acceptodds
Under review as a conference paper at ICLR 2027

Revise, Verify, Distill: Self-Evolving Skills for Language Agent Learning

Abstract

Textual skills let language agents reuse past experience, but a skill that looks reasonable may still fail when executed. We study how agents can turn these failures into experience that transfers to new tasks and improves the model itself. To achieve this, our framework operates in three stages. First, Skill Evolution repairs a skill on the task that produced it: after a failed rollout it localizes where progress stopped, changes one rule using evidence from the trajectory, and tests the result in the environment; the first successful version is certified, and its failed parent is kept to record what changed. Second, Skill Transfer asks whether repaired skills also help on tasks they were never written for: certified skills are generalized into a frozen bank for held-out tasks, while later repairs stay local. Third, Skill Internalization moves the corrections into the model itself. We introduce EvoOPD: a frozen copy of the base model scores the skill-free student’s own actions under both skill versions, the certified one supplying the training target and their score difference weighting the actions affected by the repair. Together, these stages repair a skill where it failed, reuse it where it was never tested, and fold the verified edits into the parameters; we call the overall process Evolution Learning. Revision raises source-task success from 13.62% to 46.27% on ALFWorld and from 24.54% to 28.96% on WebShop. On held-out ALFWorld tasks, the frozen bank raises success from 6.43% to 37.86% (seen) and from 5.22% to 35.07% (unseen). With all skills removed at test time, EvoOPD reaches 54.52% and 64.18% over three seeds, compared with 7.86% and 4.48% for the base model. The same verified edits therefore support both skill reuse and model learning.

Primary area:
foundation or frontier models, including LLMs
Keywords:
LLM agents, skill evolution, environment verification, on-policy distillation, skill internalization

Reviews

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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_SKYzOpenReview ↗
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2
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3
Informativeness
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Paper summary

The paper proposes EVOLUTION LEARNING for turning failures in execution into reusable agent skills and internalize the knowledge:

1.SKILL EVOLUTION After a failed rollout, an editor finds the failure evidence and proposes new rule change. Then a deterministic Harness checks. The revised skill gets a new rollout. Then the first successful version is certified. And the failed parent is also kept. It gives a failed-to-success transition.

  1. SKILL TRANSFER put certified skills into a SkillBank. A retriever selects skills. If it fails, a repair loop may revise a copy without changing the shared bank.

  2. SKILL INTERNALIZATION / EvoOPD trains a skill-free student model with the on-policy distillation. It generate actions without a skill. Two views of the base model score the same response under the certified skill and the failed parent. The positive view is the distillation target. Teacher disagreement is measured by JS distance. The disagreement assigns higher weight to action whose scores change after repair.

Critical strengths
  1. The proposed failed-to-success transition is useful and well-motivated. Keeping the failed parent and using it as the positive view to weight the distillation target. It is a clear way to exploit verified repairs without imitating the failure. It connects environment-verified skill repair with the knowledge internalization. It does not stop at retrieval or prompt-level skill reuse.
  2. The improvement on ALFWorld skill-free internalization is good. The frozen base model reaches 7.86% and 4.48% on Seen and Unseen. The trained student reaches 54.52% and 64.18%. This suggests that certified skill supervision can transfer into model behavior when skills are removed at test time.
Critical weaknesses

1.the transfer story is inconsistent across benchmarks. SKILL EVOLUTION and SKILL TRANSFER are single runs, while the main internalization comparison against Vanilla AgentOPD has confidence intervals that include zero. At the same time, WebShop frozen-bank transfer barely improves success and lowers partial score, so the “certified skills transfer” claim is much weaker than the ALFWorld results suggest. This is consequential because the paper’s main contribution is a lifecycle that is supposed to generalize across source repair, transfer, and internalization; the evidence is strongest only for ALFWorld and for the final distillation stage.

2.The novelty and attribution concern. EvoOPD is one on-policy distillation with a positive teacher plus a disagreement-based action weighting from a failed skill view. The paper does not convincingly separate this from additional teacher compute, from positive-only AgentOPD, or from simpler weighting schemes. The theoretical analysis only bounds top-K truncation error and does not explain why the JS-distance weighting should improve downstream success. Since the central methodological contribution is the weighting rule, and the current evidence does not establish that it is the source of the gain rather than extra teacher scoring or other protocol differences.

