acceptodds
Under review as a conference paper at ICLR 2027

OR-ARK: AN AUTONOMOUS MODELING LARGE LANGUAGE MODEL DRIVEN BY ACADEMIC AND RE- FLECTIVE KNOWLEDGE

Abstract

Large language models (LLMs) offer a promising approach to automating optimization modeling, yet their performance on complex problems remains constrained by the scarcity and limited diversity of high-quality training data. Existing approaches largely rely on predefined seed problems, synthetic data, or proprietary industrial data, leaving the rich optimization knowledge in academic literature underexplored. We introduce OR-ARK, a fully public-data-driven framework that extracts optimization problems, mathematical formulations, and reasoning processes from over 60,000 publicly available academic operations research papers and validates the resulting instances through executable solver code. To improve reasoning reliability, we further construct error–reflection–correction (ERC) trajectories that explicitly train the model to identify and correct plausible intermediate modeling errors. Using the resulting data, we progressively train an 8B model through supervised fine-tuning and reinforcement learning. By internalizing error correction into the reasoning process, OR-ARK generates executable optimization code in a single pass, avoiding the iterative solver-feedback-based correction required by many agent-based approaches. Experiments across five optimization-modeling benchmarks show that OR-ARK achieves state-of-the-art performance among comparable-scale models on challenging benchmarks such as IndustryOR while remaining competitive on the others, highlighting the effectiveness of academic optimization knowledge and explicit self-correction for complex optimization modeling.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
LLM;Operation Research;Optimization; Academic dataset

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_bjq5OpenReview ↗
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1
Confidence
3
Informativeness
2
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2
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Paper summary

OR-ARK constructs optimization-modeling training data from academic literature. It converts approximately 60,000 operations research papers into Markdown and uses DeepSeek to extract problem descriptions, mathematical derivations, optimization formulations, and executable solver code. The resulting structured dataset provides consistent training examples, with experimental results demonstrating its effectiveness in improving optimization-modeling capabilities.

Critical strengths

1.The data source is a real gap. Published OR papers contain formulations that seed-based synthesis does not, and the pipeline is automatic.

Critical weaknesses
  1. Potential data contamination. The paper does not report decontamination against IndustryOR, OptMATH, NL4OPT, or MAMO. This is particularly concerning for IndustryOR, a key evaluation benchmark containing only 100 problems.

  2. Limited evidence for effective self-reflection. ERC introduces scripted errors and corrections that ultimately recover the original answers. However, the paper does not demonstrate that the trained model can autonomously detect and correct errors at inference time, or outperform an iterative solver-feedback baseline using the same model.

  3. Confounded reflection ablation. The reflection ablation modifies both the SFT data and RL training, making their individual contributions unclear. Moreover, the resulting RL model achieves only 36.0% on IndustryOR, underperforming the main SFT model (40.0%).

  4. Insufficient experimental rigor. Table 1 relies on previously reported baselines with different model backbones and incomplete agent comparisons. The proposed 8B model also underperforms SIRL-7B on NL4OPT (86.9% vs. 96.3%) and MAMO-Easy (86.2% vs. 91.7%). No run-to-run variance is reported. Additionally, MIPLIB-NL is discussed but not evaluated, while the LLM-judged reflection reward and dynamic reward weights lack dedicated ablations.

  5. Presentation quality needs improvement. Several parts of the paper would benefit from clearer explanations and more informative figures. For instance, the caption of Figure 4 is overly brief and does not adequately explain the figure's key findings.

Questions for authors

See Weakness

7 comments
AuthorsOpenReview ↗

Response: Q1. Data Contamination and Benchmark Decontamination

Thank you for raising this important concern. To assess potential contamination, particularly on the 100-instance IndustryOR benchmark, we conducted exact-match and semantic similarity checks between our self-constructed training data and all six evaluation benchmarks, followed by manual verification.

1. Training Data Provenance. Our training data consists of two sources: our self-constructed OR dataset and publicly available data from SIRL. For the SIRL-derived portion, we preserve the original train–test separation established in SIRL. For our constructed dataset, we conducted additional decontamination checks against IndustryOR, OptMATH, NL4OPT, MAMO, and MIPLIB-NL.

2. Exact-Match Detection. We extracted problem descriptions, removed shared instruction templates, normalized text formatting, and applied SHA-256 hashing. No exact duplicates were found between our constructed training data and any evaluation benchmark.

