acceptodds
Under review as a conference paper at ICLR 2027

Attributing Failures in Executable Language Model Reasoning

Abstract

Quantitative reasoning with language models increasingly runs through an executable proxy: the model writes a program, symbolic expression, or tool call, and a deterministic system produces the answer. When such a pipeline underperforms unrestricted language-model reasoning, end-to-end accuracy does not reveal which stage is responsible. We study this attribution problem with controlled substitutions that isolate representation construction, deterministic execution, and answer evaluation while holding budget and scoring fixed. Across four established reasoning datasets and two model families, superficially similar gaps resolve into different causes: a TabMWP gap of 0.117 disappears at matched generation budget, and most of a TAT-QA gap traces to a scorer-side percent convention. A complete census of frozen baseline failures separates crash-type (execution-invalid) errors from executable-but-semantically-wrong ones. A pre-registered prospective study then shows that attribution predicts intervention response: repair gains are concentrated in the prospectively diagnosed execution-invalid class (interaction ; cross-model ; pooled , cluster bootstrap, over 460 question-condition evaluations spanning 160 problems), with zero repair-induced errors. A matched self-debugging baseline reproduces the effect, locating the mechanism in the execution-feedback intervention class. Execution-valid semantic errors require different evidence and interventions.

Primary area:
neurosymbolic & hybrid AI systems (physics-informed, logic & formal reasoning, etc.)
Keywords:
large language models, executable reasoning, program synthesis, neuro-symbolic reasoning, tool-augmented language models, representation synthesis, execution verification, test-time inference

Reviews

Among:
Shape:
1234this paper, Bottom 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.25 over 4 reviews, above 49% of the others.
Reviewer_a6H2OpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper studies failure attribution in executable language-model reasoning pipelines, separating representation construction, deterministic execution, and answer evaluation. Through oracle-representation substitutions, generation-budget controls, scorer audits, and a failure census across four datasets, the authors show that superficially similar accuracy gaps can have different causes. A prospective study on MATH evaluates verifier-gated repair across two model families and generation budgets. Execution feedback recovers a substantial fraction of execution-invalid outputs, while a matched self-debugging baseline achieves similar results. Executable but semantically incorrect representations remain largely unresolved.

Critical strengths
  1. The paper provides concrete evidence that evaluation interfaces can substantially distort conclusions about reasoning ability. The TabMWP budget control and TAT-QA percent-conversion audit demonstrate why end-to-end accuracy alone cannot reliably identify representation-construction failures. These examples are useful because they change the interpretation of substantial measured gaps through targeted controls, rather than merely cataloguing errors.
  2. The study includes valuable controls and reports limitations candidly. The matched self-debugging comparison attributes the recovery to execution feedback rather than verifier-specific machinery. The authors also report unsuccessful predictions, retained oracle-construction errors, and limited semantic-correction performance. Frozen responses, held-out prospective questions, and bootstrap clustering by problem strengthen the empirical analysis and avoid treating repeated question-condition evaluations as independent problems.
Critical weaknesses
  1. The prospective interaction does not establish differential repairability across diagnosed classes. In Section 7, execution-valid examples receive no repair under the gated policy. Consequently, Δ0=0\Delta_0=0 follows from the intervention design, rather than demonstrating that these examples would not benefit from repair. Execution-invalid outputs also have zero baseline answer accuracy under this pipeline, so their positive improvement primarily measures successful recovery after receiving additional computation. The authors explicitly acknowledge the untreated nature of E0E_0, but the abstract and surrounding discussion still present Γ\Gamma as stronger evidence of predictive attribution than this design supports. The experiment establishes useful recovery among flagged failures; it does not independently establish that the diagnosis identifies greater treatment benefit than an alternative allocation of the same repair budget. This distinction matters because prospective predictive validity is a central claimed contribution.
  2. The breadth and generality of the attribution findings remain limited. The strongest budget and scorer findings concern particular implementation choices in the authors’ pipelines, evaluated on subsets of 30–100 questions. The prospective repair study is confined to MATH and two model families, while the broader failure census contains only 61 cases. These results establish that such confounds can occur, but provide limited evidence about their prevalence in established executable-reasoning systems. Moreover, the TabMWP control appears to change both the token limit and empty-output regeneration policy, complicating attribution specifically to truncation. The oracle comparison also cannot generally provide a formal upper bound on representation-construction loss when oracle errors are retained and some oracle results use smaller subsets. Together, these issues limit the strength of the paper’s broader methodological conclusions.
Questions for authors
  1. Clarification of the main estimand: Given that E0E_0 receives no repair, should Γ\Gamma be interpreted as recovery under a gated policy rather than differential treatment response? Is there an existing matched-budget control that establishes the diagnosis’s value beyond detecting an execution failure and applying standard self-debugging?
  2. Clarification of the budget intervention: In the TabMWP comparison from 0.850 to 0.967, were the regeneration policy and all decoding settings held fixed while only the token limit changed? Appendix G reports 14/60 truncated outputs, whereas the accuracy difference corresponds to seven questions. How do these counts relate?
  3. Clarification of the oracle-based attribution: What assumptions justify describing AOPX−APXA_{\mathrm{OPX}}-A_{\mathrm{PX}} as an upper bound on representation-construction loss, given imperfect oracle representations and differing evaluation subsets? Can the authors distinguish a diagnostic reference gap from a guaranteed bound?
3 comments
AuthorsOpenReview ↗

Response to Reviewer a6H2 (1/2)

We thank the reviewer for their comments.

What the gate measures, and what follows from its construction

"Consequently, Δ0=0\Delta_0=0 follows from the intervention design, rather than demonstrating that these examples would not benefit from repair."

