acceptodds
Under review as a conference paper at ICLR 2027

CoTrace: Data Recipes for Training Terminal Agents with Harness-Model Co-Evolution

Abstract

Terminal-agent capability depends jointly on model weights and the runtime harness that formats prompts, binds tools, and handles error recovery. Existing harness-model co-evolution approaches improve both components, yet often treat trajectories produced during harness search as an undifferentiated replay buffer. This practice overlooks that a trajectory's value for model training depends on the harness under which it was generated. To systematically analyze this interface, we establish an alternating co-evolution framework that decouples harness search and policy training through component-wise promotion decisions. Within this framework, we introduce CoTrace, a harness-aware data recipe that explicitly governs trajectory routing, provenance matching, and curriculum refresh. Under CoTrace, recurring execution failures guide harness synthesis, while policy training is strictly conditioned on verified rollouts matched to the adopted runtime for supervised fine-tuning or fresh online interactions for reinforcement learning. On the Tmax evaluation split, CoTrace advances Qwen3.5-9B from to solved tasks under supervised fine-tuning while an online reinforcement variant reaches . Specifically, a compact harness-matched corpus produces steady model gains at substantially lower compute than much larger corpora pooled across sibling harnesses. Furthermore, evaluations on Terminal-Bench 2.1 and SWE-bench Lite show that out-of-distribution transfer depends fundamentally on harness compatibility, where maintaining consistency between training and evaluation runtimes prevents procedural execution breakdowns observed under foreign scaffolds.

Primary area:
foundation or frontier models, including LLMs
Keywords:
llm, harness, co-evolution, training recipe

Reviews

Among:
Shape:
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_hsZkOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper introduces CoTrace, a framework for jointly improving terminal agents and their execution harnesses. Its main idea is to carefully manage how execution trajectories are used during co-evolution. Failed trajectories guide harness updates, while successful trajectories train the model under the adopted harness. The framework also refreshes training tasks and separately validates model and harness updates. Experiments on Tmax show improvements from 78 to 88 solved tasks with SFT and 90 with RL. Additional evaluations on Terminal-Bench 2.1 and SWE-bench Lite highlight the importance of harness compatibility.

Critical strengths

I think the focus on trajectory provenance is interesting and useful. The paper identifies an important issue in co-evolution: successful trajectories from different harnesses may not provide suitable training signals for the deployed model.

The experimental analysis is thoughtful. I particularly appreciate the component-wise evaluation, which helps distinguish improvements from harness updates and model training. The cross-harness experiments also provide useful insights into how runtime compatibility affects performance.

Critical weaknesses

I am not fully convinced that harness matching is the main reason for the observed improvements. The compared data recipes differ in several other aspects, including corpus size, task coverage, and fresh rollout generation. Without more controlled ablations, it is difficult to isolate the actual contribution of trajectory provenance.

The main results rely on the same 102-task validation split throughout the co-evolution process. Repeatedly selecting updates against this split could lead to overfitting. The external evaluations provide limited evidence of generalization, as the SFT model does not consistently outperform the baseline, while the RL improvements are relatively modest.

Questions for authors

Could the authors isolate the effect of harness matching while keeping corpus size, task coverage, and freshness fixed? This would help establish the central contribution.

Could the authors evaluate the final models on an independent held-out Tmax split? Results across multiple runs would also help establish whether the improvements are robust.

4 comments
AuthorsOpenReview ↗

Response to Reviewer hsZk (1/2)

Thank you for recognizing the value of provenance and component-wise analysis. We added the requested controlled ablation and independent evaluation.


W1: I am not fully convinced that harness matching is the main reason for the observed improvements. The compared data recipes differ in several other aspects, including corpus size, task coverage, and fresh rollout generation. Without more controlled ablations, it is difficult to isolate the actual contribution of trajectory provenance.

A: The original experiment measures the benefit of the complete data recipe. To separately identify the provenance contrast, we added a task-paired ablation using the same generating policy, 50 common-success tasks, fresh collection campaign, one verified trajectory per task, identical per-task pair counts (556 per arm), serializer, LoRA settings, and paired seeds 42/43/44.

The intervention changes only the generating runtime: H0 versus R2c1. They share the same system prompt and tools; R2c1 changes loop detection and lifecycle self-verification. All six checkpoints are evaluated under both runtimes on the independent test.

Training dataEvaluate under H0Evaluate under R2c1
H078.176.6
R2c176.776.0

Means average three training seeds. Matched data lead by +1.4 pp under H0, with seed-and-task CI [-2.4, +5.6]; one seed favors sibling data. The mean cross-runtime matching advantage is +0.4 pp (seed-and-task CI [-2.2, +3.1]).

These results provide the requested controlled provenance comparison, with a +1.4 pp matched-data estimate and its confidence interval. The compact H0-data recipe additionally improves over base weights by +4.2 pp under fixed Hmix (seed-and-task CI [+0.7, +7.8]). Together, they establish the practical training benefit and quantify the matching contrast within the shared prompt/tool interface.


Q1: Could the authors isolate the effect of harness matching while keeping corpus size, task coverage, and freshness fixed? This would help establish the central contribution.

A: Yes. We collected both corpora on the same 50 task IDs using the same policy in one fresh campaign, with no replay. Each contains one verified trajectory per task and 556 prompt/completion pairs with identical per-task counts. The serializer, LoRA settings, and seeds 42/43/44 are identical; completion-character counts are within 3.3%. The tasks are solved under both generating harnesses, preventing a between-arm coverage difference.

All six checkpoints are evaluated under both H0 and R2c1. Under H0, H0-data models score 80.7/76.0/77.7%, and sibling-data models score 77.0/76.7/76.3%: +1.4 pp for matched data (task CI [-1.3, +4.2]; seed-and-task CI [-2.4, +5.6]). The mean diagonal-minus-off-diagonal contrast is +0.4 pp (seed-and-task CI [-2.2, +3.1]).

This experiment controls the requested factors and measures a +1.4 pp matched-data advantage within a compatible runtime family, with uncertainty quantified above. The full cross-runtime table and per-seed results make the provenance comparison directly inspectable alongside the recipe's policy-training benefit.


AuthorsOpenReview ↗

Response to Reviewer hsZk (2/2)

W2: The main results rely on the same 102-task validation split throughout the co-evolution process. Repeatedly selecting updates against this split could lead to overfitting. The external evaluations provide limited evidence of generalization, as the SFT model does not consistently outperform the baseline, while the RL improvements are relatively modest.