3. Semantic Similarity Detection. We used BGE-M3 embeddings to retrieve the top-20 most similar training instances for each test problem, flagging pairs with cosine similarity above 0.80. The results are summarized below:

BenchmarkTest InstancesExact MatchesSemantic CandidatesCandidate Pairs
IndustryOR100000
MAMO-ComplexLP211000
MAMO-EasyLP652011
NL4OPT245000
OptMATH-Bench1930912
MIPLIB-NL223000
Total1,62401013

Notably, IndustryOR exhibits zero exact matches and zero semantic overlap candidates, directly addressing the reviewer's concern about this benchmark.

4. Manual Verification. We manually examined all 13 candidate pairs, comparing their problem descriptions, mathematical formulations, and numerical parameters. No identical numerical instances or direct paraphrases were identified. The similarities primarily reflected shared optimization problem categories rather than instance-level duplication. All candidate pairs are available in candidate_pairs.csv in our anonymous repository for independent verification.

5. Train–Test Independence. For SIRL-derived data, we follow the original train–test partition. For our self-constructed data, the decontamination analyses provide additional empirical evidence of instance-level independence. While distinct optimization problems may share mathematical structures, such similarities do not inherently indicate data leakage. Together, these findings support the reliability of our evaluation and the independence of our training and test instances.

AuthorsOpenReview ↗

Response: Q2. Evidence of Autonomous Self-Reflection and Error Correction

Thank you for this important observation. To demonstrate autonomous self-correction at inference time, we provide a representative example in which the trained model identifies an intermediate reasoning error, reflects on its cause, and corrects its solution within a single generation process, without external solver feedback.

The complete inference trajectory is available in our anonymous repository as ERC_example.json for independent inspection. This provides qualitative evidence of autonomous error detection and correction, beyond merely reproducing scripted ERC training trajectories.

AuthorsOpenReview ↗

Response: Q3. Clarification of the Reflection Ablation

1. Regarding the Confounded Reflection Ablation

We would like to clarify that Table 3 already compares RL models trained with and without the reflection mechanism. Both configurations undergo SFT and RL training, and the performance gap directly reflects the overall contribution of the proposed reflection framework, rather than differences arising from whether RL is applied.

Specifically, the reflection mechanism is designed to operate across both training stages. ERC supervision during SFT introduces error–reflection–correction trajectories, while the reflection reward during RL reinforces and improves reflective reasoning. Therefore, removing reflection-related components from both stages is necessary to evaluate the effectiveness of the complete reflection framework.

To further distinguish their contributions, we conducted additional token-matched and reflection-reward ablations. The updated results are summarized below.

ModelMIPLIB-NLIndustryOROptMATHNL4OPTMAMO-ComplexMAMO-Easy
Ours-RL-8B w/o reflection15.7%36.0%26.5%74.7%45.5%81.3%
Ours-RL-8B w/o reflection (token-matched)16.1%37.0%25.4%76.3%47.9%80.5%
Ours-RL-8B w/o reflection reward21.1%45.0%29.0%83.7%56.9%85.7%
Ours-RL-8B24.7%49.0%31.6%86.9%60.1%86.2%

The results show that the complete reflection framework consistently outperforms the non-reflection RL baseline. Moreover, retaining ERC supervision while removing the reflection reward still yields substantial improvements, while adding the reflection reward provides further gains across all six benchmarks. These findings support the complementary contributions of ERC supervision and reflection rewards.

2. Regarding the Lower Performance of Non-Reflection RL

The non-reflection RL model achieves 36.0% on IndustryOR, compared with 40.0% for Ours-SFT-8B. As discussed in our original Limitations section, academic-derived training data may contain mathematical modeling errors and supervision noise due to the complexity of extracting optimization formulations from academic publications.

Without explicit reflection and correction mechanisms, RL training may reinforce imperfect modeling patterns, limiting its effectiveness. In contrast, incorporating the complete reflection framework increases IndustryOR accuracy to 49.0%, exceeding both the non-reflection RL model and Ours-SFT-8B.

This result highlights the importance of reflection mechanisms for effectively utilizing complex and potentially noisy academic optimization knowledge. Improving the mathematical accuracy of academic-data extraction remains an important direction for future work.

