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Under review as a conference paper at ICLR 2027

Understanding Scattered Forest Search: A Version-Space Perspective on Multi-Turn Program Correction

Abstract

In multi-turn program correction, the state-of-the-art method Scattered Forest Search (SFS) has been proposed, employing Monte Carlo Tree Search (MCTS) with carefully crafted initial seeds and text-based optimization. However, since SFS integrates multiple components, the effects of each component on performance and the overall behavior of SFS have not been sufficiently analyzed. In this work, we theoretically analyze the refinement process of SFS from the perspective of version spaces in learning theory and clarify its behavior. First, as a basis for the theoretical analysis, we introduce a sequential self-refinement method (Line), which starts from an initial program and repeatedly refines the resulting program. Furthermore, while Line progresses the refinement process in the depth direction, we introduce Iterative Refinement of Repair Instructions (IRRI) to capture the refinement process in the width direction, which fixes initial programs and iteratively refines repair instructions. We then analyze Line and IRRI and conduct a theoretical analysis of SFS by positioning it as an intermediate method between the two. Our theoretical analysis reveals that SFS exhibits behavior closer to IRRI than to Line, and this theoretical characteristic is also confirmed experimentally. Considering computational resources and methodological simplicity, these results suggest that a simpler method, IRRI, may achieve a similar refinement process without relying on the complex correction mechanism of SFS.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
LLM, multi-turn program correction, program generation, inference scaling, version space

Reviews

Among:
Shape:
1234this paper, Top 1%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.67 over 3 reviews, above 99% of the others.
Reviewer_pJB6OpenReview ↗
Rating
4
Confidence
4
Informativeness
3
Presentation
3
Soundness
3
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Paper summary

This paper investigates why Scattered Forest Search (SFS) is effective for multi-turn program correction. It develops a version-space framework that contrasts sequential program refinement with refinement of repair instructions, positioning SFS between these two approaches. Motivated by this analysis, the authors introduce IRRI, a simpler method that revisits fixed initial programs while accumulating insights to improve subsequent repair instructions.

The paper validates its perspective through analysis of SFS search depths and experiments across multiple coding benchmarks and language models. The results support the interpretation that, within the studied budgets, much of SFS’s benefit can be retained through shallow exploration and accumulated repair guidance. IRRI achieves performance comparable to SFS while requiring fewer model calls and tokens.

Critical strengths
  1. A thoughtful combination of theoretical and empirical analysis. The version-space perspective provides an elegant framework for distinguishing refinement of programs from refinement of repair instructions. The search-depth analysis is particularly valuable: it examines how SFS actually finds solutions and provides concrete evidence motivating the simpler approach. This connection between conceptual analysis and observed behavior makes the paper more informative than a performance comparison alone.

  2. A consequential simplification supported by broad evaluation. IRRI turns the paper’s analysis into a practical algorithm that retains much of SFS’s performance without its tree-search machinery. The evaluation across several models and benchmarks, together with the computational-cost comparisons, strengthens the case that this simplification is useful. Understanding which parts of a complex inference-time method are necessary is a meaningful contribution.

Critical weaknesses

One limitation I can think of is that the scaling plots use the number of generated solutions as the computational budget. Including plots with cumulative token usage on the x-axis would make the efficiency comparison more direct, since different methods incur different overheads per generated solution. The aggregate cost tables partially address this concern, and I view the additional plots as a useful strengthening of the evaluation. Overall though the paper is well written, and its central claims are supported by complementary analyses and experiments.

Questions for authors
  1. Could the authors provide a concrete example of how feedback from an unsuccessful repair is distilled into shared information and improves a subsequent repair instruction? This would help make the proposed mechanism more tangible.

  2. Could the authors clarify whether the reported token costs include all auxiliary calls, such as generating repair instructions and updating shared information? This would help readers interpret the efficiency comparison.

3 comments
AuthorsOpenReview ↗

Response to Reviewer pJB6

Q1. (Critical Weaknesses) One limitation I can think of is that the scaling plots use the number of generated solutions as the computational budget. Including plots with cumulative token usage on the x-axis would make the efficiency comparison more direct, since different methods incur different overheads per generated solution. The aggregate cost tables partially address this concern, and I view the additional plots as a useful strengthening of the evaluation. Overall though the paper is well written, and its central claims are supported by complementary analyses and experiments.

A1. Thank you for your insightful comment. We have added figures to the paper (pp. 35-36) comparing inference scaling, with the cumulative number of tokens used on the x-axis. We found that SFS and IRRI perform on par with prior methods at small budgets, but scale better as the token budget increases. Notably, the two methods exhibit similar behavior across the entire budget range.

Q2. (Questions For Authors 1) Could the authors provide a concrete example of how feedback from an unsuccessful repair is distilled into shared information and improves a subsequent repair instruction? This would help make the proposed mechanism more tangible.

