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Under review as a conference paper at ICLR 2027

RULER: Reasoning from Trials to Transferable Rules for Finite-Budget Online Algorithm Configuration

Abstract

Online algorithm configuration adapts solver parameters to individual instances and evolving search states under a limited evaluation budget. Yet each trial offers more than a performance score: it reveals how a parameter edit affects solver behavior in a particular context. Turning these observations into transferable tuning knowledge requires reasoning about when an edit is applicable, what response it should induce, and whether new evidence supports that expectation. We introduce RULER—Rule-guided Updating through Local Experimental Reasoning, a framework that treats configuration trials as local experiments and distills their outcomes into reusable, falsifiable edit–response rules. RULER retrieves these rules as contextual hypotheses, reassesses their applicability to the current solver state. It then plans targeted experiments to test their predictions, refine promising edits, distinguish competing explanations, or explore alternatives when existing knowledge offers little guidance. This evidence–hypothesis–experiment loop enables RULER to improve the current configuration while accumulating tuning knowledge that can be reused across instances. Experiments across four problem–solver settings show that RULER reduces the reference gap by an average of 10.7% relative to the strongest baseline under matched evaluation budgets, maintains gains under matched wall-clock budgets and across planner scales, and transfers useful configuration knowledge to unseen instances.

Primary area:
optimization
Keywords:
Online Algorithm Configuration, Large Language Models, Hyperparameter Optimization, Metaheuristic Algorithm

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_d5CPOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
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2
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Paper summary

The paper introduces RULER, an LLM-guided framework for online algorithm configuration. The main idea is to let LLMs summarize historical configuration trials into reusable edit–response rules that specify the conditions under which parameter modifications may be effective, their expected solver responses, and the corresponding supporting or contradicting evidence.

The framework has three major components: (1) edit-response rule induction which extracts reusable knowledge from historical experiments; (2) contextual hypothesis assessment, which lets an LLM decide whether retrieved rules are applicable to the current optimization state; and (3) hypothesis-guided experiment planning, which decides one of the following subsequent experiments: memory validation, guided improvement, mechanism contrast, and coverage exploration.

The authors evaluate RULER on TSP and CVRP. RULER achieves an average 10.7% relative reduction in the best-known-solution gap compared with the strongest baselines.

Critical strengths
  1. Interesting idea to summarize optimization knowledge. Instead of simply conditioning an LLM on historical results, RULER explicitly introduces edit–response hypotheses with supporting and contradicting evidence. This provides a structured mechanism for accumulating and reusing knowledge across optimization instances.

  2. Comprehensive experiment results. The paper evaluates four problem–solver settings and compares RULER against varieties of baselines, including some classical methods, and LLM-based methods such as AutoEP. RULER achieves the lowest average reference gap across all four settings.

  3. Useful component ablations and analyses. The results shown in the ablation studies generally demonstrate that removing introduced components degrades performance. The authors also provide other related results.

Critical weaknesses
  1. Do the authors run everything for multiple time and get the average? Reporting variance would be important to assess the performance of RULER compared to baselines.

  2. Analysis of experimental roles. It would be useful to understand how frequently each role is selected during optimization. Could the authors provide a breakdown of the selection frequency?

Questions for authors
  1. AutoEP implementation: The paper mentions that AutoEP does not provide a complete runnable Python evaluation pipeline or full prompt set, motivating the re-implementation, i.e., AutoEP-Rep. However, AutoEP has an official public GitHub repo containing source code. Could the authors clarify which components of the original implementation were unavailable or could not be reused, and explain any important differences between AutoEP-Rep and the released AutoEP implementation?
5 comments
AuthorsOpenReview ↗

Response to Weakness 1 – Robustness of experiment

We sincerely thank the reviewer for carefully reading our manuscript and providing valuable suggestions. The main experiments use global seed 0 and greedy decoding (temperature 0). So we conducted three independent robustness runs for each of the four main settings, using different global random seeds and an LLM temperature of 0.2. The corresponding results, including the mean, sample standard deviation, and variance, are reported in Table 3 of our response to Reviewer FJxY, Weakness 2 ("Component Ablation"). Appendix E.1 further clarifies the randomness protocol.

