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Under review as a conference paper at ICLR 2027

CCL: Counterfactual Contract Learning for Local Execution Recovery in Embodied Multi-Agent Collaboration

Abstract

In embodied multi-agent collaboration, agents must coordinate their actions since completing one action may depend on unfinished work by another agent. Existing approaches use execution feedback to revise plans and generate recovery actions. However, resolving the immediate failure does not ensure completion of the affected subtask. Such corrections require verification before they can serve as successful training examples. We propose Counterfactual Contract Learning (CCL), which learns coordinated repair programs from alternatives verified against a contract specifying the local goal and previously satisfied conditions to preserve. Specifically, we initialize a repair model through supervised fine-tuning on verified programs. The model then generates a direct repair and samples alternatives from the same input. By replaying these programs from the same saved state under the fixed contract, we identify successful alternatives to failed direct repairs as training targets. During training, CCL aligns the paired programs and emphasizes the first differing action, while weaker supervision on subsequent actions teaches complete repairs. For evaluation, we construct PARTNR-FS, a benchmark of recorded failure states with verified repair examples. CCL improves strict recovery rates over Repair-SFT across four language models and, when integrated into CoELA and PCE, improves final object transport and transport progress on TDW-MAT.

Primary area:
applications to robotics, autonomy, planning
Keywords:
embodied intelligence, multi-agent collaboration, local execution recovery, large language models, post-training, counterfactual learning, localized supervision

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_SxCvOpenReview ↗
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2
Confidence
3
Informativeness
2
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2
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Paper summary

This paper introduces Counterfactual Contract Learning (CCL), a framework for training language models to generate local recovery programs for embodied multi-agent collaboration. The authors construct PARTNR-FS, a benchmark of execution failure states with verified recovery programs. CCL first initializes a repair model through supervised fine-tuning, then generates direct and alternative repair programs from the same failure state. Successful alternatives are identified using simulator replay and fixed recovery contracts. The learning objective emphasizes the first divergent action between unsuccessful and successful programs, while retaining weaker supervision on subsequent actions and a separate preservation objective.

Experiments evaluate four language model backbones, several repair baselines, and integration with cooperative controllers on TDW-MAT.

Critical strengths
  1. Meaningful recovery evaluation.The paper distinguishes executable actions from repairs that actually restore the affected task goal while preserving previously completed work. The contract-based replay protocol provides a useful way to evaluate recovery outcomes beyond action validity.

  2. Reasonably broad empirical evaluation.The authors evaluate multiple language model backbones, include relevant learning-based repair baselines, and demonstrate integration with two cooperative controllers. The appendix also provides additional supervision-scope controls that help examine the proposed training mechanism.

Critical weaknesses
  1. Limited methodological novelty and insufficient evidence for the proposed credit-assignment mechanism.

The overall approach primarily combines established components: supervised fine-tuning, sampling alternative programs, simulator-based success verification, and token-level loss reweighting. The main methodological distinction is emphasizing the first divergent action between unsuccessful and successful repairs. However, this divergence is a syntactic alignment heuristic rather than an identified causal contributor to recovery.

More importantly, Appendix I.1 shows that ordinary full-response cross-entropy training on verified alternatives already achieves 43.90% strict recovery, compared with 47.54% for CCL. Supervising all modified actions achieves 46.27%. Thus, while verified repair training is useful, the incremental benefit attributable to the proposed localization strategy is relatively modest. The paper does not provide sufficiently strong statistical evidence establishing the robustness of these small differences.

Consequently, I am not convinced that the proposed training objective represents a sufficiently substantial methodological advance over existing verification-guided imitation or repair learning.

  1. Limited evidence for robustness and generalization beyond the constructed recovery setting.

PARTNR-FS contains 183 test failure states, selected from cases with verified recovery programs within a five-skill-call limit. The main improvements are uneven across failure categories, with relatively small gains on reachability failures and larger percentage gains on categories containing only 20 and 9 test states.

In addition, the primary backbone experiments do not establish training-seed robustness across all four models. The complete-task TDW-MAT evaluation uses only 24 episodes, and the CCL repair model is separately updated using TDW-MAT training data. Therefore, this evaluation demonstrates adaptation to a second environment rather than zero-shot cross-environment transfer.