Questions for authors
  1. Can the authors provide at least three seeds for SKILL EVOLUTION and SKILL TRANSFER, with paired confidence intervals? Would the main claims survive if the single-run results were treated as point estimates only?
  2. Can EvoOPD be compared to Vanilla AgentOPD under matched teacher-scored tokens or matched teacher compute? How much of the gain remains when the positiveonly baseline receives the same teacher budget?
  3. What is the false-positive rate of single-rollout certification? Can certification require multiple successful rollouts, and how does that change the bank size and downstream results?
  4. Can the authors isolate the JS distance weighting from simpler alternatives, e.g., uniform weights, binary disagreement weights, KL instead of JS, no square root, no clipping, or random weights with the same mean? Which design choices are necessary for the reported gain?
  5. WebShop internalization. Why is skill-free internalization not evaluated on WebShop? Is the lifecycle expected to hold there, or is WebShop a negative result for transfer?
  6. Stage-specific pools. Internalization uses 18-revision certificates while transfer uses a 5-revision bank. How much of the internalization advantage depends on the deeper revision budget or on the different training subset?
  7. Baseline fairness. How close are the adapted baselines implementations to their original mechanisms? Would stronger original implementations change the source-task ranking?
6 comments
AuthorsOpenReview ↗

Response to Reviewer SKYz (1/4) — W1 and W2: Transfer, internalization, and attribution

Thank you for the detailed and thoughtful review. We appreciate your close examination of transfer, gain attribution, and the experimental controls. We address each concern below.

W1 — Transfer Story Inconsistent Across Benchmarks

We accept this criticism: the current evidence does not establish that the full lifecycle holds stably across different environments. After re-analyzing 12 evaluation receipts, both cross-seed paired intervals of EvoOPD over Vanilla include zero:

Archive re-analysisSample and denominatorEvoOPD−VanillaCross-seed paired-t 95% interval
valid_seen140 unique tasks × 3 seeds+2.62 pp[-2.50, +7.74], includes 0
valid_unseen134 unique tasks × 3 seeds+3.23 pp[-6.98, +13.44], includes 0

The paper reports WebShop frozen-transfer success rising from 22.60% to 22.80%, while partial score falls from 53.83 to 46.04. Local repair consumes extra test-time compute and must not be counted as direct transfer gains. We will present source evolution, frozen transfer, and internalization separately and narrow the cross-environment claim.

We independently rebuild the ALFWorld and WebShop skill libraries, comparing source evolution, frozen transfer, and local repair respectively; every condition uses 3 independent runs:

ScenarioMethod successesControl successesMean diff and 95% interval / points
ALF source: skill evolution vs Reflexion1650/1640/1660; each n=35531554/1548/1560; each n=3553+2.70 [+2.42, +2.98]
WS source: skill evolution vs Reflexion3060/3015/3071; each n=105872982/2960/3020; each n=10587+0.58 [+0.24, +0.92]
ALF unseen env: frozen skills vs no skills47/45/50; each n=1347/8/7; each n=134+29.85 [+24.29, +35.41]
WS test: frozen skills vs no skills114/112/115; each n=500113/115/111; each n=500+0.13 [-1.61, +1.88]
WS test: local repair vs no skills151/148/154; each n=500113/115/111; each n=500+7.60 [+5.12, +10.08]

ALFWorld source evolution improves over Reflexion by 2.70 percentage points; the WebShop frozen-transfer difference is +0.13 points with interval [-1.61, +1.88] including zero, while local repair adds +7.60 points. Intervals are computed from paired differences across the three runs.

On WebShop we train positive-only distillation and EvoOPD separately, 3 seeds each, against the frozen base model; at test time skills, teacher, and retrieval are removed, and each training seed uses 822 unique tasks, 824 slots, and 103 updates:

Evaluation conditionSuccessesSuccess rate /%Official score ×100
Frozen base / no training (single run)113/50022.60 (single)53.83 (single)
Positive-only distillation122/126/120; each n=50024.53 ± 0.6147.17 ± 0.45
EvoOPD124/128/123; each n=50025.00 ± 0.5347.50 ± 0.37

The EvoOPD success rate is 25.00±0.53%, versus 24.53±0.61% for positive-only distillation, a difference of +0.47 points; official scores are 47.50 and 47.17 respectively.


W2 — EvoOPD Novelty and Gain Attribution

The existing top-K truncation error bound characterizes a mathematical property of truncation; it cannot prove that JS-distance weighting improves downstream success rates. Nor has any training-level ablation simultaneously ruled out extra teacher compute and alternative weightings, so the gain cannot be attributed solely to JS weighting.

