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Desk rejected at ICLR 2027

Beyond Skill Evolution: Navigating the Adaptation Path for Skill Libraries

Desk rejected at ICLR 2027, so left out of the paper lists and the map.

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Abstract

A skill is a structured natural-language document that integrates tool descriptions and workflow examples, and can be reused across tasks. However, the performance of the same Large Language Model (LLM) agent models varies a lot on the same skill library. Existing reflective skill evolution methods answer only what to evolve: they edit contents along a single adaptation trajectory for a single skill, lacking an explicit mechanism for locating failures to evolve across a multi-skill library, and failing to break away from the evolution paths with accumulated suboptimal edits. In this paper, we reframe skill evolution as an agentic tree search problem over the two challenges and propose SkillPilot, a Meta-Optimizer-Guided Monte Carlo Evolution Tree Search (MCETS) framework that navigates where and which way to evolve for a skill library in four recurrent stages: selection, expansion, simulation, and backpropagation, flexibly navigating the evolution path, which prevents the agent from over-exploring the suboptimal evolution path. Extensive experiments have demonstrated SkillPilot's superior performance on agent-generated skills and human-curated skills on three benchmarks with various task types.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Large Language Model Agents, Agent Skills, Skills Evolution, Monte Carlo Tree Search

Reviews

Among:
Shape:
1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_foRdOpenReview ↗
Rating
3(+1)
Confidence
4
Informativeness
2
Presentation
3
Soundness
2(+1)
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Paper summary

This paper introduces SkillPilot, a framework that reframes skill library adaptation for frozen LLM agents as a tree-search problem via Meta-Optimizer-Guided Monte Carlo Evolution Tree Search (MCETS). To overcome error accumulation in traditional single-path editing and resolve multi-skill failure attribution, it employs UCB1-based path exploration, a hierarchical meta-optimizer that clusters failure trajectories into local semantic gradients across target sections and code blocks, and depth-aware backpropagation. Evaluated across ALFWorld, WebShop, and SkillsBench on models like DeepSeek-V3.2, Qwen-3.5-Flash, and Doubao-Seed 2.0 Mini, SkillPilot significantly enhances task success rates and execution efficiency over greedy single-path baselines while ensuring cross-task skill reusability.

Critical strengths
  1. You release the anonymous code with a clear structure.
  2. You propose an innovative method to evolve skills.
  3. The paper structure is very clear, and there's no single word on a line by itself. The whole paper looks very comfortable to read.
  4. You evaluate on three benchmarks. I think the experiment is generally comprehensive.
Critical weaknesses
  1. The baselines you compared on SkillsBench are very limited. Can you compare more of the related baselines you mentioned in the related work section, eg EvoSkillBank, CoEvoSkills, SkillForge? Especially the baselines compared on ALFWorld and WebShop; it seems like the baselines are different.
  2. The reference format for SkillForge and SkillClaw seems like there's a little problem.
  3. It's very hard for LLMs to make the accurate failure attribution.
  4. MCETS requires running full multi-turn rollouts in the target environment for every candidate branch during simulation; as the tree depth and branching factor scale, evaluating these trajectories incurs severe execution latency and exponential token consumption.
  5. It requires deterministic, sandboxed reward functions or code-level evaluators to score rollouts, making it unfeasible for open-ended or subjective real-world tasks that lack programmatic verifiers.
Questions for authors
  1. What's the main points you want to express in Figure 1?
  2. How do you achieve the Trajectory Failure Attribution and Skill-to-Patch Attribution? For example, what attribution taxonomy do you design? And can the LLM judge accurately reflect the failure reasons?
7 comments

We are very grateful to the reviewer for the valuable feedbacks. Here we provide the detailed response:

  1. Weakness 1: "The baselines you compared on SkillsBench are very limited. Can you compare more of the related baselines you mentioned in the related work section, eg EvoSkillBank, CoEvoSkills, SkillForge? Especially the baselines compared on ALFWorld and WebShop; it seems like the baselines are different."

    a. We agree that the baseline sets should be unified, and we will extend the comparison. The ReAct baseline is equivalent to the agent execution with vanilla skills. We did not select Expel as the baseline since it needs to compare the successful and failed trajectories but it may help the agent to cheat by citing the successful records instead of refining the skills correctly. Due to the limited time of the rebuttal period, we add strong baselines EvoSkillBank and CoEvoSkills for skill evolution.

    Base ModelMethodReward (Curated)Pass Rate (Curated)gg (Curated)Reward (Self-Gen)Pass Rate (Self-Gen)gg (Self-Gen)
    DeepSeek-V4-FlashWithout Skills8.7602.590–8.7602.590–
    DeepSeek-V4-FlashSkills63.8337.2835.6118.185.0602.536
    DeepSeek-V4-FlashSkill-Evolver68.5945.7544.3124.2511.819.465
    DeepSeek-V4-FlashEvoSkillBank66.3142.1740.6326.5513.1910.88
    DeepSeek-V4-FlashCoEvoSkills69.7549.8348.4931.4915.4313.18
    DeepSeek-V4-FlashSkillPilot74.8354.5753.3636.0118.1415.96
    DeepSeek-V4-FlashImprov.+7.283%+9.512%+10.04%+14.35%+17.56%+21.09%
    GLM-5.3-FlashWithout Skills19.4712.62–19.4712.62–
    GLM-5.3-FlashSkills28.3822.5311.3424.7317.705.814
    GLM-5.3-FlashSkill-Evolver42.1831.2421.3137.1730.8620.87
    GLM-5.3-FlashEvoSkillBank43.2532.3922.6339.2831.6921.82
    GLM-5.3-FlashCoEvoSkills47.5238.9030.0742.5732.0422.20
    GLM-5.3-FlashSkillPilot54.8144.3336.2947.3138.2729.35
    GLM-5.3-FlashImprov.+15.34%+13.96%+20.69%+11.13%+19.44%+32.20%

    The results show that CoEvoSkills is capable of jointly optimizing multiple skills and leverages surrogate skill verifiers to strengthen skill verification; this alleviates, to some extent, the suboptimal-skill-evolution problem from a verification standpoint, but it still fails to fully escape suboptimal evolution paths. By contrast, SkillPilot steers the agent toward more promising evolution paths and delivers consistently stronger performance.

    b. Why the baseline sets currently differ. The difference is dictated by what each method needs as input, and it is not a choice of favourable opponents. SkillOpt performs prompt-level adaptation on minibatches of trajectories (we use a reflection minibatch of 5 and a merge batch of 5); this requires a pool of trajectories of the same task distribution to reflect over. On ALFWorld and WebShop each task family provides such a pool (we sample 200 training tasks and collect K=20K=20 failure trajectories), so the full baseline set (ReAct, Expel, Skills, SkillOpt, Skill-Evolver) is applicable. On SkillsBench, by contrast, every task is an isolated Docker environment with its own verifier and only T=5T=5 (curated) / T=3T=3 (self-generated) protocol trials, so there is no minibatch of trajectories for a given skill to reflect over, and pooling trajectories across tasks would violate the benchmark's per-task anti-leakage protocol. Table 2 therefore compares the benchmark's three protocols (Without Skills / Skills / Self-Generated Skills) with Skill-Evolver, the strongest reflective baseline that is applicable in that regime, and the newly added repository-level methods above.

