Recovering Wasted Compute in Autoresearch Agents

Abhigyan Acherjee; Amrutha Rao; Au Kwok Chun; C. Bayan Bruss; Kazem Meidani; Micah Goldblum; Zaiqian Chen

REVIEW 3 major objections 5 minor 25 references

Recovering Wasted Compute in Autoresearch Agents

T0 review · 3 major / 5 minor · reviewed 2026-08-15 · deepseek-v4-flash

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Pith's one-line read Autoresearch agents waste compute on re-solving the same bugs, and this paper shows a shared debug consultant that spreads each lesson across the search tree recovers that waste, nearly doubling MLE-bench gold medals with the language…

desk verdict The debug consultant is a promising idea, but the flagship numbers depend on an unexplained initialization that the paper must disclose; the rest of the empirical work is solid, mostly honest, and worth engaging with. read the letter →

arxiv 2608.10424 v1 pith:JNUUVQJ3 submitted 2026-08-11 cs.AI cs.LG

Au Kwok Chun , Abhigyan Acherjee , Amrutha Rao , Zaiqian Chen , Kazem Meidani , C. Bayan Bruss , Micah Goldblum This is my paper · ORCID

classification cs.AIcs.LG

keywords autoresearchagenticdatasciencetreesearchagentsdebugconsultantcontextsharinghyperparametertuningenforcementThompsonsamplingMLE-bench

verification ladder T0 review T1 audit T2 compute T3 formal

The pith

A machine-rendered reading of the paper's core claim, the machinery that carries it, and where it could break.

The reading

Autoresearch agents—LLM systems that write code to solve machine-learning tasks end-to-end—are receiving large industry investment, but much of the compute they consume is wasted rather than spent. This paper identifies four structural ways tree-search agents waste budget: re-discovering the same runtime bugs in every branch, stopping search before tuning hyperparameters, failing to explore the candidate space, and ignoring the data analysis they perform. The paper's central claim is that these failures are fixable by design alone: a 'debug consultant' that compresses each crash into a shared bug registry and injects the distilled lessons (banned patterns and proven fixes) into every branch, plus reward shaping that enforces hyperparameter tuning and Thompson Sampling that backtracks out of failing paths. Holding the language model fixed, these interventions lift AIDE's gold medals from 22 to 38 out of 90 runs on MLE-bench and raise its valid-submission rate from 81% to 100%, with comparable gains for ML-Master. If right, the paper implies current agents operate far below the ceiling their language models already permit, and that memory, reliability, and exploration belong on the agent-design agenda.

What carries the argument

The central object is the debug consultant: a shared registry that turns each node's crash into a compressed record, accumulates these records across the whole search tree, distills them into a short list of banned patterns and proven fixes, and injects that list into the prompt before every draft and debug step—so the agent learns its execution environment (library versions, valid API signatures) once instead of per branch. The registry is built by a three-step control loop (error compression, shared registry, constraint injection) plus deterministic rules that treat timeouts and empty logs as terminal dead ends. Two supporting mechanisms carry the other results: a 0–3 hyperparameter-tuning score assigned by an LLM judge and folded into node selection (an additive metric adjustment in AIDE, a $+0.25 \times \text{hpo\_score}$ term in ML-Master's UCT reward), and Thompson Sampling in which each sibling node holds a $\text{Beta}(\alpha, \beta)$ distribution over quality—updated by normalized rewards after each execution—with backtracking to the branch point where a repeated error first appeared.

What would settle it

Run the debug consultant on the same nine MLE-bench tasks with a different backbone model, or with a LightGBM version where early_stopping_rounds is a valid argument: if redundant bug encounters do not collapse and the gold-medal gain (22 to 38 on AIDE) does not persist, the headline effect is an artifact of the single environment. A complementary test is to choose tasks where no single API error dominates, since the claim that sharing failure knowledge is generally valuable predicts the consultant should still reduce redundant debugging and improve valid-node rates there.

