acceptodds
Desk rejected at ICLR 2027

Weft: Scaling Tool-Use Post-Training for General-Purpose Agents

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

Abstract

Recent efforts to scale tool-use post-training have largely centered on the synthesis of executable environments, which constitute only one component of a broader agentic interaction system comprising the environment, task, agent harness, and evaluator. Scaling environments in isolation, however, does not guarantee commensurate gains in model performance, because reliable learning signals depend on coherent interactions among all components of the agentic interaction system. To address this problem, we introduce WEFT (Whole-system Evolution For Tool-use Post-training), which couples scalable agentic interaction system construction, execution-driven self-evolution, and stable post-training. WEFT scales agentic interaction system construction across environment breadth, task complexity, and interaction diversity. Execution-driven self-evolution iteratively uses execution traces and state evidence to attribute failures and revise the responsible components, with fresh rollouts evaluating the changes and providing evidence for subsequent evolution rounds. For stable post-training at scale, WEFT addresses both optimization and execution reliability: prefix-preserving sampling retains verified progress and atomic-turn credit assignment localizes learning signals, while MegaMCP maintains isolated, recoverable state across concurrent rollouts over shared tool services. Extensive experiments across various models and benchmarks demonstrate the effectiveness of WEFT for tool-use post-training. WEFT-8B and WEFT-14B outperform all evaluated matched-size environment-scaling baselines on BFCL V4, τ²-Bench, and Claw-Eval. In particular, WEFT-14B improves over Agent-World-14B by 6.41, 2.23, and 12.27 percentage points. WEFT-35B-A3B further extends these gains to more challenging long-horizon workflow benchmarks, including Toolathlon-Verified and AutomationBench.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Tool Use, Long-Horizon Agents, Post-Training

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_1KvWOpenReview ↗
Rating
3
Confidence
2
Informativeness
3
Presentation
3
Soundness
2
Read review
Paper summary

WEFT combines stateful tool-environment synthesis, compositional task generation, multiple interaction views and harnesses, execution-driven component repair, prefix-preserving demonstration sampling, atomic-turn GRPO, and shared MCP serving. Its central idea is sensible: a failed rollout can reflect an environment, task, or verifier defect, so treating every failure as a policy error can corrupt training.

Critical strengths
  • Meaningful 14B improvements. Table 1 reports gains over Agent-World-14B of 6.41 points on BFCL V4, 2.23 on τ²-Bench, and 12.27 on Claw-Eval. The Claw-Eval improvement is particularly compelling.
  • Useful evidence for interaction diversity. In Table 2, adding OpenClaw and Hermes increases Toolathlon-Verified from 32.41 to 45.99 and AutomationBench from 13.67 to 26.50. Evaluation through benchmark-native harnesses makes this relevant evidence of transfer.
Critical weaknesses
  1. Several ablations do not fully separate the proposed factor from data or compute allocation

For harness and view diversity, a fixed task set does not establish equal numbers of demonstrations, training tokens, or optimizer updates. The cumulative harness gains could partly reflect increased training exposure.

For rejection sampling, the same retry limit applied per atomic task versus per complete trajectory does not imply equal generation cost. Fixing accepted-trace count is helpful, but efficiency requires generated-token and tool-call accounting.

For RL, atomic-turn training changes both the advantage calculation and the rollout procedure: candidates share restored states, and successful candidates preferentially supply subsequent history. It is unclear whether trajectory-level GRPO uses the same continuation rule and rollout topology.

  1. The central supervision-reliability claim is not directly validated

The reduction from 1.76% to 0.96% tool-call errors measures errors in selected teacher trajectories, including recoverable errors. It does not directly measure incorrect failure attribution, verifier false positives, or verifier false negatives.

The downstream improvements are valuable evidence that evolution helps. They do not distinguish among several explanations: repaired implementations, better demonstrations, changed task difficulty, or changed verifier permissiveness. Fixing task identities does not by itself establish that intended task semantics remain invariant across revisions.

The correlation filter has a related limitation: agreement between an LLM judge and an executable verifier does not establish that either is correct, particularly when they may share assumptions.

