acceptodds
Under review as a conference paper at ICLR 2027

G\"odel Forest: Balancing Search Depth and Breadth for Data-Centric Recursive Self-Improvement

Abstract

Recursive self-improvement (RSI) aims to achieve compounding gains by having models improve themselves. While most existing RSI systems optimize external agent harnesses or prompts around a frozen base model, data-centric RSI directly updates the model's own parameters by training on agent-generated data. However, because validating data strategies requires expensive model training, existing methods face a fundamental dilemma: a single agent gets trapped in narrow directions and lacks exploration breadth, while naive parallel search or heavy trace sharing sacrifices long-horizon search depth. To address this challenge, we introduce G\"odel Forest, a multi-agent framework that organizes recursive self-improvement as an ensemble of co-evolving search trees. In G\"odel Forest, each agent autonomously grows a persistent tree, deepening, branching, or pruning data strategies based on model feedback to secure depth, while parallel trees explore distinct regions of the data space to expand breadth. Crucially, rather than leaving trees isolated or flooding them with heavy execution logs, a dynamically co-evolving memory connects the forest: agents continuously distill their successes and failures into compact procedural lessons anchored to a global leaderboard. Through this forest ecosystem, a dead-end in one tree instantly warns the whole forest against unpromising paths, while an empirical breakthrough quickly seeds new exploration branches in neighboring trees. Evaluated on RSIBench-Data across six diverse domains, G\"odel Forest outperforms the single-agent baseline by an average of 10.70% while reducing wall-clock time on five tasks. Ablations confirm that co-evolving shared memory yields a +7.00% gain over independent parallel search, demonstrating that collective distillation is key to scalable self-improvement. The code is available at https://anonymous.4open.science/r/godel-forest-review/.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Large Language Models, Recursive Self-Improvement, LLM Agents, Multi-Agent Systems

Reviews

Among:
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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_R1oMOpenReview ↗
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2
Confidence
3
Informativeness
2
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Paper summary

This paper proposes Gödel Forest, a multi-agent framework for data-centric recursive self-improvement that balances search depth and breadth. Each agent maintains a persistent search tree to iteratively refine data generation and training strategies, while multiple agents explore different directions in parallel. An asynchronous shared memory stores distilled lessons from successful and failed experiments, along with a global leaderboard, to guide future exploration. The method is evaluated on six RSIBench-Data benchmarks, achieving an average improvement of 10.70% over a single-agent baseline. Ablation studies further show a +7.00 gain over independent parallel search, supporting the benefit of shared memory and cross-agent coordination.

Critical strengths
  • The paper is well written and accompanied by nicely made figures. It was easy to follow the paper.
  • The method shows consistent improvements across six benchmarks. The ablation study comparing against independent parallel workers further helps isolate the benefit of shared memory and cross-agent coordination.
Critical weaknesses
  • My main concern is the reliability of shared lessons and the potential accumulation of errors over time. If an agent draws an incorrect conclusion from an experiment and shares it with other workers, the error may propagate through subsequent evolution. Have the authors encountered such cases, and is there a mechanism to detect, correct, or remove misleading lessons?

  • Generalization to unseen tasks is not sufficiently evaluated. Checkpoint selection and official evaluation use the same task instances, raising concerns about overfitting to the benchmarks used during search. The authors should evaluate the final models on separate held-out instances that were never used during data strategy search to assess their generalization.

  • The contributions of different components are not fully isolated. The current ablation removes both shared lessons and the global leaderboard, making it unclear which component drives the improvement. The authors should ablate these two components separately under matched compute budgets to clarify their individual contributions.

  • Generalization across target models is not evaluated. All experiments use Qwen3.5-35B-A3B-Base as the target model. The authors should include experiments with other target models to verify whether the proposed framework generalizes beyond this specific model.

Questions for authors

Please see the weaknesses section above

3 comments
AuthorsOpenReview ↗

Response to Reviewer R1oM (1/2)

We thank the reviewer for recognizing the consistent gains and the evidence for cross-worker coordination. We address the four concerns below, focusing on the mechanisms and controlled comparisons that support our contribution.