A2. Thank you for your comment. We provide a concrete example below (which has also been added to the paper pp. 36-37). The failed repair attempt focuses on a superficial error-prevention measure: “adding a guard to ensure that the number of sticks does not become negative when −x- x is encountered”. From this failure, more general problem-solving guidelines are extracted, such as "the validation logic should account for all possible configurations of the board" and "the counting mechanism should be checked to ensure that it satisfies the problem requirements." Based on them, the successful repair improves upon the initial attempt by moving beyond simply adding exception handling and instead modifying the underlying logic to correctly maintain the state required by canbuildcanbuild.

(Unsuccessful Repair)

Ensure that the plank count is updated correctly after each event. When processing the −x-x operation, ensure that the count does not drop below zero. This can be done by checking if the count of xx is greater than zero before decrementing. This will prevent any erroneous states where the count becomes negative, which could lead to incorrect calculations in the canbuildcanbuild function.

(Shared Information Extracted)

  1. The logic for determining whether the required shapes can be built must be carefully designed to account for all possible configurations of the available planks.
  2. It is crucial to validate the logic of any counting mechanism against the specific requirements of the problem to ensure that it meets the conditions necessary for success.

(Successful Repair)

Ensure that the update logic for the counts in the event processing loop correctly reflects the changes in the number of planks. Specifically, when a plank is added or removed, check if the count of that plank length crosses the thresholds for pairs or quadruples. This will allow the canbuildcanbuild function to have accurate data to work with after each event.

Q3. (Questions For Authors 2) Could the authors clarify whether the reported token costs include all auxiliary calls, such as generating repair instructions and updating shared information? This would help readers interpret the efficiency comparison.

A3. Thank you for your comment. The numbers of LLM calls and tokens reported in Tables 8–12 include all auxiliary calls, such as those for generating repair candidates and updating shared information. We have added this clarification to the paper.

(before) To reveal the efficiency of IRRI, we compared SFS and IRRI in terms of the number of LLM calls, the number of output tokens, and the total number of tokens, reporting the average over five runs.

(after) To reveal the efficiency of IRRI, we compared SFS and IRRI in terms of the number of LLM calls, the number of output tokens, and the total number of tokens, reporting the average over five runs. The LLM calls, output tokens, and total tokens reported in all tables include every auxiliary call, such as generating repair instructions and updating the shared information.

All my concerns have been addressed. I maintain my positive assessment of the paper. Good luck!

AuthorsOpenReview ↗

Thank You for Your Feedback

Thank you very much for your positive assessment and for taking the time to consider our responses. We sincerely appreciate your time and thoughtful feedback.

Reviewer_FStkOpenReview ↗
Rating
3(+1)
Confidence
1
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

The paper studies whether the benefits of Scattered Forest Search (SFS) in multi-turn program correction require deep tree search. It contrasts sequential refinement (Line) with Iterative Refinement of Repair Instructions (IRRI), which repeatedly repairs a fixed set of initial programs using feedback-informed instructions (pp. 3–4). A version-space model represents hypotheses as program/instruction pairs and analyzes set inclusion, preservation of correct hypotheses, and non-emptiness for Line, IRRI, and SFS (Theorems 1–3, pp. 5–8).

The empirical study reports SFS tree-depth statistics with gpt-4o-mini on four datasets (Tables 1–2, p. 8), performance curves spanning four models and five datasets in selected combinations (Fig. 1 and Figs. 6–10, pp. 9, 28–29), and SFS/IRRI call and token costs (Tables 8–12, pp. 30–31). The main practical observation is that IRRI obtains similar observed performance to SFS in many tested settings while using fewer reported calls and tokens. The stronger theoretical interpretation is that SFS behaves more like IRRI than Line.

Critical strengths

S1. Useful empirical diagnosis at a short generation budget. Tables 1–2 (p. 8) distinguish explored depth from the depth of the first correct program, using five initial programs and up to eleven revisions. Depth at least two accounts for none of the first successes on three datasets and 1.16% on MBPP. This motivates evaluating whether deep search is necessary under this budget. The conclusion should remain specific to these settings: Table 1 still reports exploration to depth at least two on 31.00% of APPS and 25.45% of CodeContests tasks.

S2. A simpler search structure with encouraging observed performance and cost. IRRI removes adaptive tree-target selection while retaining instruction feedback and multiple initial programs (p. 3; Algorithm 1, p. 14). The curves are often close to SFS across the tested model/dataset combinations (pp. 9, 28–29). Tables 8–11 report approximately 4.2–13.4% fewer calls and 6.1–18.9% fewer total tokens, relative to SFS. These are meaningful measured savings, subject to clarification of cost accounting and the duplicated table entries.

