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Under review as a conference paper at ICLR 2027

RoboCoach: World Models as Active Coaches for Compositional Robot Skills

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Abstract

Long-horizon robot manipulation reuses skills across many task compositions, but improving these compositions with additional end-to-end demonstrations is costly. A practical self-improving system must decide both what to teach next and where to apply that supervision. We present ROBOCOACH, a world-model-guided coaching framework that uses imagined failures to guide demonstration requests and expert updates. Its Route–Imagine–Diagnose–Improve (RIDI) loop executes reusable skill experts inside COACHWORLD, our shared action-conditioned world model, and uses a progress judge to record the first subtask that fails to complete. Aggregated records select which subtask demonstrations to acquire and which expert adapters to update. Across two simulation suites and two real-robot platforms, imagined and deployed success correlate over 22 task–policy pairs (ρ = 0.840). Controlled comparisons show that our coaching method outperforms matched baselines under matched data budgets and update schedules. With only 150 additional subtask demonstrations, success rises from 13.3% to 75.0% on Franka and from 40.0% to 83.8% on AgileX. The coached experts also transfer to four held-out compositions, achieving an average success of 35.0%, compared with 0% for a shared-policy baseline updated with uniformly acquired demonstrations. Together, these results show that world models can serve as active coaches, turning imagined failures into targeted supervision for modular policy improvement. Project Page: https://robocoach-iclr.github.io/

Primary area:
applications to robotics, autonomy, planning
Keywords:
Robot World Models, Long-Horizon Manipulation, Adaptive Robot Learning, Modular Policy Adaptation

Reviews

Among:
Shape:
1234this paper, Top 17%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.75 over 4 reviews, above 83% of the others.
Reviewer_C3VtOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

RoboCoach uses a world model to guide demonstration acquisition and skill-specific policy updates for long-horizon manipulation. Its Route–Imagine–Diagnose–Improve loop executes skill experts in CoachWorld, uses a progress judge to identify the first timed-out subtask, and requests demonstrations for frequently failing subtask–expert pairs. The corresponding LoRA adapters are then updated while the shared policy backbone remains frozen. Experiments on LIBERO, RoboTwin, Franka, and AgileX show improvements under fixed additional demonstration budgets. The paper also evaluates whether the updated experts can be reused in previously unseen task compositions.

Critical strengths
  1. The real-robot results are substantial and consistent with the targeting. The real-robot gains are large on both platforms (13.3% to 75.0% on Franka and 40.0% to 83.8% on AgileX, against 30.0% and 47.5% for the baseline), and per-task improvements appear in the round where the corresponding subtask is selected (Tables 11, 15 and 16).
  2. Skill-specific adapters enable efficient and reusable policy improvement. Each skill uses an independent LoRA adapter on a shared, frozen policy backbone, allowing additional demonstrations to update the corresponding skill without retraining the entire policy. The updated adapter can then be reused across tasks, so targeted coaching can potentially benefit multiple tasks that involve the same skill.
Critical weaknesses
  1. The conceptual advance over existing pipelines appears limited. Policy evaluation inside action-conditioned world models (e.g., Ctrl-World; Guo et al., 2025) and failure-driven demonstration acquisition (e.g., AdaDemo; Mu et al., 2024) are both established directions. RoboCoach combines them by using imagined subtask bottlenecks to request demonstrations and selectively update skill-specific LoRA adapters. I therefore view the contribution primarily as a useful system integration, with relatively modest methodological novelty.

  2. The reliability of coaching-target selection remains unclear. Figure 3 shows task-level success agreement, while Table 2 evaluates the judge against annotations of generated videos. Neither directly establishes that imagined failures identify the skills responsible for real failures. Moreover, premature completion judgments can trigger incorrect expert switches and misattribute subsequent failures to the next skill. The overall policy gains are encouraging, but do not resolve whether the system reliably selects the right coaching targets.

Questions for authors
  1. Could the authors clarify how the expert library is constructed?
  2. Have the authors evaluated how often the router selects the correct next subtask, given that a routing error would attribute the resulting failure to the wrong expert in the scorecard?
  3. See weakness
4 comments
AuthorsOpenReview ↗

Response to Reviewer C3Vt

We thank the reviewer for highlighting the real-robot gains and skill reuse. We clarify the contribution and provide direct routing measurements.

Q1. Contribution Beyond Ctrl-World and AdaDemo

A1: RoboCoach couples two decisions at the subtask–expert level: what supervision to acquire and which reusable policy component to update.

Ctrl-World uses world models for policy evaluation and improvement; AdaDemo guides demonstration collection from policy weaknesses. RoboCoach links these directions through the same subtask–expert unit: imagined first-timeout diagnoses are aggregated into task-balanced priorities, which determine both real demonstration requests and the LoRA experts to update. This gives the world model an active coaching role—allocating scarce supervision to reusable skills whose updates can benefit multiple task compositions.