Questions for authors
  1. What independently verified evidence shows that self-evolution reduces erroneous supervision while preserving the intended task objectives? In particular, does attribution accuracy improve, and do verifier false-positive and false-negative rates decrease?
1 comment

Thank you for your careful review and for recognizing WEFT’s core motivation, the meaningful 14B gains, particularly on Claw-Eval, and the transfer evidence from benchmark-native evaluation.

Response to W1: Training volume and diversity gains, sampling costs, and RL rollout differences.

  • The task set and SFT settings stay fixed; added task formats and harnesses increase demonstrations and training updates (Table R1). We address the scarcity of executable, verifiable tasks. From the same 11,884 tasks, each added format or harness yields 7,486–8,813 accepted trajectories. Mixing Agentic and SimUser improves WEFT-35B-A3B by a mean 3.18 percentage points over Agentic alone; OpenClaw and Hermes add 9.71 more across Toolathlon-Verified, AutomationBench, and Claw-Eval under native harnesses (Table 2).

    ConditionTrajectoriesAvg. tokens per trajectoryOptimizer steps
    Agentic (ReAct)8,31859,763195
    SimUser (ReAct)7,48670,518177
    Both views (ReAct)15,80464,857372
    + OpenClaw24,47971,545576
    + Hermes33,29275,430783
  • Prefix-preserving sampling uses 28% fewer generated tokens and 30% fewer tool calls per task (Table R2). We measured both costs per task as suggested. Both methods allow k = 3 additional retries: per full trajectory for end-to-end sampling, or per atomic-task turn for prefix-preserving sampling. The downstream comparison in Figure 5 fixes accepted-trace counts.

    SamplingRetry limit kAvg. generated tokens per taskAvg. tool calls per task
    End-to-end3 per full trajectory128,13993
    Prefix-preserving (Section 3.3.1)3 per atomic-task turn92,261 (−28%)65 (−30%)
  • The GRPO variants use different rollouts but the same group size, training steps, and number of turn segments. Trajectory-level GRPO uses G independent full rollouts and trajectory-level advantages. Atomic-turn GRPO shares restored history and state, uses within-turn advantages, and continues from a uniformly selected passing candidate (a failed one if none pass). All candidates train the model; both yield G × T segments for T turns (Table 3).

Response to W2: Attribution accuracy, verifier errors, task-objective preservation, and filter reliability.

  • WEFT identifies the correct failure cause in 92.0% of audited cases (Table R3). Auditors checked WEFT's assignments to policy, backend, task, initial state, or verifier using 100 cases per category across three rounds, blind to downstream scores. This directly audits attribution, not tool-call errors.

    AttributionPolicyBackendTaskInitial stateVerifierTotal
    Correct / audited93 / 10097 / 10086 / 10094 / 10090 / 100460 / 500 (92.0%)
  • The revised verifier better distinguishes valid from invalid executions in the independent audit (Table R4). We compare rounds 0 and 3 on 200 trajectories labeled against original objectives, with verifier outputs hidden (percentages use all 200). Both false acceptances and false rejections decrease.

    VerifierFalse positivesFalse negativesAgreement with annotators
    Round 017 (8.5%)25 (12.5%)79.0%
    Round 315 (7.5%)7 (3.5%)89.0%
  • We repair faulty components without relaxing the original task requirements. After each repair, the checker evaluates fresh rollouts against the original objectives; 680 of 6,771 proposals were rejected for relaxing requirements. Appendix F.1–F.5 gives concrete cases: payment-ID binding is corrected while amount and merchant constraints remain unchanged.

  • Filter reliability. Thank you for this important question. Verifiers are hard to validate, so we used official AutomationBench verifiers as an independent reference. We rebuilt verifiers for 600 tasks from descriptions and environments alone, then filtered them. On the same rollouts, retained verifiers were more reliable: 87.5% agreement vs. 47.3% for removed ones (Table R5).

    TasksRetained by the filterAgreement (retained)Agreement (removed)Agreement (all)
    600471412 / 471 (87.5%)61 / 129 (47.3%)473 / 600 (78.8%)

Response to Q1: Independent audits of attribution and verifier errors, and checks on task objectives.