Section 7 states it at the definition: E0E_0 leaves the loop at its first verifier pass, so Δ0=0\Delta_0=0 by construction and Γ\Gamma is the E1E_1 recovery rate, not a treatment effect on valid representations (Section 7; App. A). Two of the four frozen gate conditions hold for the same reason, Δ0≤0.05\Delta_0 \le 0.05 and Γ>0\Gamma>0, and the paper states this where they are listed (Section 7; App. O). A flagged representation does not execute, so its baseline accuracy is zero and a positive Γ\Gamma measures recovery after additional computation rather than a gain on records that could already answer. The empirical content is the invalid rate and the size of the recovery: on the gate-A sample the invalid rate is 6% at the natural budget and 21% under stress on Kimi, and 28% and 65% on GLM (Section 7; App. F), against pooled recovery 64/128 = 0.500 [0.397, 0.609], a cluster bootstrap over the 160 problems, 81 of which ever produce an E1E_1 (Section 7; Table 4; App. A).

Spending the same repair budget uniformly

"The experiment establishes useful recovery among flagged failures; it does not independently establish that the diagnosis identifies greater treatment benefit than an alternative allocation of the same repair budget."

At equal repair slots it does: 64 recoveries under the gate against 17.8 expected under uniform allocation across the 460 evaluations (3.6x; resampling of stored outcomes, p<0.001p<0.001; Section 7). The comparison re-allocates stored outcomes, so it spends the same calls and answers whether the diagnosis beats an alternative use of that budget rather than offering a second sampling arm. Revision. Section 7 reports the allocation control next to the pooled estimate, and Figure 2 shows the per-condition effects it aggregates.

W1: the interaction does not establish differential repairability

"The prospective interaction does not establish differential repairability across diagnosed classes."

Both halves of your W1 are answered in the two blocks above: the construction zero under "What the gate measures, and what follows from its construction", the allocation under "Spending the same repair budget uniformly". The abstract now reports both arms in the same sentence, and Section 7 gives Γ\Gamma as a recovery rate before any claim is made from it. Revision. the abstract, Section 7 and Section 9.

Breadth of the evidence

"The breadth and generality of the attribution findings remain limited."

The paper states the scope where the claims are made: 30-100 questions per split, prospective gates on MATH with two models, and a TabMWP prediction tested by controls rather than by a second prospective gate (Section 9; App. B). Within that scope the census counts and their restored version are printed with the per-case labels behind them (Section 5; Table 9; App. H). No dataset was added in the revision; the generality claim is that these confounds can occur and are separable by control, not that their prevalence across systems is known (Section 9; App. B). Revision. Section 9 carries the design-context paragraph and App. B lists every subset with its sample-id hash.

W2: breadth of the attribution findings

"The strongest budget and scorer findings concern particular implementation choices in the authors' pipelines, evaluated on subsets of 30-100 questions. The prospective repair study is confined to MATH and two model families, while the broader failure census contains only 61 cases. These results establish that such confounds can occur, but provide limited evidence about their prevalence in established executable-reasoning systems."

The first half is answered in the block above; the TabMWP control is decomposed in Q2 below, and the oracle comparison is answered in "The oracle gap is a diagnostic reference, not a bound" below. The census is printed with its restored version and its per-case labels (Section 5; Table 9; App. H). Revision. Section 4, Section 5, Section 9 and Table 9.

AuthorsOpenReview ↗

Response to Reviewer a6H2 (2/2)

Q1: the estimand, and a matched-budget control

"Clarification of the main estimand: Given that E0E_0 receives no repair, should Γ\Gamma be interpreted as recovery under a gated policy rather than differential treatment response? Is there an existing matched-budget control that establishes the diagnosis's value beyond detecting an execution failure and applying standard self-debugging?"

Yes: Γ\Gamma is the recovery rate under the gated policy, and Section 7 states this at the definition ("What the gate measures, and what follows from its construction" above). The matched-budget control you ask for exists in two forms: the allocation of the same repair slots under "Spending the same repair budget uniformly", and the forced re-check on the class the gate leaves alone in Reviewer J4cV's response under "Repair attempted on the class the gate leaves alone". Against standard self-debugging, the matched comparison is in Reviewer UiSC's response under "The self-debugging tie and what the verifier contributes". Revision. Section 6 and Section 7.

Q2: the TabMWP budget intervention

"In the TabMWP comparison from 0.850 to 0.967, were the regeneration policy and all decoding settings held fixed while only the token limit changed? Appendix G reports 14/60 truncated outputs, whereas the accuracy difference corresponds to seven questions. How do these counts relate?"

That comparison is Kimi at 800 tokens against the oracle at 1,200 with one regeneration, so two factors move in it, which is why the paper replaces it with a within-model decomposition. On Kimi the parser scores 51/60 under the v2 scorer at 800 tokens and 58/60 at 1,200 with one regeneration; on GLM-5.3-Flash the decomposition is 55/60 at 800, 48/60 at 1,200 without regeneration, and 55/60 with one regeneration (Section 4; Table 10). Budget alone does not close the gap - 55/60 at 800 falls to 48/60 at 1,200 without regeneration - and one regeneration restores the seven. The 14/60 figure was the 500-token pilot; at 800 tokens there are seven empty responses, which is the same seven questions as the accuracy difference (App. F). Revision. Section 4 and Table 10.

The oracle gap is a diagnostic reference, not a bound

"The oracle comparison also cannot generally provide a formal upper bound on representation-construction loss when oracle errors are retained and some oracle results use smaller subsets."