Critical weaknesses

W1. The central theoretical comparison is not established by the probability arguments and the chosen version-space properties.

First, Eqs. (43) and (125) replace the probability that all targets are known by the product of the per-step marginal probabilities (pp. 17 and 22). Assumptions 2 and 4 specify independence of realizability indicators for different programs; they do not establish independence of the adaptive target-selection events across time. Similarly, Eqs. (22) and (98) factor the probability of not yet encountering a realizable target without stating the requisite history-conditional assumptions (pp. 15 and 20). Consequently, the stated assumptions do not currently justify the trajectory probability bounds. A proof using conditional probabilities given the past, with explicitly justified bounds on those probabilities, is needed.

Second, even if that factorization were repaired, “all targets known” is sufficient, but not shown necessary, for monotone non-increase. Under Eq. (8), an unknown step can leave V\mathcal{V} unchanged when Hc(e)=∅H_c(e)=\varnothing. Thus, an upper bound on the all-known event does not upper-bound monotonicity. The proof explicitly makes this leap in Eqs. (52)–(53), and Appendix E.2 concludes that Line is almost never monotone (pp. 17 and 25). That conclusion needs a separate argument or withdrawal. Likewise, a lower bound on non-emptiness remaining below one does not itself impose an upper limit on the actual non-emptiness probability (pp. 5, 24–25).

Finally, Theorem 2 provides structural guarantees for its stipulated update, but neither non-emptiness nor non-strict set inclusion guarantees that a correct hypothesis will be sampled. No quantitative connection to pass@k\mathrm{pass}@k or cost is established. The SFS bound also depends directly on the fitted root-selection model in Eq. (15). Tables 5 and 7 are model-based plug-in estimates, not independent measurements validating the probability guarantees (pp. 25, 27–28). The operational definition of “known” and a precise Cons⁡\operatorname{Cons} relation, including the randomness of applying a repair and the role of potentially incorrect validation tests, would make the scope of these results assessable (p. 4).

W2. The experiments support a promising short-budget alternative, but not yet the full mechanism or resource-efficiency interpretation.

The performance axis counts generated programs, not total inference resources (p. 2; Fig. 1, p. 9). Tables 8–12 compare SFS and IRRI but do not provide corresponding BoN, Line, and Tree costs. Therefore, equal-cost rankings across all methods cannot be inferred from the supplied results. The reported SFS/IRRI savings should be acknowledged, while requesting explicit treatment of validation generation, instruction generation, feedback, and early stopping in the accounting (Algorithm 1, p. 14).

The shallow first-success statistics do not isolate the causal contributions of seed diversity, repair-instruction diversity, shared feedback, or tree-target selection. In particular, IRRI retains several ideas analogous to SFS's components, so the results do not show that SCATTERING or SCOUTING is unnecessary. A controlled fixed-root versus adaptive-target comparison with the other components held constant would directly test the central interpretation. The nearby curves support descriptive comparability; they do not establish equivalence within a specified tolerance. A confidence interval on the performance difference would make the practical comparison clearer, especially for the three-run CodeContests results (Fig. 10, p. 29).

There is also a concrete reporting concern: Tables 9 and 12 contain exactly the same displayed call and token values despite different model captions (pp. 30–31). Please verify their provenance and correct any duplication. Table 3 already specifies five seeds and at most eleven revisions for IRRI, but the repair-instruction count mm, time/index convention, stopping/accounting details, and benchmark subset sizes remain insufficiently documented in the supplied PDF (pp. 9, 14).

Questions for authors
  1. Probability model: What justifies the factorizations in Eqs. (22), (43), (98), and (125)? Can the bounds be proved using probabilities conditional on the adaptive history, and how are those conditional assumptions supported by the measurements? (pp. 15, 17, 20, 22)
  2. Monotonicity and performance: What additional condition makes monotonicity imply that all targets are known, as required by Eqs. (52)–(53) and Appendix E.2? If none is intended, how should the Line/SFS comparison be revised?
  3. Evidence and accounting: Can you clarify the duplicated Tables 9/12 and provide consistently accounted resource/performance comparisons, including the other baselines? Which existing evidence isolates target-selection depth from the shared seed/instruction/feedback components, and what uncertainty applies to the IRRI–SFS performance difference? (pp. 8–9, 29–31)
6 comments
AuthorsOpenReview ↗

Response to Reviewer FStk (Part 1)

Q1. (Questions For Authors 1) Probability model: What justifies the factorizations in Eqs. (22), (43), (98), and (125)? Can the bounds be proved using probabilities conditional on the adaptive history, and how are those conditional assumptions supported by the measurements? (pp. 15, 17, 20, 22)

A1. Thank you for your insightful comment. Although there are no issues with the algebraic transformations in the proof, we omitted too many intermediate steps in our explanation, which may have caused confusion. To address this issue, we have revised the proof to explicitly include the arguments involving conditional probabilities without omitting the intermediate steps (pp. 15-17, 20-23). We have also added further explanations to eliminate any ambiguity.

