acceptodds
Under review as a conference paper at ICLR 2027

SA-DREAM: Utility-Aligned World Modeling for Automatic Algorithm Design

Abstract

Automated algorithm design increasingly uses large language models to propose solver modifications, but identifying which candidates deserve costly real evaluation remains a key bottleneck. We introduce SA-DREAM, a closed-loop framework that predicts the consequences of structured algorithm interventions before allocating evaluation budget. Each proposal is represented as a typed parent–edit–child transition, grounded with retrieved execution evidence, and scored by its predicted improvement over the current incumbent. Executed outcomes then update the search state and inform subsequent decisions. We evaluate SA-DREAM on five combinatorial optimization families and four scales, covering 20 problem–scale settings. Under a controlled typed-intervention protocol, SA-DREAM achieves an average rank of 1.15, compared with 2.20 for the strongest alternative, against native automated algorithm-design systems, it achieves 1.05, compared with 2.00 for the next best method. SA-DREAM also attains the highest problem-balanced best-so-far quality at every tested real-evaluation budget. Ablations confirm the importance of consequence prediction, retrieval grounding, incumbent alignment, and closed-loop adaptation. Moreover, permuting consequence–action correspondence reduces selected utility from 0.325 to 0.244, demonstrating that the gains depend on action-specific consequence information.

Primary area:
optimization
Keywords:
Automated Algorithm Design, Combinatorial Optimization, Surrogate-Assisted Optimization, World Models, Large Language Models

Reviews

Among:
Shape:
1234this paper, Bottom 1%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.00 over 3 reviews, above 0% of the others.
Reviewer_DkTcOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

The paper proposes SA-DREAM, a candidate selection framework for LLM-based AHD that prioritizes candidates worth evaluating. Candidate edits are expressed in a typed grammar and applied deterministically to a parent algorithm. A frozen Qwen2.5-Coder-7B model with a CodeReasoner adapter predicts each edit’s consequence, conditioned on past transitions. Candidates are scored by predicted improvement over the current incumbent, discounted by model–retrieval agreement, and only top-scoring candidates receive real evaluation. Experiments cover five combinatorial problem families at four scales. They compare against surrogate selectors under a shared edit interface and against native AHD systems including EoH, LLaMEA, ReEvo, PartEvo, and MCTS-AHD. The paper reports average ranks of 1.15 and 1.05, respectively.

Critical strengths
  1. The motivation is strong, and the problem is important. Prioritizing which candidates to evaluate is a meaningful, practical problem for AHD.
  2. The incumbent-relative utility is well motivated and precisely stated
  3. Separating controlled and native comparisons is a sound design choice.
Critical weaknesses

Rank-based reporting and inconsistent results.

The main claims rest on average ranks, which hide effect size. For example, SA-DREAM’s 11.6% loss to MCTS-AHD on native BPP S1 appears only as “rank 2.”

The magnitude data in the appendix conflict with the main results:

  1. Table 1(a) cannot be derived from Table 6, contrary to its caption. KNN is last in all 20 settings of Table 6, yet has overall rank 7.00 among 8 methods.
  2. Table 6 contradicts Table 9 at every budget. On BPP, Table 9 places all methods within 0.032 canonical quality, while Table 6 shows KNN using 43% more bins than SA-DREAM at S1. On CVRP, KNN is worst at every scale in Table 6 but never worst in Table 9.
  3. TSP magnitudes in Table 6 are implausible. SA-DREAM’s S4 value (25,236) is about 11× the expected optimal tour for 1,000 uniform points.

Dated backbone

The predictor is Qwen2.5-Coder-7B, a model released in 2024. Stronger models of similar cost now exist. CodeReasoner is not cited or explained, and its reasoning is suppressed by the JSON-only, 256-token output format. Figure 4 tests adaptation only at 7B and scale only without adaptation, so the two effects are confounded. “7B+Weave” is undefined.

Unspecified LLMs in the end-to-end comparison

The paper does not name the LLM used by the native baselines, by SA-DREAM’s generator, or by the Direct LLM Ranker. Native AHD systems typically run on stronger API models. Such models would generate better candidates and use evaluation feedback more effectively, which may reduce the need for pre-screening. Cheap evaluators and budgets of 8–32 evaluations make evaluation artificially scarce. Table 10 also lists fewer LLM calls than evaluated candidates for every native method, which needs explanation.