AuthorsOpenReview ↗

Response to Weakness 2 – Analysis of experimental roles

Thanks for your question and suggestion, we report detail experiment result of how frequently each role is selected during optimization in Response to Weakness 2 and Question 2-- Contribution of the Experimental Role Decomposition for Reviewer FJxY In summary, all four roles are utilized in each of the four experimental settings, although their allocation frequencies vary substantially across solvers. Guided Improvement is the most frequently selected role in both TSP settings (45.70% and 45.56%), while Coverage Exploration is dominant in CVRP PSO+ILS (44.89%), and Mechanism Contrast is most frequently selected in CVRP SA+ILS (39.77%). These results illustrate that role allocation varies with the optimization setting rather than following a fixed allocation pattern. Please refer to Table 5 in our response to Reviewer FJxY for the complete results.

AuthorsOpenReview ↗

Response to Question 1 – Autoep Implementation details

We sincerely thank the reviewer for this question and AutoEP's authors for providing open-source code. The original AutoEP's official repo includes Python solver code, a TSP FastGPT workflow export with embedded prompts, and Flask/MySQL components for data exchange. However, we were unable to run the released implementation using the public artifacts in an end-to-end manner. In particular, the released Python drivers delegate LLM-based parameter updates to a separately configured FastGPT workflow and exchange state through Flask and MySQL. Therefore, we reused the released TSP GA and CVRP PSO solver implementations and adapted AutoEP's documented configuration loop to run directly within our shared Python evaluation harness. This integration, which we call AutoEP-Rep., runs end-to-end on our evaluation benchmarks under the same evaluation protocol as RULER. We will revise the manuscript to state precisely what AutoEP releases and which parts we reused or adapted. We also provide a solver-aligned PSO-2opt comparison in our response to Reviewer FJxY's Q4.

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

This paper proposes RULER, an LLM-guided framework for finite-budget online algorithm configuration. The central idea is to transform historical configuration trials into reusable edit–response rules that describe the conditions under which parameter modifications may be effective, their expected effects on solver behavior, and the supporting or contradicting evidence. The authors evaluate RULER on TSP and CVRP using four configurable metaheuristic solvers. The experiments report an average relative reduction of 10.7% in the reference gap compared with the strongest baseline in each setting. Additional experiments examine cross-instance rule transfer, component ablations, different configuration budgets, and the influence of LLM planner size.

Critical strengths

1. A practically relevant problem formulation.

The paper addresses an important challenge in online algorithm configuration: how to reuse knowledge obtained from previous configuration trials when making decisions in new search contexts. Representing historical experience as context-dependent edit–response relations is a potentially useful approach to improving the efficiency of sequential parameter optimization.

2. Broad comparison with established configuration methods.

The experiments cover four problem–solver settings and compare RULER with sampling-based, model-based, evolutionary, and LLM-based configuration methods. The paper also includes studies of component contributions, configuration budgets, cross-instance transfer, and planner model sizes. These results provide encouraging empirical evidence that structured reuse of historical configuration experience can be beneficial.

Critical weaknesses

1. Limited methodological novelty.

The proposed framework combines experience reuse, contextual hypothesis assessment, and LLM-guided experiment planning, which are closely related to existing approaches such as ExpeL, Reasoning BO, and POPPER. In particular, the learned rules appear to be historical parameter configurations augmented with contextual information and supporting evidence, rather than genuinely predictive edit–response relationships. The four experimental roles also mainly organize the LLM's search process through predefined categories. Therefore, the methodological novelty beyond integrating existing techniques remains limited.

2. Insufficient validation of the proposed rule-based reasoning.

The experiments do not sufficiently isolate the benefit of rule induction from simply reusing historical configurations. Comparisons with direct configuration reuse or warm-start methods using the same historical information are missing. Moreover, Table 3 shows that many transferred hypotheses are contradicted or remain unproven, raising questions about their predictive reliability. The component ablations cover only four selected instances, and the main results lack uncertainty estimates or statistical significance tests. These limitations weaken the evidence supporting the claimed benefits of transferable rules.

Questions for authors

Q1. How are the predictive validity and falsifiability of learned rules established?

The paper emphasizes falsifiable edit–response hypotheses. However, each local experiment may modify several parameters simultaneously, making it difficult to identify which changes are responsible for the observed response. How are supporting, contradicting, and unproven outcomes determined in the presence of stochastic solver behavior? Could the authors provide quantitative evidence that the learned rules predict responses on unseen instances more accurately than simpler history-based alternatives?

