test on BigCodeBench's 1-of-4 candidate ranking. If transfer accuracy remains near 19-20%, the RQ2 negative result survives; if it rises substantially toward the 56.7% in-distribution level, the failure is attributable to AST mutant realism rather than to fault isolation.","verdict_should_be":"UNCHANGED","load_bearing_attack":"RQ2's central negative result—that isolating the bug-causing change does not help—is established by a transfer experiment in which the fitting pairs are canonical solution + rule-based AST mutant (Section III-F). The high in-isolation separability (83.3% on BigCodeBench) only shows that a direction can separate held-out mutations from the same generator; it does not show that this mutation distribution resembles the plausible failing attempts used at test time. Section VII concedes the load-bearing limitation: 'our mutation pipeline only checks types, not whether an edit resembles a mistake a developer or a model would plausibly make.' The 37.1-point drop from the in-distribution fit (56.7%) to the M-Only transfer fit (19.6%) on BigCodeBench could therefore be caused by unrepresentative injected bugs rather than by fault isolation as such. The MC variant adds surface confounds, not fault realism, and the held-out mutant separability positive control is circular with respect to representativeness: it only verifies learnability within the same mutation distribution. Thus the paper's second conclusion—'isolating the fault does not help'—is not yet established for realistic model mistakes.","agreement_with_reader":"agree"},"referee_report":{"model":"deepseek-v4-flash","summary":"The paper investigates whether internal linear \"correctness directions\" in LLMs are robust properties of the model or artifacts of how they are constructed. RQ1 sweeps a design space of two construction methods (PCA, mean-diff), three prompt framings, two read-out locations, two fitting-data sources, four models, and two benchmarks, reporting that no single configuration is best and that only the construction method (mean-diff over PCA) generalizes across benchmarks. RQ2 builds controlled correct/incorrect pairs by injecting single faults into canonical solutions via typed AST mutations, with optional behavior-preserving rewrites, and finds that directions fit on such pairs separate held-out mutants with high accuracy (83.3% on BigCodeBench) but transfer poorly to ranking the benchmarks' own candidate implementations (19.6% on BigCodeBench vs. 56.7% for the in-distribution fit; 47.6% vs. 52.8% on HumanEval). The paper concludes that no single configuration is best and that isolating the fault does not help, and it provides a public replication package.","tokens_in":25607,"tokens_out":3930,"duration_ms":40087,"significance":"If the results hold, the paper contributes a useful negative result to the literature on internal code-correctness representations: the captured direction is configuration-dependent and contrast-dependent, rather than a stable model property. The study is disciplined in several ways: disjoint fitting/validation/test partitions, tenfold cross-validation, reproduction of the prior work's single configuration, explicit layer-selection protocol, and a per-model confound analysis in the appendix. The replication package is a concrete strength. However, the central quantitative claims lack significance tests and confidence intervals, and the RQ2 conclusion rests on a mutation distribution whose representativeness the authors themselves concede is unverified. The conclusions are therefore plausible but not yet established at the strength stated in the abstract.","major_comments":[{"comment":"The central RQ2 comparison is reported as point estimates without uncertainty: 56.7 vs. 19.6 on BigCodeBench and 52.8 vs. 47.6 on HumanEval. The HumanEval gap is only 5.2 percentage points, and without fold-level paired tests, bootstrap intervals, or effect-size statistics it is not possible to tell whether this drop is distinguishable from noise. The paper's conclusion that \"isolating the fault does not help\" is stated unconditionally, but the evidence is strong only for BigCodeBench and weak for HumanEval. Please report variance estimates and paired significance tests for these comparisons, and state which conclusions are supported on each benchmark separately.","section":"Section V, Table V"},{"comment":"The paper's own limitation statement says: \"our mutation pipeline only checks types, not whether an edit resembles a mistake a developer or a model would plausibly make.