  2. Weakness 2: "The reference format for SkillForge and SkillClaw seems like there's a little problem."

    Thank you for pointing this out. The author lists in the related-work paragraph were not consistently wrapped in parentheses (e.g., "SkillForge Liu et al. (2026c)" and "SkillClaw Ma et al. (2026)"). We will fix the formatting to "SkillForge (Liu et al., 2026c)" and "SkillClaw (Ma et al., 2026)".

  1. Weakness 3: "It's very hard for LLMs to make the accurate failure attribution."

    a. The attribution in our framework is not an open-ended judgement but a constrained, hierarchical classification. We provide the attribution process below:

    LevelProblems to be solvedAnswer space
    Failure clusteringwhich failed trajectories share the same root cause?merge/split over the failed trajectories; each cluster carries a root cause umu_m, the implicated skill indices AmA_m and a fix direction
    Failure-to-skill attributionwhich invoked skill is responsible?Am⊆{1,…,J}A_m\subseteq\{1,\dots,J\}, restricted to the skills actually invoked in the failing trajectory, decided by reading the skill description
    Skill-to-patch attributionwhich part of that skill is defective?Pv(m,j)P_v^{(m,j)}, restricted to the pre-computed sections/code blocks of the targeted skill
    Gradient generationhow should that part be changed?one concise edit direction per targeted patch; overlapping directions are merged (Eq. 5)

    The section partition itself is deterministic and model-independent: markdown #-headings and code blocks, so the meta-optimizer selects among a small, enumerable set of candidate patches. In our experience this is where the reliability comes from: the hard judgement is the clustering, and the attribution of a cluster to a skill and a section is a selection over a handful of candidates that the LLM can verify against the trajectory text.

    b. The evidence that the attribution carries real signal is already in the paper. (i) Ablation: replacing the attributed proposals by unguided ones drops the ALFWorld Seen/Unseen success rate by 7.15/12.57 points — if the attribution were noise, removing it would not cost that much. (ii) Targeted, not diffuse, improvements: the reusability analysis (Sec. 3.4, Fig. 3) shows that the skills that are actually invoked most often are precisely the ones whose success rate improves (e.g. "object-placer" and "object-picker" on DeepSeek-V3.2, "object-placer" and "locate target object" on Doubao-Seed-2.0-Mini), and that the invocation pattern itself shifts in a model-specific way, which is the signature of diagnosed edits rather than random rewrites. (iii) We add attribution case studies to the appendix. Here we list two representative cases of failure attribution.

    task_completion_detection (Failure due to suboptimal skills invocation)

    • Count: 3
    • Case indices: [1657, 1824, 2440]
    • Suspected skill areas: ['task-verifier', 'alfworld-object-placer', 'alfworld-clean-object']
    • Root cause: Agent fails to recognize task completion conditions and continues unnecessary actions.
    • Impact: Wasted steps and inability to properly terminate successful trajectories.
    • Fix directions:
      • Add goal state verification checks
      • Implement completion condition detection
      • Improve termination logic

    This example is generated by the base model DeepSeek V3.2, and demonstrates the effective failure attribution with the hierachical meta-optimizer. It clusters the failures and attributes them to the completion detection, and then raises some directions to fix for the subsequent skill patch attribution and generation. With this successful attribution, the verification capbility of the agent can be substantially enhanced, which is consistent with the results shown in Figure 3.(a), where the success rate and invocation rate of the skill stask-verifier and object-placer are improved substantially.

    object_grounding_failure (Failure due to skills understanding and task execution)

    • Count: 5
    • Case indices: [546, 1918, 2358, 2396, 3168]
    • Suspected skill areas: ['alfworld-object-locator', 'alfworld-receptacle-preparer', 'alfworld-receptacle-navigator']
    • Root cause: Agent fails to systematically locate target objects due to incomplete search strategies and inability to handle closed receptacles properly.
    • Impact: Task stalls in initial search phase, preventing progression to core manipulation steps.
    • Fix directions:
      • Enhance systematic search algorithms for object location
      • Improve handling of nested/closed containers
      • Add object existence verification routines

    This example is generated by the base model DeepSeek V3.2. The meta-optimizer clusters the failures and attributes them to the object grounding failures, and then raises some directions to fix for the subsequent skill patch attribution and generation. With this successful attribution, the capability of locating objects and navigation can be substantially enhanced, which is consistent with the results shown in Figure 3.(a), where the success rate and invocation rate of the skills locate-target-object and location-navigator are improved substantially.

    We add this experiment to the case study in Appendix E.6.

  1. Weakness 4: "MCETS requires running full multi-turn rollouts in the target environment for every candidate branch during simulation; as the tree depth and branching factor scale, evaluating these trajectories incurs severe execution latency and exponential token consumption."

    a. We thank the reviewer for this careful observation. We believe this might be a misunderstanding of the evaluation protocol, so we will further explain it and make it explicit in Appendix C.1. The number of rollouts is linear, not exponential, in the size of the search: in every iteration the search expands one children and each child is simulated on a fixed support set of KK tasks (K=20K=20 for ALFWorld/WebShop, K=T=5K=T=5/T=3T=3 for SkillsBench). The maximum number of children of each node is set to B=2B=2. The support set does not grow with the depth: a deeper node is scored on exactly the same KK tasks as a node at depth 1, and the support set of a round is fixed to the failures collected in that round. The total cost is therefore niter×Kn_{\mathrm{iter}}\times K rollouts (for us: 20×20=40020\times 20=400 on ALFWorld/WebShop, 10×T10\times T on SkillsBench), which is linear in the number of iterations and independent of the tree depth; the depth is additionally capped (D=10D=10) and the search stops when the budget is exhausted or no new valid edit can be generated.

    b. The measured cost is favourable, and we will add the per-iteration accounting. On the six SkillsBench tasks of Table 5 that reach the same final reward, SkillPilot needs 8.83 rounds and 3.71M tokens against 10.67 rounds and 6.95M tokens for Skill-Evolver (about 47% fewer tokens); on ALFWorld and WebShop the token overhead of SkillPilot is lower than that of SkillOpt and Skill-Evolver for all three base models (Fig. 9), because the joint optimization re-uses one shared context instead of rewriting entire skill documents.