The new simulation controls test these two decisions (R1):

Controlled comparison: RoboCoach minus baselineLIBERO AUCRoboTwin AUC
Modular + Random: same expert architecture and budget; targeting differs+3.74pp+6.66pp
Single + WM-Targeted: identical demonstrations; shared vs. expert adapter updates+1.10pp+1.73pp

These controls support targeted acquisition and expert-specific adaptation separately. On held-out compositions, RoboCoach achieves 35.0% mean success versus 0% for Single + Uniform, demonstrating transfer of updated skills in the combined system. The hardware experiments further establish its practical utility.

Q2. Construction of the Expert Library

A2: We follow AtomicVLA's semantic atomic-skill decomposition. For example, pick soup can, pick mug, and pick moka pot are different subtasks but can share one Pick LoRA expert on the frozen shared backbone.

The vocabulary and expert mapping are manually defined. New semantic skills can be added by initializing another adapter from the shared base and training it on demonstrations. Autonomous expansion requires a criterion for creating categories, acquiring their data, and integrating them into the Router and Judge.

Q3. Router Correctness and Erroneous Expert Switching

A3: We added a four-platform offline Router evaluation covering 2,115 decision points from 220 reference videos (R5). We use the paper's original prompt and correct completed prefixes. Each decision is scored for the next skill category and for the exact skill–object pair; the reported accuracies aggregate decision points sampled within the videos.

PlatformNext-skill accuracyExact skill–object accuracy
LIBERO92.33% (698/756)75.26% (569/756)
RoboTwin95.24% (720/756)65.74% (497/756)
Franka89.23% (174/195)89.23% (174/195)
AgileX79.41% (324/408)58.33% (238/408)
Pooled90.59% (1,916/2,115)69.88% (1,478/2,115)

A separate 500-initial-state test gives 91.0% (455/500) next-skill accuracy and 83.4% (417/500) exact matching.

The gap between skill and exact matching highlights errors in target-object selection. In the RoboTwin object-candidate ablation, exact matching rises from 65.74% to 88.89% (+23.15pp), with next-skill accuracy remaining similar (95.24% versus 94.58%). This identifies object-candidate configuration as an effective way to improve exact routing in this test.

Errors in the Judge's completed prefix can change the next routing decision. Our diagnostic pipeline requires three consecutive positive completion judgments before advancing. R4 evaluates how perturbations of these judgments affect acquisition priorities: all three noise seeds preserve the Top-2 at 5% noise, while 10–20% noise affects the second target.

Dear Reviewer C3Vt,

Thank you again for your thoughtful review. We have provided additional analyses on Router reliability and target selection, along with further clarification of our methodological contribution.

We hope these results address your concerns and would appreciate your consideration in the final assessment :-)

Best regards, Authors

Thank you for the thoughtful response and additional experiments. The expert-library construction is now clear, and the new controlled comparisons and Router evaluation strengthen the empirical support. These additions address several of my concerns. I appreciate the practical value of this work and maintain my rating of 3 (Weak Acceptance).

We sincerely thank you for your thoughtful feedback and for maintaining your positive assessment! We appreciate your recognition of our additional experiments and clarifications, particularly regarding the expert library and Router evaluation.

Thank you again for your constructive suggestions and encouragement!

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

This paper introduces the RoboCoach framework, which integrates the acquisition of demonstration data with the selective adaptation of reusable robot skill experts. Its "Route-Imagine-Diagnose-Improve" loop assigns subtasks to specific skill-based LoRA adapters and executes them within "CoachWorld"—an action-conditioned video world model. A "progress judge" is employed to track the first incomplete subtask. By aggregating instances where the "imagination" process times out, the system identifies subtasks that require additional human demonstrations and determines which adapters need to be updated. Evaluations were conducted across platforms including LIBERO-Long, RoboTwin, Franka, and AgileX, maintaining consistency in demonstration data budgets, simulated control environments, and the protocols for data acquisition and model updates. Experimental results demonstrate that the addition of 150 demonstration sequences per platform significantly enhances the robot system's real-world execution performance. Furthermore, the framework successfully achieves skill reuse across four sets of tasks that were not included in the training phase.

Critical strengths
  1. This method ingeniously integrates the processes of "acquisition" and "adaptation," supported by an effective simulation control mechanism. It translates "envisioned execution" into concrete requirements for real-world demonstrations, which in turn prompts experts to update their respective models. By providing both the shared adapter and specific experts with identical, targeted demonstrations, the method can more precisely pinpoint the components that require updates. This approach offers more compelling evidence than simply comparing a model against an unguided policy.