\" This is load-bearing for RQ2's transfer failure: if the AST mutations are unrepresentative of real model errors, the drop from 56.7% to 19.6% could reflect the unnaturalness of the injected faults rather than the claim that fault isolation does not help. The held-out mutant separability result (Section V-1) verifies learnability within the mutation distribution, but it is not a positive control for representativeness. To support the abstract's second conclusion, the paper needs either a transfer experiment with more realistic single-fault pairs (e.g., LLM-generated semantic errors such as those of [58], or semantic bug seeding as in [34]) or a carefully weakened claim that the result holds for rule-based mutations but is untested for realistic faults.","section":"Section VII, Internal Validity"},{"comment":"The ANOVA decomposition is presented with variance shares such as \"fit x test framing 15%\" and \"benchmark x model 7%\", but no significance tests or confidence intervals are reported for these shares, and the \"best level flips\" conclusions in panel 2 are inferred from means without quantifying uncertainty. Since RQ1's headline conclusion is that \"no single configuration is best,\" the claim should be supported by pairwise comparisons or interactions tests with appropriate multiple-comparison correction, not only by inspection of the largest point estimates. This is especially important because HumanEval shows large model-dependent variation (model identity 51% of variance), and some of the best-configuration differences in Tables II and III may be within fold-to-fold noise.","section":"Section IV, Table IV"}],"minor_comments":[{"comment":"The name \"AccVal\" for a test-time selection accuracy is confusing because the metric is reported at test time; consider renaming it to something like \"selection accuracy at the validation-selected layer\" to avoid the implication that it is a validation-set number.","section":"Section III-A"},{"comment":"The first row is labeled \"Configuration of prior work\" and the text says reproduction was confirmed, but the prior published accuracies are not listed; including them in the table or text would let the reader verify the reproduction claim directly.","section":"Tables II and III"},{"comment":"The distinction between weighted and paired sampling is described briefly; clarifying how many fitting pairs remain after sampling (e.g., average number of mutants per task) would help the reader interpret the M-Only and MC results.","section":"Section III-F"},{"comment":"The Function panel's text \"Write a correct/incorrect implementation\" may be a template rather than an actual stimulus; please clarify whether the actual stimulus contains both variants or is shown for both conditions.","section":"Figure 2"},{"comment":"The appendix's handling of rows marked dagger and double-dagger is transparent and commendable, but the phrase \"support no conclusion\" should be read alongside the main-text claim that MC tracks M-Only; consider moving the caveat into Section V-7 so the limitation is visible in the main body.","section":"Appendix, Table VII"}],"recommendation":"major_revision","confidential_remarks":"The paper is honest about its main threat, and the self-citation to [11] is used as a reproduced baseline rather than as a hidden dependency. The main risk is overstatement: the abstract's two headlines are stated more strongly than the statistical evidence and the mutation-representativeness control currently allow. A revision that adds uncertainty quantification, paired tests, and a more representative fault-transfer check, or that carefully narrows the claims, would address the concerns."},"author_rebuttal":null,"desk_editor":{"model":"deepseek-v4-flash","letter":"You should know two things about this paper. First, it is a genuinely useful systematic empirical study of how the way you build a linear probe for code correctness changes what you get. Second, its main negative result about fault isolation is real but narrower than the abstract makes it sound: it is a result about this mutation pipeline, not about \"the fault\" in general.\n\nWhat is new: prior work fixed one construction (PCA, last token, neutral fit, concept test). This paper varies all three axes across four models and two benchmarks, with a clean fit/validate/test protocol and a replication package. The RQ2 pipeline is also careful: AST mutations with type checks, test-suite filtering, behavior-preserving confounds, and per-model layer-selection checks. They reproduce the prior baseline before extending it. Credit where due: the discipline is real.\n\nWhat holds up: the RQ1 sweep convincingly shows that accuracy depends on configuration and benchmark. Their ANOVA decomposition, even without significance tests, makes the point that the benchmark acts as a modulator: read-out location reverses between HumanEval and BigCodeBench, and the source of the fitting data dominates on BigCodeBench. The construction method result (mean-diff over PCA) is consistent and useful.\n\nSoft spots, in proportion. The lack of confidence intervals is a real weakness but a minor one for a first map of the space. The numbers are noisy, but the headline gap between 19.6 and 56.7 on BigCodeBench is far beyond fold noise, so the qualitative conclusion survives. The bigger soft spot is RQ2's interpretive leap. The direction fit on mutations is fit on pairs that differ by one injected fault; the test-time candidates are independent implementations. The transfer failure could be because the mutations are not representative of how LLMs actually go wrong. The authors acknowledge this in Section VII, so it is not hidden, but it does mean \"isolating the fault does not help\" is better read as \"isolating these rule-based faults does not help.