Watch

Extended reading notes

Core claim

The discovery, stated on the paper's own terms, is that a large fraction of an autoresearch agent's budget is consumed by failures the agent has already met before, and that making failure knowledge global rather than local converts that wasted compute into productive iteration. The debug consultant does this by compressing each node's traceback into a short record (error type, signature, failed strategy), accumulating records across all branches into a registry that distills 'BANNED' patterns and 'PROVEN FIX' replacements, and injecting the distillation into every subsequent generation and debug step; within one run, a single branch's crash becomes every branch's lesson. The measurable consequences in AIDE's search journals are that redundant bug encounters fall from 46.0% to 7.8% of nodes, the valid-node rate rises from 54.7% to 79.0%, the median step to a first valid submission drops from 6 to 0, and seeds with more valid nodes score better (pooled $r = +0.22$). The same philosophy extends to the other interventions: hyperparameter-tuning guidance, enforced through an LLM-judged 0–3 score folded into the search reward, recovers up to +0.388 on a single competition, and Thompson Sampling with backtracking cuts null runs from 33 to 15 of 90 on AIDE while largely preserving peak scores.

Load-bearing premise

Every experiment uses the same single language model, GPT-5-mini, in one fixed environment where one particular LightGBM API incompatibility (early_stopping_rounds raising a TypeError) accounts for most baseline failures, so the large measured gains could be largely a product of that specific environment and model rather than of the interventions themselves.

Editorial extensions

If this is right

With the language model held fixed, purely structural changes to the agent can nearly double medal-level results on MLE-bench tabular tasks: AIDE golds rise 22 to 38 with 100% valid submissions, and ML-Master golds rise 18 to 29.
An agent that shares failure knowledge across the tree reaches a working solution at median step 0 and spends its remaining budget on real modeling iteration, producing qualitatively more sophisticated solutions such as calibrated ensembles and optimized thresholds where the baseline produced single models.
Enforcing structured hyperparameter tuning through the reward function recovers performance wherever agents stop early, with gains up to +0.388 on one competition; because the same intervention hurts ML-Master by pushing it into a crashing HPO implementation, scaffold interventions must be designed with the target agent's memory architecture in mind.
Thompson Sampling with backtracking primarily buys reliability: null runs drop from 33 to 15 of 90 on AIDE at negligible cost to peak scores.
Because baseline agents ignore even adversarially injected exploratory data analysis (it changed feature selection in only 5% of AIDE runs), closing the EDA-to-decision gap is a concrete remaining design target rather than an already-solved stage of the pipeline.

Reading between the lines

Editorial extensions of the paper, not claims the author makes directly.

The paper's own asymmetry result—the same HPO intervention that helps AIDE degrades ML-Master—suggests the headline debug-consultant gains may be less universal than the framing implies: with one environment and one backbone, the consultant may be partly memorizing a single dominant bug. A direct extension would be to test the consultant across backbones and library versions, separating environmen
The pooled correlation between valid-node count and final score ($r = +0.22$) suggests the operative mechanism is simply more successful iterations per budget; if so, any intervention that raises the valid-node rate—cheaper evaluation, faster execution, better debugging—should compound into better final solutions, a testable prediction the paper does not state.
Because the consultant's knowledge is environment-level (installed versions, valid API signatures), the registry is naturally reusable across runs: persisting it between runs of the same benchmark would turn each new task into a warm start, an extension the paper does not explore.
The adversarial-EDA diagnostic is a negative result with a constructive counterpart the paper leaves implicit: a control loop that forces the agent to consume its own EDA, for instance by requiring a feature-selection justification before training, could test whether EDA becomes valuable once adherence is enforced.

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Editorial analysis

A structured set of objections, weighed in public.

Desk editor's note, referee report, and a circularity audit.