The improvements are encouraging, but the current evidence is insufficient to establish that the proposed mechanism generalizes reliably to more diverse execution failures or that its incremental gains persist across independent training runs.

Questions for authors

Q1. Can the authors provide paired, episode-aware statistical comparisons between CCL, full-response CE, and the modified-action supervision variant in Appendix I.1? In particular, how stable is the improvement specifically attributable to first-divergence supervision across independent training seeds?

Q2. Can the authors clarify the practical advantage of training a specialized repair model over inference-time repair using stronger general-purpose planners? Although larger proprietary models are included as direct-generation references, the experiments do not establish a matched online-cost comparison against stronger planners using additional feedback or refinement. How does the offline collection and verification cost affect this tradeoff?

Q3. Can the authors provide uncertainty estimates or paired episode-level results for the TDW-MAT improvements, especially the 2.50-percentage-point gain over PCE with SFT? This would help establish whether the complete-task advantage is robust.

7 comments
AuthorsOpenReview ↗

Rebuttal by Authors

We thank the reviewer for the valuable feedback. We have prepared a point-by-point response to the comments below. All modifications in the manuscript have been highlighted in blue.

Weakness 1: Limited methodological novelty and insufficient evidence for the proposed credit-assignment mechanism.

Response:

The contribution of CCL is not simply to train on successful trajectories. We pair a failed repair with a verified successful alternative from the same saved state, and use their difference to supervise recovery decisions. Verification requires completing the local goal while preserving previously completed work, rather than merely making the failed action executable.

The motivation for emphasizing the first divergence is straightforward. Before that action, the two programs share the same prefix. This is the first decision at which the successful alternative differs under the same preceding context. Analogous to autoregressive token generation, changing this decision can change subsequent predictions and execution states. We therefore emphasize this action without discarding the remaining corrective steps: the completion term supervises them with weight 0.25. We do not assume that the first divergent action alone explains the entire recovery.

The additional supervision controls examine this design:

SupervisionTest strict recovery (%)
Full-response CE43.90
All modified actions46.27
First divergence without completion supervision46.27
Random modified-action45.90
CCL47.54
Training SeedRandom modified-actionCCLDifference (pp)Paired 95% CI (pp)
18185/183 (46.45%)87/183 (47.54%)+1.09[−1.09, +3.28]
19382/183 (44.81%)86/183 (46.99%)+2.19[0.00, +4.92]
21185/183 (46.45%)88/183 (48.09%)+1.64[0.00, +3.83]

The random-position result indicates that the first divergence provides a simple, reproducible anchor for emphasizing a corrective decision while retaining supervision on the rest of the verified repair.

We have clarified the supervision rationale in Section 3.5 and added the matched controls to Section 4.4 and Table 4. Appendix I.1 provides the full supervision comparisons and the additional random modified-action control, making the evidence for this design explicit.

Weakness 2: Limited evidence for robustness and generalization beyond the constructed recovery setting.

Response: Thank you for identifying these distinctions.

Benchmark scope and category sizes. PARTNR-FS evaluates bounded local recovery within the five skill-call budget. This makes the evaluation target feasible and comparable across methods. However, it does not imply coverage of every possible execution failure. The category imbalance reflects the failure frequencies observed during our Train_2k collection process, rather than a deliberately balanced allocation. We agree that small categories require count-level interpretation. More importantly, its overall improvement also includes reachability (47 to 53/109), holding (23 to 25/45), and unsupported actions (10 to 15/20). Table 1 reports the category-wise recovery rates and subset sizes.

Training-seed variability. Our Qwen3-8B CCL runs use the same protocol with three independent training seeds. They achieve 87, 86, and 88 successes out of 183, respectively, with a mean strict recovery of 47.54%. The table below additionally reports three CCL training-seed runs for each of the other three backbones.

Training SeedQwen2.5-7BLlama3.1-8BQwen3-8BQwen3.5-9B
18174/183 (40.44%)80/183 (43.72%)87/183 (47.54%)98/183 (53.55%)
19373/183 (39.89%)80/183 (43.72%)86/183 (46.99%)96/183 (52.46%)
21176/183 (41.53%)80/183 (43.72%)88/183 (48.09%)99/183 (54.10%)

Generalization to TDW-MAT. This experiment evaluates adaptation to a second environment, not zero-shot transfer. We train the repair modules on TDW-MAT training data and evaluate complete-task performance on its 24 test episodes within CoELA and PCE. This tests whether the recovery-training approach remains useful in another environment and with different controllers.