A: The 102-task validation split has a specific role: comparing candidate updates against the incumbent on a fixed set of tasks. This avoids confounding component-wise promotion with changes in evaluation-task composition. Training and harness search draw on separate task pools. To independently assess the resulting policies, we added a frozen 300-task test outside both promotion and learning, with no further updates based on its outcomes.

SystemPass rateGain over base; task 95% CI
Base pair74.7Reference
Early SFT θ1 + H275.6+0.9 [-2.3, +4.2]
RL iteration-3 weights + H380.3+5.7 [+2.7, +8.8]
Same RL weights + H081.6+6.9 [+3.9, +9.9]

Each row averages three executions. A separate three-seed SFT experiment also improves by +4.2 pp over base weights under fixed Hmix (seed-and-task CI [+0.7, +7.8]).

The positive RL and controlled SFT comparisons demonstrate policy improvements on unseen tasks with evaluation runtime held fixed. They directly address whether the training recipe yields benefits beyond promotion-validation scores. The table separately identifies the earlier SFT pair and its interval.

The external results probe a further shift in domain and runtime: SFT is similar to the base on TB 2.1 and scores 35.0% versus 37.3% on SWE-bench Lite; RL scores 41.0% versus 37.3% (p = 0.16). The 10.3 pp recovery from changing only SFT's runtime (24.7% to 35.0%) illustrates the compatibility effect; the independent Tmax test establishes the learned policies' in-domain gains.


Q2: Could the authors evaluate the final models on an independent held-out Tmax split? Results across multiple runs would also help establish whether the improvements are robust.

A: We added 300 independent Tmax tasks, three execution repeats per fixed system, and three paired training seeds per controlled SFT arm.

The test continues the original sampling order, excluding the 102 promotion tasks and all 461 task IDs in project training/search/probe/pilot records. Of the next 400 eligible tasks, we retain the first 300 whose containers build and start, without using model outcomes. The manifest is frozen before evaluation, disjoint from the new SFT generation pools, and never used for promotion. All comparisons share greedy decoding, an 80-step cap, and 4,096 output tokens per turn.

We identify the tested configurations explicitly:

  • SFT θ1 + H2 (Table 3): the policy promoted after iteration 1's SFT update, paired with the harness adopted at iteration 2's stage B.
  • RL iteration-3 policy: the last promoted RL policy, since the fourth proposal was rejected (Table 8), evaluated with H3 and H0. The paper's 90/102 point pairs this policy with the later H4.

The RL pair scores 79.3/81.3/80.3% versus 74.3/72.3/77.3% for the base, giving +5.7 pp (task CI [+2.7, +8.8]). With H0 fixed, its weights gain +6.9 pp. The new controlled SFT models gain +4.2 pp under fixed Hmix (seed-and-task CI [+0.7, +7.8]).

These results establish independent-test policy gains and quantify execution repeatability and SFT training variation separately. We will label stage-specific configurations explicitly: the later H4 pairing and iteration-5 SFT policy are distinct from the systems in this test.

Thanks for providing the experiment results for RL gains on unseen tasks. However, it seems that the ablation gain for harness matching is merely +0.4 pp, with a CI of [−2.2, +3.1]. The +6.9 pp RL gain mostly resolves W2, but the final SFT system still lacks independent evaluation.

AuthorsOpenReview ↗

Response to Reviewer hsZk follow-up

Thank you for the follow-up. We would like to clarify the interpretation of the +0.4 pp matching contrast and provide an additional independent evaluation of the final SFT checkpoint.

1. On the +0.4 pp matching contrast.

The +0.4 pp figure is computed by averaging two runtime-specific matching contrasts, which differ in direction:

  • Under H0: H0-trained models achieve 78.1%, compared with 76.7% for R2c1-trained models, yielding a +1.4 pp matching advantage.
  • Under R2c1: R2c1-trained models achieve 76.0%, compared with 76.6% for H0-trained models, yielding a −0.6 pp contrast.

The resulting average is (+1.4 − 0.6)/2 = +0.4 pp. This average aggregates two heterogeneous effects and should not be interpreted as a universal measure of the benefit of harness-aware data selection.

Importantly, H0 and R2c1 share the same system prompt and tool schema, differing only in loop detection and lifecycle self-verification. The experiment therefore isolates provenance effects under a relatively narrow runtime variation, rather than evaluating the full range of harness differences encountered during co-evolution.

The broader CoTrace contribution concerns how experience is routed, verified, and used throughout harness–model co-evolution. The original mixed-sibling comparison examines this broader setting, while the controlled ablation measures a narrower provenance contrast. We will make this distinction clearer in the revised manuscript.

2. Independent evaluation of the final SFT checkpoint (θ5).

We have now additionally evaluated θ5, the final SFT checkpoint that achieved 88/102 solved tasks on the original validation split, on the frozen independent 300-task Tmax test.

It achieves 78.3% (235/300), compared with 74.7% for the base system (three-execution average), corresponding to an observed improvement of +3.6 percentage points.

Due to the limited discussion-period compute budget, this additional θ5 evaluation currently contains one execution, whereas the base reference averages three executions. We therefore present this as a preliminary held-out result rather than a statistically established gain. Nevertheless, it provides direct evidence on the previously unevaluated final SFT checkpoint, with a positive observed difference on tasks excluded from training and promotion. We will extend the repeated evaluation and report the corresponding uncertainty in the revised results.

Together with the independently verified RL improvement (+6.9 pp under fixed H0) and the three-seed controlled SFT improvement (+4.2 pp under fixed Hmix), this new result further supports the effectiveness of the CoTrace training recipe beyond the original promotion split.

We are incorporating these additional results, checkpoint correspondences, and more precise interpretations of the provenance ablation into the revised manuscript to make the experimental evidence and scope of our claims easier to follow.

Reviewer_BPKqOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper studies how training data should be selected when the harness and model weights of a terminal agent are optimized alternately. In each iteration, a meta-agent first proposes harness edits with the model fixed, and then the model is updated with the harness fixed. Each candidate is adopted only if it solves more tasks than it breaks on a 102-task validation split from Tmax. The proposed data recipe, CoTrace, sends failure trajectories to harness search and trains the model only on successful trajectories generated under the adopted harness, with SFT or RL. With Qwen3.5-9B, CoTrace-SFT improves the accuracy from 78 to 88 and CoTrace-RL reaches 90 on 102 tasks selected from Tmax.