Moreover, Assumptions 2–4 are kept to the minimum necessary, and their reasonableness is also supported by our experimental results. These assumptions merely prevent the true hypothesis space from becoming empty with probability one at any time. If the true hypothesis space were to become empty with probability one at every time step, the theoretical analysis would no longer be meaningful. Furthermore, the fact that the methods improve inference performance suggests that the true hypothesis exists, thereby supporting the reasonableness of our assumptions.

(before) We therefore define the probability that the refinement target ctc_t is a known program as qtoldq_t^{\text{old}}.

(after) We therefore define the probability that the refinement target ctc_t is a known program as qtold=Pr⁡[ct=known∣Ot−1]q_t^{\text{old}} = \Pr[c_t = \text{known} \mid O_{t - 1}].

(before) For different programs ct≠ct′c_t \neq c_t', ZctZ_{c_t} and Zct′Z_{c_t'} are mutually independent.

(after) For different programs c≠c’c \neq c’, ZcZ_{c} and Zc′Z_{c'} are mutually independent.

(before) We also denote the probability that the refinement target ctc_t is a node at depth kk by qtdep(k)q_t^{\text{dep}}(k). Furthermore, we define the known probability conditioned on the depth as qtold(k)=Pr⁡[ct=known∣dep(ct)=k]q_t^{\text{old}}(k) = \Pr[c_t = \text{known} \mid \text{dep}(c_t) = k].

(after) We also denote the probability that the refinement target ctc_t is a node at depth kk by qtdep(k)=Pr⁡[dep(ct)=k∣Ot−1]q_t^{\text{dep}}(k) = \Pr[\text{dep}(c_t) = k \mid O_{t - 1}]. Furthermore, we define the known probability conditioned on the depth as qtold(k)=Pr⁡[ct=known∣dep(ct)=k,Ot−1]q_t^{\text{old}}(k) = \Pr[c_t = \text{known} \mid \text{dep}(c_t) = k, O_{t - 1}].

(before) Also, for different programs c≠c′c \neq c', ZcZ_{c} and Zc′Z_{c'} are mutually independent.

(after) Also, for different programs c≠c′c \neq c', ZcZ_{c} and Zc′Z_{c'} are mutually independent.

Q2. (Questions For Authors 2) Monotonicity and performance: What additional condition makes monotonicity imply that all targets are known, as required by Eqs. (52)–(53) and Appendix E.2? If none is intended, how should the Line/SFS comparison be revised?

A2. Thank you for your comment. The theorem for Line provides an upper bound on the probability that all refinement targets are known, and claims that the hypothesis space is monotonically non-increasing in that case. Specifically, it states that "Moreover, with probability at most 1−δLine1 - \delta_{\text{Line}}, all refinement targets c1,…,ctc_1, \ldots, c_t are known, in which case Vt⊆Vt−1⊆⋯⊆V0V_t \subseteq V_{t - 1} \subseteq \cdots \subseteq V_0." (Theorem 1). However, the corresponding statements in the proof and the appendix are ambiguous. We have revised them as follows.

(before) From this, in the refinement process from time 11 to tt, we obtain Vt⊆Vt−1⊆⋯⊆V0V_t \subseteq V_{t - 1} \subseteq \cdots \subseteq V_0 with probability at most 1−δLine1 - \delta_{\text{Line}},

(after) From this, with probability at most 1−δLine1 - \delta_{\text{Line}}, all refinement targets c1,…,ctc_1, \ldots, c_t are known, in which case Vt⊆Vt−1⊆⋯⊆V0V_t \subseteq V_{t - 1} \subseteq \cdots \subseteq V_0.

(before) we computed the upper bound on the probability that the hypothesis space is monotonically non-increasing up to time t=15t = 15.

(after) we computed the upper bound on the probability that all refinement targets are known.

(before) The extremely small estimated upper bound shows that, in Line, all refinement targets are almost never known, and consequently the hypothesis space is almost never monotonically non-increasing.

(after) The extremely small estimated upper bound shows that, in Line, all refinement targets are almost never known.

AuthorsOpenReview ↗

Response to Reviewer FStk (Part 2)

Q3. (Questions For Authors 3-1) Evidence and accounting: Can you clarify the duplicated Tables 9/12 and provide consistently accounted resource/performance comparisons, including the other baselines?

A3. Thank you for your comment. Upon cross-checking the tables against the experimental results, we identified that the discrepancy was caused by an error in transcribing the values from Table 9 when preparing Table 12. We confirmed that the values in Table 9 are correct and have revised Table 12 to reflect the correct values based on the actual experimental results. We also cross-checked the other tables (Tables 8–11) against the experimental results and confirmed that no similar errors were present.