Please see W2: human auditing finds 92.0% correct failure attribution across three rounds (Table R3); the revised verifier makes fewer false acceptances and rejections against original-objective labels (Table R4). Appendix F.1–F.5 shows repairs that preserve the original requirements.

Appendices B.1, C.1, F, and G provide training settings, GRPO rollout details, cases, and reliability audits, respectively. Thank you again for your constructive feedback. We hope this evidence addresses your concerns and would appreciate your reconsideration of the score.

Reviewer_n4RWOpenReview ↗
Rating
2
Confidence
3
Informativeness
3
Presentation
3
Soundness
2
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Paper summary

WEFT treats tool-use post-training as a whole-system problem rather than only an environment-scaling problem. The framework constructs stateful MCP environments and certified atomic tasks, composes cross-MCP workflows, varies task-disclosure views and agent harnesses, and uses execution traces and state evidence to identify problems in environments, tasks, and verifiers. The training pipeline combines prefix-preserving SFT sampling, task–verifier consistency filtering, atomic-turn GRPO, and MegaMCP, a shared-serving runtime with isolated and recoverable state.

The paper reports a large corpus of executable MCPs, certified atomic tasks, and composed workflows. In the main table, WEFT-8B and WEFT-14B score above the listed matched-size environment-scaling baselines on BFCL V4, τ²-Bench, and Claw-Eval. The larger model is also evaluated on Toolathlon-Verified and AutomationBench.

Critical strengths

I like the paper’s central argument that useful tool-use training data depends on the complete interaction system, not only on the number of executable environments. The combination of deterministic state and return checks, failure attribution, targeted revision, fresh-rollout validation, stable post-training, and isolated state branching forms a coherent pipeline rather than a collection of unrelated heuristics.

The empirical scope is also a strength. The paper evaluates several model sizes and public tool-use benchmarks. The credit-assignment study is particularly useful: with the initialization, task pool, reward verification, and masking policy held fixed, atomic-turn GRPO consistently outperforms trajectory-level credit assignment. The prefix-preserving sampling study also controls the task pool, verifier, and accepted-trace count.

Critical weaknesses

My main concern is the baseline comparison. The Qwen3.5 base scores come from model cards, while the provenance of the other baseline rows is unclear. The WEFT 35B model is below the reported base values on all three main aggregates, and some 8B gains are small. Same-protocol evaluation with uncertainty estimates is needed before these comparisons can support the paper’s broad scaling claims.

The ablations also leave important mechanisms entangled. The task-view and harness study adds data cumulatively without matching training volume or compute. The self-evolution study reports improvements, but does not measure attribution accuracy or compare against simpler filtering and regeneration. The verifier filter is described, yet its thresholds and reliability are not reported. These omissions make it hard to identify which parts of the large pipeline are responsible for the gains.

The MegaMCP evaluation is similarly uneven. It clearly reduces upload overhead and performs well in the matched cold-start setting, but the large-scale comparison uses asymmetric warm-up conditions and favors local serving on latency. A fully crossed cold/warm comparison would make the systems claim much easier to interpret.

Questions for authors

Which baseline rows were rerun, and can the base and WEFT checkpoints be compared under the same evaluation protocol with multiple seeds?

Can the view, harness, and self-evolution studies be repeated with matched data and compute and with simpler controls?

Can the authors provide the missing training and verifier details and a symmetric cold/warm MegaMCP comparison?

3 comments
AuthorsOpenReview ↗

Rebuttal (1/2)

Thank you for your careful review and for recognizing WEFT’s whole-system approach, the coherence of its pipeline, and the value of the credit-assignment and prefix-preserving sampling studies. Below, we address each concern with the relevant results and details.

Response to W1: Baseline sources, the 35B gap, small 8B margins, and same-protocol and multi-seed evaluation.

  • All baseline scores in Table 1 come from the original papers or official releases. We evaluated the WEFT models ourselves.