  2. Significant practical results have been achieved across two distinct physical platforms, demonstrating an ability to reuse skills. These outcomes strongly validate the utility of the integrated system.

Critical weaknesses
  1. There is insufficient validation of the "imagination"-based diagnostic process. Figure 3 only illustrates performance correlations at the task level; it fails to show diagnostic accuracy at the sub-task level or track the process during the "coaching" phase. Table 2 evaluates human raters' interpretations of the "imagination" videos rather than the alignment of these interpretations with actual execution failures. Furthermore, the paper does not address the rejection rate under a majority-vote mechanism or its impact on target selection. The research requires direct validation against ground-truth execution outcomes.

  2. There is insufficient evidence regarding the benefits of "targeting" and the reproducibility of the results. In the LIBERO benchmark, the world-model-based targeting method shows an improvement of only 2.8 percentage points over a modular random-selection approach, compared to a 12.8 percentage point improvement in RoboTwin. The reported confidence intervals do not account for the variability across independent training runs or data collection sessions. In both hardware and held-out set evaluations, sample selection and model-updating strategies are conflated, making it difficult to isolate their individual contributions. Additionally, the released code does not appear to cover the full pipeline, which hinders independent replication of the research findings.

Questions for authors
  1. Diagnostic Validity: How well do the anticipated "failure labels" and the prioritized ordering of goals align with the actual failures encountered during execution? What proportion of trials were excluded due to discrepancies in random seeds, and would the final selection of goals change if these trials were included?

  2. Contribution of Goal Setting: Is it possible to evaluate the goal-setting component while keeping the "modular adaptation" mechanism (in hardware environments or on unseen composite tasks) constant, thereby isolating the specific gains derived from "sample selection"?

  3. Robustness and Reproducibility: Have the experiments been validated through repetitions using different random seeds? Are the performance improvements achieved by LIBERO stable? Furthermore, can the authors provide access to the resources required to reproduce the experimental results—including the specific "expert-update" configurations, the training assets used for evaluation, and the complete "coaching" pipeline?

3 comments
AuthorsOpenReview ↗

Response to Reviewer fYkM (1/2)

We thank the reviewer for the constructive suggestions. We address diagnostic validity, targeting effectiveness, and reproducibility with the following new evidence.

Q1. Diagnostic Validity and Majority-Vote Filtering

A1: We measure automatic WM–native diagnosis agreement, human-referenced target overlap, and filtering sensitivity (R2–R3).

Direct measurementResult
WM-majority/native-RoboMeter complete label agreement, on WM-accepted initial states244/402 (60.70%)
Exact failed-subtask label agreement, conditional on both automatic diagnoses reporting failure244/358 (68.16%)

Each of 500 LIBERO states has three WM rollouts and one native execution. We compare the 402 accepted WM majority labels with RoboMeter's native-video labels: SUCCESS or TIMEOUT(subtask–expert ID). Both diagnoses report failure for 358 pairs.

On the same 402 states, the task-balanced scorecards select identical Top-2 targets, with 29-candidate Spearman ρ = 0.7330. Across coaching rounds, the human-referenced comparison is:

Platform / RoundWM Top-2Human GT Top-2
LIBERO R1L4 pick white mug; L6 pick chocolate puddingL0 pick soup can; L8 pick second moka pot
LIBERO R2L0 pick soup can; L8 pick first moka potL0 pick soup can; L8 pick second moka pot
LIBERO R3L8 place first moka pot; L9 place mug in microwaveL8 pick second moka pot; L1 pick cheese box
RoboTwin R1R1 place medium block; R2 pick first bottleR0 pick green block; R2 pick third bottle
RoboTwin R2R0 pick green block; R1 place largest blockR0 pick green block; R1 pick smallest block
RoboTwin R3R4 place third block; R3 place third bowl on secondR0 place green block; R1 pick smallest block
Franka R1pull cord; place lidplace lid; pick lid
Franka R2press green button; place lidpress green button; press red button
Franka R3pull cord; press red buttonpress red button; pull cord
AgileX R1place right shoe; pick tea bagpick tea bag; place right shoe
AgileX R2pick red block; push platepick red block; push plate
AgileX R3pick red block; place left shoeplace right shoe; place left shoe

The mean Top-2 overlap is 45.83% (11/24 slots): 1/6 LIBERO, 1/6 RoboTwin, 4/6 Franka, and 5/6 AgileX. Matches require the same action–object/context, irrespective of order.

Across three rounds, selections cover human-ranked initial bottlenecks 2/3 in LIBERO (pick soup can, pick chocolate pudding) and 1/3/4/6 in RoboTwin (pick green block, place medium block, place third block, pick first bottle). Both benchmarks cover two of the initial Top-3 bottlenecks.