Missing details and baselines

There is no random-selection baseline, even though at B=8 the selector discards only about one of roughly nine rankable candidates per root. The label-to-score readout, tie rules, and parent-selection rule are deferred to the artifact. “World-model planning” overstates a one-step predictor.

Questions for authors
  1. Why are the main results reported as ranks? Please provide per-setting relative improvements over the best baseline in raw objective units, with paired confidence intervals for both panels. Please also reconcile Tables 1, 6, 8 and 9, state which budget Tables 6 and 8 correspond to, and explain why SA-DREAM’s values differ between Tables 6 and 8 for the same settings.
  2. Why Qwen2.5-Coder-7B rather than a current model? Which CodeReasoner checkpoint and training data were used? Do the results hold with a newer predictor, or with CodeReasoner-14B?
  3. Which LLM did each native baseline, the generator, and the Direct LLM Ranker use? If they differ from each other or from current strong models, why? Does the advantage persist when all systems share the same strong LLM and are matched on total compute as well as evaluations?
Reviewer_7a3JOpenReview ↗
Rating
1
Confidence
4
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

This paper introduces SA-DREAM, a structure-aware search framework designed for automated algorithm design. The framework generates candidate algorithms through structural modifications guided by a typed grammar. It leverages a frozen language model, augmented by retrieved historical execution records, to predict key performance metrics, including validity, solution quality, behavioral shifts, and execution costs. The framework translates predicted gains (relative to a parent algorithm) into improvements over the current best-performing algorithm; it then ranks candidates by incumbent-aligned predicted improvement, discounted by model–retrieval disagreement, to prioritize them for actual evaluation. Execution outcomes are subsequently fed back into the search state. The authors evaluate the framework across five categories of combinatorial optimization problems (spanning 20 distinct settings), comparing it against both controlled baselines (using a unified interface) and native automated algorithm design systems. The results demonstrate that SA-DREAM achieves the best average ranking. Furthermore, the study provides additional empirical evidence through ablation studies, budget-constrained analysis, and an action–consequence permutation experiment.

Critical strengths
  1. This paper addresses the critical challenge of high evaluation costs in Automated Algorithm Design. It proposes a candidate selection rule to prevent modifications that offer only marginal improvements over the parent algorithm from being misidentified as genuine progress in the search process; this approach holds practical significance.

  2. The “Controlled Comparison” framework standardizes interfaces for modifications, feasibility checks, and evaluation budgets. It encompasses 5 problem categories and 20 experimental settings, each featuring 70 independent roots. By conducting paired analyses using these roots as the unit of statistics (reporting means, standard deviations, and 95% confidence intervals), the study provides robust evidence to support its conclusions in “Controlled Comparison” part.

Critical weaknesses
  1. While the paper provides budget-performance curves (Figure 3, Table 9) and paired confidence intervals (Table 7) for the controlled baselines, the more directly relevant native AAD comparisons (such as EoH, ReEvo, and MCTS-AHD) report per-setting means and standard deviations (Table 8) but lack comparable confidence intervals for performance differences and budget-performance analyses. More importantly, Table 2 indicates that typed editing itself substantially impacts performance; furthermore, since the native comparison simultaneously alters both the candidate space and the search strategy, it is difficult to attribute the performance gains in that comparison specifically to world-model-guided selection. Although the controlled panel includes MCTS-Edit and BARK, the authors do not directly compare the established native AAD search strategies under the same typed-intervention interface. Finally, as the model performs only single-step predictions (H=1), and the selection score in Equation (4) relies on predicted quality improvement and model–retrieval agreement, the framework’s distinct contribution beyond that of a retrieval-augmented, one-step surrogate selection approach has not been sufficiently demonstrated.