Critical strengths
  1. The paper studies a timely question. As harnesses and models are increasingly optimized together, it is important to understand which trajectories should be used to train the model, and the paper shows that the usefulness of a trajectory can depend on the harness that produced it.

  2. The method is simple and reasonable. Training only on data generated under the harness that will actually be deployed is easy to implement and consistent with prior findings on on-policy data.

  3. The experimental record is detailed and transparent. Every promotion decision, the paired win/loss counts, the estimated evaluation noise, and the failed runs are reported.

Critical weaknesses
  1. Each configuration is run only once, the number of tasks are only 114. It is hard to tell whether each accepted update reflects a real improvement or noise. For example, according to Appendix B.5, the same 9B checkpoint scored 84 and then 88 when evaluated twice on the 102-task split. Results over multiple runs with different seeds are needed to verify if the improvement is from harness rather than random noise.

  2. The improvements may not hold beyond the 102 tasks used for selection. The same 102 tasks are used both to decide which harness and model to keep and to report the final results. It is likely that this method is simply overfitting the 102 tasks. As demonstrated in Fig 4, on TB 2.1, the SFT checkpoint performs on par with the base model (18.3 vs. 18.7), and the RL checkpoint is about one task higher. On SWE-bench Lite, the SFT checkpoint underperforms the base model under both harnesses (e.g., 24.7% vs. 34.7% using mini-swe-agent).

Questions for authors

Please refer to the weaknesses part.

4 comments
AuthorsOpenReview ↗

Response to Reviewer BPKq (1/2)

Thank you for recognizing the timely problem, simple method, and transparent experimental record. We added repeated independent-test evaluations and nine new SFT training runs to directly examine reliability and generalization.


W1: Each configuration is run only once, the number of tasks are only 114. It is hard to tell whether each accepted update reflects a real improvement or noise. For example, according to Appendix B.5, the same 9B checkpoint scored 84 and then 88 when evaluated twice on the 102-task split. Results over multiple runs with different seeds are needed to verify if the improvement is from harness rather than random noise.

A: Our main question is whether the training recipe improves the policy, and we now test this with runtime fixed, on unseen tasks, across repeated executions and SFT training seeds. The added study separates the execution variability illustrated by Appendix B.5 from policy-training gains.

1. Repeated evaluations directly measure execution variability. We run each fixed configuration three times on the same independent 300 tasks, with identical decoding, serving, and execution limits.

Weights + harnessRun 1 / 2 / 3 (%)MeanGain over base; task 95% CI
Base + H074.3 / 72.3 / 77.374.7Reference
RL iteration 3 + H080.0 / 82.3 / 82.381.6+6.9 [+3.9, +9.9]
RL iteration 3 + H379.3 / 81.3 / 80.380.3+5.7 [+2.7, +8.8]
SFT θ1 + H276.0 / 74.7 / 76.075.6+0.9 [-2.3, +4.2]
Base + Hmix74.3 / 75.3 / 77.775.8+1.1 [-1.6, +3.9]

The RL policy exceeds the base in all three repeats under the same H0, and its paired task interval is entirely positive. The unchanged base has run-to-run SD 2.5 pp on this test. On the 102-task validation split it solves 72/75/80 tasks (SD 4.0 pp). The paper's 84/88 example re-evaluates the same post-RL3 pair; it documents execution variation rather than a model or harness update. The independent comparison above measures the policy gain after accounting for repeated task outcomes.

2. New training seeds test SFT optimization variability. We train nine checkpoints: three data arms × seeds 42/43/44, using common task coverage and aligned training settings. The H0 and R2c1 arms each contain 50 verified trajectories and exactly 556 prompt/completion pairs; all six checkpoints are cross-evaluated under both generating runtimes. The Hmix arm supplies the fixed-optimized-harness control.

For the H0-data models, evaluation under the same Hmix as the base gives:

Fixed evaluation runtime: HmixSeed 42 / 43 / 44 (%)Mean
Base weightsThree execution repeats75.8
Controlled SFT weights80.0 / 78.3 / 81.780.0

The policy improvement is +4.2 pp, with task CI [+1.2, +7.2] and seed-and-task CI [+0.7, +7.8]. The latter resamples both the paired seeds and tasks. Under H0, the same SFT models average 78.1%, with seed-and-task gain CI [-0.4, +7.3]; reporting both runtimes shows where the training gain is most consistent.

3. Model-fixed controls attribute the gain. With base weights unchanged, Hmix, H2, and H3 differ from H0 by +1.1, +1.1, and -0.2 pp, respectively, with task CIs including zero. In contrast, RL adds +6.9 pp under fixed H0, and controlled SFT adds +4.2 pp under fixed Hmix. These comparisons locate the strongest independent-test gains in the learned policy, directly addressing the distinction between component improvement and execution noise.

Task CIs use 10,000 paired bootstrap resamples of per-task execution averages. RL intervals describe the evaluated policy across tasks and repeated executions; SFT seed-and-task intervals additionally include the three training seeds. These are distinct from replication of complete search chains or RL training. The promotion split contains 102 tasks, rather than 114.


AuthorsOpenReview ↗

Response to Reviewer BPKq (2/2)

W2: The improvements may not hold beyond the 102 tasks used for selection. The same 102 tasks are used both to decide which harness and model to keep and to report the final results. It is likely that this method is simply overfitting the 102 tasks. As demonstrated in Fig 4, on TB 2.1, the SFT checkpoint performs on par with the base model (18.3 vs. 18.7), and the RL checkpoint is about one task higher. On SWE-bench Lite, the SFT checkpoint underperforms the base model under both harnesses (e.g., 24.7% vs. 34.7% using mini-swe-agent).

A: The fixed 102-task split is an intentional validation reference for component-wise promotion. Learning and harness search use other task pools; validation determines whether to retain a proposed update. Keeping this reference fixed makes successive comparisons interpretable without changes in task composition. The new independent test directly examines whether the resulting policies also improve on unseen tasks.

1. A frozen 300-task test with explicit task exclusion. We continue the sampling order used for the original split and exclude all 102 validation tasks and all 461 task IDs in project training, evolution, probe, or pilot records. From the next 400 eligible tasks, we retain the first 300 whose containers build and start. This feasibility filter uses no model outcomes. The manifest is frozen and hashed before evaluation, disjoint from the new SFT generation pools, and never used for checkpoint or harness promotion.