1. Reliability and correction of shared lessons

Shared lessons guide new hypotheses; measured candidate performance determines selection. A lesson does not directly replace a checkpoint or certify an improvement. The receiving worker must implement the intervention, train the target model, and obtain experimental feedback. Only fully evaluated candidates enter the shared leaderboard used for final selection. This places an empirical check between a shared interpretation and an accepted model improvement.

Persistent private trees provide a complementary protection: earlier strategies and evaluated candidates remain available when a new intervention fails. Workers retain separate research contexts and can revisit productive branches, so one misleading proposal does not overwrite the search history or eliminate previously successful alternatives. The architecture preserves both evidence and options for subsequent decisions.

Section 4.5 documents how an initially useful but incomplete lesson is refined. Final-turn loss masking addresses unstable termination, while later feedback reveals that intermediate verification actions also require supervision. Prefix-truncated trajectories combine the two observations by making verification actions supervised terminal targets. Correction therefore occurs through subsequent experiments and revised interventions. The demonstrated mechanism is evidence-driven revision of how a lesson is applied; the paper does not posit an automatic rule for identifying and deleting every incorrect lesson.

The system-level result is also positive: the communicating forest reaches 54%, compared with 47% for independent workers, with lower Tinker expenditure (239.67 versus 421.63). Together, the evaluation gate, preserved alternatives, and observed refinement explain how procedural sharing remains useful even when individual interpretations require revision.

2. Task-conditioned research and unseen-instance generalization

Our paper studies data-centric RSI: given a target task, can the researcher generate suitable training data for that task and use it to evolve a stronger model? Data generation is inherently task-conditioned: the researcher must know the target task to diagnose where the model falls short on it and to synthesize data that addresses those gaps. Our evaluation therefore measures how effectively the research procedure improves the model on the given task, rather than how well the resulting model transfers to other tasks.

The RSIBench-Data [1] protocol is designed for exactly this question, and we follow it without modification: the researcher develops data and training strategies for a given benchmark, receives only evaluator feedback during search without access to gold solutions, and the frozen selected checkpoint is then scored in an isolated official run on the same tasks. Under this protocol, vanilla and Gödel Forest face identical tasks, feedback, and budgets, so the score difference directly reflects the difference in the research procedure.

AuthorsOpenReview ↗

Response to Reviewer R1oM (2/2)

3. Contributions of the leaderboard and shared lessons

The existing ablation directly tests whether coordination adds value beyond running more workers. Both conditions use three workers and the same resource ceilings. Removing the leaderboard and shared lessons gives 47% on SWE-bench Verified, while the full forest reaches 54%. The full forest also spends less on Tinker (239.67 versus 421.63), so its gain cannot be explained by higher training-service expenditure. This establishes the benefit of the combined communication mechanism under the tested protocol.

The channels have complementary roles. The leaderboard provides a common reference grounded in full evaluations; procedural lessons communicate interventions, observed effects, and operational rules that other workers can test. This includes information from failed experiments that would not appear as the best-performing strategy. The termination-and-verification case in §4.5 illustrates how such information helps construct a new candidate, beyond identifying an existing high-scoring one.

The new leaderboard-only control, now included in Figure 3 and §4.4, provides the requested finer attribution. Keeping K = 3, the researcher, target model, local search protocol, evaluation interfaces, and global budget ceilings fixed, leaderboard-only sharing reaches 49%, close to the 47% of three independent workers. Elapsed time is nearly identical (13.50 versus 13.38 hours), and expenditure falls from 421.63 to 378.00. Rankings alone therefore yield a modest 2-percentage-point gain. With procedural lessons added, the full forest reaches 54% in 14.06 hours at 239.67. Compared with leaderboard-only sharing, this is a further 5-percentage-point gain and 36.6% lower Tinker expenditure, with 0.56 additional hours. The similarity between independent workers and leaderboard-only sharing, followed by the larger improvement from adding lessons, supports the incremental value of procedural knowledge when a shared leaderboard is already available.