Q2. How are the proposed experimental roles distinguished from standard exploration and exploitation strategies?

The four experimental roles organize configuration proposals into memory validation, guided improvement, mechanism contrast, and coverage exploration. What is the substantive algorithmic contribution of this role decomposition beyond prompting the LLM to perform different types of search? Would a simpler history-conditioned LLM planner with the same memory and evaluation budget achieve comparable performance?

Q3. Are the improvements statistically reliable across the complete benchmark?

The main results report average reference gaps without uncertainty estimates, while the component ablations are conducted on only four selected instances. Could the authors provide results across multiple independent optimization runs and extend the component ablations to a broader set of benchmark instances? This would help determine whether the reported improvements, particularly the relatively small absolute gap reductions, are robust.

Q4. How are evaluation budgets and solver states controlled across methods?

Section 3.1 states that local edits are evaluated from a common recoverable solver checkpoint. Could the authors clarify how checkpoints and random states are restored for GA, SA, and PSO-based solvers, and how stochastic variability is controlled during edit–response comparisons?

Additionally, the comparison with published AutoEP results in Table 4 uses different evaluation procedures, and the standard RULER-8 setting does not consistently outperform the published AutoEP results. Could the authors clarify which comparisons are directly comparable and how additional tuning rounds or ILS refinement affect the conclusions?

11 comments
AuthorsOpenReview ↗

Response to Weakness 1 – Limited methodological novelty

We sincerely thank the reviewer for carefully reading our manuscript and providing valuable suggestions. Below, we respond to each concern point by point.

Thanks for highlighting these three related works. We agree that RULER shares several ideas with them, while our distinctive contribution is to test the predicted effects of retrieved tuning rules in the current solver state and use the measured responses to decide whether those rules should guide subsequent evaluations.

Specifically, ExpeL (Zhao et al., 2024) extracts reusable insights from successful and failed trajectories and uses them to guide subsequent tasks. In RULER, a retrieved rule specifies a parameter intervention and an expected solver response that can be checked in a dedicated trial alongside alternative edits from the same solver checkpoint. Reasoning BO (Yang et al., 2026) generates hypotheses and uses confidence scores to select among BO-proposed candidates. RULER distinguishes a rule's contextual match before a trial from empirical support after it. The former determines whether a rule is worth testing, and the latter informs whether it should continue to guide tuning. On \texttt{d493}, for example, the measured response contradicted the top-ranked retrieved rule, and RULER switched to an alternative (Figure~5). POPPER (Huang et al., 2025) designs sequential statistical tests for a supplied scientific hypothesis. RULER learns local tuning hypotheses during optimization and tests them within the same finite budget used to improve the incumbent.

RULER organizes evaluations into four roles: memory validation, guided improvement, mechanism contrast, and coverage exploration. The role mix varies by solver (AppendixC.1), and RULER uses a tiny LLM with 4B parameters as its local planner. In the full-benchmark ablation, both variants evaluate three candidates per round. Removing role-based planning increases the gap in all four settings. We have clarified these methodological distinctions in the Discussion (Appendix~D).

AuthorsOpenReview ↗

Response to Weakness 2 – Validation of reusing historical configurations

Thanks for your suggestion. Please refer to our Response to Question 2 -- Vanilla Retrieval Baseline Comparison of Reviewer jDHm for a detailed discussion and the corresponding experimental results. Briefly, we clarify why directly reusing historical configurations may be ineffective in online algorithm configuration, given the instance-dependent nature of hyperparameter values. We further introduce Best-history and Random-history baselines, together with the w/o induction control, to distinguish the benefits of structured rule induction from those of simply reusing historical numerical configurations. As reported in Table 1 of our response to Question 2 of Reviewer jDHm, full RULER consistently achieves lower gaps than all these alternatives across the four experimental settings. These results support the effectiveness of transferring structured, context-dependent optimization knowledge rather than absolute historical configurations.

AuthorsOpenReview ↗

Response to Weakness 2 – Component abalation

Following your suggestion, we provide additional experiments to better understand the sources of RULER's performance gains and evaluate its robustness, including the following three aspects.

(1) Full-benchmark component ablation.