Next, We have added figures to the paper (pp. 35-36) comparing inference scaling, with the cumulative number of tokens used on the x-axis. We found that SFS and IRRI perform on par with prior methods at small budgets, but scale better as the token budget increases. Notably, the two methods exhibit similar behavior across the entire budget range.

(Table 9)

gpt-4o-mini, HumanEval

SFSIRRI
Average LLM calls15.4714.04
Average output tokens33563009
Average total tokens2071418290

gpt-4o-mini, MBPP

SFSIRRI
Average LLM calls14.2313.11
Average output tokens27252463
Average total tokens1633914574

(Table 12)

llama-3.2-3b-instruct, HumanEval

SFSIRRI
Average LLM calls24.4923.02
Average output tokens81816281
Average total tokens3679731806

llama-3.2-3b-instruct, MBPP

SFSIRRI
Average LLM calls24.4123.22
Average output tokens63395929
Average total tokens3139028850

Q4. (Questions For Authors 3-2) Which existing evidence isolates target-selection depth from the shared seed/instruction/feedback components, and what uncertainty applies to the IRRI–SFS performance difference? (pp. 8–9, 29–31)

A4. Thank you for your comment. We think that the experimental results in Table 2 demonstrate that the depth of target selection affects the performance gap between IRRI and SFS. For example, in MBPP, correct programs may only be obtained for the first time at a depth of two or greater. Such correct programs can be discovered by SFS but are unreachable by IRRI. Furthermore, variations in the outputs generated by the LLM also contribute to the performance gap between IRRI and SFS.

Q5. Likewise, a lower bound on non-emptiness remaining below one does not itself impose an upper limit on the actual non-emptiness probability (pp. 5, 24–25).

A5. Thank you for your comment. Regarding the lower bound on the probability of non-emptiness, we are only evaluating its asymptotic behavior as t→∞t \rightarrow \infty and do not impose any upper bound on the probability of non-emptiness itself. Here, our claim is that non-emptiness is not necessarily guaranteed to hold with probability one, even as t→∞t \rightarrow \infty. To clarify this point, we have revised the relevant statement as follows.

(before) This means that no matter how good Line behaves, the lower bound on the probability Pr⁡[Vt≠∅]\Pr[V_t \neq \varnothing] never reaches 11.

(after) This means that no matter how good Line behaves, the lower bound on the probability Pr⁡[Vt≠∅]\Pr[V_t \neq \varnothing] never reaches 11. In other words, this analysis does not guarantee that VtV_t is non-empty with probability 11.

AuthorsOpenReview ↗

Response to Reviewer FStk (Part 3)

Q6. Finally, Theorem 2 provides structural guarantees for its stipulated update, but neither non-emptiness nor non-strict set inclusion guarantees that a correct hypothesis will be sampled. No quantitative connection to pass@k\text{pass@k} or cost is established. The SFS bound also depends directly on the fitted root-selection model in Eq. (15). Tables 5 and 7 are model-based plug-in estimates, not independent measurements validating the probability guarantees (pp. 25, 27–28). The operational definition of “known” and a precise Cons\text{Cons} relation, including the randomness of applying a repair and the role of potentially incorrect validation tests, would make the scope of these results assessable (p. 4).

A6. Thank you for your comment. The objective of this study is to analyze the behavior of the refinement process in SFS and demonstrate that its behavior is closer to that of IRRI than to that of Line. Since LLMs are black-box models, quantitative evaluations based solely on metrics such as pass@k and cost are insufficient for analyzing methods such as SFS. Moreover, most existing studies on multi-turn program repair focus primarily on proposing methods, with very few providing theoretical analyses of the proposed approaches. Motivated by this gap, as a first step toward developing a theoretical understanding of multi-turn program repair, our study provides a theoretical analysis of the behavior of the refinement process from the perspective of version spaces.

Q7. The reported SFS/IRRI savings should be acknowledged, while requesting explicit treatment of validation generation, instruction generation, feedback, and early stopping in the accounting (Algorithm 1, p. 14).

A7. Thank you for your comment. The numbers of LLM calls and tokens reported in Tables 8–12 include all auxiliary calls, such as those for generating repair candidates and updating shared information. We have added this clarification to the paper.

(before) To reveal the efficiency of IRRI, we compared SFS and IRRI in terms of the number of LLM calls, the number of output tokens, and the total number of tokens, reporting the average over five runs.

(after) To reveal the efficiency of IRRI, we compared SFS and IRRI in terms of the number of LLM calls, the number of output tokens, and the total number of tokens, reporting the average over five runs. The LLM calls, output tokens, and total tokens reported in all tables include every auxiliary call, such as generating repair instructions and updating the shared information.