All new comparisons use the same re-provisioned GPU environment and container backend, greedy decoding, an 80-step limit, and 4,096 output tokens per turn. Agent errors count as failures; infrastructure retries preserve the configuration and follow documented setup/outage criteria independently of reward. Thus the reported comparisons use a common evaluation setting rather than historical scores from different environments.

2. Both RL and controlled SFT improve outside the validation tasks.

Comparison on the 300-task testPass rates (%)Gain; 95% CI
RL iteration-3 pair vs. base pair80.3 vs. 74.7+5.7 [+2.7, +8.8], task
RL vs. base weights, H0 fixed81.6 vs. 74.7+6.9 [+3.9, +9.9], task
Controlled SFT vs. base weights, Hmix fixed80.0 vs. 75.8+4.2 [+0.7, +7.8], seed and task
SFT θ1 + H2 vs. base pair75.6 vs. 74.7+0.9 [-2.3, +4.2], task

The gains persist when the evaluation harness is unchanged, separating policy improvement from a more favorable runtime. They occur on tasks excluded from both validation-based promotion and learning. This provides direct evidence against explaining the evaluated policy gains solely as overfitting the 102 validation tasks.

Checkpoint mapping. The SFT row is Table 3's θ1 + H2: the policy trained in iteration 1 and paired with the harness adopted at iteration 2's stage B. The controlled SFT rows are new three-seed experiments. The RL policy was promoted after iteration 3; the fourth proposal was rejected (Table 8), so this is the last promoted RL policy. We evaluate it under H3 and H0; the paper's 90/102 point uses the later H4 pairing. This mapping ties the new evidence to the reported stages.

3. External transfer answers a complementary question. TB 2.1 and SWE-bench Lite change both the task distribution and, in some settings, the runtime interface. SFT is similar to the base on TB 2.1. On SWE-bench Lite, its scores are 24.7% versus 34.7% with mini-swe-agent and 35.0% versus the base pair's 37.3% with co-evolved pairings; RL reaches 41.0% versus 37.3% (p = 0.16).

For fixed SFT weights, changing only the runtime yields 24.7% → 35.0%, a 10.3 pp recovery. This supports the paper's compatibility finding: a policy's execution performance depends on the runtime interface. The independent Tmax test establishes in-domain policy gains, while the external tests characterize transfer under domain and runtime shifts. Reporting both makes the scope of each conclusion explicit.


The added study includes a frozen independent 300-task test, three execution repeats per fixed configuration, nine SFT training runs across three seeds per data arm, and model-fixed harness controls. W1 reports repeatability and component attribution; W2 reports task exclusions, held-out gains, and correspondence to the paper's checkpoints. These results directly address reliability and generalization. We would appreciate your reassessment in light of the new evidence.

Reviewer_BPKqOpenReview ↗

Response to rebuttal

Thank you for the detailed response and the new held-out experiments. The results show that the RL policy improves on held-out Tmax tasks, which partially addresses my concerns.

However, several issues remain. For W1, the model-fixed controls show that the optimized harnesses (Hmix, H2, H3) do not significantly improve over H0, and the RL policy performs slightly better under H0 than under the co-evolved H3. This suggests that the harness updates cannot be distinguished from noise, which weakens the motivation for co-evolution. The RL training and the search chain are also still run only once.

For W2, the original SFT checkpoint (theta1 + H2) improves by only 0.9 points on the held-out test, so the SFT gain on the 102 validation tasks does not transfer. On external benchmarks, SFT still does not improve over the base model, and the RL gain on SWE-bench Lite is not significant.

Thus I remain my original score.

AuthorsOpenReview ↗

Response to Reviewer BPKq

Thank you for the follow-up and for recognizing the RL improvement on held-out Tmax. We would like to clarify three distinctions that are important for interpreting the additional results.

1. Execution noise and full-chain replication concern different evidence.

The held-out policy improvement is supported by repeated evaluations with the runtime fixed. Under H0, the base scores 74.3/72.3/77.3%, while the RL policy scores 80.0/82.3/82.3%. The mean improvement is +6.9 pp, with a paired task-bootstrap 95% CI of [+3.9, +9.9]. Thus, the evaluated policy's gain persists across all three executions and on tasks excluded from both learning and promotion.

The successive co-evolution rounds provide evidence of cumulative optimization within the reported chain, and the held-out repetitions separately test the resulting policy's execution reliability. Replicating the complete training-and-search chain would measure another source of variation and requires repeating the full multi-round computation.

2. The harness-only results should be distinguished from the policy-training results.

The harness controls quantify the independent-test effects of the particular runtime changes. Their intervals include zero, so they do not establish a positive harness-only effect. However, this does not explain away the positive policy gains under an unchanged runtime: RL improves by +6.9 pp under H0, and controlled SFT improves by +4.2 pp under Hmix.

Our contribution concerns how experience is routed and used for policy training as the runtime evolves. Component-wise evaluation is important precisely because model and harness updates need not contribute equally. The results identify a clear policy-training benefit while separately reporting the measured harness effects.

3. The early SFT checkpoint and the controlled SFT study answer different questions.

The θ1 + H2 row is the iteration-1 SFT policy paired with the iteration-2 harness, rather than the later SFT policy. Its +0.9 pp estimate therefore characterizes that specific early configuration.

The new controlled study tests the SFT recipe across three training seeds. With Hmix held fixed, the trained policies score 80.0/78.3/81.7%, versus 75.8% for the base weights, yielding +4.2 pp with a seed-and-task CI of [+0.7, +7.8]. This provides positive held-out evidence for SFT policy learning, separately from the early-checkpoint result.

The external benchmarks additionally assess cross-domain transfer, where the outcomes differ across settings. They do not negate the independent in-domain gains demonstrated above.

We would appreciate clarification on whether these results resolve the concern that the reported policy improvements are attributable solely to validation selection or execution noise, separately from the remaining question of full-chain reproducibility.

Reviewer_Fo5BOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper studies how to construct and utilize training data during harness–model co-evolution for terminal agents. The authors propose CoTrace, a harness-aware data recipe within an alternating optimization framework that updates the agent harness and model weights separately. CoTrace consists of three main mechanisms: (1) Route, which directs execution failures toward harness improvement and selects runtime-matched successful trajectories for model training; (2) Ratchet, which independently evaluates and promotes harness and model updates based on a fixed validation split; and (3) Refresh, which dynamically updates the training task pool by retiring solved tasks and introducing new ones.