4. Generality across researchers and target models

Following the RSIBench-Data [1] setting, all experiments use Qwen3.5-35B-A3B-Base as the target model. Our paper asks whether a researcher can generate suitable data for a given task and thereby train a stronger model. Gödel Forest changes how the researcher generates, evaluates, and shares data strategies; the target model is only the object being trained, and the method does not depend on its architecture or internals. With the target model fixed, the score difference between vanilla and Gödel Forest comes only from the difference in the research procedure.

For our method, the key variable is the researcher that makes the decisions. In §4.3 we replace Claude Code with Codex as the researcher, and Gödel Forest still improves over the vanilla baseline: from 33% to 44% on SWE-bench Verified and from 20.22% to 23.60% on Terminal-Bench 2.0.

References

[1] RSIBench-Data: Benchmarking Data-Centric Research for Recursive Self-Improvement. arXiv:2607.25886v1, 2026.

Thank you for the detailed response and the new experimental results. The new leaderboard-only control helps clarify some of my concerns.

However, I remain concerned about the generalization of the learned models to unseen instances. My concern is not about cross-task transfer to unrelated domains (though showing that would be even better), but rather that using the same benchmark instances for both iterative search feedback and final evaluation risks overfitting to those specific test instances. Without validation on a held-out split of unseen instances, the true generalizability of the evolved checkpoints is not sufficiently established.

I will keep my current rating.

Reviewer_To3jOpenReview ↗
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Confidence
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Informativeness
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Paper summary

This paper proposes Gödel Forest, a multi-agent framework for data-centric recursive self-improvement. Each agent maintains a persistent search tree to iteratively refine data generation and training strategies based on model feedback. Multiple agents explore in parallel and coordinate through a shared memory consisting of a global leaderboard and distilled empirical lessons. Experiments on six benchmarks from RSIBench-Data show consistent improvements over the vanilla single-agent baseline, with an average absolute gain of 10.70 percentage points.

Critical strengths
  1. The paper addresses a practically important problem. Since evaluating data and training strategies requires actual model training, improving the efficiency of data-centric RSI under limited computational budgets is valuable. The proposed framework provides a practical approach to organizing parallel exploration and reusing experimental feedback.

  2. The experimental results are encouraging. Gödel Forest consistently improves upon the vanilla baseline across six benchmarks, with particularly notable gains on SWE-bench Verified and Terminal-Bench 2.0. The comparison with independent workers also provides useful evidence that cross-agent information sharing contributes to the improvements.

Critical weaknesses
  1. The experimental comparisons with existing methods are somewhat limited. Although Section 2 discusses several related works on agent-driven data generation and autonomous fine-tuning, such as FT-Dojo [1] and LaMDAgent [2], the experiments primarily compare Gödel Forest against vanilla Claude Code and Codex agents, along with internal ablations. No direct comparisons with these related methods are provided. Such comparisons would help better establish the effectiveness of the proposed framework relative to existing approaches. If direct comparisons are impractical due to differences in experimental settings or interfaces, it would be helpful for the authors to explain these limitations.

  2. The specific contribution of the proposed tree and forest structures remains unclear. In Section 3, the tree mainly maintains historical candidate strategies, while parent selection, branching, and backtracking are largely determined by the LLM agent, without an explicit mechanism for balancing search depth and breadth. The forest further connects independent workers through a shared leaderboard and distilled empirical lessons, which appears similar to general multi-agent collaboration with shared memory. Although the comparison with independent workers provides evidence that information sharing is beneficial, it does not clearly establish the advantages of the particular tree/forest design over simpler search-history management and experience-sharing mechanisms. Further clarification or more targeted analysis would help better substantiate the contribution of the proposed structures.

[1] Qizheng Li et al. FT-Dojo: Towards Autonomous LLM Fine-Tuning with Language Agents. 2026. https://arxiv.org/abs/2603.01712

[2] Taro Yano, Yoichi Ishibashi, and Masafumi Oyamada. LaMDAgent: An Autonomous Framework for Post-Training Pipeline Optimization via LLM Agents. EMNLP 2025.

Questions for authors
  1. What are the main differences between Gödel Forest and existing agent-based fine-tuning frameworks, particularly those employing iterative search and historical experiment feedback? Were there practical reasons for not including these methods as experimental baselines?