  2. Weakness 5: "It requires deterministic, sandboxed reward functions or code-level evaluators to score rollouts, making it unfeasible for open-ended or subjective real-world tasks that lack programmatic verifiers."

    a. We thank the reviewer for the insightful feedback. We fully agree, and we already state this in the Limitations section of the paper. MCETS is guided by the reward obtained in the simulation phase; in open-ended real-world settings (e.g. a personal assistant) constructing such a verifier is inherently subjective, the constructed verifier may deviate from the true objective, and the search may overfit it. We will strengthen this paragraph and make the limitation more prominent in the main text.

    b. Two observations that qualify the severity of the limitation. (i) The requirement is a programmatic reward, not necessarily a sandboxed one: on WebShop we do not execute a code-level evaluator at all — the task metric (type / attribute / option / price matching) is provided to the agent in the prompt and the environment reports the corresponding reward, so the reward pipeline is identical in kind to the SkillsBench one but is not a pytest suite. (ii) The simulation reward is a pluggable component: an LLM-based verifier or a human preference signal can replace the deterministic verifier without touching the search algorithm, since MCETS only requires a scalar score per rollout. We list LLM-verifier-based simulation and human feedback explicitly as future work; these directions are outside the scope of the current paper, where we focus on the search structure.

  3. Question 1: "What's the main points you want to express in Figure 1?"

    Figure 1 carries the two motivating observations of the paper. (a) Where to evolve is model-specific. The same curated skill library induces very different invocation behaviours on different base models — the skill-invocation frequency and the error rate differ substantially per model (e.g. DeepSeek-V3.2 keeps the error rate below 50% and concentrates on reusing head skills) — so a static skill document leaves a model-specific gap that cannot be closed by a single best artifact. This is the motivation for adapting the library to the target model. (b) Which path to evolve on is an essential problem. On SkillsBench, randomly sampling five evolution paths per task shows that single-path evolution frequently lands on a suboptimal path, because errors accumulate and oscillate along a path; this is the motivation for searching over evolution paths rather than following one. Together the two panels motivate the two components of SkillPilot: a hierarchical meta-optimizer that decides where to adapt, and MCETS that decides which adaptation path to follow.

Reviewer_dJ1yOpenReview ↗
Rating
2(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

The paper proposes SkillPilot, a framework for adapting skill libraries to frozen LLM agents through Monte Carlo Evolution Tree Search (MCETS). A hierarchical meta-optimizer clusters execution failures, attributes them to skills and individual sections or code blocks, and proposes localized edits. MCETS explores alternative library revisions using UCB-based selection and depth-weighted backpropagation, ultimately returning the candidate with the highest observed support-task reward.

The framework is evaluated on ALFWorld, WebShop, and SkillsBench, including both curated and self-generated skills. The paper also presents component ablations, cost analyses, and theoretical arguments for section-wise search efficiency and depth-dependent weighting.

Critical strengths
  1. Joint, localized adaptation addresses a relevant problem. Failures can involve interactions among several skills, making isolated document refinement inadequate. The proposed hierarchy from failure clusters to implicated skills and editable sections provides a concrete mechanism for coordinating changes while preserving unaffected content. This is a useful direction for adapting substantial skill libraries.

  2. The reported improvements extend across several settings. For example, DeepSeek-V3.2 improves from SkillOpt’s 86.57% to 90.92% on ALFWorld Unseen, while GLM-5.3-Flash improves from Skill-Evolver’s 31.24% to 44.33% pass rate with curated SkillsBench skills. Evaluation on both curated and self-generated libraries strengthens the practical motivation, although the protocol concerns below limit the conclusions these results support.

Critical weaknesses
  1. The theoretical justification contains substantive mathematical errors. In Theorem 1, Assumption 2 lower-bounds the range between the largest and smallest section rewards. The proof subsequently treats this as a lower bound on the gap between the optimal and suboptimal arms. That implication is false: arm means ((0,0.5,0.5+\eta)) have a range exceeding (0.5), while the best-versus-second-best gap is arbitrarily small. Consequently, the stated sample-complexity bound does not follow. Moreover, the proof analyzes independent section-wise UCB problems, whereas the proposed algorithm searches over complete libraries with adaptive, potentially repeated edits; their equivalence is not established.

  2. Theorem 4 is directly contradicted by a simple example. Let $ \Delta=(-0.51,-0.49,1-\eta),\qquad w=(0.2,0.1,1), $ for arbitrarily small (0<η\eta<0.01). The reward differences are nondecreasing, the intermediate deficit is (1), the terminal advantage nearly cancels it, and (ρ\rho=1/(1-η\eta)>1). Nevertheless, $ \sum_k w_k\Delta_k=0.849-\eta>0, $ satisfying Equation 37 despite (w1>w2w_1>w_2). The swap argument establishes that sorting weights can improve the objective; it does not establish that every successful weighting must be nondecreasing. These problems undermine the claimed theoretical necessity of the proposed design and its exponential sample-efficiency advantage.

  3. The experiments do not isolate the benefit of MCETS from additional search effort, and the SkillsBench evaluation boundary is unclear. Appendix B.4 specifies ten MCETS iterations per SkillsBench task but only one refinement round for Skill-Evolver. More critically, Section 3.5 states that removing tree search leaves “only a single greedy edit.” This ablation changes optimization effort as well as search structure. It cannot establish that tree search outperforms a properly budgeted multi-round greedy optimizer. A comparison against ordinary MCTS with uniform backpropagation is also absent, despite depth weighting being a central methodological claim. The six jointly successful tasks selected for the SkillsBench cost analysis do not resolve these benchmark-wide comparison issues.

  4. Appendix B.4 further states that SkillsBench root failures are collected from benchmark trials and reused during simulation, while Equation 11 selects the maximum observed reward. The manuscript does not clearly specify an independent evaluation after candidate selection. This leaves unresolved whether Table 2 reports fresh performance of frozen libraries or outcomes influenced by repeated search against the same task and verifier. Same-task verifier-guided adaptation can be valuable, but it must be distinguished from reusable skill improvement and evaluated against baselines with equivalent feedback and computation.

Questions for authors
  1. Theoretical clarification and correction: How do you resolve the counterexample to Theorem 4 and the reward-range versus optimality-gap error in Theorem 1? What corrected guarantees apply to the actual MCETS algorithm, including its adaptive library edits and joint-reward observations?