Reviewer_RK9tOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

OR-ARK constructs optimization-modeling supervision from academic OR papers and trains a Qwen3-8B model through supervised fine-tuning and reinforcement learning. The pipeline extracts 6,584 source instances and combines them with public training data; error-reflection-correction (ERC) trajectories teach recovery from injected modeling mistakes. Evaluation covers five benchmarks and ablations of academic data and reflection. The reported results are promising on IndustryOR and MAMO-Complex. We nevertheless have concerns about data validation, the attribution of the gains, and the comparability of the reported evaluations.

Critical strengths

1 A useful direction for acquiring modeling knowledge

Extracting formulations and reasoning from academic OR literature is a promising way to broaden specialized training data (Sections 3.1–3.2). The resulting resource could be valuable if its semantic and numerical fidelity is established.

2 Promising results on complex modeling tasks

Table 1 reports 49.0% on IndustryOR and 60.10% on MAMO-Complex. RL improves the paper’s own SFT checkpoint on all five benchmarks. These observations support the practical promise of the complete recipe, particularly on complex tasks, while the paper also acknowledges weaker results on NL4OPT and MAMO-Easy.

Critical weaknesses

1 Uncertainty about the validation of training examples

We are particularly concerned that the current examples do not make the reliability of the validation pipeline sufficiently clear. Appendix A.4.3 reports 12.0 as the final corrected ring-loading result (p.35). Under our reading of the stated instance and formulation, the loads on edges (3,4) and (6,1) sum to 28, implying a lower bound of 14; splitting each demand equally attains 14. This suggests a possible mismatch between the displayed instance, execution record, and final answer. In A.3.2, the displayed CVRP formulation also does not show how the supplied vehicle count is enforced.

These observations may reflect abbreviated examples or manuscript-version differences and do not establish an error rate for the full corpus. However, because verified supervision is central to the contribution, we would need a clearer record linking each source instance to the executed code and stored label, together with an independent sample audit, to assess the reliability of the resulting training data.

2 Unclear attribution of the academic data and reflection gains

Table 2 reports substantial losses without academic data, including IndustryOR decreasing from 49% to 29%. It is not clear whether unique-problem counts, training tokens, and update budgets are matched. We therefore remain concerned that the comparison may combine the effect of academic provenance with additional data or training exposure.

The note below Table 3 explains that removing reflection changes both SFT and RL. Consequently, the 49% versus 36% IndustryOR comparison does not clearly separate ERC supervision, reflection rewards, and longer reasoning. A comparison using the same problems and comparable token budgets, followed by a separate reward ablation from a fixed SFT checkpoint, would help establish the mechanism. Recovery from shared erroneous prefixes would also provide more direct evidence for the claimed self-correction ability.

3 Insufficient clarity about baseline comparability and inference cost

We find the comparative setting difficult to assess from Table 1 and the referenced appendices. Several agent results are absent, but the meaning of the dashes and the provenance of individual baseline scores are not specified clearly enough. It is unclear which methods were rerun with matching benchmark versions, prompts, solver settings, and retry budgets. Missing entries alone are not evidence of an unfair comparison, but they limit the breadth of the conclusions supported by the table.

The single-generation design is attractive, but its practical advantage over iterative methods is difficult to assess without inference-cost measurements. Token use, solver calls, or latency under a shared evaluation setting would help contextualize the reported gains. Given that performance varies across benchmarks, a matched comparison on the main complex-task benchmarks would strengthen the evidence for the claimed advantage.

Questions for authors

1 Data validation. Could the authors reconcile the final ring-loading value in A.4.3 with the stated instance, provide the corresponding input, program, solver output, and stored training record, and clarify whether A.3.2 omits constraints only for presentation? An independent audit of sampled training records would help assess whether these concerns extend beyond the examples.

2 Attribution of gains. Are data counts, tokens, and training updates matched in Tables 2 and 3? Could the authors isolate ERC supervision from the reflection reward using the same problems and a fixed SFT checkpoint, and report whether any controlled error-recovery evaluation supports the proposed mechanism?

3 Comparative evaluation. Could the authors identify the source, model checkpoint, benchmark version, and evaluation budget for each baseline, explain the missing entries, and provide a representative comparison with matched inference budgets or measured costs? These details could materially change our interpretation of Table 1.

6 comments
AuthorsOpenReview ↗

Response: Q1. Data Validation, Appendix Corrections, and Independent Audit

Thank you for these important observations. We re-examined the appendix examples, corrected the identified inconsistencies, and conducted an independent audit of sampled training records. The revised materials are available in our anonymous repository.