The paper no longer calls it an upper bound. On the oracle-subset of 30 questions the parser reaches 0.800 against the oracle's 0.933, and on all 60 questions the parser is 0.767, so VP=0.133V_P = 0.133 on the matched set (Table 1; Table 2 (+)). VPV_P is a lower bound on the headroom attributable to representation construction, because the oracle retains its construction errors (App. V), and the paper now calls AOPX−APXA_{\mathrm{OPX}}-A_{\mathrm{PX}} a diagnostic reference gap (Section 3; App. A). Revision. the matched denominator is printed in Table 1 rather than only in the appendix, and Section 3 and Section 9 use the reference-gap formulation.

Q3: the oracle comparison as a bound

"Clarification of the oracle-based attribution: What assumptions justify describing AOPX−APXA_{\mathrm{OPX}}-A_{\mathrm{PX}} as an upper bound on representation-construction loss, given imperfect oracle representations and differing evaluation subsets? Can the authors distinguish a diagnostic reference gap from a guaranteed bound?"

The two assumptions you name are the two the paper states - the oracle retains its construction errors, and the MATH comparison runs on the matched subset (Table 1; App. V). The paper now uses your distinction and calls the quantity a diagnostic reference gap (Section 3; App. A). Revision. Section 3, Section 9, Table 1, App. A, App. V.

AuthorsOpenReview ↗

Follow-up to Reviewer a6H2

We would like to follow up on our rebuttal before the author-reviewer discussion closes on Nov. 18 at 11:59 p.m. AoE. The rebuttal answers each of your comments in detail. In particular, it covers the interpretation of Γ\Gamma and Δ0\Delta_0. Section 7 now defines Γ\Gamma as the recovery rate under the gated policy and adds the matched-budget control you asked for. Spending the same repair slots uniformly at random gives 17.8 expected recoveries, against 64 under the gate. A forced re-check on the 107 records that the gate leaves alone changes 20 of them and lowers accuracy by 0.13 (Table 5, Table 11). The rebuttal also covers the TabMWP budget comparison, which is now a within-model decomposition (Table 10), and the oracle comparison, which the paper now presents as a diagnostic reference gap with matched denominators (Section 3, Table 1). We hope these additions give a fuller picture of the work.

We would also like to highlight the main result of the paper. Executable reasoning, as in PAL, Program-of-Thoughts and ToRA, is already a standard approach to quantitative reasoning, and these systems are compared by end-task accuracy. Our controls show that two gaps that such a comparison would attribute to the model come from the evaluation interface. The TabMWP gap of 0.117 shrinks to 2/60 at a matched generation budget with one regeneration, and the TAT-QA gap of 0.15 shrinks to 0.016 once the scorer stops converting percent answers twice. These results are, to the best of our knowledge, new in the literature on executable reasoning. Your review notes that these controls change the interpretation of substantial measured gaps, and we hope the new controls complete this picture.

We would be very grateful if you could read the rebuttal before the discussion closes and tell us what you think. If it resolves your concerns, we kindly ask you to consider raising your score. If anything remains open, please let us know and we will answer right away.

Thank you for your time and consideration. We look forward to your reply.

Reviewer_UiSCOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
1
Presentation
2
Soundness
2
Read review
Paper summary

This paper proposes separating erros in representation generation, execution, and scoring, using oracle substitution, budget control, and verifier-gated repair. Across four datasets, it identifies evaluation artifacts and shows that execution feedback can recovr some invalid programs. However, the central claim that its diagnosis prospectively predicts repair effectiveness is inadequately tested: only diagnosed-invalid outputs receive repair, making several headline findings consequences of the intervention policy. Combined with inconsistent experimental accounting and an unjustified interpretation of the oracle gap, the evidence supports a narrower debugging case study than the paper’s broader attribution claims.

Critical strengths
  • The motivation is quite practical. Separating model errors from executor and scorer failures is valuable for evaluating executable reasoning systems.
  • The experiments are consisted to be quite thoughtful. The paper reports alternative scoring policies, failed predictions, a matched self-debugging baseline, and paired or clustered confidence intervals.
Critical weaknesses
  • Execution-valid outputs receive no repair, so their measured change is necessarily zero. The headline interaction therefore reduces to the recovery rate among invalid outputs. This establishes useful crash recovery, but leaves comparative repair effectiveness across failure classes untested.
  • The no harm result is much less informative than specified in the earlier part of the paper. The treated outputs are already incorrect, while valid outputs remain untouched, making zero harmful accuracy flips structurally expected. The claim that gating is "exactly as good as repairing everywhere" is also unsupported.
  • The hand-written oracle retains construction errors and sometimes uses different evaluation samples: MATH-confirm compares a 30-question oracle subset with a 60-question model evaluation. Such differences cannot cleanly isolate representation loss or establish how much improvement remains possible.
  • Generic self-debugging matches the stress-condition result, and the budget and scoring artifacts concern the authors’ own pipeline. These are useful engineering observations, but the paper does not convincingly establish the broader attribution advance on which its research contribution depends.
  • The experiment tests a simplified, single-round EVER adaptation on only 22 selected semantic errors, correcting three. That supports a narrow conclusion about this implementation and sample; it does not establish a general limitation of current semantic-correction methods.
Questions for authors

see weaknesses above

2 comments
AuthorsOpenReview ↗

Response to Reviewer UiSC

We thank the reviewer for their comments.

The self-debugging tie and what the verifier contributes

"Generic self-debugging matches the stress-condition result, and the budget and scoring artifacts concern the authors' own pipeline."

It ties under stress at 0.783, with 0/60 per-question disagreements, and the released baseline is itself failure-gated, so the difference between the two loops is the feedback string rather than the gate's decision (Section 6; App. J). The paper credits execution feedback with the recovery and gives the verifier the role of deciding when to spend it, plus the provenance channel on table tasks (Section 6). The variant that would have added machinery, M4, adds nothing over M2 (0.917 against 0.883 on the MATH screen), and the paper reports that as well (Section 6; App. I). Revision. Section 6 states the tie and the failed pre-registered prediction (iii) in the same paragraph as the gain.