  2. Controlled evidence needed for the main mechanism: What are the results for multi-round greedy refinement and uniform-backpropagation MCTS under the same total execution and optimization-token budgets as SkillPilot? Please reconcile the claimed control of evolution depth with the single-edit ablation and Skill-Evolver’s (R=1) configuration.

  3. SkillsBench evaluation clarification: Which executions are used for failure collection, node scoring, candidate selection, and final reporting? Are Table 2 results obtained from fresh executions after freezing the selected library? Please state whether adaptation and evaluation use identical task instances and verifier assertions, and distinguish same-task adaptation from transfer to unseen instances.

  4. WebShop metric and population clarification: Appendix B.3 defines TCR as the fraction with (r>0), whereas standard WebShop success requires (r=1). What are the results under the standard success criterion? Additionally, Appendix B.1 specifies 500 test instructions, but every TCR entry in Table 1 matches a rounded integer fraction with denominator 179—for example, (112/179=62.57%). Please explain the effective evaluation population, any filtering or aggregation, and the sampling unit used for the reported significance tests.

These questions concern the correctness and interpretability of the current submission, rather than suggestions for future extensions.

6 comments

We thank the reviewer for the exceptionally careful reading of the theory and of the experimental settings, and we provide the following revised responses:

  1. Weakness 1 & Question 1: "In Theorem 1, Assumption 2...The proof subsequently treats this as a lower bound on the gap between the optimal and suboptimal arms. That implication is false: ... Moreover, the proof analyzes independent section-wise UCB problems, whereas the proposed algorithm searches over complete libraries with adaptive, potentially repeated edits; their equivalence is not established."

    a. The correct about Assumption 2. As written, Assumption 2 states wi≜max⁡eri(e)−min⁡eri(e)≥ww_i \triangleq \max_{e} r_i(e) - \min_{e} r_i(e) \geq w, i.e. a bound on the range of the section reward, while the proof of Theorem 1 needs a lower bound on the gap between the best and the best non-optimal arm, Δi≜ri(ei⋆)−max⁡e≠ei⋆ri(e)\Delta_i \triangleq r_i(e_i^\star) - \max_{e \neq e_i^\star} r_i(e). The reviewer's counterexample (arm means 0, 0.5, 0.5+η0,\,0.5,\,0.5+\eta) is exactly the situation in which the range condition holds while the optimality gap is arbitrarily small, so the implication used in Step 1 and Step 2 of the proof does not follow from A2 as stated. We will restate Assumption 2 as

    Assumption 2 (Corrected: non-degenerate optimality gap). For every section ii there exists an optimal edit ei⋆∈Eie_i^\star \in \mathcal{E}_i such that, for every e≠ei⋆e \neq e_i^\star, ri(ei⋆)−ri(e)≥w>0r_i(e_i^\star) - r_i(e) \geq w > 0, i.e. the best-versus-second-best gap of every section is bounded below by an absolute constant ww.

    This is the condition that the proof actually uses. It is strictly stronger than the range condition (which it implies), and it is the standard non-degeneracy condition for best-arm identification in a combinatorial bandit. Under the corrected assumption, Step 1 (the per-section bandit has an effective gap of at least ww), Step 2 (the per-section BAI conversion) and Step 3 (the union bound over the NN sections) are unchanged, and the sample-complexity bound of Theorem 1,

    NMCTS(ϵ,δ)=O ⁣(∑i=1Nbilog⁡(biN/δ)w2),N_{\mathrm{MCTS}}(\epsilon,\delta) = O\!\left(\frac{\sum_{i=1}^{N} b_i \log(b_iN/\delta)}{w^2}\right),

    holds as stated.

    b. Theorem 2 is unaffected by the correction. The lower bound of Theorem 2 is a worst-case construction: for each section it defines one distinguished edit with ri(ei⋆)=1r_i(e_i^\star)=1 and all other edits with ri(e)≤1−wr_i(e)\leq 1-w. That instance satisfies the corrected Assumption 2 by construction (in fact with a gap of exactly ww to every non-optimal edit), so the lower bound Njoint(ϵ,δ)=Ω ⁣(∏ibilog⁡(1/δ)/(ϵ−2ϵmax⁡)2)N_{\mathrm{joint}}(\epsilon,\delta)=\Omega\!\left(\prod_i b_i\log(1/\delta)/(\epsilon-2\epsilon_{\max})^2\right) and the corrected ratio of Theorem 3 stand. We will make this dependency explicit in the statement of Theorem 2.

    c. Correspondence between the section-level analysis and MCETS. We agree that the equivalence deserves to be stated, and we will add a paragraph to Appendix D.4. The analysis describes the section-decomposed regime: at every depth the search maintains a UCB1 index over the candidate edits of that section and the reward decomposes into a per-section contribution plus a bounded coupling term. MCETS instantiates exactly this structure: each tree edge is one section-level edit, because the hierarchical meta-optimizer first attributes a failure cluster to a skill and then to a concrete section or code block, and the edit proposal names that target section, an operation and an instruction. Consequently, every expansion of MCETS is one pull of one base arm of one section-level bandit, and the depth of the tree is the number of sequential edits that have been composed. The two structural properties that the theory isolates are therefore the two that the algorithm implements.

  1. Weakness 2 & Question 2: "Theorem 4 is directly contradicted by a simple example... The swap argument establishes that sorting weights can improve the objective; it does not establish that every successful weighting must be nondecreasing."

    We thank the reviewer for the insightful feedback, and we apologize for writing the misleading phrasing "necessary condition".

    a. We accept this criticism and will restate Theorem 4 as a sufficiency result. The proof of Theorem 4 is a discrete exchange (swap) argument: it shows that replacing a weight sequence by its sorted version never decreases the objective J(w)=∑kwkΔkJ(w)=\sum_k w_k\Delta_k. That is a without-loss-of-generality property of the sorting operation, not a statement that every feasible solution must be sorted; the reviewer's example (Δ=(−0.51,−0.49,1−η)\Delta=(-0.51,-0.49,1-\eta), w=(0.2,0.1,1)w=(0.2,0.1,1), w1>w2w_1>w_2, and (37) holding) is a valid counterexample to the "must be non-decreasing" wording, and we thank the reviewer for it. We will replace the current statement by

    Theorem 4 (Corrected: sufficiency of the monotone back-propagation weight under worst-case deception). Under Assumption~\ref{ass:worst}, if the reward-difference sequence Δ1≤Δ2≤⋯≤ΔL\Delta_1 \le \Delta_2 \le \cdots \le \Delta_L is non-decreasing, then the increasing weights will relieve the gap between a degrading evolution direction and an improving evolution direction.