  2. To what extent do the improvements from shared memory depend on structured lesson distillation, rather than simply sharing the best-performing strategies or recent experimental outcomes?

3 comments
AuthorsOpenReview ↗

Response to Reviewer To3j (1/2)

We thank the reviewer for recognizing the practical importance of the problem and the consistent experimental gains. We address the related weaknesses and questions together below.

1. W1 + Q1 — Relation to prior work and choice of baselines

Gödel Forest addresses the organization of persistent parallel data-strategy research under a shared training budget. Iterative improvement and historical feedback are relevant ingredients in prior work; our contribution is their organization into private strategy lineages with asynchronous exchange of evaluated outcomes and reusable procedural lessons. This directly targets the tension between preserving sequential progress and exploring alternative hypotheses when each experiment requires model training.

The cited methods study related post-training problems, but their published experiments use different optimization environments. FT-Dojo [1] evaluates autonomous fine-tuning across 13 tasks using Qwen2.5-7B-Instruct, a single B200 GPU, a 12-hour budget, and at most 2,000 training samples per task. Its accompanying FT-Agent also uses historical feedback. LaMDAgent [2] constructs post-training pipelines by selecting combinations of predefined action types and available objects; its experiments include SFT and TIES model merging over a fixed 100-iteration horizon. Our setting evaluates executable data-generation and curation strategies through LoRA training of Qwen3.5-35B-A3B-Base under the RSIBench-Data interfaces [3] and a global 16-hour/$500 Tinker ceiling. These methods cannot be applied directly to our task, so a direct comparison is not possible. Our contribution also lies in addressing the data problem of model training: the researcher must autonomously generate and curate suitable training data for a given task.

Our baselines hold that research environment fixed and test the proposed organization directly. On SWE-bench Verified, the same vanilla Claude Code researcher scores 35%, the local K = 1 configuration 45%, and three independent workers 47%, compared with 54% for the full forest. These controls distinguish the local search configuration from additional concurrency and coordinated exploration. Across all six benchmarks, the forest improves over vanilla Claude Code by an average of 10.70 percentage points. The Codex experiments additionally test a different researcher implementation while retaining the target model. Together, these comparisons establish the contribution under a common task and resource protocol, which is the basis for attributing the gains to the research architecture.

AuthorsOpenReview ↗

Response to Reviewer To3j (2/2)

2. W2 + Q2 — What the tree, forest, and procedural lessons contribute

The tree makes previous experiments actionable. Each node is an executable strategy program with a recorded parent and experimental evidence. A worker can revise a productive strategy, branch to test a different hypothesis, or return to an earlier version when a descendant regresses. Earlier candidates remain available for selection. This explicit lineage preserves reusable experimental states across non-monotonic trials; a record of scores or an undifferentiated conversation history does not itself specify these operations.

Parent selection is deliberately LLM-mediated because the successors are open-ended program and training interventions, rather than a fixed action set. The archive, parent relationships, branching, backtracking, and evaluation protocol nevertheless define concrete search behavior. Depth comes from sequential refinement within a persistent lineage; breadth comes from alternative branches and concurrent workers. Both consume the same global budget. The architecture organizes this allocation without requiring a hand-designed numerical tree policy.

The forest enables information reuse while preserving distinct search contexts. Workers exchange information asynchronously, so they can incorporate discoveries without synchronizing every experiment or merging their complete histories. The two shared channels serve different purposes: the leaderboard supplies fully evaluated performance references, while lessons record a hypothesis, observed utility change, interpretation, and operational rule. A lesson can therefore convey an intervention from an unsuccessful trial that would never top the leaderboard. It supplies a new hypothesis to test, rather than simply identifying a checkpoint to copy.

Section 4.5 provides a concrete example: final-turn loss masking addresses termination behavior, later feedback identifies the need to supervise intermediate verification actions, and prefix-truncated trajectories combine these observations into a revised strategy. This illustrates how procedural information supports further refinement beyond ranking existing candidates.

The controlled results support this organization: increasing K from 1 to 2 to 3 yields 45%, 51%, and 54% on SWE-bench Verified, while three independent workers reach 47%. Thus, worker count alone does not explain the full forest's performance. The 7-percentage-point difference measures the combined communication mechanism.