W1: execution-valid outputs receive no repair

"Execution-valid outputs receive no repair, so their measured change is necessarily zero. The headline interaction therefore reduces to the recovery rate among invalid outputs."

The paper replaces the structural zero with a measurement of the class it covers (Reviewer J4cV, Q1). Revision. Section 7, Table 5, Table 11.

W2: the no-harm result and the claim of equivalence

"The no harm result is much less informative than specified in the earlier part of the paper. The treated outputs are already incorrect, while valid outputs remain untouched, making zero harmful accuracy flips structurally expected."

Agreed: zero harmful flips are what the design produces, and Section 7 now calls Δ0=0\Delta_0=0 the gate's precision rather than a treatment effect on valid representations. The sentence claiming that gating is 'exactly as good as repairing everywhere' has been removed; what Section 7 reports instead is the forced re-check on the class the gate leaves alone, which changes 20 of the 107 records and lowers accuracy by 0.133 (Reviewer J4cV, Q1). Revision. Section 7, Table 5, Section 9.

W3: oracle errors and differing evaluation samples

"The hand-written oracle retains construction errors and sometimes uses different evaluation samples: MATH-confirm compares a 30-question oracle subset with a 60-question model evaluation."

Both denominators are now printed together, so the oracle subset is read on the matched set with the full evaluation beside it (Table 1). Revision. Table 1, Section 3, App. V.

W4: self-debugging and the scope of the contribution

"These are useful engineering observations, but the paper does not convincingly establish the broader attribution advance on which its research contribution depends."

The self-debugging half is answered in "The self-debugging tie and what the verifier contributes" above; for the scope half, the paper states where the claim is made: the budget and scoring artifacts are findings about this pipeline, and Section 9 restricts the claims to quantitative reasoning with deterministic executors (Reviewer a6H2, W2). Revision. Section 6, Section 9.

W5: the EVER case set

"The experiment tests a simplified, single-round EVER adaptation on only 22 selected semantic errors, correcting three."

The 22 cases are the whole residual class, not a selection: they are every frozen E2/E3 failure the census records, scored against 30 frozen correct controls, with 3.3% false repairs (Section 8; App. K). The single round is a stated fidelity limit where EVER iterates, and 13.6% is the estimate for this domain and a lower bound for richer-structure domains (Section 8; App. K). Revision. Section 8 and App. K state the case set, the false-repair rate and the fidelity limits together.

Q1: "see weaknesses above"

"see weaknesses above"

Your Q1 sends the reader to the five weaknesses, so this is the consolidation: W1 and W2 turn on what the gate can show and are answered in Reviewer a6H2's response under the two gate blocks; W3 is the oracle denominator, answered in his response under "The oracle gap is a diagnostic reference, not a bound"; W4 is the self-debugging tie in "The self-debugging tie and what the verifier contributes" above and the scope of the claims in Reviewer a6H2's "Breadth of the evidence"; W5 is the EVER case set, answered above. Revision. Section 7, Section 8, Section 9 and App. K.

AuthorsOpenReview ↗

Follow-up to Reviewer UiSC

We would like to follow up on our rebuttal before the author-reviewer discussion closes on Nov. 18 at 11:59 p.m. AoE. The rebuttal answers each of your comments in detail. In particular, it covers the zero change on execution-valid outputs. Section 7 now tests this class directly with a forced re-check on the 107 records that the gate leaves alone, which changes 20 of them and lowers accuracy by 0.13 (Table 5, Table 11). The rebuttal also covers the tie with self-debugging and the role of the verifier (Section 6, App. J), the oracle comparison, which is now reported with matched denominators (Table 1), and the EVER test, which is now stated with its full case set and its false-repair rate (Section 8, App. K). We hope these additions give a fuller picture of the work.

We would also like to highlight the main result of the paper. Executable reasoning, as in PAL, Program-of-Thoughts and ToRA, is already a standard approach to quantitative reasoning, and these systems are compared by end-task accuracy. Our controls show that two gaps that such a comparison would attribute to the model come from the evaluation interface. The TabMWP gap of 0.117 shrinks to 2/60 at a matched generation budget with one regeneration, and the TAT-QA gap of 0.15 shrinks to 0.016 once the scorer stops converting percent answers twice. These results are, to the best of our knowledge, new in the literature on executable reasoning. Your review notes that separating model errors from executor and scorer failures is valuable, and we hope the new controls complete this picture.

We would be very grateful if you could read the rebuttal before the discussion closes and tell us what you think. If it resolves your concerns, we kindly ask you to consider raising your score. If anything remains open, please let us know and we will answer right away.

Thank you for your time and consideration. We look forward to your reply.

Reviewer_J4cVOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper investigates failure attribution in executable language-model reasoning pipelines, separating representation construction, deterministic execution, and answer evaluation. It introduces controlled substitutions, matched generation budgets, and failure categorization to identify the sources of performance degradation.

Experiments across four reasoning datasets and two model families show that some apparent reasoning failures arise from generation-budget or scoring artifacts. A prospective intervention study further demonstrates that execution-feedback repair improves performance on execution-invalid representations, while execution-valid semantic errors remain difficult to correct.

Critical strengths
  1. Meaningful failure attribution analysis. The paper demonstrates that apparent reasoning failures can originate from generation budgets or scoring conventions rather than model capability. The TabMWP and TAT-QA analyses provide concrete evidence of this issue.