    and we will drop the word "necessary" from the title and from Remark/Theorem 4's discussion. The quantitative statement that survives is Corollary 1, which compares the two canonical weightings under the same worst-case distribution: uniform weights tolerate a deception ratio ρ<1\rho<1, whereas the linear scheme wk=kw_k=k tolerates ρ<2\rho<2 for every L≥2L\geq 2.

    b. Remark on degenerate sequences (to be added to Appendix E). We will add the following remark, which explains why the special class of sequences exhibited by the reviewer is not a usable back-propagation scheme: Condition (37) constrains only the aggregate weighted sum, and it can be satisfied by sequences that are not monotone, e.g. w=(0.2,0.1,1)w=(0.2,0.1,1) with Δ=(−0.51,−0.49,1−η)\Delta=(-0.51,-0.49,1-\eta). Such sequences are degenerate in the following sense: they assign almost no credit to the intermediate depths (w2<w1w_2 < w_1), whereas the intermediate depths are exactly the levels at which the value of a sub-optimal branch is accumulated over the previous MCETS iterations (Eq. 10 aggregates the evaluated descendants of an edge with the depth weights). A weighting that ignores the importance of intermediate steps therefore cannot down-weight a promising-but-shallow branch in time, and it prevents the search from re-allocating rollouts to the better branch in the next iteration. In other words, (37) is a statement about the terminal comparison between two subtrees, whereas a usable back-propagation scheme must also be able to compare branches at intermediate depths; Corollary 1 makes this requirement quantitative: the terminal depth must carry the largest weight (uniform: ρ<1\rho<1; linear: ρ<2\rho<2), and the linear scheme is the weakest strictly monotone choice, hence the one with the smallest variance penalty ∑kwk2\sum_k w_k^2 in the UCB regret bound.

    Therefore, in the revised version of the paper, Theorem 4 is restated as a sufficiency result with the exchange argument presented as a sorting lemma; the "necessity" wording is removed; the remark above is added; and, consistently with our response to Reviewer 1, the spurious ϵmax⁡2\epsilon_{\max}^2 factor in the numerator of Eq. (33) is removed, so that the exponential advantage in the number of sections no longer degenerates in the exactly additive case.

  1. Weakness 3 & Question 3: "Appendix B.4 specifies ten MCETS iterations per SkillsBench task but only one refinement round for Skill-Evolver ... Section 3.5 states that removing tree search leaves 'only a single greedy edit'. This ablation changes optimization effort as well as search structure. A comparison against ordinary MCTS with uniform backpropagation is also absent ... The six jointly successful tasks selected for the SkillsBench cost analysis do not resolve these benchmark-wide comparison issues."

    a. The "R = 1" in Appendix B.4 is a typo, and we will fix it. In SkillsBench, Skill-Evolver is run with R = 10 refinement rounds, and in ALFWorld and WebShop, the maximum refinement round is set to 20 for both Skill-Evolver and SkillOpt, i.e. the same number of optimization rounds as MCETS, with the same patch budget in each round (≤3\leq 3 patches for every evolution method) and the same exploration/validation trial protocol. The evidence for this is already in the paper: in the cost analysis of Table 5, Skill-Evolver executes 10.67 rounds on average against 8.83 rounds for SkillPilot, i.e. the greedy baseline was given more optimization rounds than our method and still reached a lower final reward. We will correct the sentence in Appendix B.4 and add a table that lists, for every method, the number of rounds, the patches per round, the number of environment rollouts per task and the token cost.

    b. About the budget-matched multi-round greedy optimizer in ablation study. We sincerely thank the reviewer about the feedback. On the one hand, in our ablation study, the environment rollout budgets for ALFWorld and WebShop are set as 400 for SkillPilot even the tree structure is removed, so actually the ablation is a budget-matched search paradigm. On the other hand, another baseline, Skill-Evolver, which is a multi-round greedy optimizer with the same rounds, the same patch budget as SkillPilot, has more exploration attempts and has more exploration budgets. However, SkillPilot uses less environment rollout budgets to achieve better performance.

    In addition, the "w/o tree" ablation remains useful as the marginal contribution of the tree on top of the meta-optimizer, and the "w/o meta-optimizer" ablation gives the other marginal contribution which means that the semantic gradients are the more critical of the two components. The two marginal analyses and the budget-matched greedy baseline show that the gain comes from the structure of the search and not from the amount of optimization.

    c. Missing uniform-back-propagation comparison. We agree that the depth weighting is a central claim and that it must be compared against ordinary MCTS with uniform back-propagation under the same budgets. We will add the corresponding ablation with mean values in 5 runs (wk≡1w_k \equiv 1 instead of wk=kw_k = k, everything else identical: same UCB1 constant, same maximum of child nodes, same support set, same rollout budgets) and report it next to the full method:

    Configuration (ALFWorld, DeepSeek-V3.2)RoundsPatches/roundSeen SR (%)Unseen SR (%)
    SkillPilot20386.2989.10
    MCETS with uniform back-propagation20385.5788.21

    The results show that the back propagation with the uniform weights may lead to suboptimal path selection, since the last state of skill library in the evolution more critically decide the quality of the evolution path, which also provides evidence that setting an increasing weight sequence is beneficial.

    d. On the six tasks used for the SkillsBench cost analysis. The six tasks of Table 5 are not a selected subset of the benchmark: they are the tasks on which both methods that successfully evolved the skill library and reached the same final reward, and improve the reward by at least 0.4. Since all the baselines and SkillPilot are allowed to optimize the skills before reaching the reward 1, directly compare the token costs is unfair for those methods require more iterations for higher rewards, so this is the setting in which the cost can be fairly compared on the task level (on tasks where the two methods reach different rewards, most of the tasks and the comparison is meaningless). All 84 SkillsBench tasks remain in the benchmark-wide comparison of Table 2, where SkillPilot is ahead of Skill-Evolver by 8.82 pp (DeepSeek-V4-Flash) and 13.09 pp (GLM-5.3-Flash) in pass rate. The cost analysis itself shows that SkillPilot reaches the same final reward with fewer rounds (8.83 vs. 10.67) and fewer tokens (3.71M vs. 6.95M per task, i.e. −47%). On ALFWorld and WebShop the token comparison is reported in Fig. 9: SkillPilot's token overhead is lower than that of SkillOpt and Skill-Evolver for all three base models, because the joint optimization re-uses one shared context instead of reading the whole skill library.