We demonstrate that our method is not only useful for offline repair but also enhances performance during the execution of complete tasks.

We have added the analysis excluding Relation to Section 4.2 and the cross-backbone results to Appendix I.5. Section 4.5 now explicitly describes training on TDW-MAT data, and Table 5 reports complete-task performance. Appendix H.3 details the training data and controller integration.

AuthorsOpenReview ↗

Rebuttal by Authors

Question 1: Can the authors provide paired, episode-aware statistical comparisons between CCL, full-response CE, and the modified-action supervision variant in Appendix I.1? In particular, how stable is the improvement specifically attributable to first-divergence supervision across independent training seeds?

Response: Thank you for this suggestion. We provide additional comparisons using the same Qwen3-8B Repair-SFT initialization and training seeds 181, 193, and 211. All variants use the same update budget and unconstrained evaluation protocol.

Training seedFull-response CEModified-actionsCCL
18183/183 (45.36%)87/183 (47.54%)87/183 (47.54%)
19379/183 (43.17%)82/183 (44.81%)86/183 (46.99%)
21179/183 (43.17%)85/183 (46.45%)88/183 (48.09%)

The following intervals use 5,000 episode-cluster bootstrap resamples. We resample the source episodes with replacement and keep all states from each sampled episode together, recomputing the recovery-rate difference over the resampled states.

Training seedCCL − Full-response CE, 95% CI (pp)CCL − Modified-action, 95% CI (pp)
181+2.19 [+0.83, +5.59]0.00 [−2.99, +3.14]
193+3.83 [+1.09, +6.56]+2.19 [+0.83, +5.59]
211+4.92 [+2.19, +8.20]+1.64 [−1.72, +5.14]

CCL improves over full-response CE in all three runs, with paired 95% bootstrap confidence intervals excluding zero for each seed. Compared with modified-action supervision, CCL has higher point estimates for most seeds.

We have added the per-seed results and training-seed variability to Section 4.4 and Table 4. Section 4.1 and Appendix H.1 describe the episode-cluster bootstrap procedure, and Appendix I reports the paired intervals and supports the distinction between the two comparisons.

Question 2: Can the authors clarify the practical advantage of training a specialized repair model over inference-time repair using stronger general-purpose planners? How does the offline collection and verification cost affect this tradeoff?

Response: Thank you for raising this practical comparison. The intended advantage is to move recovery search and verification offline, allowing deployment through one local model call. To test whether a stronger planner can instead recover through additional inference-time computation, we evaluated GPT-5.6 Sol with both self-refinement and actual execution feedback on Test183.

MethodRecovery (%)Mean calls per repair request
GPT-5.6 Sol34.971.00
GPT-5.6 Sol + self-refinement44.263.00
GPT-5.6 Sol + execution feedback41.531.89
Qwen3-8B + CCL47.541.00
Qwen3.5-9B + CCL53.551.00

Self-refinement uses three calls: an initial program, a critique, and a revised program. The execution-feedback variant receives feedback from its executed actions and can make up to three decisions within five cumulative skill calls. Both reported scores require success under all three replay seeds.

These results show that the specialized repair model remains competitive with a stronger planner given additional refinement or execution feedback, while requiring fewer online model calls.

The offline cost is a genuine part of the tradeoff. Accordingly, our practical claim is lower online interaction overhead after training, rather than universally lower total cost. Whether training is economical depends on how often the repair model is subsequently used.

We have added the stronger-planner comparison to Section 4.3 and Table 3, with the inference protocols specified in Appendix H.2.

Question 3: Can the authors provide uncertainty estimates or paired episode-level results for the TDW-MAT improvements, especially the 2.50-percentage-point gain over PCE with SFT?

Response: Thank you for this suggestion. We now supplement the aggregate transport rates with paired results on the same 24 test episodes. For PCE, we compare Repair-SFT and CCL under the same controller protocol.