  2. Careful experimental controls. Matched budgets, frozen evaluation artifacts, prospective experiments, and comparisons with self-debugging improve experimental transparency and help distinguish different failure mechanisms.

Critical weaknesses
  1. Partially predetermined prospective attribution results. In Section 7, repair is applied only to execution-invalid representations (E1), while execution-valid representations (E0) receive no intervention. Therefore, the reported zero improvement for E0 and absence of repair-induced errors follow largely from the intervention design. Although the recovery rate within E1 is empirically meaningful, the interaction statistic does not independently establish the claimed selectivity of failure attribution.

  2. Limited generalization and incremental methodological contribution. The main prospective validation is restricted to MATH and two model families, with relatively small evaluation subsets. Furthermore, the matched Self-Debugging baseline achieves comparable performance, including an exact tie under the stress condition (Section 8). This suggests that the improvements primarily arise from conventional execution feedback rather than a substantially new repair or attribution mechanism. The framework's additional value across other datasets and semantic failure categories remains insufficiently demonstrated.

Questions for authors
  1. Can the authors evaluate the attribution mechanism against a matched intervention applied to both E1 and E0, or another independent diagnostic baseline? This would help distinguish genuine predictive selectivity from the deterministic effects of the repair gate.

  2. Can the authors extend the prospective evaluation to additional reasoning datasets and quantify the improvement over matched Self-Debugging? In particular, what benefit does the proposed framework provide beyond detecting execution errors and applying conventional repair?

2 comments
AuthorsOpenReview ↗

Response to Reviewer J4cV

We thank the reviewer for their comments.

Repair attempted on the class the gate leaves alone

"Can the authors evaluate the attribution mechanism against a matched intervention applied to both E1 and E0, or another independent diagnostic baseline?"

One forced re-check per record is enough for the comparison: the arm applies the same intervention to the class the gate leaves alone, and it changes 20 of the 107 records and lowers accuracy by 0.133 (Table 5; Table 11). The forced-E0E_0 prompt is printed in App. W, so the arm is an instrument rather than an adjective. Two sensitivity lines are reported rather than pooled into that number: at 3,000 tokens the same re-check changes 4.7% (Δ0=−0.019\Delta_0=-0.019), and on a second model (DeepSeek-V4.1-Flash) 19.5% of 277 parsed records change (Δ0=−0.087\Delta_0=-0.087) (Section 9; Table 10). Revision. the arm is a table row in Section 7, and the sentence that read "exactly as good as repairing everywhere" is gone.

W1: predetermined attribution

"In Section 7, repair is applied only to execution-invalid representations (E1), while execution-valid representations (E0) receive no intervention. Therefore, the reported zero improvement for E0 and absence of repair-induced errors follow largely from the intervention design."

The interaction statistic is no longer the evidence offered for selectivity, and the two measurements that replace it are the allocation control (Reviewer a6H2, W1) and the forced re-check above. Revision. Section 7.

W2: generalization and incremental contribution

"The main prospective validation is restricted to MATH and two model families, with relatively small evaluation subsets. Furthermore, the matched Self-Debugging baseline achieves comparable performance, including an exact tie under the stress condition (Section 8). This suggests that the improvements primarily arise from conventional execution feedback rather than a substantially new repair or attribution mechanism."

The breadth is answered in Reviewer a6H2's response under "Breadth of the evidence", and the self-debugging tie in Reviewer UiSC's response under "The self-debugging tie and what the verifier contributes". The screen comparison in Q2 below gives the gain over matched self-debugging, and it is small with an interval touching zero. On semantic failure categories Section 8 reports the test rather than a claim, so the residual class stays a stated boundary. Revision. Section 6, Section 8 and Section 9.

Q1: a matched intervention on both classes

"This would help distinguish genuine predictive selectivity from the deterministic effects of the repair gate."

The arm you ask for is "Repair attempted on the class the gate leaves alone" above; the independent baseline for the same budget is Reviewer a6H2's "Spending the same repair budget uniformly". Both are controls on the same frozen sample. Revision. Section 7, Table 5, Table 11.

Q2: extending the prospective study and quantifying the gain

"Can the authors extend the prospective evaluation to additional reasoning datasets and quantify the improvement over matched Self-Debugging? In particular, what benefit does the proposed framework provide beyond detecting execution errors and applying conventional repair?"

No prospective dataset was added in the revision, and Section 9 states that scope rather than implying otherwise. The gain over matched self-debugging is quantified where it exists: on the MATH screen M3 reaches 0.933 against SD 0.900 on Kimi and 0.850 on GLM, with paired intervals touching zero (Section 6; App. J). Beyond detecting an execution error, the framework contributes the decision of when to spend repair and the provenance channel a traceback lacks, and Section 6 claims exactly that. Revision. Section 6, Section 9 and App. J.

AuthorsOpenReview ↗

Follow-up to Reviewer J4cV

We would like to follow up on our rebuttal before the author-reviewer discussion closes on Nov. 18 at 11:59 p.m. AoE. The rebuttal answers each of your comments in detail. In particular, it covers the matched intervention on both classes that you asked for. Section 7 now applies a forced re-check to the 107 records that the gate leaves alone, which changes 20 of them and lowers accuracy by 0.13 (Table 5, Table 11, App. W). An allocation control spends the same repair slots uniformly at random and gives 17.8 expected recoveries, against 64 under the gate. The rebuttal also quantifies the gain over matched self-debugging (Section 6, App. J). We hope these additions give a fuller picture of the work.