1. Ring-Loading Example (Appendix A.4.3).

Our framework first translates problem descriptions into mathematical formulations, generates executable optimization code, and extracts numerical answers from program execution results. Since ERC introduces multiple code versions through error–reflection–correction trajectories, our training-data construction pipeline consistently extracts and executes the final corrected code, as supported by the implementation released in our anonymous repository.

The inconsistency in Appendix A.4.3 arose during example presentation: the evaluation procedure mistakenly extracted and executed the initial code rather than the final ERC-corrected code. The underlying training record remains correct, as demonstrated by the complete ERC trajectory in our repository. And you also verify by the final code in Appendix A.4.3 demonstrated in original manuscript. Re-executing the final corrected code confirms an optimal objective value of 14.0 for the original instance:

DemandOriginDestinationVolume
0164
1158
2258
3368

The final executable implementation (appendix_A4_3.py) and original training record (appendix_A4_3_output.json) are available in our anonymous repository for independent verification.

2. Missing Constraints (Appendix A.3.2).

We acknowledge that several CVRP constraints were inadvertently omitted when preparing the appendix example. We have supplemented the presentation using the original generated output, restoring the customer in-degree/out-degree constraints, depot departure/return constraints, and capacity-cut constraints. The complete revised formulation is available in appendix_A3_2.pdf in our anonymous repository.

3. Independent Training-Data Audit.

We randomly sampled 1,000 academic-derived training records and re-executed their optimization programs to verify consistency with stored numerical results. We additionally manually inspected 20 instances for mathematical formulation correctness.

Audit CriterionSamplesPassedFailedPass Rate
Numerical execution consistency1,0001,0000100.0%
Mathematical formulation consistency2014670.0%

These results distinguish execution consistency from mathematical correctness: although all sampled programs reproduced their stored numerical results, 6 of the 20 manually inspected formulations contained modeling errors.

Such errors reflect the challenges of extracting complex mathematical formulations from academic literature and may introduce supervision noise, as discussed in our ablation analysis and Limitations section. This motivates combining academically diverse data with more reliably validated public datasets. As discussed in our Limitations section, further improving the accuracy of data extraction from academic literature remains an important direction for future research, with substantial potential to further enhance model performance.

4. Reproducibility Materials.

We have uploaded the corrected RLP implementation, its complete ERC training record, and the revised CVRP formulation to our anonymous repository. We will incorporate the audit findings and corresponding clarifications into the revised manuscript.

AuthorsOpenReview ↗

Response: Q2. Attribution of Gains and Controlled Ablation Studies

Thank you for these important questions. We clarify the training-budget controls, provide additional ablation results, and present qualitative evidence of ERC-based self-correction.

1. Are data counts, tokens, and training updates matched in Tables 2 and 3?

  • Table 2 (Academic Data Ablation): We repeated approximately 3,000 publicly available training instances to match the example count of the full-data configuration, while keeping epochs, batch size, and optimizer settings identical. Thus, optimizer updates were matched, but token counts were not strictly controlled due to differences in problem complexity and reasoning length.
  • Table 3 (ERC Ablation): The original experiments used identical training problems, example counts, hyperparameters, and optimizer updates, but ERC trajectories contained more tokens. We therefore conducted an additional token-matched ablation by repeating non-ERC examples:
Training ConfigurationTotal Tokens
ERC-augmented corpus136,184,936
Token-matched non-ERC corpus136,184,977
Difference41

The additional experiment matches total token exposure through repeated non-ERC examples. Under otherwise identical training settings, including fixed epochs and batch size, increasing the number of training examples necessarily increases the number of optimizer updates. Thus, matching token counts while maintaining these training controls inevitably results in different update counts.

2. Can ERC supervision and reflection rewards be isolated?

ERC supervision introduces error–reflection–correction trajectories during SFT, whereas reflection rewards encourage reflective behavior during RL. We additionally removed the reflection reward while retaining ERC supervision, allowing its contribution to be evaluated under the same ERC-trained SFT initialization.