  • The submitted 35B model is post-trained from Qwen3.5-35B-A3B-Base using only our 11,884 tasks. In contrast, the official Qwen baseline has undergone large-scale, multi-domain post-training, so the two settings differ in training scale and domain coverage. To test whether WEFT can further improve the official post-trained model, we applied WEFT training to its instruction-tuned checkpoint on the same task set. The resulting model exceeds the official release by 5.70, 4.40, and 7.10 points on BFCL V4, τ²-Bench, and Claw-Eval (Table R1).

    ModelBFCL V4τ²-BenchClaw-Eval
    Qwen3.5-35B-A3B (official post-trained release)67.381.265.4
    WEFT-35B-A3B (from base, submitted)63.474.3464.0
    WEFT-35B-A3B (from instruct)73.0085.6072.5
  • The small 8B margins are against Agent-World, the strongest baseline. WEFT-8B and WEFT-14B also start from base checkpoints and outperform the official post-trained Qwen3 models by 10 to 36 points (Table 1). The margins over Agent-World increase to 6.41, 2.23, and 12.27 points at 14B.

  • We evaluated Qwen3-8B, Qwen3-14B, and WEFT-14B with three random seeds under matched harnesses and decoding settings. Table R2 reports mean ± standard deviation. Qwen3 means agree with reported scores within 0.8 percentage points, supporting the consistency of our evaluation protocol and the fairness of the comparison; WEFT-14B exceeds the reported Agent-World-14B scores on every benchmark and seed.

    ModelBFCL V4τ²-BenchClaw-Eval
    Qwen3-8B (3 seeds)40.4 ± 0.426.2 ± 0.625.4 ± 0.8
    Qwen3-14B (3 seeds)41.0 ± 0.432.4 ± 0.623.9 ± 0.7
    WEFT-14B (3 seeds)62.2 ± 0.767.6 ± 1.543.8 ± 0.8
    Agent-World-14B (reported)55.865.431.5

Response to W2: Training volume and diversity gains, self-evolution attribution and control, and verifier-filter thresholds and reliability.

  • Mixing task formats and harnesses improves downstream performance without adding tasks; demonstrations and training updates increase. We focus on the scarcity of executable, verifiable tasks. On the same 11,884 tasks, mixing Agentic and SimUser improves WEFT-35B-A3B by a mean 3.18 percentage points over Agentic alone; OpenClaw and Hermes add 9.71 more across Toolathlon-Verified, AutomationBench, and Claw-Eval under native harnesses (Table 2). Table R3 reports the increased data and updates. All runs use peak LR 5×10⁻⁶, 3% warmup, cosine decay to 1×10⁻⁷, 3 epochs, batch 128, context 128K, and assistant-token loss only.

    ConditionTrajectoriesAvg. tokens per trajectoryOptimizer steps
    Agentic (ReAct)8,31859,763195
    SimUser (ReAct)7,48670,518177
    Both views (ReAct)15,80464,857372
    + OpenClaw24,47971,545576
    + Hermes33,29275,430783
  • WEFT identifies failure causes with 92.0% accuracy, and repair improves on filtering alone. Human auditors, blind to downstream scores, checked whether WEFT correctly assigned each failure to the policy, backend, task, initial state, or verifier, using 100 cases per category across three rounds (Table R4). With tasks and rollout budget fixed, repair outperforms the round 0 filtering-only control by 3.65–5.25 points (Figure 4).

    AttributionPolicyBackendTaskInitial stateVerifierTotal
    Correct / audited93 / 10097 / 10086 / 10094 / 10090 / 100460 / 500 (92.0%)
  • The filter requires both Pearson and Spearman correlations to reach 0.8 and retains more accurate verifiers. We score 16 Nex-N2-mini pilot rollouts per task with the judge and verifier; 1,954 of 5,000 tasks pass the filter. RL uses executable-verifier rewards. On 600 AutomationBench tasks, agreement with official judgments on the same rollouts is 87.5% for retained verifiers versus 47.3% for removed ones (Table R5).

    TasksRetained by the filterAgreement (retained)Agreement (removed)
    600471412 / 471 (87.5%)61 / 129 (47.3%)
AuthorsOpenReview ↗

Rebuttal (2/2)

Response to W3: Symmetric cold/warm comparison and latency results.