[Majority-Vote Rejection] The rejection rates aggregated across three rounds are 12.73% / 26.00% / 3.89% / 34.17% for LIBERO / RoboTwin / Franka / AgileX. In a separate Base-to-Round-1 filtered-versus-unfiltered analysis (R3), the first target remains unchanged on all four platforms. The second changes from pick pudding to pick cheese box (LIBERO), becomes a three-way tie (RoboTwin), remains unchanged (Franka), or changes from pick tea bag to place the plate (AgileX). Filtering therefore affects secondary acquisition priorities.

AuthorsOpenReview ↗

Response to Reviewer fYkM (2/2)

Q2. Isolating Targeting and Modular Adaptation

A2: We ran a new four-method comparison with human-teleoperated demonstrations, using 100 accepted demonstrations per round over three rounds (R1). This extends the original teacher-rollout evaluation to a second supervision source under matched data budgets.

MethodLIBERO Budget AUCRoboTwin Budget AUC
Single + Uniform69.2756.70
Single + WM-Targeted70.8758.90
Modular + Random68.2353.97
RoboCoach71.9760.63

[Acquisition] RoboCoach vs. Modular + Random holds the modular architecture and demonstration budget fixed. WM-guided targeting improves Budget AUC by +3.74/+6.66pp on LIBERO/RoboTwin.

[Adaptation] RoboCoach vs. Single + WM-Targeted uses exactly the same demonstrations every round. Skill-specific updates improve Budget AUC by another +1.10/+1.73pp.

RoboCoach achieves the highest success rate at every coaching round on both benchmarks. This supports consistency across supervision protocols. Notably, the learning value of targeted acquisition also depends on whether the demonstrations provide complementary experience to the existing expert.

Q3. Robustness and Reproducibility

A3: We completed one additional end-to-end run per method on each benchmark with fresh seeds and human-teleoperated demonstrations. The acquisition advantage over Modular + Random has the same direction in the original teacher-rollout experiments (+1.5/+6.8pp AUC) and the new campaign (+3.74/+6.66pp). This supports consistency across supervision protocols. The original bootstrap intervals quantify evaluation-sampling uncertainty at fixed checkpoints.

We have released the RIDI orchestration framework, diagnostic pipeline, and expert-update configurations (R5):

https://github.com/RoboCoach-ICLR/RoboCoach-Framework

Dear Reviewer fYkM,

Thank you again for your constructive feedback. We have conducted additional experiments addressing diagnostic validity, targeted acquisition, and reproducibility.

We hope our rebuttal has addressed your key concerns and would greatly appreciate your reconsideration of our work. We would be happy to clarify any remaining questions :-)

Best regards, Authors

Reviewer_2tzsOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper presents RoboCoach, a world-model-guided learning framework for long-horizon compositional robotic manipulation. Following a Route-Imagine-Diagnose-Improve loop, it routes tasks to reusable skill experts, runs policies within the action-conditioned world model CoachWorld, and leverages a progress judge to record the first-timeout (subtask-expert) pairs. The system then allocates additional demonstration budget according to task-balanced failure frequency and updates LoRA parameters of corresponding experts. The core contribution lies in aligning demonstration-collection targets with policy-update objects at the skill level. Evaluations on LIBERO and RoboTwin compare diverse data-collection and parameter-update paradigms, verifying the effectiveness of combining world-model-driven targeted collection with modular updates.

Critical strengths
  1. Well-defined problem setup, with designs closely aligned with research goals. For long-horizon tasks that reuse skills, treating subtask-expert pairs as correction units is intuitive. This design explicitly specifies required demonstrations and policy components for supervision, so newly collected demonstrations benefit cross-task reusable skills.

  2. Key ablation comparisons validate the merits of combined collection-update design. Single VLA + WM-targeted shares identical targeted demonstrations with RoboCoach and isolates the difference between shared-adapter updates and expert-specific updates. Modular + Random contrasts random sampling against world-model-guided sampling under the same modular architecture. Appendix E.2 further clarifies shared initialization, router and progress judge to improve interpretability.

Critical weaknesses
  1. Statistical stability of the full learning pipeline requires further validation. Confidence intervals in Appendix E.2 are resampled from fixed-checkpoint per-task evaluations and only reflect measurement noise. They do not account for randomness introduced by target selection, demonstration collection and expert training. Notably, the 2.8-point gain over random sampling on LIBERO needs independent repetitions to confirm robustness. Repeating Modular + Random with diverse target-selection sequences is also necessary.

  2. The mechanism whereby world-model diagnosis enables useful data collection requires deeper explanation. Task-level success-rate correlations verify overall performance prediction, and judge accuracy on generated videos supports within-video progress recognition. However, they cannot measure consistency of failed subtasks between imagined rollouts and real-environment execution. First-timeout frequency is also affected by preceding-skill performance and subsequent-skill reachability. As a collection heuristic, optimality of selected skills under fixed budget is not claimed, and existing ablations already prove practical value. Even so, consistency analyses for failed subtasks / collection targets would help explain when this heuristic works and how world-model errors distort target picking.