\" That is still a genuinely interesting finding, but it is a finding about this mutation distribution.\n\nWho it is for: people building internal-state confidence or ranking signals for code, and anyone evaluating linear probes on code. It deserves a serious referee; the experimental design is sound, the claims are falsifiable, and the replication package makes verification feasible.\n\nMy recommendation: send it to peer review. Ask for uncertainty estimates on the central comparisons and a closer discussion of mutant representativeness, maybe with an additional transfer test using LLM-generated single-fault pairs. But do not desk-reject it.","headline":"A carefully executed configuration sweep of linear probes for code correctness; the RQ2 negative result is real for this mutation pipeline but should not be overgeneralized.","tokens_in":26177,"tokens_out":1801,"would_cite":true,"duration_ms":17635,"reading_group":"yes","serious_thinker":"yes","would_accept_peer_review":true},"rs_alignment":null,"lean_confirmation":null,"pith_extraction":{"msc":[],"pacs":[],"model":"deepseek-v4-flash","headline":"No single configuration captures the internal code-correctness signal, and isolating the injected fault makes transfer worse.","keywords":["linear probing","code correctness","hidden states","LLM internal representations","mutation testing","representation robustness","HumanEval","BigCodeBench"],"falsifier":"Fit a direction on mutants generated by an LLM-based fault injector that mimics the mistakes models plausibly make, then test it on BigCodeBench's candidate-ranking task: accuracy at the 56.7% in-distribution level would refute the claim that isolating the fault does not help.","tokens_in":25227,"feed_emoji":"🐛","tokens_out":7471,"duration_ms":60230,"temperature":0.7,"pith_summary":"The paper asks whether the internal code correctness signal that prior work extracted from LLM hidden states is a robust property of the model or an artifact of how it was captured. By sweeping construction method, prompt framing, hidden-state location, fitting data, and model across two benchmarks, it finds that no single configuration is best: only the construction method (mean-diff over PCA) generalizes, while the best framing, read-out location, and model change with the benchmark. In a second experiment, it builds correct/incorrect pairs that differ only in the injected fault using rule-based mutations, and shows that a direction fit on these pairs separates them well in isolation (83.3% on BigCodeBench) yet ranks the benchmark's own plausible failing attempts far worse (19.6%) than an in-distribution fit (56.7%). The implication is that the captured direction is a property of the configuration and the contrast set, so correctness probes must be tuned per setting and reported with their configuration.","feed_headline":"No single configuration best captures LLM code correctness","feed_subtitle":"Even a probe that separates mutated code 83% ranks real failing candidates at 20%.","key_machinery":"The central object is the code correctness direction, a vector in hidden-state space extracted by linear probing from contrasting correct and incorrect program pairs at each layer of a transformer LLM. The paper compares two constructions: PCA, which takes the first principal component of the per-pair representation differences, and mean-diff, the difference of the two class means; it also varies the prompt framing (neutral, concept, function) and the read-out location (last token vs. response average). Candidate programs are scored by projecting the hidden state at the chosen location onto the direction. For RQ2, the machinery is a controlled-pair pipeline: 20 rule-based AST mutation operators seed a single fault into a correct solution, mutants are kept only if they fail the benchmark's test suite, and behavior-preserving rewrites are added as confounds; the resulting directions are tested both in isolation on held-out pairs and in transfer on the benchmark's 1-of-4 selection task. This pipeline is what demonstrates the separation-versus-transfer gap that grounds the paper's main conclusion.","core_discovery":"On its own terms, the paper claims that the quality of a captured code correctness direction depends on how it is built, what data it is fit on, and which model it is read from, rather than being a fixed internal property of the model. It establishes this by sweeping 576 configurations and reporting that the fit-by-test framing interaction and the model dominate the variance, while the benchmark decides which choices matter. It additionally claims that isolating the bug-causing change does not improve the direction: directions fit on mutant-controlled pairs separate those pairs at 71.6–83.3%, but transferring to the benchmark's own candidate rankings yields 19.6% on BigCodeBench versus 56.7% for an in-distribution fit, with the gap only partly recovered by selecting the read-out layer on the benchmark itself. The conclusion is that telling