The authors evaluate CoTrace on Tmax using Qwen3.5-9B and Qwen3.5-4B models, with both SFT and online RL training. On the 102-task promotion split, CoTrace-SFT improves the 9B model–harness pair from 78 to 88 solved tasks, while CoTrace-RL reaches 90. The experiments also compare different trajectory construction strategies, showing that harness-matched supervision yields accepted model updates where pooling successful trajectories across candidate harnesses does not. Additional evaluations on Terminal-Bench 2.1 and SWE-bench Lite investigate cross-domain transfer and demonstrate the influence of harness compatibility on model performance.

Critical strengths
  1. Practically relevant problem formulation.

The paper addresses an important practical challenge in terminal-agent training: how to manage trajectory data when both the model and its execution harness evolve over time. The emphasis on trajectory provenance and runtime compatibility is meaningful, as changes in prompts, tools, and observation processing can affect the usefulness of collected training data. This provides a useful perspective on the interaction between harness optimization and model training.

  1. Comprehensive experimental analysis of co-evolution dynamics.

The paper provides detailed experimental records across SFT and RL settings, including component-wise promotion decisions, accepted and rejected updates, and comparisons of different trajectory construction strategies. The cross-harness evaluations on external benchmarks are particularly informative, illustrating how the same model checkpoint can exhibit substantially different performance under different execution runtimes. These analyses offer useful empirical insights into harness–model interactions beyond reporting aggregate performance improvements.

Critical weaknesses
  1. Limited methodological novelty and overstated framework contribution.

The paper presents its inspectable co-evolution framework as a primary contribution, emphasizing separate tracking of harness and model updates, trajectory provenance logging, and component-wise promotion decisions. However, these mechanisms largely reflect standard experimental and engineering practices for maintaining reproducibility, controlling variables, and evaluating component-wise improvements. While their integration into a co-evolution pipeline is practically useful, it is unclear why such practices constitute a substantial methodological contribution rather than necessary elements of a rigorous experimental setup. More broadly, the proposed data recipes also rely on relatively intuitive principles, such as matching training trajectories to the deployment harness and refreshing the task curriculum, further limiting the methodological novelty of the work.

  1. Insufficient isolation of the core contribution.

The comparison between Mixed Siblings and CoTrace-SFT simultaneously changes several factors, including harness provenance matching, prompt conditioning, per-task sampling caps, trajectory freshness, task coverage, and historical replay. Consequently, the observed differences in model-side gains cannot be conclusively attributed to provenance matching alone, which is presented as a central motivation of the work. A more controlled ablation that isolates harness matching while holding the other data construction choices fixed would substantially strengthen the main claim.

  1. Limited independent evaluation of generalization.

The main performance gains are reported on the same 102-task promotion split repeatedly used to select harness and model updates, potentially introducing selection bias given the reported evaluation variance. Although the authors provide evaluations on external benchmarks, the transfer results are less conclusive. On SWE-bench Lite, CoTrace-SFT under its co-evolved harness underperforms the base model–harness pair (35.0% vs. 37.3%). While CoTrace-RL achieves a higher resolved rate than the base pair (41.0% vs. 37.3%), the difference does not reach statistical significance under the reported paired McNemar test (p = 0.16). An additional held-out Tmax test set, not used for promotion decisions, would provide stronger evidence that the reported gains generalize beyond the selection split.

Questions for authors

Benefit of alternating harness–model co-evolution.

The proposed framework alternates between harness optimization and model training, but the incremental benefit of this alternating procedure remains unclear. How would CoTrace compare against a simpler two-stage baseline that first optimizes the harness and then keeps it fixed during subsequent SFT or RL, under a comparable compute budget? Such a comparison would help clarify whether alternating co-evolution provides meaningful advantages over harness-aware model training with a fixed, optimized harness.

4 comments
AuthorsOpenReview ↗

Response to Reviewer Fo5B (1/3)

Thank you for recognizing the practical motivation and detailed analysis. We address your concerns regarding contribution and attribution as below.


W1: Limited methodological novelty and overstated framework contribution.

The paper presents its inspectable co-evolution framework as a primary contribution, emphasizing separate tracking of harness and model updates, trajectory provenance logging, and component-wise promotion decisions. However, these mechanisms largely reflect standard experimental and engineering practices for maintaining reproducibility, controlling variables, and evaluating component-wise improvements. While their integration into a co-evolution pipeline is practically useful, it is unclear why such practices constitute a substantial methodological contribution rather than necessary elements of a rigorous experimental setup. More broadly, the proposed data recipes also rely on relatively intuitive principles, such as matching training trajectories to the deployment harness and refreshing the task curriculum, further limiting the methodological novelty of the work.

A: CoTrace addresses how experience should be used when both policy and runtime change. A successful search rollout is not automatically suitable policy supervision: its provenance and verification determine its role. CoTrace makes these data-routing decisions explicit and tests their training consequences. Provenance tracking and separate promotion make the resulting model–harness interaction measurable.

CoTrace routes failures to harness repair, uses verified runtime-matched successes for SFT, and refreshes the training-task frontier. Its online RL variant instead learns from fresh interactions and rewards under the adopted runtime, including unsuccessful interactions.

The added independent 300-task test and controlled SFT experiments directly measure the recipe's model-training benefit. With only 50 verified trajectories, SFT improves over base weights by +4.2 pp under the same optimized harness Hmix (seed-and-task 95% CI [+0.7, +7.8]). The last promoted RL policy improves by +6.9 pp under the unchanged H0 (task CI [+3.9, +9.9]).

These results establish policy improvements with deployment runtime held fixed. CoTrace makes experience collected during co-evolution useful for policy learning and makes each component's contribution measurable. The provenance ablation below further separates the matching contrast from the complete recipe's effect.


W2: Insufficient isolation of the core contribution.

The comparison between Mixed Siblings and CoTrace-SFT simultaneously changes several factors, including harness provenance matching, prompt conditioning, per-task sampling caps, trajectory freshness, task coverage, and historical replay. Consequently, the observed differences in model-side gains cannot be conclusively attributed to provenance matching alone, which is presented as a central motivation of the work. A more controlled ablation that isolates harness matching while holding the other data construction choices fixed would substantially strengthen the main claim.

A: The original comparison evaluates complete data-construction recipes, including how each uses experience collected during harness search. To measure provenance separately, we added a task-paired ablation with the same generating policy, 50 common-success tasks, one fresh collection campaign, no replay, identical per-task pair counts (556 pairs per arm), serializer, LoRA settings, and paired seeds 42/43/44. Completion-character counts are within 3.3%.