MetricPCE + Repair-SFTPCE + CCL
Mean transport rate210/240 (87.50%)216/240 (90.00%)
Fully successful episodes11/24 (45.83%)13/24 (54.17%)

CCL increases the mean transport rate from 87.50% to 90.00% compared with Repair-SFT. It also increases the number of fully successful episodes from 11/24 to 13/24, indicating an observed improvement on the same 24 test episodes.

We have added the paired episode-bootstrap 95% interval of [+0.83, +4.58] percentage points to Section 4.5. Appendix H.3 and Table H.2 provide the bootstrap procedure and all 24 paired episode outcomes.

Reviewer_SxCvOpenReview ↗

Response to the Authors' Rebuttal

Thank you for the detailed rebuttal and the additional experiments. I appreciate the authors' efforts to address my concerns, particularly the new paired statistical comparisons, multi-seed evaluations, stronger-planner baselines, and end-to-end results on TDW-MAT.

These additions substantially strengthen the empirical evaluation, and several of my original concerns have been meaningfully addressed.

1. Credit assignment and methodological contribution

The new three-seed comparisons provide useful evidence that CCL consistently outperforms full-response cross-entropy supervision. In particular, the paired bootstrap confidence intervals for CCL versus full-response CE exclude zero across all three training seeds. I acknowledge that this supports the effectiveness of the proposed supervision strategy relative to conventional full-response training.

However, my main concern regarding the independent contribution of first-divergence supervision remains.

Compared with modified-action supervision, the improvements across the three training seeds are 0.00, 2.19, and 1.64 percentage points. Two of the three paired confidence intervals include zero.

Similarly, the new random modified-action control achieves competitive performance. Although CCL obtains higher point estimates, the reported confidence intervals for the differences do not strictly exclude zero.

These results suggest that emphasizing modified actions within verified counterfactual repair pairs is useful, but they do not yet establish that selecting the first divergent action provides a consistently meaningful advantage over more general modified-action weighting strategies.

I appreciate the authors' clarification that the first divergence is intended as a practical supervision anchor rather than a complete causal explanation of recovery. This is a reasonable interpretation, but it also narrows the methodological claim.

2. Robustness, practical utility, and generalization

The additional training-seed results across four backbones substantially address my concern about training stability.

I also find the new GPT-5.6 Sol comparisons valuable. They provide evidence that a specialized repair model can achieve competitive or better recovery performance with fewer online model calls under the evaluated protocols. The authors' distinction between reduced online overhead and total amortized training cost is appropriate.

The additional TDW-MAT paired results and bootstrap confidence interval further strengthen the evidence for end-to-end utility in a second environment.

I appreciate the clarification that TDW-MAT involves environment-specific training rather than zero-shot transfer. The corresponding results should therefore be interpreted as evidence of applicability to another environment, not direct cross-environment generalization.

Overall, I consider these concerns substantially addressed within the stated evaluation scope.

3. Remaining assessment

My remaining reservation is primarily methodological rather than experimental.

The rebuttal provides stronger evidence that the overall CCL pipeline is useful: verified counterfactual repair pairs, contract-preserving replay, and targeted supervision together improve local recovery.

However, the results still do not convincingly isolate a substantial, consistent advantage specifically attributable to first-divergence credit assignment over generic modified-action supervision.

The distinction matters because the latter already captures much of the observed improvement, while the additional gain from first-divergence weighting remains relatively small and statistically uncertain across training seeds.

I therefore acknowledge the significant improvements made in the rebuttal, but maintain my overall rating of 2 (Weak Rejection).

My recommendation is based on the remaining uncertainty about the independent methodological novelty, rather than a lack of evidence for practical effectiveness or training stability.

Thank you again for the careful and constructive response.

Reviewer_A1SAOpenReview ↗
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3
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper is easy to follow and proposes a novel and interesting perspective on failure recovery in embodied multi-agent collaboration: "Counterfactual Contract Learning" (CCL). CCL combines verified, successful recovery programs with a special design that focuses on the first divergent action between a "failed recovery attempt" and a "successful alternative." Furthermore, the authors introduce the PARTNR-FS benchmark, which comprises 756 failure states. Across four large language model (LLM) backbones, CCL achieves a 2.74%–9.29% improvement in strict recovery rates compared to Repair-SFT. Additionally, CCL also improve the performance in another TDW-MAT environment.