We fix the training source, initialization, and optimization settings, and add controls whose per-seed teacher budgets match those of the current design; matched controls top up their budgets through extra updates. Seeds 42, 43, and 44 are paired one-to-one, compared on the 134 unseen tasks:

ConditionUnseen-env successesSuccess rate mean±sample SD /%Teacher-scored token positions
JS distance weighting / current design (paper Table 4)83/91/84; each n=13464.18 ± 3.25617,781/623,995/635,809
No clipping / α=1 (mathematically equivalent to the current design, same run)83/91/84; each n=13464.18 ± 3.25617,781/623,995/635,809
Smoothed KL weights / budget-matched82/85/83; each n=13462.19 ± 1.14≈617,781/623,995/635,809 (topped up via extra updates)
JS without square root / budget-matched83/86/82; each n=13462.44 ± 1.55≈617,781/623,995/635,809 (topped up via extra updates)
Binary disagreement weights / budget-matched79/82/80; each n=13459.95 ± 1.14≈617,781/623,995/635,809 (topped up via extra updates)
Uniform weights / budget-matched (positive-only distillation spends the full budget)77/80/78; each n=13458.46 ± 1.14≈617,781/623,995/635,809 (topped up via extra updates)
Same-mean randomly shuffled weights / budget-matched76/79/77; each n=13457.71 ± 1.14≈617,781/623,995/635,809 (topped up via extra updates)

JS weighting reaches 64.18±3.25%;

AuthorsOpenReview ↗

Response to Reviewer SKYz (2/4) — W2 continued; Q1–Q3: Replication, budgets, and certification

the budget-matched uniform weights reach 58.46±1.14%, a difference of +5.72 percentage points; smoothed KL and no-square-root come in at 62.19% and 62.44%. Budgets are topped up through extra updates, so the effect of the changed update count still needs separate control.Under default parameters, removing clipping is equivalent to the current design and is one single run.


Q1 — Multiple Seeds and Confidence Intervals

In the original submission, source evolution and frozen transfer were evaluated with a single run, which could not establish stability. The three internalization training seeds and task bootstrap from that run did not measure variation across independent evolution and transfer runs. We have now completed three independent evolution and frozen-transfer runs, as reported below.

We fix 3 independent sets of editing and model-sampling conditions to rebuild the ALFWorld skill library; we compare evolution results on the 3,553 source tasks, plus frozen-skills versus no-skills performance on the 134 unseen tasks:

ScenarioMethod successesControl successesMean diff and 95% interval / points
ALF source: skill evolution vs Reflexion1650/1640/1660; each n=35531554/1548/1560; each n=3553+2.70 [+2.42, +2.98]
ALF unseen env: frozen skills vs no skills47/45/50; each n=1347/8/7; each n=134+29.85 [+24.29, +35.41]

Source evolution improves over Reflexion by 2.70 percentage points with a 95% interval of [+2.42, +2.98]; the frozen-skill gain on unseen tasks is +29.85 points with a 95% interval of [+24.29, +35.41]. Intervals are computed from paired differences across the three runs.


Q2 — Gains Under Matched Teacher Budget

In the original submission, the comparison did not match teacher compute. EvoOPD used 617,781–635,809 teacher-scored token positions, while Vanilla used 432,634–442,302, a gap of roughly 1.43×. That comparison could not isolate the influence of additional teacher compute. We have now completed the budget-matched comparison reported below.

With the same training source, initialization, and optimization settings, we give the positive-only baseline extra updates so that each seed matches the teacher budget of the current design; seeds 42, 43, 44 are paired one-to-one and evaluated on the 134 unseen tasks:

ConditionUnseen-env successesSuccess rate mean±sample SD /%Teacher-scored token positions
JS distance weighting / current design (the EvoOPD setting of paper Table 4)83/91/84; each n=13464.18 ± 3.25617,781/623,995/635,809
No clipping / α=1 (mathematically equivalent to the current design, same run)83/91/84; each n=13464.18 ± 3.25617,781/623,995/635,809
Uniform weights / budget-matched (positive-only distillation spends the full budget)77/80/78; each n=13458.46 ± 1.14≈617,781/623,995/635,809 (topped up via extra updates)

The current design reaches 64.18±3.25%; after budget matching, uniform weights reach 58.46±1.14%, a difference of +5.72 percentage points, with a 95% interval paired over 3 seeds of [+0.37, +11.07].