Q8. The nearby curves support descriptive comparability; they do not establish equivalence within a specified tolerance. A confidence interval on the performance difference would make the practical comparison clearer, especially for the three-run CodeContests results (Fig. 10, p. 29).

A8. Thank you for your comment. We evaluated the performance gap between SFS and IRRI on CodeContests. The results show that, while the average performance gap between the two methods is approximately 2% or less, some variability emerges as inference progresses. We consider that this is because SFS may explore deeper levels of the search space as the repair process proceeds, and such deeper exploration can sometimes lead to variability in performance.

gpt-4o-mini, CodeContests

pass@1 diff (%)pass@4 diff (%)pass@8 diff (%)pass@12 diff (%)pass@16 diff(%)
SFS - IRRI−0.20±0.36- 0.20 \pm 0.360.81±0.950.81 \pm 0.951.82±2.371.82 \pm 2.372.22±2.812.22 \pm 2.812.02±2.502.02 \pm 2.50
Reviewer_zzpbOpenReview ↗
Rating
4(+2)
Confidence
2
Informativeness
3
Presentation
2
Soundness
1
Read review
Paper summary

The paper analyzes Scattered Forest Search (SFS; Light et al., ICLR 2025), using the version-space framework from classical learning theory (Mitchell, 1977). The basic idea of SFS is that an LLM generates test cases DvalD_{val} given an initial prompt and refines on these to eventually pass hidden ground-truth tests DgtD_{gt}. This paper attempts to analyze why this works and compares it against two simpler references. Line (classic sequential self-refine, "depth" direction) and IRRI (fix the initial programs, iteratively refine the repair instructions, "width" direction). SFS is positioned as intermediate. The authors introduce various assumptions (soundness, probabilistic realizability assumptions supplying repairability bounds and two parametric modeling assumptions for how the target-selection probabilities evolve: qtold=1−exp(−τt)q_t^{old} = 1 - exp(-\tau t) for Line and qtdep(0)=exp(−γ(t−1))q_t^{dep(0)} = exp(-\gamma (t-1)) for SFS) and show that (i) Line has a non-emptiness "ceiling" that never reaches 1, i.e., there is a non-zero probability that Line will not satisfy DgtD_{gt}, (ii) IRRI's bound goes to 1 in the number of initial programs N, i.e., the probability that a repairable initial program exists approaches 1 as N grows, and (iii) SFS behaves like IRRI for short refinement horizons. An experimental analysis concludes the paper. Here, maybe the most surprising takeaway is that IRRI works nearly as good as SFS without Monte Carlo Tree Search

Critical strengths
  1. Legitimate and timely question: Disentangling which components of increasingly complex inference-scaling methods actually drive gains is a genuinely useful research direction, and using a simplified control (IRRI which is basically SFS without MCTS) to probe it is a sensible design.
  2. The key empirical observation is somewhat surprising and useful. In Table 2, the first correct program appears at depth ≤0\le 0 in 58-93% of cases and ≥98\ge 98% of solved cases at depth 1. This is a clean and informative result that directly supports "SFS's MCTS depth is nearly unused." This alone would be a respectable short/analysis contribution.
Critical weaknesses
  1. The theoretical analysis is lacking, and in particular the assumptions are debatable. Soundness (Assumption 1) requires that the true hypothesis is consistent with every observation. i.e., the self-generated tests never falsely reject a correct solution. LLM-generated test cases are buggy and often only partly reflect the actual specification (in particular, they can be stricter than the spec). Any such test breaks the paper's core preservation guarantee (Tt⊂VtT_t \subset V_t), effectively letting the refinement loop discard the true solution while chasing phantom failures. The paper never measures the "false-positive" rate of DvalD_{val}, nor even discusses when soundness could hold. I understand that the authors had to start somewhere, but this implicit assumption makes large parts of the theory self-fulfilling: if we assume soundness, we are basically guranteed that we do not reject a correct solution at any point. Neither this assumption nor whether we can actually find a solution is addressed. At the very least, this should be a significant point of tension in the paper with a deeper discussion.

  2. The derived theory is more descriptive than predictive. A good theory should predict outcomes and not become a mere "post hoc" curve fitting tool. In particular, there are three issues:

    a) Line's "ceiling" follows directly from assuming qtold=1−exp(−τt)q_t^{old} = 1 - exp(-\tau t), i.e., an exponentially decaying chance of hitting unknown programs (a finite total of rescue opportunities), which makes the non-emptiness bound saturate below 1. A heavier-tailed alternative (e.g., unknown-probability ∼c/t\sim c/t) removes the ceiling entirely.

    b) "SFS behaves like IRRI for small t" is, in a way, a restatement of the assumption qtdep(0)=exp⁡(−γ(t−1))q_t^{dep(0)} = \exp(-\gamma (t-1)), because "always refining the initial programs" is the definition of IRRI (MCTS mostly picks depth-0 nodes early as shown by the experiments).

    c) The experiments also reflect this approach: they are not hypothesis-driven and do not test the theory. The scaling curves, for example, compare methods and then do post-hoc fits to the theory, but they do not use the theory to predict the behavior. There is no ablation of what inside IRRI matters (the shared information ItI_t vs. the multiple roots), no measurement of DvalD_{val} quality, and the one genuinely convincing result (Table 2) is a descriptive statistic that needs no theorems.