Critical strengths

The paper is well written, and the examples are clear. The experimental results are complete and strong. One key idea is that CCL combines program-level verification with action-level supervision. After training, the model is able to generate a complete recovery program in a single inference call.

Critical weaknesses

The test set of PARTNR-FS is small with only 183 test cases. Moreover, the "Relation" category comprises only 9 test instances. Thus, the success of just a few cases can lead to a substantial percentage-point increase. For example, the performance of Qwen3.5-9B improved from 11.11% to 55.56%, but in reality, the successful cases raise from 1 to 5.

Questions for authors

What is the rationale for prioritizing the "first operation that deviates"? We know that multiple corrective actions are often possible, and a successful resolution might involve changes across several points. Moreover, is this approach robust?

3 comments
AuthorsOpenReview ↗

Rebuttal by Authors

We thank the reviewer for your positive feedback on our writing and experiments. We address the concerns below.

Weakness: The test set of PARTNR-FS is small, particularly the Relation category.

Response: The PARTNR-FS set contains only 756 states because, during the sampling process for the PARTNR Train_2k dataset, most episodes are completed successfully, whereas failure states tend to be concentrated within difficult episodes. Relation failures were uncommon among the failure states collected from PARTNR Train_2k. Therefore, this imbalance reflects the actual distribution of failures observed during our data collection process.

However, the overall gain is not driven solely by Relation. Excluding these nine cases, Qwen3.5-9B still improves from 80/174 to 93/174, a gain of 7.47 percentage points.

We have added the analysis excluding Relation to Section 4.2 of the revised main text. Table 1, Appendix B.2 and Table B.1 provide the category sizes and dataset composition for interpreting these results.

Question: Why prioritize the first divergent operation when recovery may require multiple changes? Is this choice robust?

Response: The intuition is analogous to autoregressive token generation. An earlier decision changes the context on which subsequent decisions depend. The point of initial divergence marks the first decision where a successful solution begins to differ from other sampled alternatives. This provides a natural entry point for implementing corrective supervision.

CCL emphasizes this operation while retaining supervision on subsequent steps with a completion weight of 0.25, so it still learns repairs involving multiple changes. Acceptance is based on the complete repair succeeding across three replay seeds, not on the first action alone.

To assess robustness, we evaluated completion weights 0, 0.125, 0.25, 0.5, and 1 with three random seeds. Mean unconstrained validation recovery is 55.74% without completion supervision and 58.91% at λc = 0.25.

We have clarified in Section 3.5 that first-divergence weighting is combined with completion supervision. Appendix I.2 and Figure I.2 report the completion-weight study, including the validation results.

Thanks for your response. I maintain my rating.

Thank you for your positive assessment and for considering our response. Your feedback has helped us improve the paper, particularly by clarifying the rationale for first-divergence supervision and the interpretation of results on smaller failure categories. We appreciate your constructive suggestions and continued support.

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

The paper addresses a useful distinction in embodied multi-agent recovery: making a failed action executable does not necessarily complete the subtask that depends on it. CCL trains a model to produce short repair programs that satisfy a local goal while preserving completed work. Starting from a supervised repair model, it samples alternative programs and checks them through simulator replay against a fixed recovery contract. Successful alternatives to failed direct repairs become training targets, with greater weight placed on the first divergent action and weaker supervision on the remaining steps. A separate loss is used to retain previously successful behavior. The authors introduce PARTNR-FS, a dataset of 756 failure states, and report improvements across four backbones. They also train repair modules on TDW-MAT and evaluate them within CoELA and PCE.

Critical strengths

The strongest part of the paper is its definition of successful recovery. A program must finish the relevant local goal and preserve completed work, rather than simply avoid another execution error. The contracts are fixed before candidate testing and allow alternative valid outcomes (Appendix B.1). Together with saved checkpoints and verified repair witnesses, this gives PARTNR-FS a clear evaluation target. The example in Appendix J.2 where one object is successfully moved but the second remains unhandled illustrates why this distinction matters.