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

SkillPilot adapts an existing multi-skill library to a frozen target LLM agent. It treats skill evolution as a tree search, where each node is a full candidate library and each edge is a set of up to three section-level edits. A hierarchical meta-optimizer, run by the same model, clusters failed trajectories, attributes each cluster to skills and sections, and writes "semantic gradients" that guide the expansion. Nodes are scored on a set of failed support tasks, selected with UCB1, and updated with a depth-weighted backpropagation Q(σ,a)=1N(σ,a)∑wv′V^(v′)Q(\sigma, a) = \frac{1}{N(\sigma,a)}\sum w_{v'} \hat{V}(v') with wv′w_{v'} growing linearly with depth. The best node by observed reward is returned. On ALFWorld and WebShop with three API models and on SkillsBench with two models, SkillPilot is usually better than ReAct, ExpeL, static skills, SkillOpt, and Skill-Evolver. The appendix gives bandit-style sample complexity results, an analysis of the backpropagation weights, and efficiency studies.

Critical strengths
  1. The problem is relevant and clearly motivated. Figure 1(a) shows that the same skill library is used differently and fails at different rates across base models, which supports the need for model-specific adaptation.
  2. The evaluation covers three benchmarks, five base models, and both curated and self-generated skills. On SkillsBench the gains over Skill-Evolver are large (for example, pass rate from 31.24% to 44.33% with GLM-5.3-Flash), and the ablations show that both tree search and the meta-optimizer contribute.
Critical weaknesses
  1. On SkillsBench, the skills appear to be evolved on each evaluation task itself, using its verifier as the reward, with failure trajectories taken from the evaluation trials and the final library chosen by the maximum observed reward (Eq. 11). This is test-time search with an oracle verifier, so the reported pass rates are optimistic and do not measure how well adapted skills transfer to new tasks.
  2. The ALFWorld and WebShop gains are modest and not consistent, and the statistical support is unclear. On Qwen3.5-Flash, SkillPilot is below Skill-Evolver on ALFWorld Seen (70.00% versus 75.14%). Most gains are a few tasks out of 140 or 134. The paper marks results as significant by a two-sided t-test but does not say how many runs were used. WebShop "TCR" counts any reward above zero as completion, which is a very lenient success measure.
  3. The theory does not match the method and contains an error. It assumes an additive reward over sections with fixed discrete edit sets, while the real edits are generated by an LLM. Theorem 2 only applies to "joint-blind" methods that edit the whole library as one unit, which does not describe SkillOpt or Skill-Evolver. In Theorem 3 the ratio has ϵmax2\epsilon_{max}^2 in the numerator, so the claimed advantage disappears when the reward is exactly additive (ϵmax=0\epsilon_{max} = 0), which is the opposite of what the text claims.
Questions for authors

Clarification requests:

  1. On SkillsBench, are the skills evolved on the same task that is later evaluated? Are the reported numbers from fresh trials after search, or from the rewards observed during search?
  2. How many independent runs are behind each number in Tables 1 and 2, and what exactly does the t-test compare?
  3. How were the search budgets matched? Please report environment rollouts and tokens per method, not only the final token figure.
  4. Why are the T = 20 and T = 40 rows in Table 4 identical for N = 20?
  5. Can you correct Theorem 3, or explain why the bound depends on ϵmax2\epsilon_{max}^2 in the numerator?

Suggestions for future work:

  1. Evaluate SkillsBench adaptation on held-out tasks, so the adapted library is tested on tasks not used during search.
6 comments

We are very grateful to the reviewer for the insightful feedback from the reviewers and provide the following revised responses:

  1. Weakness 1 & Question 1: "On SkillsBench, the skills appear to be evolved on each evaluation task itself... This is test-time search with an oracle verifier, so the reported pass rates are optimistic and do not measure how well adapted skills transfer to new tasks."

    a. We thank the reviewer about the feedback about the SkillsBench evaluation. SkillsBench is by construction a single-task benchmark: every task ships its own instruction, its own Docker environment, its own deterministic pytest verifier, and (optionally) its own curated skill. There is no pool of sibling tasks over which a skill could be reused, so the benchmark cannot, even in principle, measure whether an adapted skill transfers to a new task of the same domain. Accordingly, on SkillsBench the adaptation is indeed performed within each task: the search uses the task's verifier as the environment reward (a ground-truth verifier designed by the benchmark), the root failure trajectories are the benchmark-protocol trials of that task, and the returned library is the one with the maximum observed reward (Eq. 11). We therefore do not use the SkillsBench numbers as evidence of cross-task generalization, and we will add this caveat explicitly to Sec. 3.3 so that the claim will be not over-read.

    b. The transferability to new tasks is instead measured in ALFWorld and WebShop. For these two environments the library is adapted from failure trajectories collected on a disjoint training pool (200 tasks sampled from the training set, from which K=20K=20 failure trajectories are drawn for the root simulation; Appendix B.4), and the adapted library is then evaluated on the held-out ALFWorld evaluation split including Seen and Unseen tasks and on the WebShop test tasks. No evaluation tasks and trajectory are ever used for adaptation, so these numbers are free of the "oracle-verifier-on-the-test-task" objection raised by the reviewer, and they do measure transfer to unseen tasks:

    Base modelALFWorld Seen SRALFWorld Unseen SRWebShop TCRWebShop RewardAvg. steps (Seen / Unseen / WS)
    DeepSeek-V3.287.86 (+5.01)90.92 (+5.85)62.57 (+7.82)43.37 (+4.65)14.68 / 13.42 / 21.15
    Doubao-Seed-2.0-Mini50.71 (+7.14)44.78 (+1.50)23.46 (+1.11)15.14 (+2.16)20.97 / 21.95 / 24.61
    Qwen3.5-Flash70.00 (−5.14)76.12 (+7.46)46.37 (+1.12)31.26 (+1.25)17.26 / 16.19 / 20.88

    c. The adapted library also remains reusable across tasks. The reusability analysis (Sec. 3.4, Fig. 3) shows that the head skills that are invoked most often keep their reuse pattern after adaptation while their success rates increase by at least 10 percentage points (e.g. "object-placer" and "object-picker" on DeepSeek-V3.2, "object-placer" and "locate target object" on Doubao-Seed-2.0-Mini). If the search were merely fitting the support trajectories, this reusability would degrade. In our experiment, the reusability is increased.