Desk Editor's Note

read the letter

You should read this paper for the debug consultant alone, and you should read it with the stress-test note in hand. The core mechanism is a shared registry of runtime constraints across a tree search, which is a genuinely new and useful design. The evidence that it works is rich: redundant bug encounters drop from 46% to 7.8%, first-attempt fix rates double, and the two case studies include full generated code showing how valid-node budget translates into ensembles and calibration. The ML-Master HPO degradation is reported honestly and is itself a finding about scaffold-transfer. The MLEvolve controlled TS study is clean and supports a stability claim. Those parts deserve credit.

But the main experiment has a load-bearing ambiguity. Section 3.1 describes a within-run registry that starts empty and accumulates errors as nodes crash. Section 4.2 says the consultant supplies the environment's constraints before the agent writes its first line of code, and Table 5 shows 69% of treatment seeds already have a valid submission at step 0 versus 3% for baseline. A within-run registry cannot explain that. Either the registry is pre-seeded with known environment facts (the LightGBM early_stopping_rounds incompatibility being the obvious candidate), or there is an undocumented pre-flight probe. The paper does not say. The 'Code available here' link points nowhere, so the initialization cannot be checked. This matters because the headline claim—that agentic design alone, via adaptive learning, recovers wasted compute—collapses to environment-specific prompt engineering if the BANNED list is seeded. This is not a minor omission; it is the difference between the paper's central contribution and a much less interesting result. The paper itself contains the contradiction in Section 4.2 versus Section 3.1, so either the text is misleading or the mechanism is different from what is described.

Other soft spots are proportionate. The AIDE Thompson Sampling headline conflates the selection strategy with raising initial drafts from 5 to 20; the controlled comparison shows TS mainly reduces null runs rather than raising peak scores, which is a weaker but still defensible claim. Single-backbone evaluation on GPT-5-mini is a real limitation, and the paper acknowledges cost constraints. These are minor-to-moderate.

My bottom line: this deserves a serious referee, but only conditionally. The debug consultant idea should see the light of day; the ambiguity about registry initialization is checkable and fixable. I would ask the authors to describe exactly what is in the registry at step 0, release the code, and run an ablation with a truly empty registry. If the 69%-at-S0 effect disappears, the paper becomes a study in environment-specific prompting, still useful but not the contribution it claims. If the effect persists, the paper is a solid systems result. Either way, it is worth engaging with, provided the authors answer the initialization question before publication.

Referee Report

3 major / 5 minor

Summary. The paper studies four interventions aimed at recovering wasted compute in tree-search-based autoresearch agents (AIDE, ML-Master, and MLEvolve) applied to nine tabular Kaggle/MLE-bench tasks with a fixed GPT-5-mini backbone and a two-hour compute budget per run. The interventions are: (1) a global debug consultant that shares discovered runtime constraints across the search tree via a shared bug registry and injected BANNED/USE lists; (2) prompt- and control-loop-level enforcement of hyperparameter tuning; (3) Thompson Sampling with backtracking to replace random sibling selection; and (4) a diagnostic injecting adversarial EDA results to test whether agents act on analysis. Headline results include raising AIDE gold medals from 22 to 38 and valid-submission rate from 81% to 100% with the debug consultant, large AIDE gains from HPO guidance (with a documented degradation for ML-Master), and a 54.5% reduction in null runs from Thompson Sampling in a controlled comparison. The paper also includes detailed journals, case studies, per-seed scores, and an honest discussion of where interventions fail. The central claim is that large gains are achievable through agentic design alone, holding the underlying language model fixed.