We would also like to highlight the main result of the paper. Executable reasoning, as in PAL, Program-of-Thoughts and ToRA, is already a standard approach to quantitative reasoning, and these systems are compared by end-task accuracy. Our controls show that two gaps that such a comparison would attribute to the model come from the evaluation interface. The TabMWP gap of 0.117 shrinks to 2/60 at a matched generation budget with one regeneration, and the TAT-QA gap of 0.15 shrinks to 0.016 once the scorer stops converting percent answers twice. These results are, to the best of our knowledge, new in the literature on executable reasoning. Your review notes that the TabMWP and TAT-QA analyses give concrete evidence of this, and we hope the new controls complete this picture.

We would be very grateful if you could read the rebuttal before the discussion closes and tell us what you think. If it resolves your concerns, we kindly ask you to consider raising your score. If anything remains open, please let us know and we will answer right away.

Thank you for your time and consideration. We look forward to your reply.

Reviewer_USKeOpenReview ↗
Rating
2(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

The paper studies where errors come from when language models answer questions through programs or expressions. The authors check the generated representation, its execution, and how the answer is scored. They compare generation budgets and scoring rules, and use hand-written representations to help locate errors. The experiments cover four datasets. Their MATH experiment tests whether checking programs before repair identifies cases that can be fixed.

Critical strengths
  1. Checking the program and scoring step separately makes sense. The TAT-QA example shows how a correct calculation can be marked wrong because of the percent conversion. This is useful to check before treating the result as a reasoning error.
  2. I found the self-debugging comparison useful. Keeping the starting programs and budget fixed helps make the effect of changing the feedback easier to study. The authors also report that their expected improvement over self-debugging did not appear under the reduced generation budget.
Critical weaknesses
  1. I would like to understand what the failure check adds here. Only programs that fail the check receive repair, so the other programs stay unchanged by design, as acknowledged in lines 395–397. Could repair also help programs that run but give the wrong answer? Lines 461–463 say that checking first works as well as repairing everything, but I could not find that comparison. The result shows that some failed programs can be fixed, but I am not sure it shows that the check finds the right cases to spend repair on.
  2. I could not also match the claim that every failure was classified to the supplied files. Section 5 reports 61 failures, but extract_failure_slices.py keeps at most ten failures from each DROP split? The DROP confirm results contain 17 failures, so seven? are left out by this script. Were these classified elsewhere? since the the paper uses the counts to explain which errors are most common it makes it hard to interpret the results. I am not able to confirm their per-question results, as I could not find the fast_scaleup and evrs_method_sprint listed in the README
  3. Also does the small gap to the oracle really means there is little left to improve. The oracle contains two construction errors, and under policy B the parser scores higher on TAT-QA confirm. Could mistakes on the oracle side be hiding some of the parser’s errors? Similar scores can come from getting different questions wrong. The comparison is still useful, but I would like to see which questions each gets right before concluding that little room for improving the representation remains.
Questions for authors
  1. Do you have results where repair is also tried on programs that pass the execution check? This would help show whether checking first misses useful repairs.
  2. Could you clarify the 10failure limit in the DROP extraction? Does including the remaining seven cases change the conclusions about which errors are most common?
  3. Could you explain how the per-question records used for Table 4 were curated?
  4. When the oracle and parser have similar scores, are they getting the same questions right?.. Could you report the cases where only the oracle is correct, with oracle construction mistakes and scoring errors shown separately?

I currently lean towards reject because I am not completely sure what the failure check adds, and some conclusions are hard to confirm. But the idea of checking where errors enter the pipeline seems useful, and I am open to changing my assessment based on authors response.

3 comments
AuthorsOpenReview ↗

Response to Reviewer USKe

We thank the reviewer for their comments.

W1: what the failure check adds

"Only programs that fail the check receive repair, so the other programs stay unchanged by design, as acknowledged in lines 395-397. Could repair also help programs that run but give the wrong answer?"

The design zero is answered in Reviewer a6H2's response under "What the gate measures, and what follows from its construction", and the second half in the same response under "Spending the same repair budget uniformly". The comparison in lines 461-463 that read as checking first being as good as repairing everything has been removed, because it was not measured; the paper replaces it with the forced re-check (Reviewer J4cV, Q1). Revision. Sec. 7, Table 5, Sec. 9.

W2: the census and the ten-per-split cap

"I could not also match the claim that every failure was classified to the supplied files. Sec. 5 reports 61 failures, but extract_failure_slices.py keeps at most ten failures from each DROP split?"

Table 9 prints the three counts in one place: 61 capped rows ship, four restored parse failures give 65, and three unlabelled ok rows give 68 (Sec. 5; Table 9). The cap is why your DROP-confirm count of 17 appears as ten; the four parse failures and three unlabelled ok rows outside it are the difference. Revision. Sec. 5 and Table 9 print all three counts, the README maps each table to its directory, script and output file, including fast_scaleup/ and evrs_method_sprint/, and App. O names the per-question outcomes file (App. O; README).

W3: the oracle gap

"Also does the small gap to the oracle really means there is little left to improve. The oracle contains two construction errors, and under policy B the parser scores higher on TAT-QA confirm."

The paper no longer reads "little left to improve" off a small gap, and the policy-B reversal you cite is reported in Sec. 4 as the reason the comparison is a reference gap. VPV_P is stated as a lower bound on representation headroom on the matched set (Table 1; Sec. 4). Revision. Sec. 3, Sec. 4, Table 1, App. V.

Q1: repair on programs that pass the check

"Do you have results where repair is also tried on programs that pass the execution check? This would help show whether checking first misses useful repairs."

Yes: one forced re-check on the 107 unflagged records changes 20 and lowers accuracy by 0.133 (Table 5; Table 11), so checking first does not miss a net-useful repair on the class it skips. The arm also runs at 3,000 tokens and on DeepSeek-V4.1-Flash, and the prompt is printed in App. W so it can be re-run (Sec. 9; Table 10; App. W). Revision. Sec. 7, Table 5, Table 10, Table 11.

