acceptodds
Withdrawn from ICLR 2027

World Models Dream of Success: Diagnosing and Repairing Failure Insensitivity in Robot World Models

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

18 views

Abstract

Robot world models support policy evaluation, planning, and synthetic data generation, but these applications require predictions that distinguish successful actions from failures. Across four released checkpoints from two architecture families, we observe weak sensitivity to action changes and success-like predictions on verified failures. Although recent work incorporates failures into model training, which data can repair released checkpoints without changing their architecture or training objective still remains underexplored. To this end, we introduce CureWM, which constructs alternative actions from successful demonstrations across a severity grid, verifies their outcomes through execution in simulation or on hardware, and fine-tunes released models on the resulting failures and surviving successes alongside nominal demonstrations. This construction provides controlled action contrasts from shared starting contexts. On 484 held-out LIBERO failure counterfactuals, optimism falls from 80% after fine-tuning on the official data to 30–43% across four independently fine-tuned CureWM models (38% mean). In two separate evaluations on a physical robot arm, failure predictions scored as success-like by a latent-distance diagnostic decrease from 90% after fine-tuning on successful demonstrations alone to 33% with CureWM. With failure counts per task, successful replay data, and training budget matched, counterfactual failures yield a success–failure value gap of 0.124, compared with 0.014 for freshly collected on-policy failures. These findings support execution-verified counterfactual replay for post-hoc repair and show why reduced optimism must be evaluated alongside success–failure discrimination.

Primary area:
applications to robotics, autonomy, planning
Keywords:
World action models, robot learning, failure detection, counterfactual data, model diagnosis and repair

Reviews

Among:
Shape:
1234this paper, Bottom 25%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.75 over 4 reviews, above 25% of the others.
Reviewer_7cNhOpenReview ↗
Rating
1
Confidence
3
Informativeness
3
Presentation
2
Soundness
2
Read review
Paper summary

This paper investigates failure insensitivity in robot world models, showing that released models can produce success-like predictions on execution-verified failures. The authors propose CureWM, which constructs alternative actions from successful demonstrations across a severity grid, verifies their outcomes through execution, and fine-tunes released models on the resulting failures and surviving successes alongside nominal demonstrations, without changing their architecture or training objective. Experiments in simulation and on a physical robot arm show that CureWM reduces optimism.

Critical strengths
  1. Performance. The paper separates optimism from discrimination. The distinction is valuable and is supported by the paper's own evidence. On LIBERO-10, optimism is only 2.5% while the false-positive rate reaches 99.4%. The unverified-label ablation does lower training optimism, but it does so by also pushing the values of successful actions down to 0.147.

  2. Experiments. The comparison between counterfactual failures and policy failures matches the number of failures, the per-task counts, the successful replays, and the training steps. It is the most informative experiment in the paper.

  3. Experiments. The hardware evaluation includes blinded assessments by three non-author raters, and the supplementary materials provide anonymized code and analysis scripts.

Critical weaknesses
  1. Unclear presentation of experimental findings. The manuscript contains several statements indicating that a result “does not establish,” “does not guarantee,” or is “not statistically established.” These qualifications appear across multiple simulation experiments. I would like the authors to clarify which conclusions are supported by the reported results and provide more conclusive experimental evidence.

  2. Insufficient evidence for the central claim. The authors do not convincingly demonstrate whether repairing failure prediction makes world models more useful for policy evaluation, planning, or synthetic data generation, which is the central motivation of this work. Carefully qualifying conclusions is important, but it cannot substitute for empirical evidence.

  3. Missing related word and limited novelty. The motivation, experimental setup, models, and platforms used in this paper are similar to those in VLAW [1], yet the paper neither cites nor compares against this work. VLAW explicitly identifies the excessive optimism of world models trained only on demonstrations. On the DROID Franka platform, it fine-tunes Ctrl-World using real rollouts labeled as success or failure, reports fewer false-positive interaction predictions, and demonstrates policy improvement across five real-world task categories. The authors should therefore clearly articulate the differences from VLAW and provide evidence of improvements over it.

  4. Limited original methodological contributions. The perturbation families used in this paper come from MiraBench. I consider “without changing the architecture or training objective” a constraint, which VLAW also satisfies. Setting these existing elements aside, the paper’s original contributions appear limited to two aspects: the specific construction of counterfactual failures through perturbations that preserve a shared action prefix with the source demonstration, and the comparison between counterfactual failures and policy failures.

[1] VLAW: Iterative Co-Improvement of Vision-Language-Action Policy and World Model.

Questions for authors

The paper positions itself as repairing released checkpoints, so the most direct comparison should be with the released model before repair. Across the experiments that measure control performance, CureWM does not improve average performance, and performance declines in most cases. For example, applying CureWM to the released checkpoint lowers average task success on LIBERO, while every CureWM variant performs worse than the released model in RoboCasa. The authors acknowledge a “repair–control trade-off” on RoboCasa in their Limitations section. In other words, improvements in prediction metrics come at the expense of control performance. I consider this the most important aspect to improve, how to repair failure prediction while preserving the world model’s existing capabilities as much as possible.

4 comments

We thank the reviewer. The control question is where most of the new compute went. New arms are at 17,500 steps like the paper's and intervals are bootstraps clustered by source trajectory (prediction) or paired by task (closed loop).

W1. Supported conclusions. Established over seeds (intervals exclude zero): (1) released and step-matched baselines are failure-insensitive on verified counterfactual failures (AUROC 0.495 to 0.499); (2) CureWM repairs this on the held-out, off-grid and unseen-source sets (+0.15 to +0.26 AUROC, four seeds); (3) verified labels are necessary (relabeled survivors: 0.545 to 0.583); (4) the repair transfers to the released policy's natural failures once under way (value drop 0.13 to 0.21, successes at most 0.03), not before; (5) the policy's own failures do not repair counterfactual sensitivity but are the stronger data on policy rollouts. Not established, said so in one limitations paragraph: same-demonstration survivors, cup-to-cube transfer, early anticipation, planning gains, hardware gains over the adaptation point.