Significance. If the central claim holds, the paper would be a meaningful contribution to agentic AutoML design: it identifies concrete structural causes of wasted compute and evaluates targeted fixes with extensive logs and per-seed results. The strengths are the detailed case studies (e.g., S5E3 and Wine showing the same early_stopping_rounds bug dominating baseline budgets), the controlled Thompson Sampling comparison in Table 16, and the transparent reporting of the ML-Master HPO degradation. However, the significance is currently undercut by a load-bearing ambiguity about how the debug consultant is initialized (Section 4.2 says it supplies environment constraints 'before the agent writes its first line of code' while Section 3.1 describes a within-run registry that starts empty), the absence of a working code link, and the use of a single backbone and environment in which one LightGBM API incompatibility dominates failures. These issues must be resolved before the paper's broad claim about agentic design alone is established.

major comments (3)

[Section 3.1 vs. Section 4.2 and Table 5] There is an internal contradiction about the debug consultant's registry initialization that is load-bearing for the paper's central claim. Section 3.1 describes a within-run process: Step 1 starts 'When a node crashes', Step 2 accumulates records into a shared registry, and Step 3 injects constraints into subsequent generations. This implies the registry is empty before the first node executes. Yet Section 4.2 states that the consultant 'supplies the environment's constraints before the agent writes its first line of code', and Table 5 reports that 69% of treatment seeds already have a valid submission at step 0, versus 3% for the baseline. A within-run registry cannot be non-empty before any node has executed, so either the registry is pre-seeded with known environment facts (e.g., the LightGBM early_stopping_rounds/verbose incompatibility), or there is an undocumented pre-flight environment probe, or the definition of 'step 0' differs from what I assume. This matters because if the BANNED list is pre-seeded with the specific LightGBM API incompatibility, the headline gains are attributable to environment-specific prompt engineering rather than to the claimed adaptive, within-run learning of the execution environment, and the abstract's claim that large gains come from 'agentic design alone' is not established. Please clarify the initialization of the registry, define step 0 precisely, and if pre-seeding is used, disclose it and re-frame the mechanism accordingly, ideally with an ablation that removes the pre-seeded entries.
[Section 2 and Appendix 'Code available here'] The manuscript contains the text 'Code available here' (in Section 2) but no URL or repository identifier follows it. The debug consultant's mechanism, including whether the registry is pre-seeded, cannot be verified without the code. Since the central claims rely on implementation details (the sharing of the registry, the exact injection of BANNED/USE constraints, and the Thompson Sampling updates), the absence of a working code link is a serious reproducibility problem. Please provide a complete code release or, if the link was accidentally omitted, include it in the revision.
[Section 4.4, Tables 12-13 and Table 16] The headline Thompson Sampling results in Table 12 are obtained under a configuration that differs from the baseline in two additional hyperparameters: Table 13 changes initial drafts from 5 to 20 and max-debug depth from 20 to 5, alongside the TS selection strategy. The paper correctly includes the controlled comparison in Table 16 (AIDE+TS+More Drafts vs. AIDE+More Drafts), which isolates TS and shows the null-run reduction from 33 to 15. However, Table 16 also shows that TS loses the score comparison on 6 of 9 competitions (Cirrhosis, S5E3, S5E6, S5E7, S5E12) and ties a seventh, so the claim that the added stability comes 'at no cost to peak performance' should be hedged to 'at no cost in mean score beyond sampling error on most competitions.' I recommend presenting Table 16 (or an equivalent controlled comparison) as the primary evidence for the TS contribution, with Table 12 relabeled as the combined-intervention result, so that readers do not attribute the draft-count and max-debug-depth effects to TS alone.

minor comments (5)

[Table 5 and Figure 5] Please define 'step 0' explicitly in the table caption and text. The current phrasing 'Fraction of seeds with ≥1 valid submission by step N' is ambiguous about whether step 0 is the initial draft before any execution or the first executed node, which is central to interpreting the 69% S0 value.
[Tables 1 and 2] The gold-count comparisons (e.g., 22 vs. 38 for AIDE) are reported without uncertainty or a significance test. Since gold medals are derived from thresholds on the leaderboard, a per-competition Fisher exact test or a permutation test across seeds would strengthen the claim that the intervention changes medal counts.
[Appendix B.5, Table 10] The pooled correlation is computed after z-normalizing within each competition; please state this explicitly in the main text or table caption and provide the number of seeds per competition, since the per-competition correlations range from r=-0.27 to r=+0.63.
[Appendix C, Table 18 footnote] The footnote notes that the ML-Master baseline in the EDA study was based on 'a different set of runs than the baseline used for the debug consultant.' Please clarify how this affects comparability and whether the baseline conditions were otherwise identical.
[Section 4.3 and Appendix C] The HPO quality scorer uses gpt-4o-2024-08-06 as the judge while the agent backbone is GPT-5-mini. Please confirm that the judge is independent of the agent's own model and discuss any risk of the judge favoring code patterns it recognizes from its training data.