The improvements are consistent across the four backbones in Table 1, with gains of roughly 2.7–9.3 percentage points over Repair-SFT. On Qwen3-8B, CCL also improves over the adapted Agent-R and CSO baselines while retaining one model call per repair (Table 2). I find the full-response CE and alternative supervision controls in Appendix I particularly useful, since they help separate the effect of the loss from that of additional verified training targets. The TDW-MAT results provide further support: after training on that domain, CCL improves transport over SFT repairs with both CoELA and PCE.

Critical weaknesses

t is less clear how much the specific first-divergence weighting contributes. In Table I.1, CCL reaches 47.54%, compared with 43.90% for full-response CE, but both the modified-actions and no-completion variants already reach 46.27%. The remaining 1.27-point difference is small on a test set of 183 states. Although several controls are run with three training seeds, the table gives no test-set variability or paired uncertainty for these comparisons. The training protocol for the CE and full-suffix controls is also less explicit than for S1/S3/S4/S5. These ablations support learning from verified alternatives, but I would like stronger evidence that the proposed weighting is consistently preferable to the closest alternatives.

The TDW-MAT results are harder to assess. There are 24 test episodes, and the planner uses stochastic decoding, yet Table 3 gives no indication of variation across repeated runs. This matters especially for the 2.50-point gain of PCE with CCL over PCE with SFT repairs. Appendix H.3 also leaves out details of the TDW repair-training data, the SFT initialization, and the exact repair triggers and handoff rules. Without these details, it is difficult to check whether the SFT and CCL comparisons use the same controller integration and comparable training settings. The results are promising, but I would not place as much weight on them as on the local-recovery experiments yet.

Questions for authors

Could you provide per-seed test results for CCL, full-response CE, modified-actions supervision, and the no-completion variant, along with paired uncertainty that accounts for states from the same episode? Do the CE and full-suffix controls use the same accepted examples, preservation data, initialization, and update budget as CCL?

How are the TDW-MAT repair-training examples collected, and how many are used for SFT and CCL? Are repair triggers, execution rules, and handoff to the base controller identical? Paired episode results and any repeated-run results would help assess whether the PCE improvement is stable.

How is the scope of a local recovery goal chosen? Appendix B.1 describes human selection using task predicates and saved history, while Table C.1 excludes the contract and full evaluation history from the model input. What checks ensure that the intended local goal and protected conditions are inferable from the public input alone?

2 comments
AuthorsOpenReview ↗

Rebuttal by Authors

We thank the reviewer for the positive feedback. We have prepared a point-by-point response to the comments below. All modifications in the manuscript have been highlighted in blue.

Comment 1: Contribution of first-divergence weighting and statistical reliability of the supervision controls.

Response: Thank you for highlighting the distinction benefiting specifically from first-divergence weighting. We address the training conditions and statistical comparisons below.

Matched training conditions. Full-response CE, modified-action supervision, no-completion supervision, and CCL use the same Qwen3-8B Repair-SFT initialization, 62 accepted counterfactual examples, 62 preservation examples, and training seeds 181/193/211. Each run uses six epochs.

Training seedFull-response CEModified actionsNo completionCCL
18145.3647.5446.9947.54
19343.1744.8146.4546.99
21143.1746.4545.3648.09
Mean ± SD43.90 ± 1.2646.27 ± 1.3846.27 ± 0.8347.54 ± 0.55

Episode-aware paired comparisons. We pair predictions on the same test states and resample source episodes, keeping all states from an episode together. The table reports CCL-minus-control differences and 95% confidence intervals from 5,000 bootstrap resamples.

Training seedCCL − Full-response CE, 95% CI (pp)CCL − Modified-action, 95% CI (pp)
181+2.19 [+0.83, +5.59]0.00 [−2.99, +3.14]
193+3.83 [+1.09, +6.56]+2.19 [+0.83, +5.59]
211+4.92 [+2.19, +8.20]+1.64 [−1.72, +5.14]

Across all three experimental runs, CCL consistently outperformed full-response CE, with confidence intervals that did not include zero. CCL also demonstrated an advantage over modified-actions. Consequently, these results support the use of CCL as a simple supervised approach, which robustly performs at least as well as other comparable alternatives.