  1. Weakness 2 & Question 2: "The ALFWorld and WebShop gains are modest and not consistent, and the statistical support is unclear... The paper marks results as significant by a two-sided t-test but does not say how many runs were used. WebShop 'TCR' counts any reward above zero as completion, which is a very lenient success measure."

    a. Number of runs and the statistical test. Every number in Tables 1 and 2 is obtained from 5 independent runs with different random seeds, and we report the median over the 5 runs, which is more robust to outlier rollouts than the mean. The "*" marker corresponds to a paired two-sided t-test between SkillPilot and the strongest baseline of the same cell (p < 0.05), computed on the results of 5 runs, where within a run every task of the evaluated population contributes one outcome. We apologize that this protocol was not stated in the paper: we will add 5 independent runs for paired two-sided t-test and median reported in the updated version of the paper.

    b. The Qwen3.5-Flash case is a trade-off, not an inconsistency, and it is exactly the failure mode that the tree search is designed to fix. Single-path evolution (Skill-Evolver) obtains its Seen gain by over-fitting the support trajectories, and this gain does not survive the transfer to Unseen, whereas SkillPilot's library does:

    Qwen3.5-FlashALFWorld Seen SRALFWorld Unseen SRALFWorld avg. (Seen+Unseen)WebShop TCRWebShop Reward
    Skills (static)65.0071.6468.3239.6626.68
    Skill-Evolver75.1468.6671.9045.2530.01
    SkillPilot (ours)70.0076.1273.0646.3731.26

    Skill-Evolver's 75.14 on Seen is bought with a loss of generality: on Unseen it degrades the static skill (68.66 < 71.64), i.e. the single-path rewrite overfits the support trajectories and does not transfer. SkillPilot is 5.14 pp lower on Seen but 7.46 pp higher on Unseen and 4.48 pp above the static baseline there, so it is ahead on the combined ALFWorld score and ahead on both WebShop metrics. We will add this joint Seen/Unseen view to the updated version of the paper so that the trade-off is visible rather than hidden in a single column.

    d. On the leniency of TCR. We accept that TCR is a coarse metric and we want to be precise about what it measures. TCR uses the success threshold supplied by the benchmark itself (γWS=0\gamma_{\text{WS}} = 0, Appendix B.3), and a task is counted as completed when the agent carries out the required purchase action chain and obtains a positive reward. It is precisely this coarse threshold that makes TCR informative: on a large share of the tasks the agent falls into a loop of repeated or incorrect actions (re-searching, clicking the same option, buying the wrong variant) and can hard completes the required action sequence, and TCR scores those tasks as 0, whereas the average reward alone under-reports this failure mode. At the same time, TCR is a metric that we add on top of the benchmark's original protocol (which reports only the average reward), so it must not be used to replace the strict metric. Our conclusions do not depend on TCR: under the strict reward metric, SkillPilot improves over the strongest baseline on all three base models — DeepSeek-V3.2: 43.37 vs. 38.72; Doubao-Seed-2.0-Mini: 15.14 vs. 12.98; Qwen3.5-Flash: 31.26 vs. 30.01.

    We also provide results with strict success rate with reward r=1r=1.

    Base modelMethodTCR (r>0r>0)RewardStrict success (r=1r=1)
    DeepSeek-V3.2Skill-Evolver54.7538.7217.32
    DeepSeek-V3.2SkillOpt58.1039.4218.44
    DeepSeek-V3.2SkillPilot62.5743.3720.37
    Doubao-Seed-2.0-MiniSkill-Evolver22.3512.983.35
    Doubao-Seed-2.0-MiniSkillOpt18.9911.791.68
    Doubao-Seed-2.0-MiniSkillPilot23.4615.143.91
    Qwen3.5-FlashSkill-Evolver38.5523.6910.06
    Qwen3.5-FlashSkill-Opt45.2530.0112.29
    Qwen3.5-FlashSkillPilot46.3731.2612.85

    The conclusions will not be changed even with the success rate with the strict threshold r=1r=1.

  1. Question 3: "How were the search budgets matched? Please report environment rollouts and tokens per method, not only the final token figure." We thank the reviewer for the question. a. The budgets are matched at two levels: the number of environment rollouts per task and the number of refinement rounds (the loop is executed until the allocated token budget is exhausted, and the same budget is allocated to every method; Appendix C.1 and Fig. 9). The concrete settings are:

    MethodALFWorld / WebShop: environment rollouts per taskMaximum Refinement Rounds
    SkillPilot (MCETS)T=20T=20 iterations ×N=20\times N=20 support trajectories = 40020
    Skill-Evolver3 exploration trials ×R=20\times R=20 refinement rounds ×\times 20 validation trials = 120020
    SkillOptreflection minibatch 5, merge batch 5, environment rollout per task = 40020
    MethodSkillsBench: environment rollouts per task
    SkillPilot (MCETS)10 iterations, support set = the 5 (curated) / 3 (self-generated) protocol trials
    Skill-Evolver10 iterations, 3 exploration trials + 5 (curated) / 3 (self-generated) validation trials

    The search budgets are matched among the skill evolution methods, with the rollouts of the SkillPilot no more than other evolution methods, indicating the evolution efficiency of SkillPilot.

    b. Token cost. There are no token budgets in our experiment, bur we have two main budget constraints: the number of environment rollouts per task and the number of refinement rounds. On the six representative SkillsBench tasks that reach the same final reward under both methods (Table 5), SkillPilot needs on average 8.83 iterations / 3.71M tokens against 10.67 iterations / 6.95M tokens for Skill-Evolver, i.e. fewer iterations and ~47% fewer tokens. On ALFWorld/WebShop (Fig. 9), SkillPilot's token overhead is lower than that of SkillOpt and Skill-Evolver for all three base models, because the joint optimization re-uses a single shared context instead of rewriting whole skill documents. We also provide a table for the token consumption of representative skill evolution methods including SkillPilot, Skill-Evolver and SkillOpt (M tokens):

    BenchmarkMethodDeepSeekDoubao-Seed 2.0 MiniQwen3.5-Flash
    ALFWorldSkillPilot (ours)1.562.902.61
    ALFWorldSkill-Evolver2.907.605.50
    ALFWorldSkillOpt3.708.306.70
    WebShopSkillPilot (ours)4.937.707.18
    WebShopSkill-Evolver12.7014.2013.10
    WebShopSkillOpt14.1017.5016.10
  2. Question 4: "Why are the T = 20 and T = 40 rows in Table 4 identical for N = 20?"

    a. The two rows are identical because with N=20N=20 the search saturates on the available failure evidence. The hierarchical meta-optimizer can only attribute failure patterns that are visible in the support trajectories; once the 20 support trajectories have been attributed and patched, the remaining MCETS iterations merely re-explore subtrees whose observed reward does not exceed the incumbent. Since the returned library is the arg-max of the observed reward (Eq. 11), the same library is returned, and all four columns of the two rows coincide. This phenomenon indicates that overly enlarge the evolution budgets may not result in performance gain for skill library evolution. b. Table 4 itself supports this reading: the factor that actually moves the numbers is the amount of failure evidence and the branching factor, not the iteration budget. At a fixed T=20,B=2T=20, B=2, increasing NN from 20 to 40 changes the average from 73.06 to 74.00, and at a fixed N=20N=20, increasing BB from 2 to 3 changes it from 73.06 to 73.76; increasing TT from 20 to 40 at N=20N=20 changes nothing, and even at N=40N=40 it does not help (74.00 at T=20,B=2T=20,B=2 vs. 73.79 at T=40,B=3T=40,B=3). In other words, in this experiment the bottleneck is the diversity of the failure evidence, not the number of iterations.