  2. There are unexplained numerical inconsistencies regarding the paper’s key experimental results, specifically concerning the TSP data presented in Table 6, Equation (12), and Table 9. According to Table 4, the TSP S4 instance set consists of 1,000 2D Euclidean points distributed within a [0,100]2[0, 100]^2 square, yet Table 6 reports an average tour length of 25,236.25 for the SA-DREAM algorithm. By dividing this square into 32 vertical strips of equal width, traversing all points within each strip by alternating the vertical direction, and connecting the paths between adjacent strips, one can construct a tour with a total length not exceeding 32×100+(1000+32)×(100/32)+100=6,52532 \times 100 + (1000 + 32) \times (100/32) + 100 = 6,525. Consequently, the length of the MST must also be no greater than 6,525. Based on Equation (12), the canonical quality QQ for each instance satisfies Q≤1−f/6525Q \le 1 - f/6525. Assuming that Tables 6 and 9 are derived from the same complete experimental dataset and utilize consistent aggregation methods, the average quality QQ for the TSP S4 set should satisfy Q≤1−25,236.25/6525≈−2.868Q \le 1 - 25,236.25/6525 \approx -2.868. Given that the canonical quality values for the other three instance scales are no greater than zero, an equal-weighted average across all four scales would yield a family-level Q@32Q@32 for the TSP instances of no more than −2.868/4≈−0.717-2.868/4 \approx -0.717. This figure is clearly inconsistent with the value of −0.407-0.407 reported in Table 9. If the authors cannot offer a reasonable and verifiable explanation, the credibility of Table 9 and the performance conclusions drawn from it will be significantly undermined. Furthermore, Table 10 reports 11,200 charged evaluations but only 4,820 LLM calls when B=8; this does not clearly align with the per-candidate consequence prediction process described in the paper. The authors should clarify the specific methodology used to track these invocation statistics. Given that these figures directly substantiate the paper’s claims regarding performance and evaluation efficiency, I believe this issue raises significant concerns about the reliability of the experiments.

Questions for authors

Q1. Could the authors provide the per-scale TSP MST reference values, canonical-quality calculations, and aggregation procedures underlying Tables 6 and 9? Do both tables use the same evaluation cohort?

Q2. Could the authors provide confidence intervals for performance differences (paired where identical roots and instances are shared) and budget-performance curves for the native AAD baselines, along with further controlled comparisons that disentangle the contributions of typed editing and world-model-guided selection?

Q3. How do the predicted consequence fields beyond quality improvement affect the actual search decisions, given that the selection score in Equation (4) explicitly relies on predicted quality gain and model–retrieval agreement? What evidence distinguishes the proposed H=1 world-model formulation from a retrieval-augmented, one-step surrogate selector?

Q4. Could the authors clarify the categorical-to-numerical prediction mapping, retrieval weighting, and parent selection rules? How are the LLM-call counts in Table 10 reconciled with the per-candidate prediction protocol?

These questions are central to my assessment, particularly Q1–Q3. I am willing to reconsider my rating if the authors provide convincing, verifiable evidence that resolves these concerns.

Reviewer_TG3cOpenReview ↗
Rating
1
Confidence
4
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

This paper uses a predictor: Qwen2.5-Coder-7B with a CodeReasoner adapter plus retrieval to estimate how much each LLM-proposed solver edit will improve over the current best, and only actually runs the most promising edits. On 5 CO families and 4 scales, it ranks first on average both against learned/BO selectors and against native AAD systems.

Critical strengths
  • Scoring candidates by incumbent-relative gain rather than parent-relative improvement is a reasonable framing for budgeted algorithm design. The controlled panel includes appropriate learned and BO-style selectors (RF, GBDT, LambdaMART, BARK).
Critical weaknesses
  • The result tables look odd, in Table 6, Flow-shop S4, every baseline's mean is exactly KNN's mean (93720.00) times a round factor: 0.95, 0.92, 0.88, 0.89, 0.80, 0.75, 0.68. The S3 row shows the same pattern. In Table 8, adjacent methods differ by constant steps (e.g., four decrements of 7668 on Flow-shop S4). For BPP S4 (2,500 items, sizes in [10, 60], C=100), if sizes are uniform the volume lower bound is about 875 bins, yet SA-DREAM reports 713 (Table 6) and 576 (Table 8); the two tables also disagree. Each root is run only once. Without raw logs, these results are hard to accept as evidence.
  • The term of world model is weak and its cost is not fully counted. It is just a one-step prediction (H=1) with no rollout. Pairwise accuracy is only 0.54 (0.58 with retrieval), vs. 0.52 for KNN, and it is below chance on TSP. The paper does not say what data CodeReasoner was trained on or which LLM proposes the edits. Native baselines get only 8 evaluations per root. Table 10 lists 4,820 LLM calls, while about 13k candidates each need a 7B prediction, so model inference does not seem to be counted.
Questions for authors
  1. How were Tables 6 and 8 produced? Please explain the exact multiplicative patterns, the BPP values below the bound, and why the two tables differ (713 vs. 576).
  2. The paper has no code, please share an anonymous repo.
  3. What data was CodeReasoner trained on, does it overlap with the test families, and which LLM proposes the edits?
  4. Does Table 10 include the 7B prediction calls?

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

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