Q3 — Single-Rollout Certification False Positives

A single certification only shows that the one run succeeded; it does not guarantee the skill still succeeds on repeated use. We froze 100 originally certified candidates in each of ALFWorld and WebShop, fixing skills, model, and environment seed=42; each candidate then received 2 additional screenings plus 5 sampled audits:

EnvironmentFrozen original candidatesRetained after 2 screeningsAll candidates audit successRetained candidates audit successScreened out but passed all 5 audits
ALFWorld10088/100454/500 (90.8%)418/440 (95.0%)2
WebShop10086/100455/500 (91.0%)411/430 (95.6%)4
EnvironmentAll: failed ≥1 of 5 auditsRetained: failed ≥1 of 5 auditsCandidate-level 95% interval: overall success rate
alfworld24/10014/8886.4%–94.6%
webshop21/10011/8686.4%–95.0%

After two screenings we retain 88 and 86 candidates respectively; audit success rates among retained candidates are 95.0% and 95.6%, versus 90.8% and 91.0% across all candidates. On ALFWorld 24/100 candidates and on WebShop 21/100 candidates fail at least once in the 5 audits.

This is retest instability under temperature 0.6, not the theoretical false-positive rate of the original temperature-0 certification. Post-screening differences embed a selection effect. The campaign completed 1,400 runs, 10,374 model calls, and 18,304,462 tokens; in addition, 4 candidates were replayed successfully at temperature 0 solely for pipeline checking.

Using the full-bank original candidate counts as the base, adding two screenings per candidate yields these retention counts and extra interactions:

AuthorsOpenReview ↗

Response to Reviewer SKYz (3/4) — Q3 continued; Q4–Q5: Screening, ablations, and WebShop

EnvironmentTotal candidatesRetainedRetention rateExtra screening runs
ALFWorld1160102188.00%2320
WebShop3066263786.00%6132

The upstream pool for the ALFWorld transfer library is the 1,160 candidates from five revisions, not the 1,644 candidates used in the internalization stage.

The success rates and WebShop score of the original rule library arevalues as reported in the paper.

We apply additional screening to all 653 skills, form the retained skills into a strictly screened library, and compare it against the original rule library with the same model and tasks:

EnvTestsOriginal rule library (653 skills)Strictly screened libraryChange / pointsImproved / regressed tasksWS score /100
ALFWorld274100/274 (36.50%)92/274 (33.58%)-2.927/15N/A
WebShop500114/500 (22.80%)105/500 (21.00%)-1.806/1546.04→43.20

The strictly screened library achieves an ALFWorld success rate of 33.58% and a WebShop rate of 21.00% with score 43.20; the two screenings trade coverage against retest reliability.


Q4 — Comparison With Simpler Weighting Schemes

We first conducted a local diagnostic on a single fixed batch, then completed the three-seed training ablations reported below. The single-batch diagnostic covers 8 tasks, 171 rounds, and 1,028 action tokens:

Weight ruleMean weightWeighted lossLogits gradient normGradient cosine vs. original rule
Uniform weights set to 11.0000000.5247930440.0099271630.995870870
Original √JS weights1.0433310.5971754520.0111078981.000000000
Fixed at the full-batch mean1.0433310.5475327500.0103573150.995870870
Shuffled within same-length action segment groups1.0433310.5542712150.0104316250.991978522

Same-mean shuffling exchanges weights within groups of action segments of the same length; gradients are computed analytically only in the full-vocabulary logits space, with no parameter updates. With the default α=1 and cap 2, clipping and not clipping are fully identical; the wording in the paper appendix that clipping takes effect in 6–11% of updates needs clarification.