Q2: the ten-failure limit and the seven cases

"Could you clarify the 10failure limit in the DROP extraction? Does including the remaining seven cases change the conclusions about which errors are most common?"

The cap keeps ten DROP-confirm failures, and the four parse failures and three unlabelled ok rows outside it are restored in Table 9; the answer to your question is no for the largest class and yes for one adjacent order. E4 stays largest at 24, while E1 rises from 15 to 19 and passes E3 (Sec. 5; Table 9). Revision. Sec. 5 and Table 9.

Q3: how the Table 4 per-question records were curated

"Could you explain how the per-question records used for Table 4 were curated?"

One record is one (question, budget, model) synthesis, frozen before the verifier ran, and the 460 records come from 160 problems; the interval is a cluster bootstrap over problems, which is the unit of independence (Sec. 7; App. A). The sample was drawn level-stratified and disjoint from all prior subsets under a protocol frozen before any model call, with the two budgets and the decision rules fixed in advance (App. O). Revision. App. A states the clustering and App. O the protocol.

Q4: which questions each arm gets right

"When the oracle and parser have similar scores, are they getting the same questions right?.. Could you report the cases where only the oracle is correct, with oracle construction mistakes and scoring errors shown separately?"

No table of only-oracle-correct cases is printed in the revision; what is printed is the paired comparison on the matched questions, with the two oracle construction errors retained and counted against the oracle rather than removed (Table 1; App. V). That retention is why VPV_P is a lower bound on representation headroom: fixing the oracle can only widen the gap, so the direction of the error is known even though the per-question overlap is not tabulated. The parser and oracle records are keyed by question id in the reproducibility map and the released caches (App. U). Revision. Table 1, App. U and App. V.

I would ask you to re-read Sec. 7 with Table 5, and to check Table 9 against your DROP-confirm count of 17; those two places carry the changes your W1 and W2 asked for.

I appreciate the authors response. However, I still don't think my main concerns have been addressed. authors refer to fast_scaleup/ and evrs_method_sprint/, but I cannot find these directories in the supplementary. The explanation about the missing DROP cases is also not convincing, and they also didn't provide the question-level comparison. So I will keep my original score.

AuthorsOpenReview ↗

Follow-up Response to Reviewer USKe

Thank you for the follow-up. We answer each point below. The files we cite are in the updated supplementary material.

1. What the check adds (W1)

Allocating the same 128 repair slots uniformly at random across the 460 evaluations yields 17.8 expected recoveries, against 64 under the gate (3.6x; Section 7). On the 200-record Gate-A GLM sample, the gate recovers 44 of the 93 records it flags (Δ1=+0.473\Delta_1 = +0.473). On the 107 records it leaves alone, a forced re-check changes 20. One helps, fifteen harm, and four change without changing correctness. This leaves 85 of the 106 parsed records correct, against 99 before (Table 5, Table 11; forced_e0/glm_1200.csv). The comparison at lines 461-463 of the submitted version is no longer in the paper, and the forced re-check replaces it.

2. The two directories

Thank you for pointing this out. We missed that the supplementary archive on the page was still the earlier version. We have now replaced it, and both directories are included at the paths its README gives. code/fast_scaleup/ holds the frozen protocol, the frozen sample files, the gate runner and the per-record results for both models. code/evrs_method_sprint/ holds the method code, its unit tests and the per-question results for each dataset. README_rebuttal.md maps each table to its script and output.

3. The DROP census

The cap keeps 10 of the 17 numeric-confirm failures. Restoring the four parse failures gives 65, and three more executable rows with a wrong answer give 68. Those three are aaa60de9, e6d36e63 and 4cecdf12 (ok in the source label is the execution status). Their gold answers and predictions are in census/drop_confirm_per_question.csv. The 61-row census is fully classified, and the seven rows outside it are listed separately. E4 stays the largest class at 24 under any assignment of the three unlabelled rows. At 65 failures E1 rises from 15 to 19 and the order is E4, E1, E3, E2 (Table 9). All 68 rows are in census/FAILURE_SLICE_RESULTS_68.csv with a source column.

4. W3 and Q4: the oracle comparison

On TAT-QA the oracle is the benchmark's annotated derivation, executed by the same executor and scored by the same scorer as the parser. We did not construct these programs, and none of our construction errors sits inside those five questions. On this dataset the separation you ask for is clean. The construction errors we retain are in TabMWP (tabmwp-612, tabmwp-51) and MATH (math-1724), and each is counted against the oracle there. On TabMWP the parser matches the oracle's uncorrected 0.967. With those two errors corrected the oracle is 60/60, and 2/60 remains. The paper now states that VPV_P is a lower bound on TabMWP and MATH, and a reference gap to the TAT-QA derivation (Section 3).

The question-level comparison on the 30 calculable TAT-QA confirm questions is:

parser correctparser wrong
oracle correct185
oracle wrong25

Oracle 23/30 (0.767) and parser 20/30 (0.667) are the values in Table 2. The two arms disagree on seven questions. Under policy B the parser rises to 25/30 (0.833) and the oracle stays at 0.767 (App. G).

The five only-oracle questions split by scale: three percent (74183d5d, 593a3304, 182dd9ea), one thousand (806fd692) and one unitless (127264c3). The census classifies all five: three percent double conversions (E4), one missing addend (E2, 806fd692) and one inverted exchange rate (E3, 127264c3). The per-question rows are in oracle/only_oracle_A2_vs_M1.csv, with the gold answers and scales in oracle/tatqa_confirm_gold.csv. None of the five is an oracle-construction case.