We extend the original four-instance ablation to the complete benchmark panels. All six component-removal variants retain the same underlying solvers, feasible configuration spaces, eight decision rounds, and three candidate evaluations per round. For clarity, w/o Mem. removes stored rules, trial history, and reference configurations; w/o Retr. replaces context-ranked retrieval with a fixed three-entry memory pool; w/o Ind. replaces induced edit–response rules with raw parameter examples; w/o Hyp. removes explicit rule binding and rule-enforced interventions; w/o Guard removes suitability screening and negative-evidence reuse vetoes while retaining feedback recording and best-child selection; and w/o Role removes role labels, functional candidate lanes, and role-specific parameter directions. Point-LLM serves as a separate LLM-only reference, using the 8B model to generate one candidate per round for eight rounds based on the current state, configuration, and previous trial, without cross-instance memory or role allocation.

Table 2. Full-benchmark component ablation. Mean reference gap (%); lower is better.

SettingFullw/o Mem.w/o Retr.w/o Ind.w/o Hyp.w/o Guardw/o RolePoint-LLM
TSP GA+2opt0.6200.7520.7050.7200.7000.7620.7390.926
TSP-SA4.0275.8564.1134.1384.1134.0675.0816.544
CVRP PSO+ILS1.9512.8092.8032.4912.7582.3792.6082.860
CVRP SA+ILS1.5462.2121.8021.9041.9631.8801.8352.221

Full RULER achieves the lowest aggregate gap across all four settings. In particular, removing induction, memory, or role assignment consistently increases the mean gap, supporting the complementary contributions of structured experience management and hypothesis-guided planning. Point-LLM is included as a separate LLM-only reference rather than a budget-matched component ablation.

(2) Robustness across independent runs.

We additionally conduct three independent runs for each main setting, varying the global random seed and using an LLM temperature of 0.2. The main results remain based on the fixed-seed, greedy-decoding protocol (seed 0, temperature 0). Here, Mean is the arithmetic average of the aggregate gaps across the three independent runs, while SD and Variance denote the sample standard deviation and sample variance, respectively, calculated across these runs using Bessel's correction (denominator n−1n-1). SD is the square root of the sample variance.

Table 3. Three-run robustness evaluation of the complete RULER framework.

SettingMean ± SD (%)Variance (pp²)
TSP GA+2opt0.6370 ± 0.01960.000383
TSP-SA3.9707 ± 0.19050.036293
CVRP PSO+ILS1.8943 ± 0.25190.063458
CVRP SA+ILS1.5609 ± 0.02150.000464

These results characterize run-to-run variability under stochastic LLM generation and different random seeds. We do not interpret them as formal significance tests against all baselines.

(3) Instance-level comparisons.

To complement the aggregate ablations, we retain two representative instances for each optimization setting. The results provide additional evidence of component contributions under individual optimization contexts.

Table 4. Instance-level component ablation. All values are reference gaps (%); lower is better.

SettingInstanceFullw/o Mem.w/o Retr.w/o Ind.w/o Hyp.w/o Guardw/o RolePoint-LLM
TSP GA+2optgr4311.4111.8182.1542.1321.7992.0491.9541.902
TSP GA+2optlinhp3182.1862.6802.5542.4622.4502.7602.4773.577
TSP-SAu7244.8229.5995.5245.5245.5244.8276.3718.000
TSP-SAatt5323.9156.2993.9154.0243.9153.9484.6025.086
CVRP PSO+ILSX-n200-k363.0908.99011.4517.1875.8796.7993.4983.252
CVRP PSO+ILSX-n101-k256.98413.6179.96311.91313.6969.48513.69617.187
CVRP SA+ILSX-n200-k367.27910.2968.8608.9189.4568.3329.3359.442
CVRP SA+ILSX-n101-k255.5829.3475.5826.6436.6006.8145.0708.945

These instance-level results further illustrate that the contributions of individual components depend on the optimization context, rather than being uniformly additive.

Reviewer_jDHmOpenReview ↗
Rating
3
Confidence
1
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

RULER uses an LLM to guide online algorithm configuration under a limited trial budget. It evaluates candidate configurations from a shared solver checkpoint, records their outcomes as contextual rules with supporting and conflicting evidence, and uses this memory to guide later trials and transfer experience across instances. The evaluation covers TSP and CVRP with four solver settings, together with studies of configuration budgets, planner size, runtime, and individual components.