ModelMIPLIB-NLIndustryOROptMATHNL4OPTMAMO-ComplexMAMO-Easy
w/o ERC & Reflection Reward15.7%36.0%26.5%74.7%45.5%81.3%
w/o ERC & Reflection Reward (token-matched)16.1%37.0%25.4%76.3%47.9%80.5%
w/o Reflection Reward21.1%45.0%29.0%83.7%56.9%85.7%
Full OR-ARK24.7%49.0%31.6%86.9%60.1%86.2%

The full model outperforms the token-matched non-ERC baseline by 5.7–12.2 percentage points across all six benchmarks. Removing only the reflection reward reduces accuracy by 0.5–4.0 percentage points, demonstrating its additional contribution beyond ERC supervision. These comparisons help distinguish the respective contributions of ERC supervision and reflection rewards.

3. Is there evidence of error recovery?

We uploaded a representative self-correction example (ERC_example.json) to our anonymous repository. It illustrates how the model identifies an intermediate reasoning or modeling error, reflects on its cause, and revises its solution within a single generation process, without external iterative solver feedback.

This provides qualitative evidence of ERC-based self-correction, complementing the quantitative improvements observed in our ablation studies.

AuthorsOpenReview ↗

Response: Q3. Baseline Provenance and Comparative Evaluation

Thank you for this valuable suggestion regarding transparency and reproducibility. We clarify baseline provenance, checkpoints, benchmark versions, missing entries, and inference budgets below.

1. Baseline Sources, Checkpoints, and Benchmark Versions.

Most baseline results on the original five benchmarks are adopted from SIRL (arXiv:2505.11792v1), while OR-LLM-Agent and LLMOpt results come from their original publications. MIPLIB-NL baseline results are sourced from arXiv:2602.10450. Our models are independently evaluated.

Table A: Baseline Result Provenance

Baseline ModelsResult Source
GPT-4, DeepSeek-V3.1, DeepSeek-R1, OpenAI-o3SIRL (2505.11792v1)
SIRL-7B/32B, OptMUS, CoE, OptMATH-7B/32B, ORLM-8BSIRL (2505.11792v1)
OR-LLM-AgentarXiv:2503.10009
LLMOpt-14BarXiv:2410.13213
MIPLIB-NL baselinesarXiv:2602.10450
Ours-SFT-8B / Ours-RL-8BThis work (independently evaluated)

Table B: Model References and Checkpoints/Backbones

BaselinePaper / ReferenceCheckpoint / Backbone
OR-LLM-Agent2503.10009DeepSeek-R1-based agent
OptMUS2402.10172LLM-based agent
CoEICLR 2024Multi-agent framework
ORLM-8BOriginal paperLLaMA-3-8B
LLMOpt-14B2410.13213Qwen2.5-14B
OptMATH-7B/32B2502.11102Qwen2.5-7B/32B
SIRL-7B/32B2505.11792Qwen2.5-7B/32B-Gurobi

The original five benchmark versions are documented in Appendix A.2. Following reviewers' suggestions, we added MIPLIB-NL from its official repository. Previously reported baselines follow the model versions and evaluation protocols of their source publications.

2. Missing Baseline Entries.

Missing entries indicate benchmark–model combinations without available published results. Reproducing all configurations would require additional computational resources and potentially introduce inconsistencies in model versions and evaluation protocols. We therefore retain only verifiable reported results.

3. Inference Budgets and Computational Costs.

Our primary objective is to investigate how academic-derived optimization data and ERC supervision improve model capabilities and generalization, rather than optimize inference efficiency. Similar to prior studies such as SIRL, ORLM, and LLMOpt, which do not provide dedicated inference-cost evaluations, our experiments primarily focus on optimization-modeling accuracy. Moreover, ERC supervision and reflection rewards operate during training without requiring additional inference-stage modules.

We acknowledge the value of budget-matched comparisons. However, re-evaluating baselines and measuring token consumption and latency would require substantial resources and time beyond the limited rebuttal period. We will conduct these additional evaluations at a later stage.

Reviewer_nVqXOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

OR-ARK constructs optimization-modeling training data from academic OR literature and augments reasoning trajectories with error–reflection–correction (ERC) sequences. The corpus combines 6,584 academic-derived instances with approximately 3,000 public SIRL examples and expands them into 25,751 training samples. A Qwen3-8B model is trained through SFT and reinforcement learning with dynamically aggregated task and reflection rewards. The model achieves promising results on IndustryOR, while performance on other benchmarks is mixed relative to specialized baselines.