Only the generating harness changes: adopted H0 versus candidate R2c1. Both use exactly the same system prompt and tool schema; R2c1 changes loop detection and lifecycle self-verification. All six trained checkpoints are evaluated under both runtimes on the independent 300-task test.

Training dataEvaluate under H0Evaluate under R2c1
H080.7 / 76.0 / 77.7 (78.1)77.3 / 75.7 / 76.7 (76.6)
R2c177.0 / 76.7 / 76.3 (76.7)78.0 / 76.3 / 73.7 (76.0)

Cells give seeds 42/43/44 and the mean. Under H0, matched data lead by +1.4 pp (task CI [-1.3, +4.2]; seed-and-task CI [-2.4, +5.6]). The mean diagonal-minus-off-diagonal matching advantage is +0.4 pp (seed-and-task CI [-2.2, +3.1]).

The ablation favors matched data by +1.4 pp under H0 and quantifies its uncertainty through both intervals. Together with the +4.2 pp policy gain under fixed Hmix, it provides two complementary results: the compact recipe produces useful policy updates, and the controlled provenance contrast measures the additional effect of matching within a shared prompt/tool interface.


AuthorsOpenReview ↗

Response to Reviewer Fo5B (2/3)

W3: Limited independent evaluation of generalization.

The main performance gains are reported on the same 102-task promotion split repeatedly used to select harness and model updates, potentially introducing selection bias given the reported evaluation variance. Although the authors provide evaluations on external benchmarks, the transfer results are less conclusive. On SWE-bench Lite, CoTrace-SFT under its co-evolved harness underperforms the base model–harness pair (35.0% vs. 37.3%). While CoTrace-RL achieves a higher resolved rate than the base pair (41.0% vs. 37.3%), the difference does not reach statistical significance under the reported paired McNemar test (p = 0.16). An additional held-out Tmax test set, not used for promotion decisions, would provide stronger evidence that the reported gains generalize beyond the selection split.

A: The 102-task split is deliberately used as a fixed validation reference for component-wise promotion. Keeping the tasks fixed makes successive model and harness proposals comparable, without changes in task composition confounding retention decisions. Training and harness search use separate tasks, keeping candidate construction disjoint from validation.

To independently assess the resulting policies, we added a frozen 300-task Tmax test, excluding the 102 validation tasks and all 461 task IDs in project learning/search/probe/pilot records. The split is also disjoint from the new SFT pools; no promotion uses it.

SystemPass rateGain over base; task 95% CI
Base weights + H074.7Reference
SFT θ1 + H275.6+0.9 [-2.3, +4.2]
RL iteration-3 weights + H380.3+5.7 [+2.7, +8.8]
Same RL weights + H081.6+6.9 [+3.9, +9.9]

Each row averages three executions. SFT is Table 3's θ1 + H2: the iteration-1 policy with the iteration-2 harness. The RL policy was promoted after iteration 3; Table 8 rejects the fourth RL proposal, making this the last promoted RL policy.

These results demonstrate RL policy gains on unseen tasks with H0 fixed. The three-seed SFT study independently yields +4.2 pp under fixed Hmix (seed-and-task CI [+0.7, +7.8]). Table 3's earlier SFT pair is reported separately, with its +0.9 pp estimate and confidence interval.

External evaluation tests a further domain/runtime shift: SWE-bench Lite scores are 35.0% versus 37.3% for SFT and 41.0% versus 37.3% for RL (p = 0.16). Changing only the SFT runtime recovers 10.3 pp (24.7% to 35.0%), supporting the importance of runtime compatibility. The new Tmax test separately establishes in-domain policy generalization.


AuthorsOpenReview ↗

Response to Reviewer Fo5B (3/3)

Q1: Benefit of alternating harness–model co-evolution.

The proposed framework alternates between harness optimization and model training, but the incremental benefit of this alternating procedure remains unclear. How would CoTrace compare against a simpler two-stage baseline that first optimizes the harness and then keeps it fixed during subsequent SFT or RL, under a comparable compute budget? Such a comparison would help clarify whether alternating co-evolution provides meaningful advantages over harness-aware model training with a fixed, optimized harness.

A: We examine the two update steps through SFT under frozen optimized Hmix and a model-fixed Hmix/H2 comparison.

Hmix was optimized with the base policy fixed. We freeze it, generate data on the same 50 tasks as H0-data SFT, and use identical training settings and seeds 42/43/44. All rows use the same evaluation harness Hmix.

Training dataSeed 42 / 43 / 44Mean
H080.0 / 78.3 / 81.780.0
Hmix78.0 / 80.3 / 76.078.1
Base weightsThree execution repeats75.8

The H0-data policy improves by +4.2 pp over base weights under fixed Hmix (seed-and-task CI [+0.7, +7.8]). Hmix-data minus H0-data is -1.9 pp (seed-and-task CI [-6.8, +3.0]). The corpora contain 529 versus 556 pairs; Hmix has 7.5% fewer completion characters. Tasks and training settings are aligned.

We also evaluate whether H2, adopted after the first policy update, improves over Hmix with weights fixed:

WeightsHmixH2H2 minus Hmix; task CI
Base75.875.80.0 [-2.8, +2.9]
SFT θ175.775.6-0.1 [-2.9, +2.8]

These controls identify a +4.2 pp policy-training benefit under an optimized runtime, alongside a -0.1 pp post-update harness contrast. This component-level result also motivates CoTrace's separate promotion decisions: policy and harness changes should be evaluated on their own merits. We will report the fixed-harness settings and both component comparisons explicitly.

AuthorsOpenReview ↗

Follow-up to Reviewer Fo5B

Thank you again for your constructive review. We would like to follow up and invite you to revisit our rebuttal and the additional experimental evidence, particularly regarding the concerns raised in your review.

Since the initial submission, we have added substantial new experiments, including:

  • Independent generalization: A frozen 300-task Tmax test, showing a +6.9 pp RL policy improvement under a fixed harness (95% CI [+3.9, +9.9]), and a +4.2 pp controlled SFT improvement across three training seeds (95% CI [+0.7, +7.8]).
  • Final SFT checkpoint: The final θ5 checkpoint achieves 78.3% on the independent test, compared with 74.7% for the base system (one preliminary evaluation).
  • Contribution and attribution: A controlled provenance ablation and fixed-harness comparisons, together with a clarification that CoTrace's central contribution is harness-aware experience management, rather than attributing all improvements to provenance matching alone.
  • Alternation versus fixed-harness training: Additional controls that distinguish policy-training gains from harness-only effects.