  3. Reproducibility and efficiency details are incomplete. Key hyper-parameters are missing: expert LoRA rank, learning rate, per-round update steps, replay-buffer mixing ratios for old/new data. Though baselines claim matched training settings, these values are critical for reproducibility and fair comparison. Besides, statistics on per-round imagination latency, imagination invocation count and data-collection overhead would help assess real-world costs.

Questions for authors
  1. Could you report results from multiple independent runs of the full collection-update pipeline in simulation, including Modular + Random with varied random target-selection sequences, to validate stability of final success rates or Budget-AUC metrics?

  2. How consistent are first-timeout subtasks and top-2 collection targets between imagined rollouts and real-simulation execution? Are there typical mis-selection cases caused by world-model inaccuracy or upstream-skill failures?

  3. Please supply critical hyper-parameters for expert LoRA training, replay ratios, and per-round imagination overhead. Also clarify how these settings are kept consistent between shared-update and modular-update baselines.

3 comments
AuthorsOpenReview ↗

Response to Reviewer 2tzs

We appreciate the reviewer's precise questions about full-pipeline randomness, failure-target consistency, and training details.

Q1. Independent Runs and Targeting Stability

A1: We completed one additional, independently seeded end-to-end run per method on each benchmark using human-teleoperated demonstrations. All methods use 100 accepted demonstrations per round, 300 total, covering collection and training across three rounds. The original experiments used segmented teacher-policy rollouts.

MethodLIBERO AUCRoboTwin AUCLIBERO SR@300RoboTwin SR@300
Single + Uniform69.2756.7070.855.6
Single + WM-Targeted70.8758.9070.857.2
Modular + Random68.2353.9769.451.6
RoboCoach71.9760.6373.859.6

RoboCoach leads all methods at each of three rounds, improving AUC over Modular + Random by +3.74pp / +6.66pp on LIBERO / RoboTwin under matched data budgets and evaluation protocols. The original teacher-rollout advantage was +1.5pp / +6.8pp, supporting consistency across the two campaigns.

Q2. Consistency Between Imagined and Actual Failure Targets

A2: We compare both diagnosis labels and acquisition targets (R2). On 500 fixed-policy LIBERO initial states, we pair each three-seed WM majority label with RoboMeter's diagnosis of one native execution. Among 402 WM-accepted states, complete-label agreement is 244/402 (60.70%). Exact subtask–expert labels agree in 244/358 pairs (68.16%) that both diagnoses classify as failures. Task-balanced scorecards on those same 402 states select identical Top-2 targets (ρ = 0.7330).

The round-level comparison against human-annotated execution targets is:

Benchmark / RoundWM Top-2Execution Top-2
LIBERO R1pick white mug; pick chocolate puddingpick soup can; pick second moka pot
LIBERO R2pick soup can; pick first moka potpick soup can; pick second moka pot
LIBERO R3place first moka pot; place mug in microwavepick second moka pot; pick cheese box
RoboTwin R1place medium block; pick first bottlepick green block; pick third bottle
RoboTwin R2pick green block; place largest blockpick green block; pick smallest block
RoboTwin R3place third block; place third bowl on secondplace green block; pick smallest block

Exact action–object Top-2 overlap is 1/6 in each simulation benchmark.

Across three rounds, selections cover the initial policy's human-ranked bottlenecks 2 and 3 in LIBERO and 1, 3, 4, and 6 in RoboTwin—including two of the initial Top-3 in each benchmark.

First-timeout frequency depends on preceding-skill success, which may mask downstream bottlenecks. However, during human labeling period, our manual inspection suggested that such masking was relatively uncommon. More importantly, R1 empirically validates the effectiveness of our task-balanced acquisition strategy against Modular + Random under matched demonstration budgets.

Q3. Training Hyperparameters, Replay, and Efficiency

A3: The released expert-update configurations use the following settings:

SettingSingle Arm SettingDual Arm Setting
LoRA rank / alpha / dropout32 / 32 / 032 / 32 / 0.05
Learning rate / global batch3e-5 / 163e-5 / 32
Warmup steps125200
Update steps / evaluated checkpoint1250 / 12501250 / 1250
LoRA scale0.50.5

Each setting applies to both simulation and hardware of the corresponding embodiment. Both use action-expert LoRA with frozen shared weights and evaluate the 1,250-step update checkpoint. The table specifies per-update settings. Demonstration budgets are matched across methods.

[Replay Mixing] We use a universal 80:20 new-to-replay mixing ratio for adapter updates: 80% demonstrations acquired in the current coaching round and 20% replay data. Training configurations are released with the RIDI framework (R5).