Circularity Check

0 steps flagged · score 0.0 of 10

No significant circularity: the headline gains are empirical held-out comparisons, with no fitted-parameter or self-citation reduction; the S0 anomaly is a confounding concern, not circularity.

full rationale

The paper's central claims—debug-consultant gold gains (22 to 38 for AIDE, 18 to 29 for ML-Master), hyperparameter-guidance deltas, and Thompson-Sampling null-run reductions—are empirical measurements against held-out Kaggle test sets using the official MLE-bench grading scripts. No parameter is fitted to the target metric and then re-reported as a prediction, and no equation defines an output in terms of its input. The LLM-based HPO judge is a measurement and control instrument: it shapes the search reward, while final scores come from official leaderboard metrics, so there is no reduction. The scaffolds and benchmarks (AIDE, ML-Master, MLEvolve, MLE-bench) are external, and the paper does not rest on a load-bearing self-citation. Two non-circularity caveats are worth flagging. First, Section 3.1 describes a per-run registry that starts empty and accumulates compressed failures, yet Section 4.2 and Table 5 report a 69% first-step valid-submission rate under treatment and state that the consultant 'supplies the environment's constraints before the agent writes its first line of code'; this internal inconsistency suggests possible pre-seeding or an undocumented pre-flight probe, which is a validity and generalization concern rather than a circular derivation. Second, the manuscript's 'Code available here' points to no URL, harming reproducibility but not indicating circularity. Overall, the derivation chain is not circular because the reported outcomes are directly measured on held-out test data rather than constructed from the intervention's own definitions.

Assumptions & free parameters 5 free parameters · 4 assumptions · 0 invented entities

The empirical claims rest on several hand-chosen hyperparameters (draft count, backtracking threshold, HPO reward weights) and on assumptions about task representativeness and model generality. The debug consultant itself is a software component, not a newly postulated physical or mathematical entity, so no invented entities are listed.

free parameters (5)

initial_drafts_for_TS = 20 (vs 5 baseline)
The number of initial solution nodes was raised from 5 to 20 because TS realizes its advantage only when it has a rich pool of candidates (Section 4.4). This is a hand-chosen hyperparameter that changes the comparison between TS and baseline.
similar_error_backtracking_threshold = 3
Lets the agent backtrack to the node that first triggered a repeated error (Section 4.4, Table 13). Set by hand without ablation.
hpo_reward_weight_ML-Master = +0.25 * hpo_score
Reward shaping coefficient that folds the 0-3 HPO score into UCT reward (Section 3.2). Chosen without reported sensitivity analysis.
hpo_metric_adjustment_coefficients_AIDE = 0.1 scaling, -0.300 penalty for HPO score 0
Metric adjustment formula metric_adj = metric_base + 0.1*s*(r_hpo + r_div + r_corr) with a -0.300 penalty shown in the Appendix C log. Coefficients are hand-set.
beta_prior_for_thompson_sampling = Beta(1,1)
Uniform prior over sibling quality; standard choice, but not varied or tested in the paper.