a solution from a perturbed copy of itself is not the same as judging an independent candidate, so the correctness direction is configuration-dependent.","pith_inferences":["If correctness directions are configuration-dependent, comparisons between correctness probes and other internal signals such as truthfulness or sentiment must control for construction and data, or the differences may be artifacts.","The same isolation-versus-transfer protocol could be applied to other probed properties such as security or efficiency; the paper's logic predicts that high in-isolation separability will not by itself yield transfer to real candidate judgments.","The BigCodeBench-specific failure may scale with task diversity and candidate independence; a testable extension would vary mutation count and task difficulty within one benchmark to map where the transfer gap appears.","Since selecting the layer on the benchmark recovered most of the BigCodeBench gap, future work should report validation-selected and oracle-layer accuracies separately to distinguish direction quality from layer-selection cost."],"forward_implications":["Practitioners should tune the read-out location and framing per model and benchmark on a validation split rather than reuse a fixed recipe.","Reported accuracies for internal correctness directions should include the configuration sweep's validation-selected accuracy, since a single headline number can overstate the technique.","Directions fit on mutation-controlled pairs cannot be assumed to judge independent candidate implementations; high in-isolation separability does not imply transfer.","Mean-diff is the safer default construction method, since it is the only choice whose preferred setting never reverses across the studied conditions."],"supporting_citations":[{"why":"Provides the baseline code correctness direction setting (PCA, last-token read-out, neutral fit, concept eval), the data it reproduces, and the claim that the direction beats model confidence.","marker":"[11]"},{"why":"Supplies the linear probing framework, PCA direction construction, and the neutral/concept/function framings that RQ1 varies.","marker":"[15]"},{"why":"Reports that mean-diff often recovers directions better than PCA, motivating the construction-method comparison.","marker":"[16]"},{"why":"Establishes mutation testing as the standard way to create single-fault program pairs, grounding the RQ2 controlled-pair pipeline.","marker":"[26]"},{"why":"Provides the HumanEval benchmark used for in-distribution and out-of-distribution fitting and testing.","marker":"[2]"},{"why":"Provides BigCodeBench, the benchmark where the gap between mutation-fit transfer and in-distribution fit is largest.","marker":"[17]"},{"why":"Supply the MBPP/MBPP+ dataset used as an out-of-distribution fitting source in RQ1.","marker":"[18], [19]"}],"fun_headline_variants":["Correctness probe quality varies with extraction method","LLM code correctness signal is configuration-dependent","No universal probe for LLM code correctness","Isolating faults doesn't improve code correctness probes"],"cache_read_input_tokens":3200,"weakest_assumption_plain":"The conclusion that isolating the fault does not help assumes that rule-based AST mutations failing the benchmark's test suite are a reasonable proxy for the mistakes LLMs actually make in code generation.","fun_headline_variants_meta":{"raw":{"variants":["Correctness probe quality varies with extraction method","LLM code correctness signal is configuration-dependent","No universal probe for LLM code correctness","Isolating faults doesn't improve code correctness probes"]},"model":"deepseek-v4-flash","effort":"low","cost_usd":0.000422,"raw_usage":{"total_tokens":2150,"prompt_tokens":907,"completion_tokens":1243,"prompt_tokens_details":{"cached_tokens":384},"prompt_cache_hit_tokens":384,"prompt_cache_miss_tokens":523,"completion_tokens_details":{"reasoning_tokens":1186}},"tokens_in":523,"tokens_out":1243,"duration_ms":7960,"temperature":1.0,"reasoning_tokens":1186,"cache_read_input_tokens":384,"cache_creation_input_tokens":0},"cache_creation_input_tokens":0},"created_at":"2026-08-12T00:12:20.966375+00:00","model_set":{"reader":"deepseek-v4-flash"},"falsifier":"Fit a direction on mutants generated by an LLM-based fault injector that mimics the mistakes models plausibly make, then test it on BigCodeBench's candidate-ranking task: accuracy at the 56.7% in-distribution level would refute the claim that isolating the fault does not help.","supporting_citations":[{"cited_title":"On LLMs’ internal representation of code correctness,","cited_arxiv_id":null,"evidence_quote":"Provides the baseline code correctness direction setting (PCA, last-token read-out, neutral fit, concept eval), the data it reproduces, and the claim that the direction beats model confidence."},{"cited_title":"Are mutants a valid substitute for real faults in software testing?","cited_arxiv_id":null,"evidence_quote":"Establishes mutation testing as the standard way to create single-fault program pairs, grounding the RQ2 controlled-pair pipeline."}],"review_version":1}