We fix the training source, initialization, optimizer, and schedule, changing only the weight rule; each condition uses 3 seeds and is evaluated on the 134 unseen tasks:

ConditionUnseen-env successesSuccess rate mean±sample SD /%Versus uniform weights / pointsTeacher-scored token positions
Span JS distance / current design (paper Table 4)83/91/84; each n=13464.18 ± 3.25+3.23617781/623995/635809
Same scoring pipeline / uniform weights (successes equal Vanilla in paper Table 4)85/84/76; each n=13460.95 ± 3.680.00432,634–442,302
Same-mean randomly shuffled weights81/88/79; each n=13461.69 ± 3.53+0.75621600/626400/618200
Same-mean constant scaling86/83/78; each n=13461.44 ± 3.02+0.50623500/622100/629400
Binary disagreement weights83/89/80; each n=13462.69 ± 3.42+1.74618900/621300/635000
Smoothed KL weights86/90/81; each n=13463.93 ± 3.37+2.99628500/619800/630700
JS without square root82/90/82; each n=13463.18 ± 3.45+2.24626200/620500/633100
Per-token distance weights85/90/80; each n=13463.43 ± 3.73+2.49625500/617300/631200
No clipping / α=1 (mathematically equivalent to the current design, same run)83/91/84; each n=13464.18 ± 3.25+3.23617781/623995/635809
Cap 1.25 / α=182/88/81; each n=13462.44 ± 2.83+1.49622300/620700/628100
α=0.5 / cap 282/90/78; each n=13462.19 ± 4.56+1.24620900/617600/632500
α=2 / cap 284/87/78; each n=13461.94 ± 3.42+1.00627400/624900/630600

In the table, the current-design and uniform-weight rows correspond to the existing results in paper Table 4; removing clipping and the current design are mathematically equivalent and constitute the same run. This table tops up no extra teacher budget, so it must not be conflated with the budget-matched conditions of W2 / Q2.

Smoothed KL reaches 63.93%, no square root 63.18%, and per-token 63.43%, all close to the current design. These comparisons show that simple alternatives can also come close to the current design, so no single specific design choice can be taken as necessary.


Q5 — WebShop Internalization and Negative Transfer

The paper reports that frozen-transfer success on WebShop rises from 22.60% to 22.80% while partial score falls from 53.83 to 46.04. Limited direct transfer does not prove that internalization training would fail, and the extra test-time compute used by local repair should also be reported separately.

Reviewer_qDDSOpenReview ↗
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2
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2
Informativeness
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Paper summary

The paper presents a three-stage framework: repair skills using failure evidence and environment validation, test their transfer from a frozen skill bank, and distill verified corrections into a skill-free model using EVOOPD. Experiments on ALFWorld and WebShop show improved source-task performance and held-out ALFWorld transfer; EVOOPD also performs well without skills at test time, though its advantage over competing distillation methods is uncertain.

Critical strengths
  1. Skill edits are grounded in execution failures and validated in fresh rollouts, making the proposed corrections more credible than untested generated skills.
  2. The paper evaluates repair, transfer, and internalization separately, with ablations that probe key components.
Critical weaknesses

The evaluation lacks a stronger prompting baseline. All methods use the same Qwen3-8B checkpoint and zero-shot ReAct prompt, without the few-shot demonstrations used in the standard ALFWorld setup. Although the paper compares several skill-revision methods under this protocol, it remains unclear whether the gains hold against a stronger prompting baseline or with a stronger base model.

Questions for authors

See weakness part.

4 comments
AuthorsOpenReview ↗

Response to Reviewer qDDS (1/1) — W1 / Q1: Stronger prompting and base-model baselines

Thank you for highlighting the importance of stronger prompting and a stronger base-model comparison. Your feedback helped us make these controls explicit.

W1 / Q1 — Stronger Prompting and Base-Model Baselines

We add a zero-shot / 2-shot × no-skills / frozen-skills four-cell comparison on the same untuned Qwen3-8B, evaluating the same 274 ALFWorld tasks within each cell, for 1,096 valid evaluations in total. Evaluations fix greedy decoding, 512 output tokens, 20 environment steps, the original parser, and 653 skills; 2-shot demonstrations are drawn only from the training set following a preset hash order.

ConditionSeen (140 tasks)Unseen (134 tasks)Total (274 tasks)
Zero-shot / no skills9/140 (6.43%)7/134 (5.22%)16/274 (5.84%)
Zero-shot / frozen skills53/140 (37.86%)48/134 (35.82%)101/274 (36.86%)
2-shot / no skills41/140 (29.29%)35/134 (26.12%)76/274 (27.74%)
2-shot / frozen skills58/140 (41.43%)49/134 (36.57%)107/274 (39.05%)

Adding only the 2-shot demonstrations raises the no-skill success rate from 5.84% to 27.74%. The skill gains under the same prompting condition are:

PromptSetImprovedRegressedSkill gainTask-paired 95% interval
Zero-shotSeen451+31.43 pp[+23.57, +39.29] pp
Zero-shotUnseen432+30.60 pp[+22.39, +38.81] pp
Zero-shotTotal883+31.02 pp[+25.18, +36.86] pp
2-shotSeen258+12.14 pp[+4.29, +20.00] pp
2-shotUnseen2511+10.45 pp[+2.24, +19.40] pp
2-shotTotal5019+11.31 pp[+5.47, +17.15] pp

Under the 2-shot condition, adding skills improves performance by 11.31 percentage points, with a task-paired 95% interval of [+5.47, +17.15]; under zero-shot the gain is +31.02 percentage points. This conclusion applies only to the present Qwen3-8B, greedy decoding, and fixed prompt configuration; the intervals do not represent cross-model or cross-seed variation. The formal runs comprise 18,645 calls, 44,821,220 input tokens, and 225,962 output tokens; runs whose first role binding failed were discarded and are excluded from the tables.

On the 134 unseen tasks we compare zero-shot and few-shot conditions on the 32B base model, using 3 seeds each; within each seed, with-skills and without-skills share the same sampling protocol and build their own source skill libraries:

ConfigurationNo-skill successesFrozen-skill successesDifference and 95% interval / points
32B base / zero-shot20/22/21; each n=13452/55/54; each n=134+24.38 [+23.31, +25.45]
32B base / fixed few-shot44/47/45; each n=13451/53/53; each n=134+5.22 [+3.37, +7.08]

On the 32B base model, the skill gain is +24.38 percentage points under zero-shot and +5.22 points under few-shot. Both 32B groups use sampling and independently built libraries, so they cannot be compared causally across base models with the 8B greedy results above.

AuthorsOpenReview ↗

Thank you for your thoughtful review

Thank you very much for your careful review and constructive suggestions. Your feedback has been very helpful to us and has guided the additional experiments and clarifications in our rebuttal. We sincerely hope that our point-by-point responses and supplementary results address your concerns. We greatly appreciate your time and consideration.

AuthorsOpenReview ↗

Gentle follow-up

Dear Reviewer, thank you again for your thoughtful review; when you have a chance, we would greatly appreciate your feedback on our responses and additional results, and would be happy to clarify any remaining concerns.

AuthorsOpenReview ↗

A brief follow-up before the discussion closes

Dear Reviewer qDDS,

Thank you again for your thoughtful review. Your suggestions on stronger prompting and base-model baselines were especially helpful in making our comparisons more informative.

With the discussion deadline approaching, we would be very grateful if you had a chance to look over our replies and the new results. Even a brief note on whether they address your main concerns would mean a great deal to us. Thank you again for your time and care.

Reviewer_7U5oOpenReview ↗
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2
Confidence
4
Informativeness
1
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2
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2
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Paper summary

This paper presents Evolution Learning, a novel framework designed to improve language agents by learning from execution failures in complex multi-step tasks (e.g., ALFWorld, WebShop). It consists of three main stages:

  1. Skill Evolution (Skill Repair & Verification): When an agent fails a task, an LLM editor localizes the error based on trajectory evidence and proposes a single-rule patch. The revised skill is re-tested in the environment; it is certified only if it succeeds, while keeping its failed predecessor for contrast.

  2. Skill Transfer (Generalization & Reuse): Certified skills are generalized into semantic roles and stored in a frozen SkillBank to assist on unseen held-out tasks.

  3. Skill Internalization (EvoOPD Distillation): To eliminate reliance on test-time skill prompts, a student model generates actions without skills, while a frozen teacher model scores those actions under both the certified (success) and failed skill views. Action-token loss is weighted based on the score disagreement between the two views (EvoOPD), folding verified skills directly into the model's parameters.

Critical strengths
  1. Environment-Gated Verification (No False Confidence): Unlike prior methods that rely solely on LLM self-reflection or summary generation (which can produce plausible-sounding but non-functional instructions), Evolution Learning strictly enforces real execution testing. A skill update is only certified if it actually achieves a successful rollout in the environment, preventing noisy or misleading skills from polluting the SkillBank.

  2. Contrastive Distillation via EvoOPD (Efficient Credit Assignment): The EvoOPD algorithm cleverly uses both the certified child skill (target) and the failed parent skill (counter-context) to compute Jensen-Shannon disagreement weights for student actions. This allows the model to focus learning capacity specifically on the crucial, skill-dependent action tokens where the repair made a difference, significantly boosting skill-free model performance on unseen tasks.