  • Both serving methods use the same timing boundaries: cold runs include preparation, and warm runs exclude it (Table R6). We tested 1,000 tasks at identical concurrency. Cold timing includes server startup and session provisioning; warm timing starts with local servers running and MegaMCP sessions already provisioned. TTFT is time to first tool call, E2E is per-task latency, and wall time covers the batch.

    ServingConditionTTFT p50 (s)TTFT p95 (s)E2E p50 (s)Wall time (s)
    LocalCold428.6593.4444.8968.9
    MegaMCPCold17.422.530.5550.3
    LocalWarm0.0090.01615.097501.220
    MegaMCPWarm0.0080.01313.117431.762
  • MegaMCP is faster in both matched cold and warm runs. With symmetric warm-up, median end-to-end latency decreases by 13.1% and wall time by 13.9% relative to local serving.

Response to Q1: Which baselines were rerun, and what same-protocol and multi-seed evaluations are available?

Please see W1 and Table R2 for the three-seed results. Qwen3 means reproduce reported scores within 0.8 percentage points, supporting a fair comparison under our evaluation protocol. WEFT-14B's advantage over reported Agent-World scores persists across seeds. Table R1 also shows that WEFT improves the 35B instruct model.

Response to Q2: Data and compute controls for diversity and self-evolution.

Please see W2. The diversity comparison fixes the task set, while larger mixtures use more training data and updates (Table R3), yielding mean gains of 3.18 and a further 9.71 points (Table 2). Self-evolution fixes both tasks and rollout budget and improves over filtering alone by 3.65–5.25 points (Figure 4).

Response to Q3: What are the missing training and verifier details, and is the cold/warm comparison now symmetric?

Please see W2 for training statistics (Table R3) and the 0.8 filter thresholds; Table R5 shows that retained verifiers agree more with official judgments. W3 and Table R6 provide the symmetric cold/warm comparison: MegaMCP is faster in both conditions.

The revised manuscript provides training and evaluation protocols in Appendix B, instruction-tuned initialization results in C.3, matched cold/warm comparisons in D.2, and supervision audits in G. Thank you for the constructive review; we hope these additions address your concerns and would be grateful if you would reconsider your score.

Thank you for the response. After considering the additional analyses and clarifications, I will maintain my current score.

Reviewer_NArZOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

WEFT builds stateful tool environments, composes tasks across them, and revises the environments, tasks and verifiers using execution traces. It collects demonstrations across task views and harnesses, keeps successful prefixes during resampling, and assigns RL rewards per subtask. MegaMCP shares tool servers while keeping each rollout's state separate.

Critical strengths

Figure 4 is the most useful result: with the task set and rollout budget fixed, three repair rounds improve three external benchmarks by 3.65 to 5.25 points. This tests whether repair helps post-training, beyond EigenData's benchmark-repair setting. Table 3 also shows benefits from atomic-turn credit assignment at both model sizes. MegaMCP reduces median task latency by 23.3 percent under matched cold-start conditions.

Critical weaknesses
  1. The paper gives too little detail about what the repair loop actually changes. Section 3.2 permits changes to task graphs, initial states and verifiers, but only promises fixed task semantics across views within one version. Figure 4 shows that training on revised versions improves downstream performance, but the paper gives no examples showing how requirement changes were justified. Correcting a contradictory task and relaxing a valid requirement have different implications for the claim of more reliable supervision.

  2. Table 2 is presented as evidence for diversity, but adding views and harnesses may also add demonstrations and training. The task set is fixed, but the paper does not report the number of accepted trajectories, training tokens or updates for each condition. Appendix B documents RL settings but leaves the SFT schedule and mixture sizes unspecified. The results support the combined training recipe, while the contribution of diversity itself remains unclear.

Questions for authors
  1. What changed across the Figure 4 rounds? Please use existing examples to explain how you checked the repairs and justified any changes to task requirements.
  2. For each Table 2 condition, how many demonstrations were used?
1 comment

Thank you for your careful review and for highlighting the post-training gains from self-evolution in Figure 4, alongside the benefits of atomic-turn credit assignment and MegaMCP. Below, we address each concern with the relevant evidence and details.

Response to W1: What is repaired, where the examples are, and whether task requirements are relaxed.