[Efficiency] The paper reports RoboMeter inference latency of 0.1049/0.1164 s (p50/p95) on an A100 at batch size one. End-to-end coaching additionally involves world-model generation and routing.

The authors' response has addressed some of my concerns, and the stability of the overall training pipeline and computational efficiency have been further improved. Therefore, I maintain my positive rating. Meanwhile, I think the reliability of world-model-guided target selection is an aspect that can be further discussed and analyzed. I hope the authors can further discuss these discrepancies and their impacts in future work.

We sincerely thank you for your feedback and for maintaining the positive assessment :) We appreciate your recognition of our additional experiments and clarifications.

We agree that the reliability of world-model-guided target selection deserves further investigation. Your suggestions on understanding the discrepancies between imagined and actual failures, as well as their implications for supervision allocation, are valuable and will help guide our future research.

Thank you again for your constructive feedback and encouragement!

Reviewer_5CnKOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This work introduces Robocoach, a world‑model‑driven active coaching framework for long‑horizon compositional robot manipulation. It builds the RIDI loop on top of coachworld, an action‑conditioned multi‑embodiment world model. It localizes bottleneck subtask‑expert pairs from imagined failures, requests targeted human demonstrations, and only updates corresponding LoRA skill experts. Evaluations cover two simulation benchmarks and two real‑robot platforms. Imagined and real‑world policy success yield Spearman ρ=0.840. With limited extra demonstrations, real‑robot performance improves greatly, and the system generalizes to unseen held‑out skill compositions.

Critical strengths
  1. This paper addresses a meaningful practical bottleneck: costly real‑robot data collection for long‑horizon manipulation. It proposes that world models should not only simulate trajectories but also act as active coaches to select high‑value supervision targets.
  2. Well‑structured controlled ablations cleanly separate two factors: demonstration acquisition strategy and parameter‑update target. Results verify that applying targeted data to matched modular experts brings larger gains than shared‑adapter updates.
  3. Solid multi‑domain evaluation including both simulation and real‑hardware. Component‑wise validations cover world‑model fidelity, imagined‑real correlation and progress‑judge reliability. Held‑out composition tests confirm compositional transfer of learned skills.
Critical weaknesses
  1. The atomic‑skill expert library is predefined by humans. The system cannot discover new skills or expand experts autonomously, limiting deployment for open‑ended real‑world tasks.
  2. The whole coaching loop heavily hinges on COACHWORLD prediction quality and RoboMeter progress‑judge accuracy. Systematic world‑model hallucinations or judge mis‑attribution will waste limited demonstration budgets. There is no quantified analysis for mis‑diagnosis rates.
Questions for authors
  1. The expert library is manually predefined. What are the key barriers to enable automatic skill discovery and dynamic expert‑library expansion in your framework?
  2. Could you report the mis‑attribution rate of bottleneck subtask‑expert pairs in your experiments? How would overall performance degrade under controlled mis‑diagnosis noise?
  3. Could you add rebuttal‑time ablation results with a weaker progress judge (e.g. Contrastive‑λ), to quantify end‑to‑end sensitivity to judge performance?
  4. Since real‑robot experiments lack two baselines used in simulation, what performance trends do you expect would transfer to hardware, based on simulation observations?
2 comments
AuthorsOpenReview ↗

Response to Reviewer 5CnK

We thank the reviewer for the questions on skill discovery, misattribution, weaker judges, and hardware comparisons. We provide the additional diagnosis-level measurements below.

Q1. Skill-Library Construction and Expansion

A1: The current library uses manually defined AtomicVLA-style semantic skills, such as a Pick expert shared by pick mug and pick soup can. A new semantic category can be introduced by initializing another LoRA adapter from the shared pretrained base and training it with corresponding demonstrations. A new expert is be initialized from the shared pretrained base and fine-tuned on demonstrations of a new semantic skill. Autonomous skill discovery remains future work.

Q2. Bottleneck Misattribution

A2: We measure automatic diagnosis agreement and human-referenced acquisition overlap (R2). For 500 LIBERO initial states with three WM rollouts and one native execution each, the WM majority vote accepts 402 states. Its labels agree with native-video RoboMeter diagnoses in 244/402 cases (60.70%); exact subtask–expert labels agree in 244/358 pairs (68.16%) classified as failures by both. On the same accepted states, task-balanced scorecards select identical Top-2 targets (ρ = 0.7330).