The additional leaderboard-only control, now included in Figure 3 and §4.4, shows why sharing procedural lessons matters. With K = 3 and the same researcher, target model, local search protocol, evaluation interfaces, and global budget ceilings, leaderboard-only sharing reaches 49%, close to 47% for three independent workers. Their elapsed times are nearly identical (13.50 versus 13.38 hours), while expenditure decreases from 421.63 to 378.00. Thus, rankings alone provide only a modest 2-percentage-point gain. Adding lessons raises the score to 54%, a further 5-percentage-point improvement, while reducing Tinker expenditure from $378.00 to $239.67 (36.6%). Elapsed time increases modestly from 13.50 to 14.06 hours. These results support the additional value of reusable procedural knowledge beyond sharing evaluated outcomes.

References

[1] FT-Dojo: Towards Autonomous LLM Fine-Tuning with Language Agents. arXiv:2603.01712v2, 2026.

[2] LaMDAgent: An Autonomous Framework for Post-Training Pipeline Optimization via LLM Agents. EMNLP 2025.

[3] RSIBench-Data: Benchmarking Data-Centric Research for Recursive Self-Improvement. arXiv:2607.25886v1, 2026.

Thank you for the detailed response and additional experiments. The new leaderboard-only ablation addresses part of my earlier concerns.

However, I remain concerned about the overall methodological contribution. The proposed framework still appears to be a combination of existing search and multi-agent experience-sharing mechanisms. While the experiments demonstrate the benefits of sharing experiences, I am not convinced that the tree/forest design introduces a distinct mechanism for addressing the claimed depth–breadth trade-off.

I will maintain my current score.

Reviewer_C1LdOpenReview ↗
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Paper summary

The paper studies automated experiments for training data research where traditionally, an LLM researcher proposes a data generation or curation strategy and then a target model is trained on the resulting data. The paper proposes three components. Persistent private search trees. A diagnostic eval. And a shared procedural memory. The main finding is that the Godel Forest leads to large improvements over a vanilla researcher across a large number of tasks when using models like Qwen and Claude Sonnet.

Critical strengths
  • Worthwhile Problem: I think this problem is very useful. Training data is the most painful aspect of training and is very difficult to overcome. I also think the distinction between score leaderboard and procedural knowledge is useful.
  • Training experiments: The paper has experiments via LoRA SFT so I think the numerical evaluations are trustworthy and useful.
  • Substantial Gains: Huge improvements on SWE-bench Pro and Terminal Bench.
Critical weaknesses
  • Writing and presentation: Some parts of this paper are a bit tough to read and follow. I want to list these below although I think the main idea of this paper is clear enough to engage with.
    • Although “agent” is a general term and is fine to use, it is used interchangeably to describe the “worker LLM”, the trained target model, etc. I found this hard to handle at some point. Could the paper be made more precise?
    • The central motivation is repeated fairly often and the abstract uses the same description over and over again with forest ecosystems, guardrails, etc.
    • In Figure 3, I can’t make out category labels. They are crowded.
    • Unfortunately, the introduction and conclusion read a bit like AI wrote it to me. This may just be me but I think the conclusions are a bit difficult to follow at times. I have read the AI Statement and can't tell if AI being used for translation means that writing incorporated AI.
  • Unseen Tasks: There is no established improvement on unseen tasks and the authors do acknowledge this. I think this is important for strengthening the contribution of the paper and I wonder why this was not included. Have the authors tried including having a reserve set of evaluator tasks.
  • Comparison with RSIBench: One small comparison here is that the reported RSIBench numbers are slightly different that is reported here. I took a quick look and it seems RSIBench reports 61% on GPQA Diamond. This is with an unadapted Qwen model. Godel Forest achieves 55% and the researcher achieves 52%. I’m curious why this discrepancy actually arises. Have the authors tried reproducing the original baseline.
  • Statistical Reliability: I think having multiple seeds over independent search-runs is very important and the paper should add them. The improvements are large enough that I won’t say this is a very large weakness but I do think this is imperative before I recommend acceptance.
  • Details: The manuscript should eventually have many more details on how the worker LLM is used. The actual stage skills and researcher instructions, the backtracking behavior, none of this is described.
Questions for authors
  • How does the method compare with a leaderboard-only condition?
  • What actually determines termination of the method? How should efficiency be interpreted in this setting?
  • What evidence shows that additional concurrency reduces useful search depth? I still don’t see in this paper unless I am missing something?
3 comments
AuthorsOpenReview ↗

Response to Reviewer C1Ld (1/2)

We thank the reviewer for recognizing the importance of data-centric research and the substantial experimental gains. We address each weakness and question below.