We have added the matched supervision results to Section 4.4 and Table 4. Appendix G.2 specifies the shared training conditions. Appendix H.1 defines the episode-cluster bootstrap, and Appendix I.1 reports the paired comparisons.

Comment 3: Selection and public-input inferability of the local recovery goal.

Response: Thank you for raising this distinction. The local goal is selected from the task’s current responsibility, rather than defined by whichever repair happens to succeed. As described in Appendix B.1, automated processing links the failed action, held objects, and relevant container contents to task predicates. We distinguish conditions that must hold after repair from earlier milestones that only need to have been completed. The contract is frozen before candidate testing and permits alternative valid outcomes rather than prescribing an action sequence.

For example, when the instruction requires placing an airplane and a helmet next to each other on shelves, and the public state shows that the two agents hold these objects, recovery concerns completing that joint placement—not merely making one placement call executable. Either object can be placed first, provided the resulting arrangement satisfies the task.

The public input includes the task instruction, current agent and object states, failure feedback, and recent history—not just an isolated error message. The contract operationalizes these task requirements for verification. Protected conditions concern previously completed task requirements, rather than every aspect of the current state.

During construction, we check the selected responsibility against the instruction and task stage, and discrepancies between the instruction and available predicates are flagged for review.

We have expanded Section 3.2 to describe contract construction and freezing before candidate testing. Appendix B.1 details the selection procedure, while Appendix C.1 clarifies the scope of protected conditions.

AuthorsOpenReview ↗

Rebuttal by Authors

Comment 2: Reproducibility and statistical reliability of the TDW-MAT evaluation.

Response: Thank you for highlighting these missing details. We clarify the training data and matched controller integration below.

Training data and initialization. We collect repair data from 19 TDW-MAT training episodes, following the same collection and verification procedure as PARTNR-FS. Repair-SFT initializes from the original Qwen3.5-9B model and learns from verified successful local repair programs. We then freeze the Repair-SFT checkpoint, generate direct repairs and alternative programs, and replay them from the same failure state under the same recovery contract. Accepted alternative pairs provide the CCL correction data. Preservation examples are verified successful direct repairs from states disjoint from the correction set.

Training stageInitializationTraining examples
Repair-SFTOriginal Qwen3.5-9B216 verified repairs
CCLCorresponding Repair-SFT checkpoint48 counterfactual corrections + 48 preservation examples

Matched controller integration. PCE + SFT and PCE + CCL share exactly the same triggering conditions, public inputs, generation and execution budgets, failure handling, partner policy, and handoff rules. Only the repair-model weights differ.

Repair is invoked when PCE returns to its high-level planning interface and the public failure-trigger conditions are met. At an eligible high-level boundary, one local model call generates 1–5 repair actions. The repairing agent temporarily suspends its regular planning calls and executes the program through the original skills and low-level controller, while its partner continues following the original PCE policy. Control returns to PCE after the final action finishes, or earlier if execution fails or the next action is no longer available. Malformed outputs fall back to PCE without correction or replacement. Repair cannot recursively retrigger at the same handoff boundary, but subsequent eligible failures may trigger another intervention.

Paired results and uncertainty. We now supplement the aggregate result with paired outcomes on the same 24 test episodes and repeated-run statistics.

Food episodeSFT / CCL objects transportedStuff episodeSFT / CCL objects transported
008/81210/10
019/10138/8
0210/10147/8
0310/101510/10
0410/10168/8
0510/10177/7
0610/101810/10
076/6197/8
087/72010/10
0910/102110/10
109/10228/8
118/9238/9
ComparisonTransport-rate gain (pp)Paired episode-bootstrap 95% CI (pp)Repeated-run gain (pp)
PCE + CCL vs. PCE + SFT+2.50[+0.83, +4.58]2.50 ± 0.83

CCL improves transport in 6 of the 24 episodes, matches SFT in the remaining 18, and degrades none. The paired episode-bootstrap interval, [+0.83, +4.58] percentage points, excludes zero, supporting a positive average effect on this test set. Across 3 independent paired runs, the gain is 2.50 ± 0.83 percentage points, providing additional evidence that the improvement persists under stochastic planning.

Because the two systems share the same controller integration and differ only in repair-model weights, this comparison isolates the effect of the CCL update relative to the SFT repair model within PCE.