Platform / RoundWM Top-2Execution Top-2
LIBERO R1pick white mug; pick chocolate puddingpick soup can; pick second moka pot
LIBERO R2pick soup can; pick first moka potpick soup can; pick second moka pot
LIBERO R3place first moka pot; place mug in microwavepick second moka pot; pick cheese box
RoboTwin R1place medium block; pick first bottlepick green block; pick third bottle
RoboTwin R2pick green block; place largest blockpick green block; pick smallest block
RoboTwin R3place third block; place third bowl on secondplace green block; pick smallest block
Franka R1pull cord; place lidplace lid; pick lid
Franka R2press green button; place lidpress green button; press red button
Franka R3pull cord; press red buttonpress red button; pull cord
AgileX R1place right shoe; pick tea bagpick tea bag; place right shoe
AgileX R2pick red block; push platepick red block; push plate
AgileX R3pick red block; place left shoeplace right shoe; place left shoe

The mean Top-2 overlap is 45.83% (11/24 slots): 1/6 LIBERO, 1/6 RoboTwin, 4/6 Franka, and 5/6 AgileX.

Across three rounds, selections cover two of the initial Top-3 human-ranked bottlenecks in each simulation benchmark: LIBERO ranks 2/3 and RoboTwin ranks 1/3/4/6. R1 evaluates the learning gains achieved with these supervision priorities.

Q3. Weaker Judge and Controlled Diagnosis Noise

A3: We test judge sensitivity through controlled perturbations of completion judgments (R4). Using the initial LIBERO checkpoint, we test on 1,500 WM videos from 500 states. In offline replay, each thresholded completion judgment is flipped with probability pp before the persistence update. switching requires three consecutive positive judgments. We recompute terminal labels, three-seed consensus, and task-balanced scores for three noise-sampling seeds per probability.

Flip probabilityAcquisition result
5%All three seeds retain pick alphabet soup can and pick white mug.
10%Two seeds retain this pair; one changes the second target.
20%All three retain pick alphabet soup can and replace pick white mug with place alphabet soup can (Top-2 IoU 1/3).

The Top-2 is stable at 5% noise across tested seeds, while stronger perturbations affect the second acquisition priority.

Dear Reviewer 5CnK,

Thank you again for your valuable feedback. We have supplemented our rebuttal with analyses of failure attribution, diagnosis robustness, and skill-library extensibility.

As the discussion period draws to a close, we would like to kindly follow up on our rebuttal. We hope these additions help clarify our approach and would appreciate any further feedback before the discussion concludes :-)

Best regards, Authors

Comments on the paper

2 comments
AuthorsOpenReview ↗

General Response (1/2)

We sincerely thank all four reviewers for their constructive feedback and for recognizing the practical value of targeted robot supervision, our controlled acquisition–adaptation design, and the substantial improvements on real robots.

In response to the reviews, we conducted new end-to-end coaching experiments on LIBERO and RoboTwin, directly compared world-model diagnoses with execution-derived bottlenecks, and performed additional analyses. We also release the RoboCoach framework code.

Summary of Reviews and Our Responses

ConcernOur ResponseReviewers
Diagnostic validityExecution-derived bottleneck comparisons and initial-policy rankings (R2)5CnK, 2tzs, fYkM, C3Vt
Targeting effectiveness and reproducibilityNew four-method coaching experiments using human teleoperation (R1)2tzs, fYkM
Majority-vote filteringRejection rates and filtered/unfiltered target comparisons (R3)fYkM
Judge and Router reliabilityCompletion-noise analysis and four-platform offline Router evaluation (R4–R5)5CnK, C3Vt
Novelty and skill-library scopeClarification of joint acquisition–adaptation decisions and semantic expert extensibilityC3Vt, 5CnK
Training and code reproducibilityPublic RIDI framework and training configurations (R5; 2tzs Q3)2tzs, fYkM

Summary of Additional Experiments and Findings

R1. New Human-Teleoperation Coaching Experiments

In the original simulation experiments, additional subtask demonstrations were manually segmented from separately trained VLA-teacher rollouts. Our real-robot experiments instead used human teleoperation. To test the acquisition–adaptation design with an additional supervision source, we conducted one new end-to-end simulation comparison using human-teleoperated demonstrations. All four methods are compared within this new protocol. The new results are shown below.

MethodLIBERO Budget AUC ↑RoboTwin Budget AUC ↑
Single + Uniform69.2756.70
Single + WM-Targeted70.8758.90
Modular + Random68.2353.97
RoboCoach71.9760.63

RoboCoach achieves the highest success rate at every coaching round on both benchmarks.

[Targeted acquisition] Compared with Modular + Random, RoboCoach improves Budget AUC by +3.74pp on LIBERO and +6.66pp on RoboTwin.

[Modular adaptation] RoboCoach and Single + WM-Targeted use exactly the same additional demonstrations at each round. Updating skill-specific experts instead of a shared adapter further improves Budget AUC by +1.10pp and +1.73pp, respectively.