assumptions (4)

domain assumption The nine selected Kaggle competitions are representative of tabular ML tasks and MLE-bench.
Section 4.1 selects tasks by criteria (postdate knowledge cutoff, moderate size, diverse metrics); this assumes these choices do not bias results.
domain assumption GPT-5-mini is representative of language models used in autoresearch agents.
Section 4.1 'Note on API models' states all experiments use GPT-5-mini for cost reasons; transfer to frontier models is not tested.
domain assumption MLE-bench grading scripts and the official leaderboard positions provide a valid held-out evaluation.
All scores are measured on the official held-out test set via MLE-bench graders (Section 4.1).
standard math Thompson Sampling with Beta(1,1) priors and the update rule alpha += r, beta += 1-r implements the stated exploration/exploitation tradeoff.
Standard Bayesian bandit background from multi-armed bandit literature; Section 3.3.

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Cite this review

Pith. "Pith review of Recovering Wasted Compute in Autoresearch Agents." pith.science (2026). https://pith.science/paper/JNUUVQJ3

@misc{pith2026260810424,
  author       = {Pith},
  title        = {Pith review of: Recovering Wasted Compute in Autoresearch Agents},
  year         = {2026},
  howpublished = {\url{https://pith.science/paper/JNUUVQJ3}},
  note         = {Machine review of arXiv:2608.10424}
}

read the original abstract

A slew of recent works develop agents for solving research problems end-to-end, a paradigm increasingly referred to as autoresearch. Such agents have inspired large industry investment, motivated by their potential to automate time-consuming human labor and customize machine learning solutions for specialized applications. In this paper, we study the modeling pipeline at the core of these autoresearch systems and identify common failure modes when they are applied to tabular datasets: (1) they waste compute resolving the same bugs over and over again; (2) they often fail to tune hyperparameters even when they have a large remaining compute budget; (3) the tree-search algorithms that power them do not explore; and (4) they perform data analysis, mimicking the humans whose data they are trained on, but do not use that analysis to make downstream decisions. We explore targeted interventions and find that a global debug consultant that shares discovered runtime constraints across all branches of the search tree, prompt- and control-level enhancements, and refined tree-search algorithms successfully recover wasted compute. Our results show that large gains in autoresearch agent performance are achievable through agentic design alone, holding the underlying language model fixed.

Figures

Figures reproduced from arXiv: 2608.10424 by the authors.

**Figure 1.** The debug consultant shares context across the search tree: one node’s failure becomes every node’s lesson. Crashed nodes are compressed into a shared bug index of failed and successful repairs, distilled into banned patterns and proven fixes, and injected into every subsequent generation step, so the agent learns its runtime environment once instead of rediscovering each bug per branch. node, or improve a valid one… view at source ↗

**Figure 2.** Budget dependent control-loop enforcement of hyperparameter tuning in AIDE. Each node is scored for hyperparameter-tuning quality on a 0–3 scale by an LLM judge. Buggy nodes are assigned the worst possible metric and their score is ignored; for a valid node, the score both conditions the agent’s next prompt and adjusts the metric used for node selection. The reward depends on how much budget remains: weak tuning (sc… view at source ↗

**Figure 3.** Thompson Sampling with backtracking reallocates budget away from repeatedly failing branches. Each sibling node carries a Beta distribution over its quality, stored in global memory and updated from observed rewards after every execution. When the agent detects an identical error recurring down a path (S1 → S2 → S3), it backtracks to the branch point where the error first appeared (S1) and re-samples among the sibli… view at source ↗

Figures from the paper (7 more)

**Figure 4.** Figure 4: The consultant raises first-attempt fix rate from 41.4% to 72.4%. Bug recovery rate (left) and first-attempt fix rate (right) per competition. Constraint injection converts random retries into informed corrections. Treatment (%) Baseline (%) Competition S0 S1 S3 S5 S0 …

**Figure 5.** Figure 5: Treatment reaches 100% submission rate by step 3; mean baseline submission rate remains below 40% through step 5. Cumulative submission rate by exploration step for treatment vs. baseline across all 9 competitions (AIDE, 10 seeds each). Treatment Baseline Comp. Tot. Va…