We have expanded Section 4.5 with the TDW-MAT details. Appendix H.3 documents the integration and resampling procedures, and the new Table H.2 lists all 24 paired episode outcomes.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Rebuttal Summary

Dear Program Chairs, SACs, ACs, and Reviewers,

Thank you for your time and consideration. We thank Reviewers A1SA and bHrE for their positive assessments, and Reviewer SxCv for the sustained discussion and repeated acknowledgment of the improvements across successive rounds. This constructive exchange has helped us substantially improve the paper and its evaluation. We summarize the recognized strengths, the progress made during the rebuttal, and the corresponding manuscript revisions below.

1. Points recognized by the reviewers

  • Reviewer A1SA highlighted the combination of program-level verification and action-level supervision, the clear presentation, and the strong experimental results.
  • Reviewer bHrE emphasized the definition of successful recovery as completing the local goal while preserving completed work. The reviewer also recognized the clear evaluation target provided by PARTNR-FS, the consistent improvements across four backbones, and the complete-task benefits within both CoELA and PCE.
  • Reviewer SxCv acknowledged CCL’s highest mean recovery among the tested supervision variants, low training-seed variability, and the reasonable structural rationale for emphasizing the earliest divergence under a shared execution prefix.

2. Progress during the rebuttal discussion

  • Evidence for the supervision strategy and scope of the contribution. SxCv initially questioned the evidence for first-divergence supervision. After the matched three-seed comparisons, the reviewer acknowledged the consistent improvement, with paired confidence intervals excluding zero across all three seeds. Following further clarification, the reviewer also agreed that CCL should be evaluated as a complete framework rather than through the weighting choice alone.
  • Training stability and practical utility. SxCv initially questioned stability across backbones and the advantage over stronger planners with additional inference-time computation. We added multi-seed results across four backbones and GPT-5.6 Sol comparisons. The reviewer subsequently acknowledged that these results substantially addressed the stability concern and supported the practical value of specialized repair with fewer online model calls.
  • TDW-MAT reliability and applicability. Both bHrE and SxCv requested stronger statistical evidence and clearer evaluation details. We supplied paired episode outcomes, bootstrap confidence intervals, repeated-run results, and the matched integration protocol. SxCv acknowledged the strengthened evidence for end-to-end utility and accepted the distinction between applicability to another environment and zero-shot transfer.
  • Small categories and the supervision rationale. A1SA raised concerns about the small Relation category and the motivation for prioritizing the first divergence. We provided an analysis excluding Relation and clarified the role of completion supervision and its sensitivity analysis. After considering our response, A1SA explicitly maintained their positive rating.

3. Revisions to the manuscript

  • Clarified the methodological contribution and recovery contracts. Section 2 now explains how contract-based acceptance determines which repairs become training targets, while comparison with failed attempts guides supervision. Sections 3 and Appendices B and C clarify contract details and the rationale for emphasizing the first divergence while retaining completion supervision.
  • Added matched supervision controls and uncertainty estimates. Section 4.4 and Appendix I.1 report three-seed comparisons under matched initialization, data, and update budgets, including a random modified-action control. Episode-cluster bootstrap intervals support the gains all three seeds.
  • Expanded robustness analysis. Appendix I.5 reports three training seeds for all four backbones. It also shows that excluding the two smallest failure categories still leaves gains of 3.25–5.84 percentage points across all four backbones on the remaining states.
  • Added stronger inference-time repair baselines. Section 4.3 and Appendix H.2 compare CCL with GPT-5.6 Sol using self-refinement and actual execution feedback. Appendix I.4 distinguishes reduced online model calls from offline collection and training costs.
  • Expanded TDW-MAT reproducibility and statistical analysis. Section 4.5 and Appendix H.3 specify repair-training protocol. Table H.2 provides paired outcomes for all 24 episodes. PCE gains over SFT repairs 2.50 percentage points with a paired 95% confidence interval, and 2.50 ± 0.83 points across three independent paired runs.

We appreciate the constructive feedback by reviewers, which has strengthened both the manuscript and its evaluation. We hope these revisions help the final assessment consider the complete contribution of the recovery formulation, learning method, and benchmark. We would be happy to clarify any remaining questions and provide further responses as needed.

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

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