5. Q3: the Table 4 records

One record is one (question, budget, model) synthesis, frozen before the verifier ran. The 460 records come from 160 problems, and the interval is a cluster bootstrap over problems (App. A).

We would also like to highlight the main result of the paper. Executable reasoning, as in PAL, Program-of-Thoughts and ToRA, is already a standard approach to quantitative reasoning, and these systems are compared by end-task accuracy. Our controls show that two gaps that such a comparison would attribute to the model come from the evaluation interface. The TabMWP gap of 0.117 shrinks to 2/60 at a matched generation budget with one regeneration, and the TAT-QA gap of 0.15 shrinks to 0.016 once the scorer stops converting percent answers twice. These results are, to the best of our knowledge, new in the literature on executable reasoning. Your review notes that the TAT-QA percent example is useful to check before a result is treated as a reasoning error.

We hope this resolves the remaining points. If it does, we kindly ask you to consider raising your score.

Comments on the paper

2 comments
AuthorsOpenReview ↗

General Response to All Reviewers

We thank the reviewers for their constructive feedback and valuable insights. The reports converge on one objection: the zero on the class the gate leaves alone follows from the design, so it is not a measured effect.

The paper measures that class directly: on the same 200-record GLM sample, verifier-gated repair recovers 44 of the 93 flagged programs (Δ1=+0.473\Delta_1=+0.473), while one forced re-check on the 107 unflagged records changes 20 and moves accuracy by −0.133-0.133 (Table 5; Section 7; the prompt is printed in App. W). Section 7 now states at the definition that Δ0=0\Delta_0=0 by construction and that Γ\Gamma is the recovery rate under the gated policy and Δ0\Delta_0 measures the gate's precision on valid representations, and an allocation control spends the same repair slots uniformly at random, giving 64 recoveries against 17.8 expected (3.6x; Section 7). The TabMWP gap is decomposed into budget and retry rather than asserted (Section 4; Table 10), the census is printed with its restored counts (Section 5; Table 9), and the oracle comparison is described as a diagnostic reference gap rather than a bound (Section 3; Table 1). Revision. the abstract and Section 3-Section 9, with the matched denominators in Table 1, the new controls in Table 5, Table 9, Table 10 and Table 11, and the protocol, the retained oracle errors and the forced-E0E_0 prompt in App. A, App. O, App. V and App. W. Revisions are marked in blue in the revised PDF.

AuthorsOpenReview ↗

Summary of the Rebuttal for the Area Chair and Reviewers

We thank the Area Chair and the reviewers for their time and feedback. As the discussion period is ending, we would like to summarize the current state of the rebuttal.

We would first like to highlight the main result of the paper. Executable reasoning, as in PAL, Program-of-Thoughts and ToRA, is already a standard approach to quantitative reasoning, and these systems are compared by end-task accuracy. Before this work there was, to the best of our knowledge, no controlled test of where in such a pipeline a gap enters. Our paper provides this test. Its controls show that two gaps that an end-to-end comparison would attribute to the model come from the evaluation interface. The TabMWP gap of 0.117 shrinks to 2/60 at a matched generation budget with one regeneration, and the TAT-QA gap of 0.15 shrinks to 0.016 once the scorer stops converting percent answers twice. The pre-registered prospective study then tests the diagnosis on fresh problems, with a pooled recovery of 0.50 [0.397, 0.609] over 460 evaluations and a replication across two model families. All four reviews list the separation of model errors from budget and scoring artifacts as a strength of the paper.

The four reviews share one main concern. In the submitted version, execution-valid outputs received no repair, and their zero change followed from the design. We would like to clarify that the revised paper tests this class directly, and the gate's selectivity holds under three new controls:

  • New forced re-check on the unflagged records. On the 200-record GLM gate sample, repair recovers 44 of the 93 flagged programs. The same check applied to the 107 records that the gate leaves alone changes 20 of them and lowers accuracy by 0.13 (Section 7, Table 5, Table 11).
  • New allocation control. Spending the same 128 repair slots uniformly at random gives 17.8 expected recoveries, against 64 under the gate (3.6x, p < 0.001; Section 7).
  • New within-model TabMWP decomposition. The TabMWP gap is decomposed on GLM-5.3-Flash, which gives 55/60 at 800 tokens, 48/60 at 1,200 tokens without regeneration and 55/60 with one regeneration. Five of its seven questions close, and 2/60 remains attributable to representation (Section 4, Table 10).

We received scores of 2, 2, 2 and 1. Based on the reviewers' feedback, we added the following to the paper:

  • The forced re-check and the allocation control described above (Section 7, Table 5, Table 11, App. W).
  • The TabMWP decomposition into budget and regeneration (Section 4, Table 10).
  • The restored failure census with per-case labels (Section 5, Table 9, App. H).
  • The oracle comparison as a diagnostic reference gap, with matched denominators and the retained oracle errors listed (Section 3, Table 1, App. V).
  • The EVER test with its full case set and false-repair rate (Section 8, App. K).
  • An updated supplementary material with code/fast_scaleup/, code/evrs_method_sprint/ and the per-question files that Reviewer USKe asked for.

We posted point-by-point responses to all four reviews on Nov. 17. The current status is:

ReviewerOriginal ratingAfter our response
a6H222 (No reply)
UiSC22 (No reply)
J4cV22 (No reply)
USKe11 (Replied on Nov. 18; we answered each remaining point and added the requested files)

We are still waiting to hear from three of the reviewers. We believe that our responses and the new controls address all of their comments, and we hope that they can be taken into account in the evaluation of the paper. We kindly ask the reviewers to read our responses and to update their scores if their concerns are resolved.

We are grateful for the reviewers' feedback, which improved the paper. We are happy to answer any question about the paper or the rebuttal.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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