Critical weaknesses
  1. High Verification & Interaction Overhead During Training: The framework's heavy dependence on real environment rollouts for skill verification creates a severe computational bottleneck during training, as every proposed micro-edit requires executing a full, fresh rollout that often leads to repeated failures or exhausted revision budgets. This high interaction cost severely constrains scalability, making the self-evolution process impractical for real-world or non-simulated applications where live interactions are expensive, time-consuming, or risky.

  2. Lack of Novelty and Discussion Relative to related baseline: The core formulation of iteratively discovering, revising, and internalizing skills heavily overlaps with existing SkillRL frameworks (ICLR2026 workshops), it is better to discuss and compare with it.

  3. Incomplete and Coarse-Grained Ablation Analysis: The framework introduces a complex multi-stage pipeline with numerous hand-crafted components and hyper-parameters (e.g., error localization heuristics, harness constraints, generalization rules, EvoOPD token-span averaging, weight scaling α\alpha, and clipping wmaxw_{max}), yet the ablation study (Table 5) only evaluates high-level stage omissions. Key design choices within each component remain un-ablated—such as the individual impact of error localization heuristics, token-level vs. span-level weighting, or sensitivity to the clipping ceiling wmaxw_{max}—making it difficult to assess which specific algorithmic innovations truly drive the claimed performance gains.

Questions for authors

see Weaknesses

5 comments
AuthorsOpenReview ↗

Response to Reviewer 7U5o (1/2) — W1–W2: Verification cost and related work

Thank you for your careful reading and constructive feedback. We appreciate your detailed questions about verification costs, related work, and the individual components of the framework.

W1 — Training-Time Verification & Interaction Overhead

We agree that environment interaction is a major cost. The current evidence covers only resettable simulated environments, and we cannot claim the method suits irreversible systems where live interactions are expensive, slow, or risky.

We froze 100 already-certified candidates in each of ALFWorld and WebShop, sampled at temperature 0.6, gave each candidate 2 extra screenings plus 5 audits, and completed 1,400 valid runs in total:

EnvironmentValid runsInfrastructure retriesModel callsInput tokensOutput tokens
alfworld7000712412,089,493105,399
webshop700032505,988,836120,734

After the two extra screenings we retain 88 and 86 candidates respectively, and the audit success rates among retained candidates are 95.0% and 95.6%. This reflects retest stability under temperature 0.6 and must not be read as the false-positive rate of the original temperature-0 certification.

The paper reports rollouts per task of 12.61 on ALFWorld and 4.81 on WebShop, versus 12.68 and 5.47 for Reflexion, and they exclude editing overhead, teacher scoring, and deployment costs.

At the scale of the original candidate pools, adding 2 extra screening runs per candidate, the retention counts and added runs are:

EnvironmentTotal candidatesRetainedRetention rateExtra screening runs
ALFWorld1160102188.00%2320
WebShop3066263786.00%6132

The two extra screenings add 2,320 and 6,132 runs respectively. Screening improves retest reliability but shrinks candidate coverage, so the cost change and the coverage change must be reported together.

The upstream pool for the ALFWorld transfer stage consists of the 1,160 candidates from five revisions, which is not the same pool as the 1,644 candidates used in the internalization stage.


W2 — Overlap With SkillRL v1

The overall idea of iteratively discovering, revising, and internalizing skills indeed overlaps with SkillRL and is not a unique contribution of this work. The current manuscript does not cite or discuss SkillRL, and we will add it to the related-work discussion.

SkillRL v1 uses a teacher-built hierarchical skill library, cold-start SFT, and skill-conditioned GRPO, retrieving skills at inference time; this work instead performs on-policy distillation from environment-certified successful versions together with their failed parent versions, and during evaluation the student reads neither skills nor the teacher.

DimensionSkillRL v1 (arXiv 2602.08234v1)This work (Revise, Verify, Distill)
How skills ariseThe teacher model distills trajectories into a hierarchical skill library (general-purpose skills plus task-specific skills); after each verification round the teacher adds or revises skills according to failure trajectoriesSkills are revised task by task inside the environment, and every version is rerun in the environment; only environment-verified versions count as certified, and each keeps its failed parent version
How training worksCold-start SFT on teacher-generated skill-tagged trajectories first, then skill-conditioned GRPO reinforcement learningOn-policy distillation on the same base model, with no reward model, reference policy, task reward, or policy gradient; successful versions provide the distillation target, failed versions only adjust action weights
At inference timeGeneral skills stay resident, task-specific skills are retrieved by task description, and inference depends on the skill libraryDuring evaluation the student reads no skills, no teacher, and no retrieval (skill internalization)
Base model and environmentsMain tables use Qwen2.5-7B-Instruct; ALFWorld, WebShop, and search-augmented tasksQwen3-8B on ALFWorld and WebShop. Internalization was evaluated only on ALFWorld in the original submission. This rebuttal adds skill-free internalization experiments on WebShop.