  • Self-evolution repairs backends, task inputs, initial states, and verifiers; policy failures leave tasks unchanged. Only the faulty component is revised. Across Figure 4's three rounds, the task set, original objectives, completion requirements, and rollout budget stay fixed. Most revisions address initial states and verifiers, and total revisions fall by 83% (Table R1). Repaired defects do not recur.

    RoundBackendTaskInitial stateVerifierAttributed to policy (unchanged)Rejected by checker
    0 → 16372411,5231,3181,376409
    1 → 23521096865921,150174
    2 → 3119401982761,02597
    Total1,1083902,4072,1863,551680
  • We have added five execution-log cases to Appendix F.1–F.5 of the revised manuscript. Each shows the task, failure evidence, and repair decision. F.3 supplies the already-selected image URL without changing processing requirements; F.4 corrects payment-ID binding without changing amounts or merchant. F.5 keeps the task unchanged when the failure comes from the policy.

  • We preserve the original task objectives and reject repairs that relax completion requirements. After re-execution, the checker assesses trajectories against the original objectives; 680 of 6,771 repair proposals were rejected for relaxing requirements. Independent annotators labeled 200 trajectories against those objectives, blind to verifier outputs. We compared round 0 and round 3 on these trajectories (error percentages use all 200). The audit shows more accurate task verification, rather than higher acceptance through looser checks.

    VerifierFalse positivesFalse negativesAgreement with annotators
    Round 017 (8.5%)25 (12.5%)79.0%
    Round 315 (7.5%)7 (3.5%)89.0%

Response to W2: Training statistics, SFT settings, and the contribution of diversity.

  • On the same 11,884 tasks, accepted demonstrations rise from 8,318 for Agentic alone to 33,292 for the full mixture (Table R3). We combine Agentic and SimUser demonstrations, then add OpenClaw and Hermes cumulatively. The table reports accepted trajectories, average tokens per trajectory, and optimizer updates.

    ConditionTrajectoriesAvg. tokens per trajectoryOptimizer steps
    Agentic (ReAct)8,31859,763195
    SimUser (ReAct)7,48670,518177
    Both views (ReAct)15,80464,857372
    + OpenClaw24,47971,545576
    + Hermes33,29275,430783
  • The SFT schedule is identical across conditions. We use a peak learning rate of 5×10⁻⁶, 3% warmup, cosine decay to 1×10⁻⁷, 3 epochs, batch size 128, a 128K context, and loss on assistant tokens only.

  • Interaction diversity provides more useful demonstrations from the same tasks and improves downstream performance. We target the scarcity of executable, verifiable tasks, not training volume alone. Mixing Agentic and SimUser improves WEFT-35B-A3B by a mean 3.18 percentage points over Agentic alone; OpenClaw and Hermes add a further 9.71 across Toolathlon-Verified, AutomationBench, and Claw-Eval under native harnesses (Table 2).

Response to Q1: What changed across the Figure 4 rounds, and how were the repairs checked?

Please see our response to W1 above. Table R1 shows that revisions mainly correct initial states and verifiers; Table R2 shows fewer false rejections without more false acceptances. Appendix F.1–F.5 illustrates the corrections and the requirements kept unchanged.

Response to Q2: How many demonstrations were used in each Table 2 condition?

Please see W2 and Table R3 for the counts. All conditions reuse 11,884 tasks, with 8,318 demonstrations for Agentic and 33,292 for the full mixture.

The revised manuscript includes SFT settings in Appendix B.1, human audits in Appendix G.1, and the five cases in Appendix F. Thank you for the constructive questions; we hope these additions address your concerns and would be grateful if you would reconsider your score.

Comments on the paper

1 comment
Area_Chair_J7fNOpenReview ↗

urgent!

Thank you to the authors for the detailed rebuttal and additional experiments. I noticed that none of the reviewers has provided follow-up feedback so far. As the discussion period is approaching its end, I would strongly encourage all reviewers to take a moment to review the authors' responses and revised manuscript.

Please provide your feedback before the discussion closes so that we can have a sufficiently informed discussion of this submission. Thank you.

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

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