1. W1 — Writing and terminology

We have revised the manuscript following your suggestions on terminology and repeated motivation. We now distinguish the worker LLM, which makes research decisions; the strategy program, which specifies a data-generation, curation, and training intervention; and the target model, which is trained and evaluated. This makes both the object being modified and the component making each decision explicit. We have also replaced the recurring forest, guardrail, and seed metaphors in the abstract, introduction, method, and conclusion with concrete descriptions of how workers use shared lessons. Figure 3 is now redrawn at full text width with horizontal bars, so every condition label is legible. All added or rewritten text is marked in blue in the revised manuscript.

2. W2 — Evaluation on unseen tasks

Our paper studies data-centric RSI: given a target task, can the researcher generate suitable training data for that task and use it to evolve a stronger model? Data generation is inherently task-conditioned: the researcher must know the target task to diagnose where the model falls short on it and to synthesize data that addresses those gaps. Our evaluation therefore measures how effectively the research procedure improves the model on the given task, rather than how well the resulting model transfers to other tasks.

The RSIBench-Data [1] protocol is designed for exactly this question, and we follow it without modification: the researcher develops data and training strategies for a given benchmark, receives only evaluator feedback during search without access to gold solutions, and the frozen selected checkpoint is then scored in an isolated official run on the same tasks. Under this protocol, vanilla and Gödel Forest face identical tasks, feedback, and budgets, so the score difference directly reflects the difference in the research procedure.

3. W3 — Comparison with RSIBench-Data

Our Sonnet-5 baseline matches RSIBench-Data. Its main results table reports 52% on GPQA Diamond for Claude Code with Sonnet-5, exactly the baseline in our Table 1 [1]. The 61% figure belongs to the unadapted Qwen base model, whereas 52% evaluates the checkpoint produced by the Sonnet-5 research procedure.

Gödel Forest retains the Sonnet-5 researcher and target-model setting and reaches 55%. The controlled comparison is therefore 52% to 55%, a 3-percentage-point gain from changing the research organization.

4. W4 — Statistical reliability and experimental cost

Each independent search repeatedly performs data generation, LoRA training, and sandbox evaluation, with ceilings of 16 hours and $500 in Tinker expenditure for the entire run. Replicating every task, researcher, and ablation is therefore substantially more expensive than repeating inference on a fixed model. Comparable studies also constrain replication: RSIBench-Data reports one representative run per setting [1]; FT-Dojo uses single controlled runs for its comparison baselines, noting that three seeds across all methods and tasks would require over 1,500 GPU-hours [2].

Our argument rests on convergent evidence across six benchmarks, two researcher implementations, and controlled comparisons of local, independent parallel, and coordinated search. Gains are consistent across all six tasks and both researchers. This evidence supports the search architecture beyond an isolated favorable result, while the reported resource costs make the scope of the evaluation transparent.

AuthorsOpenReview ↗

Response to Reviewer C1Ld (2/2)

5. W5 — Worker instructions and implementation details

The complete worker instructions and stage skills are provided in the anonymous repository linked in the abstract. DATAGEN_AGENT_FLOW.md describes the Diagnose–Propose–Validate loop, multiagent/prompts.py defines worker instructions, and the packaged stage skills specify how the worker carries out each stage of the loop. These instructions are lengthy, so the manuscript presents the mechanism and Algorithm 1 while the repository supplies the full implementation.

Backtracking means selecting an earlier archived strategy program as the parent of a new intervention, using its recorded outcomes to guide the choice. Earlier candidates and their evidence remain available when a descendant regresses. The tree thus preserves reusable experimental states instead of requiring the worker to reconstruct previous strategies from conversational history.