These controls support complementary benefits from targeted acquisition and modular adaptation. The original teacher-rollout experiments also favored RoboCoach over Modular + Random (+1.5pp LIBERO; +6.8pp RoboTwin), giving a consistent direction across both supervision protocols and benchmarks.

AuthorsOpenReview ↗

General Response (2/2)

R2. Agreement Between Imagined and Native-Execution Diagnoses

On our fixed-policy LIBERO diagnostic set, we compare RoboMeter's diagnoses of imagined rollouts and matched native executions. Each initial state has three WM rollouts and one native execution. The WM-side three-seed majority vote accepts 402 of 500 initial states. Complete terminal labels, SUCCESS or TIMEOUT(subtask–expert ID), agree in 244/402 cases (60.70%). Among the 358 pairs that both diagnoses label as failures, exact subtask–expert agreement is 244/358 (68.16%).

[Human-referenced coaching targets] We separately compare WM-selected Top-2 targets with the human-annotated execution-derived Top-2 across three coaching rounds on four platforms. The mean Top-2 overlap is 45.83% (11/24 selected target slots). With WrW_r and HrH_r denoting the two target sets in each of the 12 platform–round comparisons,

Overlap@2=112∑r=112∣Wr∩Hr∣2=1124.\text{Overlap@2} = \frac 1{12} \sum_{r=1}^12 \frac{|W_r \cap H_r|}{2} = \frac {11}{24}.

We also examine cumulative coverage of the initial policy's human-ranked bottlenecks:

BenchmarkInitial-policy bottlenecks selected across three rounds
LIBERORank 2 (pick soup can), Rank 3 (pick chocolate pudding)
RoboTwinRank 1 (pick green block), Rank 3 (place medium block), Rank 4 (place third block), Rank 6 (pick first bottle)

The three-round selections cover two of the initial Top-3 bottlenecks in each simulation benchmark. These analyses characterize target agreement and cumulative coverage; R1 evaluates the learning gains from the selected supervision.

R3. Majority-Vote Rejection and Target Sensitivity

We quantify the three-seed majority-vote rejection rates across all coaching rounds:

LIBERORoboTwinFrankaAgileX
12.73%26.00%3.89%34.17%

The filtered scorecard uses majority-label frequencies among accepted states. The unfiltered scorecard retains all three seed labels per complete state group, each weighted by 1/3. Both normalize within tasks, retain SUCCESS in the denominator, and average across tasks.

For the initial acquisition round, the first target remains unchanged on all four platforms. The second changes on LIBERO and AgileX, becomes a three-way tie on RoboTwin, and remains unchanged on Franka.

R4. Sensitivity to Completion-Judgment Noise

We test acquisition sensitivity through offline perturbations of completion judgments. Using the initial LIBERO policy checkpoint, we generate 1,500 WM videos from 500 states, with three rollouts per state.

We flip the thresholded binary result with probability pp, before updating the persistence counter. A completion event requires three consecutive positive judgments. We then recompute terminal labels, three-seed majority votes, and task-balanced acquisition scores. Each perturbation probability is evaluated with three noise-sampling seeds.

The unperturbed scorecard selects pick alphabet soup can and pick white mug. The perturbation results are:

Completion-judgment flip probabilityAcquisition targets across three noise seeds
5%All three seeds retain the original Top-2.
10%Two seeds retain the original Top-2. One changes the second target.
20%All three seeds retain pick alphabet soup can and replace pick white mug with place alphabet soup can. One target changes, giving Top-2 IoU 1/3 relative to the unperturbed pair.

The selected acquisition pair is stable at 5% completion noise across the tested seeds. At higher noise levels, changes affect the second target.

R5. Router Reliability and Public Code Release

We evaluate the Router offline using the paper's original prompt and correct completed prefixes at 2,115 decision points extracted from 220 reference videos. Next-skill accuracy measures the semantic skill category. Exact skill–object accuracy additionally requires the correct target object. Accuracies are computed over decision points sampled within the videos.

PlatformNext-skill accuracyExact skill–object accuracy
LIBERO92.33% (698/756)75.26% (569/756)
RoboTwin95.24% (720/756)65.74% (497/756)
Franka89.23% (174/195)89.23% (174/195)
AgileX79.41% (324/408)58.33% (238/408)
Pooled90.59% (1,916/2,115)69.88% (1,478/2,115)

A separate test on 500 initial states yields 91.0% (455/500) next-skill accuracy and 83.4% (417/500) exact skill–object accuracy.

In the RoboTwin object-candidate ablation, exact matching increases from 65.74% to 88.89% (+23.15pp), while next-skill accuracy changes from 95.24% to 94.58%.

We have released the RIDI orchestration framework, diagnostic pipeline, and expert-update configurations:

https://github.com/RoboCoach-ICLR/RoboCoach-Framework

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

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