Critical strengths

The complete method performs well across all four solver settings in Table 1. Its relative reduction in the gap to the reference solution ranges from 7.8% to 16.6% against the strongest baseline in each setting. Figure 4 also includes matched wall-clock comparisons on three larger TSP instances. Although that experiment covers only part of the evaluation, it provides useful evidence that the improvement can survive accounting for planning overhead. The treatment of previous trials as conditional evidence is a useful idea. Rules retain the context in which a configuration worked, record contradictory outcomes, and can be checked again on a new instance. This gives the memory a more meaningful role than simply storing a list of successful configurations. The component ablations in Table 5 support the framework: removing rule induction and transfer, context assessment, or role-based planning worsens the reported results on the four evaluated targets.

Critical weaknesses

The transfer protocol is not sufficiently explicit. RULER accumulates evidence across instances, but I found the instance order, memory initialization and reset policy, and accounting for earlier trials difficult to reconstruct. It is also unclear whether competing methods can use the same previous-instance outcomes. These details matter because they determine how much of the improvement can be attributed to the rule representation. The ablation that removes induction and transfer together does not fully separate the benefit of structured rules from the benefit of access to prior experience. The interpretation of positive rule evidence also needs to be more precise. In Section 3.1, a child’s response is measured against the reference checkpoint before the child receives additional solver computation. A positive response can therefore reflect progress from continued search as well as the effect of changing the configuration. The trace in Appendix B includes consecutive rounds using the same configuration. This is still useful evidence that a configuration remains productive in a particular context, but it does not isolate the effect of an edit.

Questions for authors
  1. What is the exact sequence of source and target instances, when is memory initialized or reset, and how are the trials used to build that memory counted? Which previous-instance outcomes are available to the baselines?
  2. Have you compared the rule memory with retrieving successful configurations from the same trial history? This would help establish what is gained from rule induction itself.
  3. Is a positive rule response intended to mean that a configuration makes progress, or that an edit improves progress relative to continuing unchanged for the same budget? Please clarify how this interpretation affects the rule updates.
5 comments
AuthorsOpenReview ↗

Response to Weakness 1 and Question 1– Transfer Protocol, Interpretation of Positive Rule, and More Implementation Details

We sincerely thank the reviewer for carefully reading our manuscript and providing valuable suggestions. Below, we respond to each concern point by point.

Regarding the concern about the transfer protocol, we have revised Section F.1 and Appendix E.1 of the manuscript to clarify the experimental protocol and avoid potential misunderstandings. Specifically, all instances are processed strictly in the fixed order specified in Appendix E.1, without manually tuning the source--target split or instance order. Each independent run starts with empty rule memory, which accumulates experience only from preceding instances within that run. Memory is reset across different solver settings, ablation variants, and independent random seeds, ensuring that no knowledge is transferred across these settings. Baselines follow their respective history-access protocols, and RULER's rule memory is not shared with them. Furthermore, the cost of acquiring experience is charged to the earlier instances that generate it and is not charged again to subsequent target instances.

Regarding positive rule and candidate evaluation, configurations within each round are evaluated independently from the same solver checkpoint, using controlled randomness and matched evaluation budgets. Candidate responses are compared against an unchanged-continuation reference under the same evaluation conditions. Thus, positive evidence indicates that a candidate configuration outperforms continuing with the original configuration from the same checkpoint and under the same evaluation budget, rather than merely reflecting progress from continued search.

Regarding random seeds, the main experiments use a fixed global seed of 0, from which controlled phase-level seeds are derived for candidate evaluations, while robustness experiments use three independent seeds. We have clarified these procedures and the associated computational costs in Appendix E.1. Finally, we further include a w/o induction control that retains historical numerical configurations while removing induced rules, allowing us to isolate the contribution of rule induction. Further details are provided in our responses to Q2--Q3 below.

AuthorsOpenReview ↗

Response to Question 2 – vanilla retrieving baseline comparation

Directly replaying historical configurations in an in-context learning manner may not be an appropriate transfer strategy in online algorithm configuration. Specifically, even within the same problem family, such as TSP, instances can differ substantially in scale, making effective hyperparameter values highly instance-dependent. Namely, a configuration that works well on a small instance may be poorly suited to a much larger one when transferred without adaptation.