We have also posted a general response clarifying the scope of our contribution and its relationship to recent co-evolution research, including data efficiency and compute budgets.

We would greatly appreciate your thoughts on whether these additional results address your original concerns. If they do, we would be grateful if you could reconsider your assessment. We would also be happy to clarify any remaining questions during the discussion period.

Comments on the paper

4 comments
AuthorsOpenReview ↗

General Comment to All Reviewers and the Area Chair (1/1)

We sincerely thank all reviewers and the area chair for their thoughtful and constructive feedback. We appreciate their recognition of the following strengths:

  • A timely and practically relevant problem (Fo5B, BPKq): managing training experience as both policy and harness evolve.
  • An interesting focus on trajectory provenance and runtime compatibility (Fo5B, BPKq, hsZk).
  • Thoughtful and transparent experimental analysis (Fo5B, BPKq, hsZk): component-wise evaluation, promotion records, and cross-harness comparisons.

To address the main concerns, we added an independent 300-task Tmax test, three executions per fixed configuration, three training seeds per controlled SFT arm, a task-paired provenance ablation, and fixed-harness controls.

ConcernAdded experimentFinding
Generalization beyond promotion validation (Fo5B W3; BPKq W2; hsZk W2/Q2)Frozen 300-task test disjoint from promotion and learningRL gains +6.9 pp with H0 fixed; controlled SFT gains +4.2 pp with Hmix fixed
Provenance attribution (Fo5B W2; hsZk W1/Q1)Same 50 tasks, policy, freshness, pair counts, prompt/tools, and training settingsMatched data lead by +1.4 pp under H0; seed-and-task CI [-2.4, +5.6]
Noise and robustness (BPKq W1; hsZk Q2)Execution repeats and paired SFT training seedsQuantified execution and training variation; positive fixed-runtime policy comparisons
Alternation versus fixed-harness training (Fo5B Q1)SFT with optimized Hmix frozen; model-fixed Hmix/H2 comparisonSFT adds +4.2 pp under Hmix; post-update harness contrast is -0.1 pp
Contribution framing (Fo5B W1)Controlled data and component comparisonsPractical data recipe and empirical evidence for useful compact-data policy updates

Key independent-test results. Pass rates are percentages; gains are percentage points (pp). Task intervals use paired bootstrap resampling; seed-and-task intervals additionally resample the controlled SFT training seeds.

ComparisonPass ratesGain and 95% CI
RL iteration-3 weights vs. base weights, H0 fixed81.6 vs. 74.7+6.9 [+3.9, +9.9], task
RL iteration-3 pair vs. base pair80.3 vs. 74.7+5.7 [+2.7, +8.8], task
Controlled SFT vs. base weights, Hmix fixed80.0 vs. 75.8+4.2 [+0.7, +7.8], seed and task
SFT θ1 + H2 vs. base pair75.6 vs. 74.7+0.9 [-2.3, +4.2], task

Checkpoint correspondence. SFT θ1 + H2 is the Table 3 pair: the iteration-1 policy with the harness adopted at iteration 2's stage B. The RL policy was promoted after iteration 3; the fourth RL proposal was rejected (Table 8), making it the last promoted RL policy. We test it with H3 and H0; its later H4 pairing produces the 90/102 validation point. The newly trained controlled SFT models are reported separately.

Shared protocol. A fixed validation set provides a consistent promotion reference; separate tasks supply training and harness-search experience. The independent test excludes the 102 promotion tasks and all 461 task IDs in project learning/search/probe/pilot records. Following the original sampling order, we retain the first 300 of the next 400 eligible tasks whose containers build and start. This model-independent filter and the test manifest are fixed before evaluation; the test is also disjoint from the new training-data pools. No promotion is performed on this split.

All new comparisons share a re-provisioned GPU environment and reimplemented container backend, greedy decoding, an 80-step cap, and 4,096 output tokens per turn. Agent errors count as failures; documented infrastructure failures are retried with the same configuration, independently of reward. Fixed-system task CIs use 10,000 paired bootstrap resamples over three execution averages and are conditional on the evaluated checkpoints. Controlled SFT uses paired seeds 42/43/44. Execution repeats, SFT training seeds, and complete search-chain repetition measure different sources of variation.

Dear Reviewers,

We're the half-way through the discussion phase. The authors have provided their response to your reviews. Please engage with the authors as soon as possible, we need to keep the conversation going!

Many thanks,

AC

AuthorsOpenReview ↗

General Response to Reviewers and Area Chair about Common Concerns Follow-up (1/2)

What CoTrace Contributes and How to Interpret Matching

We would like to clarify a recurring question across the reviews: is harness-provenance matching the decisive cause of CoTrace's gains? This is not the claim our paper sets out to establish. Our motivating question (Introduction, lines 43–47) is how execution data should flow between policy learning and harness optimization when both change over time.

CoTrace's contribution is not that provenance matching alone explains every improvement, but that explicitly managing the roles and reuse of execution experience enables effective policy adaptation throughout harness–model co-evolution. More concretely, our focus is not merely generating more experience during co-evolution, but making better use of the experience it produces.

This requires a coordinated data recipe, not one binary matching decision. Route uses recurring runtime failures to guide harness repair, while constructing policy supervision from verified successful traces (or fresh interactions and rewards for online RL). Refresh retires solved-and-harvested tasks and moves learning toward the residual frontier. Ratchet evaluates model and harness updates separately, preventing a gain in one component from being misattributed to the other. Provenance is an important variable within Route, but the complete recipe also controls verification, task coverage, freshness, per-task sampling, and replay.

What the matching ablation establishes. In response to the request for isolation, we compared H0 and R2c1 using the same 50 common-success tasks, 556 pairs per arm, prompt and tool schema, collection freshness, training settings, and three paired seeds. The H0 deployment contrast is +1.4 pp (matched vs. R2c1-generated data); the R2c1 deployment contrast is −0.6 pp. Averaging them gives +0.4 pp, with a seed-and-task 95% CI of [−2.2, +3.1]. This is a valid but statistically inconclusive average interaction contrast, not a measure of the full CoTrace recipe's improvement. It averages effects with opposite signs and does not show a reliable standalone matching benefit in this setting. Furthermore, H0 and R2c1 share the system prompt and tool schema and differ in loop detection and lifecycle self-verification; this is a deliberately narrow runtime intervention, not a test of every interface shift during co-evolution.