**Figure 6.** Figure 6: Search tree comparison for S5E3 seed 6. Left: baseline (74 nodes, 2 valid, 2.7%). [PITH_FULL_IMAGE:figures/full_fig_p017_6.png]

**Figure 7.** Figure 7: Search tree comparison for Wine seed 1. Left: baseline (10 nodes, 2 valid, 20%). [PITH_FULL_IMAGE:figures/full_fig_p018_7.png]

**Figure 8.** Figure 8: Malicious EDA results inserted into agent’s context at the draft(), debug() and [PITH_FULL_IMAGE:figures/full_fig_p037_8.png]

**Figure 9.** Figure 9: Control evaluation prompt used to test whether the model conducted exploratory [PITH_FULL_IMAGE:figures/full_fig_p038_9.png]

**Figure 10.** Figure 10: Secondary evaluation prompt used to test whether the model conducted ex [PITH_FULL_IMAGE:figures/full_fig_p038_10.png]

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Reviewed August 15, 2026 · model on record in the stance chip above.

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2606.06473 , archivePrefix=

Shangheng Du and Xiangchao Yan and Jinxin Shi and Zongsheng Cao and Shiyang Feng and Zichen Liang and Boyuan Sun and Tianshuo Peng and Yifan Zhou and Xin Li and Jie Zhou and Liang He and Bo Zhang and Lei Bai , year=. 2606.06473 , archivePrefix=

arXiv

[2] [2]

Miller and Abhishek Charnalia and Derek Dunfield and Carole-Jean Wu and Pontus Stenetorp and Nicola Cancedda and Jakob Nicolaus Foerster and Yoram Bachrach , year=

Edan Toledo and Karen Hambardzumyan and Martin Josifoski and Rishi Hazra and Nicolas Baldwin and Alexis Audran-Reiss and Michael Kuchnik and Despoina Magka and Minqi Jiang and Alisia Maria Lupidi and Andrei Lupu and Roberta Raileanu and Kelvin Niu and Tatiana Shavrina and Jean-Christophe Gagnon-Audet and Michael Shvartsman and Shagun Sodhani and Alexander...

arXiv

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2025 , url=

Xu Yang and Xiao Yang and Shikai Fang and Yifei Zhang and Jian Wang and Bowen Xian and Qizheng Li and Jingyuan Li and Minrui Xu and Yuante Li and Haoran Pan and Yuge Zhang and Weiqing Liu and Yelong Shen and Weizhu Chen and Jiang Bian , journal=. 2025 , url=

work page 2025

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arXiv preprint arXiv:2410.07095 , year=

Jun Shern Chan and Neil Chowdhury and Oliver Jaffe and James Aung and Dane Sherburn and Evan Mays and Giulio Starace and Kevin Liu and Leon Maksin and Tejal Patwardhan and Lilian Weng and Aleksander M. arXiv preprint arXiv:2410.07095 , year=

arXiv

[5] [5]

2409.07703 , archivePrefix=

Liqiang Jing and Zhehui Huang and Xiaoyang Wang and Wenlin Yao and Wenhao Yu and Kaixin Ma and Hongming Zhang and Xinya Du and Dong Yu , year=. 2409.07703 , archivePrefix=

arXiv

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Proceedings of the 41st International Conference on Machine Learning , pages =

Language Agent Tree Search Unifies Reasoning, Acting, and Planning in Language Models , author =. Proceedings of the 41st International Conference on Machine Learning , pages =. 2024 , editor =

work page 2024

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International Conference on Learning Representations (ICLR) , year=

Teaching Large Language Models to Self-Debug , author=. International Conference on Learning Representations (ICLR) , year=

[8] [8]

2024 , url=

John Yang and Carlos E Jimenez and Alexander Wettig and Kilian Lieret and Shunyu Yao and Karthik R Narasimhan and Ofir Press , booktitle=. 2024 , url=

2024