Critical strengths
  1. Academic OR literature is a valuable source of expert-designed modeling knowledge. The proposed pipeline offers a useful direction for expanding training data beyond conventional seed-based synthesis.
  2. ERC supervision addresses a meaningful limitation of successful-only trajectories by explicitly demonstrating intermediate error identification and recovery.
  3. The 8B model achieves promising IndustryOR results. The extraction prompts, training configurations, and reward definitions also help explain the overall pipeline.
Critical weaknesses
  1. The validation of academic-derived instances needs clarification. The pipeline compares generated-code outputs with results reported in source papers, but the code-generation prompt permits random dummy data when numerical inputs are unavailable. Results from newly instantiated data cannot generally be validated against an original paper’s objective value. The authors should distinguish original-instance reproduction from newly constructed instances and explain how trustworthy reference results are established for each. LLM judgments of approximate numerical agreement alone do not establish modeling correctness.
  2. The data contribution would benefit from stronger provenance and independence evidence. Given the broad literature collection and inclusion of public SIRL examples, the paper should substantiate the distinction between its training corpus and evaluation problems. Source summaries, paper-to-instance mappings, and an explanation of duplicate and benchmark-overlap checks would strengthen confidence that the improvements reflect generalization. This is a request for supporting evidence, rather than an allegation of contamination.
  3. The additional token contribution of ERC is not quantified or controlled. The paper does not report how many tokens ERC adds per trajectory or to the training corpus overall. The reflection ablation also changes both SFT supervision and the RL reflection mechanism. Without trajectory-length statistics and training-token-matched controls, the experiments cannot clearly distinguish benefits from ERC structure from those of additional supervision.
  4. The dynamic reward design and efficiency claims lack targeted evaluation. Dynamic aggregation and gradual introduction of reflection rewards are specified, but not independently compared with fixed weights or immediate activation. Single-generation inference also does not necessarily imply lower cost, since ERC may lengthen outputs. Accuracy-matched token and latency comparisons are needed to substantiate the efficiency argument.
  5. Evaluation on more recent and structurally challenging benchmarks is limited. The most prominent result is on IndustryOR, but this alone does not sufficiently establish the claimed advantage on complex optimization modeling. Evaluation on newer challenging benchmarks would help determine whether the benefits extend to different problem structures and failure modes beyond the current benchmark suite.
Questions for authors
  1. How many retained examples reproduce original numerical instances versus use newly generated data? How are reliable reference results established for these categories?
  2. Can the authors provide provenance summaries and evidence supporting train–test independence, including the duplicate and benchmark-overlap checks performed?
  3. How many additional tokens does ERC introduce per example and overall? Does its benefit remain under matched training-token budgets?
  4. Can the effects of ERC supervision, reflection rewards, dynamic weighting, and reward annealing be evaluated separately? What are the inference-token and latency costs at comparable accuracy?
  5. Can the authors evaluate the model on more recent, challenging optimization-modeling benchmarks and analyze whether the IndustryOR gains generalize to different problem structures?
7 comments
AuthorsOpenReview ↗

Response: Q1.Numerical Instance Provenance and Reference Reliability

Thank you for this important question. We address the concerns as follows.

1. How many instances reproduce original numerical data versus use newly generated parameters?

Among the 6,584 retained academic-derived instances, 4,172 (63.4%) directly reproduce numerical instances from the original publications, while 2,412 (36.6%) use newly generated parameters based on mathematical formulations extracted from the literature.

2. How are reliable reference results established?

We adopt different validation strategies for the two categories:

  • Original numerical instances: We execute the generated optimization code and compare its numerical results with those reported in the source publications.
  • Newly generated instances: Some publications do not provide complete numerical datasets or parameters, making direct reproduction infeasible. In such cases, we generate reasonable parameters consistent with the original mathematical formulations and assess the resulting numerical discrepancies against applicable theoretical results or mathematical guarantees, rather than directly comparing objective values from different instances.

For example, if a minimization algorithm has a proven approximation ratio of 1+ϵ1+\epsilon, where ϵ=0.1\epsilon=0.1, and a newly generated instance has an independently established optimum of 100 and a feasible solution of 108, the relative gap is 8%, satisfying the theoretical 10% guarantee. Our LLM-as-a-Judge can assess such consistency by examining the numerical results and applicable theoretical conditions. This is one illustrative validation scenario rather than the sole criterion applied to all generated instances.

3. Why are newly generated instances valuable?

These instances preserve expert-designed mathematical formulations, constraint structures, and reasoning strategies, providing valuable supervision for generalizable optimization modeling.