RULER is therefore designed to transfer conditional parameter-edit knowledge rather than absolute historical configurations: it retrieves potentially relevant rules, instantiates bounded edits around the current configuration, and validates their effects through target-side solver evaluations.

Following your suggestion, we introduce two historical configuration baselines: Best-history, which reuses the best-performing configuration from previous instances, and Random-history, which randomly selects a previously evaluated configuration. We compare them with the w/o induction control. Unlike direct configuration reuse, w/o induction retains historical numerical configurations as raw examples and allows the LLM to generate new proposals without induced edit–response rules. As shown in Table 1, full RULER achieves lower gaps than all alternatives across the four settings, demonstrating the benefit of transferring structured, context-dependent optimization knowledge rather than relying solely on historical parameter values.

Table 1. Historical configuration reuse and rule induction. Mean gap (%); lower is better. The final column reports the relative gap reduction achieved by Full RULER compared with w/o induction.

SettingFull RULERw/o inductionBest-historyRandom-historyGap Reduction (%)
TSP GA+2opt0.6200.7200.7460.681+16.15%
TSP-SA4.0274.1385.2695.359+2.76%
CVRP PSO+ILS1.9512.4912.3302.373+27.67%
CVRP SA+ILS1.5461.9041.9402.083+23.12%
AuthorsOpenReview ↗

Response to Question 3 – About positive rule

We thank the reviewer for identifying this ambiguity. We use an unchanged-continuation reference: the unchanged configuration and each candidate are run independently from copies of the same checkpoint, with equal solver budgets and controlled random streams. For minimization, the measured response is Δf=funchanged−fcandidate\Delta f=f_{\mathrm{unchanged}}-f_{\mathrm{candidate}}; thus, a positive value means that the candidate improves upon continuing with the original configuration for the same budget. Supporting, contradicting, and unproven labels are computed programmatically from solver measurements using predefined thresholds, not assigned by the LLM. These labels are practical evidence categories rather than statistical-significance tests. The checkpoint, budget, and randomness controls are detailed in AppendixE.1.

Comments on the paper

1 comment

We sincerely thank all reviewers for their valuable and insightful feedback. We appreciate their recognition of the practical relevance of our work and the potential of RULER for facilitating knowledge transfer in online algorithm configuration.

  • Reviewer jDHm highlights RULER's strong performance across all four problem–solver settings, the usefulness of treating previous trials as contextual evidence, and the effectiveness of the proposed framework supported by component ablations. The reviewer also appreciates the matched wall-clock comparisons.

  • Reviewer FJxY recognizes the practical importance of online algorithm configuration, appreciates the broad comparisons with established configuration methods, and acknowledges the potential of structured reuse of historical optimization experience.

  • Reviewer d5CP appreciates the idea of summarizing optimization experience into structured edit–response rules, the comprehensive experimental evaluation across TSP and CVRP, and the usefulness of component ablation studies.

The main concerns raised by the reviewers relate to methodological novelty, the effectiveness of rule-based knowledge transfer, experimental reliability, and the clarity and fairness of evaluation protocols. In our rebuttal, we have addressed these concerns through additional experiments and clarifications:

  • Methodology and Knowledge Transfer – We introduced Best-history and Random-history baselines, together with a full-benchmark w/o induction ablation, to distinguish structured rule induction from simply reusing historical configurations. We also clarified the roles of the proposed experimental strategies and the evaluation of rule evidence.
  • Experimental Validation – We extended component ablations to the complete benchmark and conducted three independent runs for each of the four main settings, reporting the mean, standard deviation, and variance. We further analyzed the allocation frequencies of the four experimental roles.
  • Evaluation and Reproducibility – We clarified solver checkpoint restoration, random seed control, and evaluation budget accounting. We also provided additional details on AutoEP-Rep and conducted additional comparisons, including RULER-16 and a solver-aligned RULER-8+2opt experiment. We are committed to incorporating these additional analyses and clarifications into the revised manuscript to improve its clarity, reproducibility, and overall presentation. We sincerely thank all reviewers for their constructive feedback and valuable suggestions.

We also note that Reviewer FJxY has not yet provided a follow-up response during the discussion period. We would greatly appreciate it if the AC could kindly remind the reviewer to share any remaining feedback or concerns, if possible, so that we may have an opportunity to address them.

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

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