Our original Mixed Siblings vs. CoTrace-SFT comparison instead tests complete data-construction recipes: on the 9B validation split, Mixed Siblings consumes 149–308 trajectories/iteration yet yields 0/3 accepted model updates, whereas CoTrace-SFT uses 30–50 trajectories/iteration and obtains 2/5 accepted updates, totaling +6 solved tasks through the model channel (Tables 1–2). We do not attribute this entire difference causally to matching alone: freshness, coverage, prompt conditioning, per-task caps, and replay also change. The key observation is that more successful search trajectories do not automatically produce more useful policy-training data.

This broader concern is consistent with emerging independent evidence. Yu et al. (2026) [1], find that imitating complete expert trajectories under an evolved harness can regress performance by 4–30 pp across seven enterprise tasks, because learned behavior disrupts model–harness fit; they instead use on-policy correction. HarnessForge (Chen et al., 2026) [2] independently studies harness-conditioned policy alignment. These are related evidence of the importance of behavioral/runtime compatibility, not direct replications of our H0/R2c1 provenance effect.

We will revise the abstract, contributions, and RQ2 discussion to separate the complete recipe's observed effect from the uncertain isolated matching contrast, so neither the ablation nor our central claim is overstated.

References
[1] Yu et al. (2026). Co-Evolving Harnesses and Models: On-Policy Correction Helps Weaker Models Catch Up Where Imitation Fails. arXiv:2609.09134. https://arxiv.org/abs/2609.09134
[2] Chen et al. (2026). HarnessForge: Joint Harness and Policy Evolution for Adaptive Agent Systems. EMNLP 2026. https://aclanthology.org/2026.emnlp-main.1893/

AuthorsOpenReview ↗

General Response to Reviewers and Area Chair about Common Concerns Follow-up (2/2)

Compute, Held-Out Improvements, and Scope

A second concern is whether the measured improvements are meaningful given their scale and generalization. Our results should be assessed alongside the amount and role of training experience, not by validation gains alone. CoTrace targets data management in expensive, long-horizon, containerized terminal-agent execution, where harness search, full rollouts, and evaluation dominate the cost of a small SFT update.

The paper already reports a concrete within-study compute comparison. For Qwen3.5-9B, Table 1 and Appendix B.4 report 47 GPU-hours per iteration for CoTrace-SFT, versus 54 GPU-hours per iteration for Mixed Siblings, on the paper's recorded eight-GPU-node accounting (~13% lower per iteration). CoTrace-SFT obtains +6 cumulative model-channel tasks, while Mixed Siblings obtains zero, despite drawing from more successful search trajectories. The LoRA gradient step is only ~4% of the reported chain compute; search, verification, and evaluations dominate. Importantly, these are per-iteration numbers: the full five-iteration CoTrace-SFT chain costs approximately 235 GPU-hours, versus 162 GPU-hours for the three-iteration Mixed Siblings chain. We therefore claim more productive model-side learning with a compact data recipe, not lower total end-to-end compute for those unequal-length chains. The recorded CoTrace-RL chain is 4 × 62 ≈ 248 GPU-hours with 2,304 online RL episodes (Tables 1–2, Appendix B.4).

This efficiency perspective is relevant to recent work, while acknowledging non-identical settings. HarnessForge [3] reports 12K SFT rollouts and 45.6K RL-style rollouts in the cited configurations. CoHARL [4] (October 2026) uses a population-based RL protocol with 150 steps × 48 nominal rollout slots/step, in addition to harness proposal and validation. Zhang et al., Knowledge in the Harness, Reliability in the Weights [5] (November 2026) report ~50K conversations and ~340 GPU-hours per round, over two rounds. These works differ in domain, model, environment, rollout definition, and accounting; we do not claim a matched-budget superiority or equate 50 SFT demonstrations with another paper's entire co-evolution budget. They illustrate why improving the utility of costly interactions is a substantive goal in its own right.

The newly added held-out evidence strengthens that claim. On a frozen 300-task Tmax test, disjoint from the 102 promotion tasks and the project learning/search/probe/pilot task IDs:

  • RL policy, H0 fixed: 81.6% vs. 74.7% base, +6.9 pp, paired task-bootstrap 95% CI [+3.9, +9.9], across three executions per configuration.
  • Controlled SFT, Hmix fixed: 80.0% vs. 75.8% base, +4.2 pp, seed-and-task 95% CI [+0.7, +7.8], with just 50 verified trajectories / 556 prompt-completion pairs and three training seeds.
  • Final SFT θ5: 78.3% (235/300) vs. 74.7% base, an observed +3.6 pp. Unlike the repeated base reference, θ5 has one evaluation execution so far; this is preliminary and we do not claim a significant gain from this result alone.

The original SFT θ1+H2 and the final θ5 are different checkpoints; their test numbers should not be conflated. Likewise, in-domain held-out generalization is distinct from cross-domain transfer: we transparently report mixed Terminal-Bench 2.1/SWE-bench Lite results. In SWE-bench Lite, keeping SFT weights fixed while replacing mini-swe-agent with the co-evolved harness changes success from 24.7% to 35.0%, illustrating that runtime choice can materially affect observed transfer, without proving a universal matching benefit.

Finally, WHALE [6] (2026) finds that bottlenecks can be harness-dominant or policy-dominant depending on the task. This aligns with our reason for evaluating component updates separately: co-evolution does not require each harness edit and each policy update to contribute equally or significantly on every split. Our strongest held-out evidence is currently on the policy side. We will make these distinctions, costs, checkpoint identities, and limitations clearer in the revised manuscript and provide code and evaluation details for inspection.

References
[3] Chen et al. (2026). HarnessForge: Joint Harness and Policy Evolution for Adaptive Agent Systems. EMNLP 2026. https://aclanthology.org/2026.emnlp-main.1893/
[4] CoHARL: Co-Evolving Agent Policies and Executable Harnesses with Reinforcement Learning. (2026). arXiv:2610.36469. https://arxiv.org/abs/2610.36469
[5] Zhang et al. (2026). Knowledge in the Harness, Reliability in the Weights: Teacher-Free Co-Evolution of an LLM Agent. arXiv:2611.15268. https://arxiv.org/abs/2611.15268
[6] WHALE: A Simple Recipe for Joint Harness-Weight Optimization. (2026). arXiv:2609.00196. https://arxiv.org/abs/2609.00196

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.