EDIT: After the rebuttal, many of the weaknesses have been explained and resolved. I raised my score accordingly. I sincerely hope the authors manage to rewrite the paper for the camera ready to include the new results and improved wording from the rebuttal.

Questions for authors

Did you consider removing/weakening your assumptions, in particular the assumptions on q for Line and IRRI (maybe there is a good reason you chose these probabilities?), as well as soundness?

11 comments
AuthorsOpenReview ↗

Response to Reviewer zzpb (Part 1)

Q1. (Critical Weaknesses 1) The theoretical analysis is lacking, and in particular the assumptions are debatable. Soundness (Assumption 1) requires that the true hypothesis is consistent with every observation. i.e., the self-generated tests never falsely reject a correct solution. LLM-generated test cases are buggy and often only partly reflect the actual specification (in particular, they can be stricter than the spec). Any such test breaks the paper's core preservation guarantee (Tt⊂VtT_t \subset V_t), effectively letting the refinement loop discard the true solution while chasing phantom failures. The paper never measures the "false-positive" rate of DvalD_{val}, nor even discusses when soundness could hold. I understand that the authors had to start somewhere, but this implicit assumption makes large parts of the theory self-fulfilling: if we assume soundness, we are basically guaranteed that we do not reject a correct solution at any point. Neither this assumption nor whether we can actually find a solution is addressed. At the very least, this should be a significant point of tension in the paper with a deeper discussion.

A1. Thank you for your insightful comment. In practical applications, validation tests are expected to be correct, and Soundness (Assumption 1) simply reflects this requirement. Therefore, we consider that this assumption is reasonable. Furthermore, following prior studies, we have LLM-generated tests in our experiments. We think that the assumption approximately holds in this setting as well. As you pointed out, LLM-generated tests may contain bugs, potentially resulting in false positives and false negatives. False positives do not pose a problem in our setting. However, false negatives may cause correct solutions to be discarded, potentially compromising soundness.

To investigate this issue, we computed confusion matrices to evaluate how accurately LLM-generated validation test cases predict the correctness of solutions (pp. 25-27). The results show that the false negative rates range from approximately 12.5% to 32.3%, varying across models and datasets. Thus, false negatives do occur to some extent in all settings. Nevertheless, since the false negative rate remains at approximately 30% or below even in the worst case, the majority of correct solutions are not rejected by LLM-generated validation tests. Therefore, we consider that the assumption approximately holds in our experimental settings as well.

(gpt-4o-mini)

APPSHumanEvalMBPP
False Negative Rate18.90%26.80%21.21%

(gpt-4.1-mini)

HumanEvalMBPP
False Negative Rate14.62%12.54%

(llama-3.1-8b-instruct)

HumanEvalMBPP
False Negative Rate27.38%26.05%

(llama-3.2-3b-instruct)

HumanEvalMBPP
False Negative Rate32.25%29.92%

Q2. (Critical Weaknesses 2) The derived theory is more descriptive than predictive. A good theory should predict outcomes and not become a mere "post hoc" curve fitting tool.

A2. Thank you for your comment. In this study, we hypothesize that the behavior of SFS is more similar to that of IRRI than to that of Line, and we investigate this hypothesis through experiments. Most existing studies on multi-turn program repair focus primarily on proposing methods, with very few providing theoretical analyses of the proposed approaches. Motivated by this gap, as a first step toward developing a theoretical understanding of multi-turn program repair, our study provides a theoretical analysis of the behavior of the refinement process from the perspective of version spaces.

AuthorsOpenReview ↗

Response to Reviewer zzpb (Part 2)

Q3. (Critical Weaknesses 2a) Line's "ceiling" follows directly from assuming qtold=1−exp(−τt)q^{old}_{t} = 1 - exp(- \tau t), i.e., an exponentially decaying chance of hitting unknown programs (a finite total of rescue opportunities), which makes the non-emptiness bound saturate below 1. A heavier-tailed alternative (e.g., unknown-probability  c/t~ c/t) removes the ceiling entirely.