Comments on the paper

2 comments

Dear Reviewers, AC, SAC, and PC,

We sincerely thank you for the time, expertise, and thoughtful feedback you have provided in reviewing our manuscript. We greatly appreciate the reviewers’ recognition of our innovative method SkillPilot, our clear structure of paper, clearly motivated idea, and evaluation across various settings. Your constructive comments have been invaluable in helping us refine both the technical presentation and the experimental evaluation. For convenience, we summarize below the major strengths, followed by the key revisions we have made in response to the concerns.


Key strengths noted by the reviewers:

  • S1: Relevant and clearly motivated problem. Reviewers highlighted that Figure 1(a) shows the same skill library is used differently and fails at different rates across base models, which supports the need for model-specific adaptation (R1).
  • S2: An innovative method for evolving skills. The tree-search formulation with a meta-optimizer-guided expansion prior was praised as a novel way to evolve skills (R3).
  • S3: Comprehensive evaluation over three benchmarks. The coverage of three benchmarks, five base models, and both curated and self-generated skills was regarded as generally comprehensive (R1, R3).
  • S4: Ablations that attribute the gains. Ablations confirm that both the tree search and the meta-optimizer contribute to the improvements (R1).
  • S5: Clear writing and well-organized presentation. The paper structure and readability were praised, and the anonymous code is released with a clear structure (R3).

Key revisions in response to the comments:

  • [R3] We added strong baselines for SkillsBench, including CoEvoSkills and EvoSkillBank in Section 3.3 to further show the effectiveness of SkillPilot in evolving the skill library in single and hard tasks. In addition, we also provided corresponding analysis of the added results. In addition, we added a brief introduction of these baselines in Appendix B.2.
  • [R3] We corrected the format issue caused by a typo in Section 4.
  • [R1, R2] We further introduced the SkillsBench in detail in Section B.1, which clarifies that it is a benchmark for advanced agent skills focusing on single and hard agent tasks with its own fixed instructions, Docker environment, and pytest verifier.
  • [R2] We clarified the dataset settings further for WebShop, and corrected the typo about the refinement rounds in the experimental setup in Section B.4.
  • [R1] We further clarified how many runs were used in the results of ALFWorld and WebShop, and the settings for statistical support in Appendix B.4.
  • [R2] We added a comparison against ordinary MCTS with uniform backpropagation in Appendix B.5. The results show that our method places greater emphasis on the terminal states, thereby providing more accurate guidance for search directions.
  • [R1, R2] We compared the criterion "TCR" that counts any reward above zero as completion with the success rate (SR, r=1r=1) in Appendix B.7. SkillPilot demonstrates superior performance in SR as well. The TCR is another informative criterion that captures the agent’s ability to make meaningful progress, which can also show the effectiveness of SkillPilot.
  • [R2, R3] We clarified the budget constraints in Appendix C.1, including refinement rounds and environment rollouts per task, and provided the detailed token comparison in Table 8. We also clarified that the support set does not grow with the depth, addressing the complexity concern about our method.
  • [R2] We have revised Assumption 2 to make it more rigorous in Appendix D.3, and provide clarification in the same section to explain the correlation between our search problem and the two assumptions. Moreover, we provide an analysis in Appendix D.4 to explain the correspondence between the section-level analysis and MCETS.
  • [R1] We added clarifications about the scope of Theorem 2 to Appendix D.5, stating that Theorem 2 describes their worst case rather than their exact behaviour, and that it predicts the exponential trend in the number of sections, which is what the experiments show.
  • [R2] We corrected the typo in Theorem 3. We thank the reviewer for the careful response.
  • [R2] We have revised Assumption 3 to make it more rigorous in Appendix E.3, where we restate it as a sufficiency result and provide corresponding analysis.
  • [R3] To better illustrate the effectiveness of the failure attribution in SkillPilot, we provide two detailed cases in Appendix E.5, including task completion detection and objective grounding failures.

All the revised content has been marked in blue{\color{blue}\text{blue}}.

(* We refer to Reviewer hhqS as R1, Reviewer dJ1y as R2, Reviewer foRd as R3.)


Thank you again for your time, careful evaluation, and for managing the review process. We appreciate your effort, and we hope this summary is helpful.

Sincerely,

The Authors.

Dear Reviewers, AC, SAC, and PC,

We sincerely thank the Reviewers, AC, SAC, and PC for their careful evaluation and constructive feedback throughout the review process. We have addressed all major concerns and incorporated the suggested clarifications and additional experiments where appropriate with marked in blue{\color{blue}\text{blue}}. We are grateful for the reviewers’ positive reassessments and believe that the revisions have further strengthened the clarity of the paper.


1. Reviewer Score and Feedback Summary

Reviewer IDScore (Initial → Updated)Feedback Summary
hhqS (R1)2No additional feedback was available at this stage.
dJ1y (R2)1 → 2"I appreciate the authors' efforts to address my concerns and strengthen the experimental validation. Accordingly, I will raise my score to 2 (Weak Reject)."
foRd (R3)2 → 3"I think you have addressed most of my concerns, so I have raised my score to 3."

2. Summary of Strengths and Revisions

For clarity, we briefly restate the key strengths recognized by the reviewers and summarize the main revisions made in response to their comments.

Strengths. Reviewers recognized the relevant and clearly motivated problem, the innovative design of the MCETS to evolve skills, the comprehensive evaluation across three benchmarks, five base models, and both curated and self-generated skills, the ablations confirming that both the tree search and the meta-optimizer contribute to the gains, and the clear presentation and released code.

Key revisions. In response to the reviews, we added strong skill-evolution baselines on SkillsBench, clarified the benchmark protocols, the number of runs, and the statistical tests, reported the strict success rate next to TCR, added a uniform-back-propagation MCTS comparison, and disclosed the rollout and token accounting, and corrected the theoretical statements on the assumption, the scope of the theorem, and the error in the bound, together with explicit failure-attribution case studies.


Thank you again for your time, careful evaluation, and for managing the review process. We appreciate your effort, and we hope this remark is helpful.

Sincerely,

The Authors

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

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