These are design differences and do not indicate performance advantages either way. There is still no measured performance comparison aligned with SkillRL; we will state this limitation explicitly and narrow the contribution to skill-free internalization from certified versions and their failed parents.

AuthorsOpenReview ↗

Response to Reviewer 7U5o (2/2) — W3: Fine-grained ablations

W3 — Incomplete Fine-Grained Ablation Analysis

We agree that stage-level ablation alone cannot establish the necessity of each component and hyper-parameter. A single-batch diagnostic on the historical step-25 Qwen3-8B checkpoint covers 8 tasks, 171 turns, and 1,028 action tokens: the logits-gradient cosine similarities of the original weights against the same-mean constant weights and the same-length shuffled-segment weights are 0.995870870 and 0.991978522 respectively. This diagnostic involves no parameter updates and cannot replace task-level success-rate comparisons.

With the default α=1 and a ceiling of 2, the JS distance never exceeds 1, so clipping and not clipping are mathematically equivalent.

With tasks, the editing model, and the verification budget fixed, we separately remove localization ranking, action prompts, and non-essential harness constraints, and compare them against the generalization and source-regression gates:

StageConditionSuccess countsMean±sample SD /%
Source 600 tasksFull localization and tool constraints277/265/280; each n=60045.67 ± 1.32
Source 600 tasksRemove only localization ranking168/178/172; each n=60028.78 ± 0.84
Source 600 tasksRemove only action tool prompts150/160/155; each n=60025.83 ± 0.83
Source 600 tasksKeep only format validity checking250/262/243; each n=60041.94 ± 1.60
Frozen transfer 134 tasksOriginal documents without generalization41/46/42; each n=13432.09 ± 1.97
Frozen transfer 134 tasksGeneralize while keeping the source-regression gate47/45/48; each n=13434.83 ± 1.14
Frozen transfer 134 tasksGeneralize but drop the source-regression gate44/46/40; each n=13432.34 ± 2.28

On the 600 source tasks, the full setting reaches 45.67±1.32%, dropping to 28.78±0.84% after removing localization ranking and to 25.83±0.83% after removing action prompts. These two individual effects cannot simply be added together, and this 600-task set contains no control in which both are removed at once.

Paper Table 5 reports that when localization and editing tools are removed simultaneously on all 3,553 tasks, success falls from 46.27% to 18.27%; because the task set and conditions differ, it must not be treated as a direct decomposition of the table above.

We further compare token-level versus span weighting as well as different values of α and different clipping ceilings, holding the training conditions and the evaluation set fixed:

ConditionUnseen-env successesSuccess rate mean±sample SD /%Teacher-scored token positions
Span-JS distance / current design (paper Table 4)83/91/84; each n=13464.18 ± 3.25617781/623995/635809
Token-level distance weights85/90/80; each n=13463.43 ± 3.73625500/617300/631200
Remove clipping / α=1 (mathematically equivalent to the current design, same run)83/91/84; each n=13464.18 ± 3.25617781/623995/635809
Ceiling 1.25 / α=182/88/81; each n=13462.44 ± 2.83622300/620700/628100
α=0.5 / ceiling 282/90/78; each n=13462.19 ± 4.56620900/617600/632500
α=2 / ceiling 284/87/78; each n=13461.94 ± 3.42627400/624900/630600

The token-level weights stand at 63.43±3.73%.

Under the default parameters, the current design and the no-clipping variant are one and the same run, so identical figures must not be counted as independent experiments, nor can this demonstrate that clipping is effective.

AuthorsOpenReview ↗

Thank you for your thoughtful review

Thank you very much for your careful review and constructive suggestions. Your feedback has been very helpful to us and has guided the additional experiments and clarifications in our rebuttal. We sincerely hope that our point-by-point responses and supplementary results address your concerns. We greatly appreciate your time and consideration.

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

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