A3. Thank you for your comment. The exponential form of qtoldq^{old}_t naturally arises from a model in which a limited set of candidates is repeatedly generated. As a simple model, consider an LLM that primarily generates MM distinct programs for a given problem, with each program being generated independently and uniformly at random. In this case, after nn previous generations, the probability that the next program is previously unknown is Pr⁡[next program is unknown]=(1−1M)n=e−τn(τ=−log⁡(1−1M))\Pr[next\ program\ is\ unknown] = \left( 1 - \frac{1}{M} \right)^n = e^{- \tau n} \quad \left( \tau = - \log \left( 1 - \frac{1}{M} \right) \right).

This yields qtold=1−e−τnq^{old}_{t} = 1 - e^{- \tau n}.

Although there is a slight discrepancy in the time indexing compared with the paper due to initialization, the exponential form itself follows directly from this generation mechanism. The same reasoning extends to the case of non-uniform generation probabilities p1,…,pMp_1, \dots, p_M, for which Pr⁡[next program is unknown]=∑j=1Mpj(1−pj)n\Pr[next\ program\ is\ unknown] = \sum_{j = 1}^{M} p_j (1 - p_j)^n. In this case, the probability is a mixture of exponentially decaying terms.

Moreover, we do not think that assuming a heavier-tailed distribution for the probability that the refinement target is unknown is appropriate. Under such an assumption, the probability that the refinement target is unknown would remain relatively high even for comparatively large values of tt. However, this contradicts the empirical observation that the generated programs exhibit very high similarity to one another. To verify this observation, we measured the cosine similarities between all pairs of programs generated during the repair process. The results are shown in the table below, indicating that the generated programs are highly similar to one another. Based on this observation, we model the probability that the refinement target is unknown using an exponentially decaying distribution.

(gpt-4o-mini)

APPSHumanEvalMBPP
Program Diversity0.99910.99960.9992

Q4. (Critical Weaknesses 2b) "SFS behaves like IRRI for small t" is, in a way, a restatement of the assumption qtdep(0)=exp(−γ(t−1))q^{dep(0)}_t = exp(- \gamma (t - 1)), because "always refining the initial programs" is the definition of IRRI (MCTS mostly picks depth-0 nodes early as shown by the experiments).

A4. Thank you for your comment. "SFS behaves like IRRI for small tt" is not simply a restatement of the assumption qtdep(0)=exp⁡(−γ(t−1))q^{dep(0)}_t = \exp(-\gamma (t - 1)). In this study, we first establish that the hypothesis space in IRRI is monotonically non-increasing. We then show that, in SFS, the hypothesis space is stochastically monotonically non-increasing. Furthermore, since the probability that the hypothesis space is monotonically non-increasing is high for small values of tt, we conclude that SFS behaves similarly to IRRI in this regime. This finding is obtained through an analysis of the dynamics of the hypothesis space, rather than simply by rephrasing the underlying assumption.

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Response to Reviewer zzpb (Part 3)

Q5. (Critical Weaknesses 2c) The experiments also reflect this approach: they are not hypothesis-driven and do not test the theory. The scaling curves, for example, compare methods and then do post-hoc fits to the theory, but they do not use the theory to predict the behavior. There is no ablation of what inside IRRI matters (the shared information ItI_t vs. the multiple roots), no measurement of DvalD_{val} quality, and the one genuinely convincing result (Table 2) is a descriptive statistic that needs no theorems.

A5. Thank you for your comment. In this study, we hypothesize that the behavior of SFS is closer to that of IRRI than to that of Line, and we investigate this hypothesis through experiments. We consider that Tables 1 and 2, as well as the inference scaling plot, support our hypothesis that SFS exhibits behavior more similar to IRRI than to Line.

We also conducted ablation experiments on IRRI. The results show performance degradation in both settings: when using only a single initial program and when not utilizing shared information. In particular, the performance degradation is more pronounced when shared information is not utilized. Regarding the quality of DvalD_{val}, we refer the reviewer to our response to Q1.

gpt-4o-mini, APPS

Pass@1 (%)Pass@16 (%)
IRRI23.044.0
IRRI (single initial program)24.540.0
IRRI w/o shared information23.038.0

Q6. Did you consider removing/weakening your assumptions, in particular the assumptions on q for Line and IRRI (maybe there is a good reason you chose these probabilities?), as well as soundness?

A6. Thank you for your comment. We consider that our assumptions are kept to the minimum necessary. For example, the assumption for Line (Assumption 2) only requires that the probability of the LLM generating a feasible program be non-zero at the initial step and at each subsequent repair step. This requirement merely prevents the true hypothesis space from becoming empty with probability one at any time in Line. If the true hypothesis space were to become empty with probability one at every time step, the theoretical analysis of Line would no longer be meaningful. The same reasoning applies to the assumptions for IRRI (Assumption 3) and SFS (Assumption 4). Furthermore, the Soundness assumption (Assumption 1) is also reasonable, as it simply reflects the practical requirement that validation tests should be correct.

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

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