As demonstrated by our ablation studies, academic-derived data particularly benefit complex optimization tasks. However, extracting accurate numerical information from academic publications remains challenging. We therefore combine academic-derived data with publicly available optimization datasets with high accuracy, leveraging the structural diversity and mathematical depth of academic knowledge alongside more reliable numerical supervision.

AuthorsOpenReview ↗

Response: Q2 Data Provenance and Train–Test Independence

Thank you for this important question. Our training data comprises two sources: our self-constructed OR dataset and publicly available data from SIRL. We clarify their provenance and train–test independence separately.

1. Publicly available data: The open-source portion of our training data is adopted from SIRL, and our evaluation benchmarks also follow those used in SIRL. Thus, we retain the train–test separation established in the original study.

2. Exact-match detection for our constructed data: We extracted problem descriptions, removed shared instruction templates, and normalized text formatting before applying SHA-256 hashing. No exact duplicates were found between our constructed training data and the six evaluation benchmarks.

3. Semantic similarity detection for our constructed data: We used BGE-M3 embeddings to retrieve the top-20 most similar training instances for each test instance, flagging pairs with cosine similarity above 0.80. The results are summarized below:

BenchmarkTest InstancesExact MatchesSemantic CandidatesCandidate Pairs
IndustryOR100000
MAMO-ComplexLP211000
MAMO-EasyLP652011
NL4OPT245000
OptMATH-Bench1930912
MIPLIB-NL223000
Total1,62401013

4. Manual verification: We examined all 13 candidate pairs, comparing problem descriptions, mathematical formulations, and numerical parameters. No identical numerical instances or direct paraphrases were found. The similarities primarily reflected shared optimization problem categories rather than instance-level duplication. All candidate pairs are available in candidate_pairs.csv our anonymous repository and you can verify that no pair of them are actually overlap.

5. Train–test independence: For the SIRL-derived data, we follow the original train–test partition. For our self-constructed data, the additional overlap checks provide empirical evidence of instance-level independence. Although distinct OR instances may share mathematical structures, such problem-type similarities do not inherently constitute data contamination. Together, these findings support the reliability of our evaluation and train–test Independence.

AuthorsOpenReview ↗

Response: Q3 ERC Token Overhead and Token-Matched Ablation

Thank you for this important question. We conducted token-level analysis and a token-matched ablation to quantify ERC overhead and isolate its contribution from increased token exposure.

1. How many additional tokens does ERC introduce per example and overall?

Using the Qwen3-8B tokenizer, we obtained the following statistics:

Token CategoryTotal TokensMean per ExampleMedian per Example
Prompt16,954,201658.39529
Completion119,230,7354,630.144,154
Total136,184,9365,288.534,974
Reflection46,374,7181,800.891,753

ERC introduces approximately 1,801 reflection tokens per example, totaling 46.37M tokens (34.1% of the corpus), covering explicit error identification and correction.

2. Does ERC remain beneficial under matched training-token budgets?

We randomly repeated non-ERC training examples to match the ERC corpus size (136,184,977 vs. 136,184,936 tokens, differing by only 41 tokens), while preserving complete examples.

ModelMIPLIB-NLIndustryOROptMATHNL4OPTMAMO-ComplexMAMO-Easy
Qwen3-8B5.8%24.0%13.6%73.9%16.7%79.1%
Ours-RL-8B w/o reflection15.7%36.0%26.5%74.7%45.5%81.3%
Ours-RL-8B w/o reflection (token-matched)16.1%37.0%25.4%76.3%47.9%80.5%
Ours-RL-8B w/o reflection reward21.1%45.0%29.0%83.7%56.9%85.7%
Ours-RL-8B24.7%49.0%31.6%86.9%60.1%86.2%

The token-matched non-ERC baseline shows only marginal and inconsistent changes (−1.1 to +2.4 percentage points) relative to the original non-ERC baseline. In contrast, full OR-ARK consistently outperforms the token-matched baseline across all six benchmarks by 5.7–12.2 percentage points.

These results demonstrate that ERC's benefits cannot be explained solely by increased training-token exposure, highlighting the value of explicit error-reflection-correction supervision.

Comments on the paper

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Dear Reviewers,

Please note that the author rebuttal is now available. We kindly ask you to read it, join the discussion, and update the review as soon as possible. Your prompt action will help us proceed to the final decision. Thanks.

Best regards

AC

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