6. Q1 — Comparison with leaderboard-only sharing

Leaderboard-only sharing performs close to three independent workers, whereas adding procedural lessons produces a larger improvement. We have run the requested control on SWE-bench Verified and added it to Figure 3 and §4.4, alongside the three-independent-worker and full-forest results. All three conditions use K = 3, Sonnet-5, the same target model, local search protocol, evaluation interfaces, and global budget ceilings.

ConfigurationShared leaderboardShared lessonsOfficial scoreTime (h)Tinker cost ($)
3 Independent WorkersNoNo47.00%13.38421.63
Leaderboard onlyYesNo49.00%13.50378.00
Gödel ForestYesYes54.00%14.06239.67

Leaderboard-only sharing achieves 49% versus 47% for independent workers, a modest 2-percentage-point gain, with nearly identical elapsed time (13.50 versus 13.38 hours). Although expenditure decreases from $421.63 to $378.00, sharing rankings alone leaves performance close to uncoordinated parallel search.

Adding procedural lessons increases the score further to 54%, exceeding leaderboard-only sharing by 5 percentage points and independent workers by 7 percentage points. Relative to leaderboard-only sharing, the full forest reduces expenditure by 36.6%, with only 0.56 additional hours. These results support the value of procedural knowledge beyond outcome rankings. The termination-and-verification case in §4.5 illustrates how workers use this information to construct improved strategies.

7. Q2 — Termination and efficiency

The run terminates when all workers in the multi-agent system have autonomously stopped exploring, or when the global time or cost limit is reached. Each worker decides from its experimental feedback whether to continue or stop; we neither prescribe a fixed iteration count nor manually decide when a trajectory has explored enough. Once either condition is met, the manager returns the best fully evaluated checkpoint on the leaderboard as the final result. We have stated this termination rule in §3.3 of the revised manuscript.

Efficiency refers to the score reached relative to the resources actually used, under the same time and cost limits. Because workers stop autonomously, a run need not use up its limits, so we report the official score together with the actual wall-clock time and Tinker expenditure (Table 1). On this basis, Gödel Forest reaches a higher score on all six benchmarks and finishes earlier on five of them.

8. Q3 — Concurrency and effective search depth

The total budget is shared by the forest and does not increase with worker count. More workers launch training and evaluation concurrently, drawing down the same allowance. When expenditure is the binding constraint, higher concurrency can reach the cap earlier and leave fewer sequential refinement opportunities along each lineage. Breadth and depth consequently compete for a common experimental budget.

The ablation shows this practical trade-off: increasing K from 3 to 4 leaves SWE-bench Verified performance at 54%, while increasing Tinker expenditure from $239.67 to $404.43 and elapsed time from 14.06 to 15.80 hours. The additional cost and time were spread across more parallel branches without yielding a higher score, which is our basis for saying that concurrency competes with search depth. We have revised §4.4 accordingly. The design addresses this trade-off by combining persistent local search with bounded parallel exploration.

References

[1] RSIBench-Data: Benchmarking Data-Centric Research for Recursive Self-Improvement. arXiv:2607.25886v1, 2026.

[2] FT-Dojo: Towards Autonomous LLM Fine-Tuning with Language Agents. arXiv:2603.01712v2, 2026.

Thank you for the revisions and the additional leaderboard experiment. The clearer distinction between the worker LLM, strategy program, and target model is super helpful. Also the new Figure 3 looks much better. So this addresses many of my presentation concerns. Also the stopping rule is now much clearer.

Unfortunately, my main empirical concerns remain. The task-conditioned data generation is compatible with evaluating on held-out instances of the same benchmark so the stated scope does not resolve the lack of evidence for unseen generation. I appreciate the authors taking the time of repeating the full search. But, consistency across different benchmarks does not establish the reliability of individual comparisons. The concurrency results also point to hihger expenditure without a score improvement at four workers, but do not show reduced search depth as the explanation. So this means that reliability evaluation-scope concerns remain unresolved. I'll retain my score.

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

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