W2. Usefulness. Monitoring the released policy (818 rollouts, 238 failures unseen by both arms), at 10 % false alarms: the baseline catches 41 % of failures at the midpoint and 79 to 81 % at three quarters, CureWM 61 to 65 % and 90 to 92 % (two seeds each). Ranking 30 perturbed controller variants (success 27 to 100 %) by mean predicted value: Spearman 0.31 to 0.66 (+0.345 [+0.236, +0.440]), calibration unchanged; variants of the trained families, not learned policies. Hardware policy evaluation (31 real policy conditions, no new robot time): counterfactual repair recovers part of the loss from success-only fine-tuning (+0.05 [-0.00, +0.10] AUROC), not beyond the adaptation point. Planning: no established gain. So: a late failure monitor and a ranker of perturbed variants, no planning or hardware evaluation gain by itself.

W3. VLAW. The revision cites it. VLAW fine-tunes Ctrl-World on the policy's own real rollouts labelled by outcome, without perturbation, counterfactuals or severity. Our policy-failure arm is that recipe under matched failures, per-task counts, successes and steps (7,500 for these 140-failure pools); the comparison cuts both ways. Counterfactual failures repair sensitivity on every counterfactual set (AUROC 0.606 / 0.584 / 0.635 against 0.518 / 0.498 / 0.510), need no policy in the loop and cost 0.33 GPU-minutes per verified failure against 7.9. The policy's own failures are stronger on policy rollouts: midpoint AUROC 0.925 against 0.755 on natural failures held out from both arms; on the robot, an arm trained on other policies' real rollouts predicts unseen policies at AUROC 0.94 against 0.83 (+0.11 [+0.03, +0.19]); counterfactual repair adds +0.04, interval containing zero (different camera placement, not a clean head-to-head). We claim no improvement over VLAW: the two sources repair different things, and an arm trained on both keeps both properties.

W4. Novelty. The revision states the contribution as those two elements plus the controlled finding above and the measured cost.

Q. Control cost. The reviewer is right. New: two seeds per arm on all 40 LIBERO tasks, 500 episodes per suite, task-paired intervals:

SuiteBaseline (seeds)CureWM (seeds)CureWM - baseline
Spatial95.6 / 97.496.2 / 97.2+0.2 [-1.1, +1.5]
Object99.0 / 99.699.8 / 99.2+0.2 [-0.5, +0.8]
Goal96.4 / 96.2 / 96.894.8 / 95.2 / 95.0 / 95.2-1.42 [-2.97, +0.08]
LIBERO-1096.2 / 96.895.4 / 94.8-1.4 [-2.4, -0.5]
40 tasks (2 seeds/arm)96.80 / 97.5096.55 / 96.60-0.57 [-1.18, +0.00]

The submission's single seed (-0.25 [-1.30, +0.75]) hid a small, suite-dependent cost: Goal and LIBERO-10, not Spatial and Object. Fine-tuning itself costs more (baseline minus released -1.85 [-2.85, -0.90]; CureWM -2.07 [-3.00, -1.20]). The RoboCasa trade-off stands (OpenDrawer 17/30 at 5,000 steps against 28/30 released; 26/30 at 20,000). Mitigations: masking the action loss on failed replays keeps the prediction repair (optimism 32.9 % against 30.2 %) but not the control (Goal 94.6, -1.87 [-4.00, -0.00]); and interpolating weights between baseline and CureWM, one model per point:

Weight on CureWM00.250.50.751
Goal success96.496.294.096.694.8
Natural failures caught at 10 % false alarms, midpoint / three quarters41 / 81 %45 / 8253 / 8759 / 8865 / 92

The repair grows with the weight, the cost does not: the 0.75 point keeps about three quarters of the repair (+0.18 [+0.10, +0.27] over the baseline, -0.06 [-0.13, -0.02] under CureWM) at the baseline's success rate; with single-seed endpoints, a candidate trade-off, not a result. The revision reports the cost as a result and the interpolation as open.

Dear Reviewer 7cNh,

Thank you again for your thoughtful review and constructive comments on our paper. We have posted our response to your review and hope it addresses your concerns.

We can totally understand this is a busy period. When you have a moment, we would greatly appreciate it if you could take a look and let us know whether anything remains unclear. We would be happy to provide further clarification or additional results if needed.

Thank you for your time and consideration.

Best, The authors

Thank you for your response, and I apologize for not reading and replying to it sooner. If time permits, I would appreciate a further response before the discussion deadline. I will reassess my rating in the next phase.

I appreciate the candor of your rebuttal and the additional experiments and analyses. My first two weaknesses have been addressed. Regarding Weakness 3, is there evidence that the proposed method offers advantages over VLAW?

Regarding my question about the loss of control performance during prediction repair, could this issue be mitigated by isolating parameter updates for prediction repair from those for action generation, or by addressing gradient conflicts between prediction and control objectives?

We thank the reviewer for the follow-up questions.

  1. Evidence regarding VLAW (W3). With the two failure sources matched (140 unique failures each, the same 580 successes, 7,500 and 17,500 steps, two seeds), the evidence indicates complementary strengths rather than a uniform advantage.

(a) Counterfactual failures repair sensitivity to action contrasts, and the policy's own failures (the VLAW recipe) do not: AUROC 0.57 to 0.61 against 0.52 on held-out counterfactuals, 0.55 to 0.58 against 0.50 on unseen severities, and 0.57 to 0.64 against 0.51 on counterfactuals built around the policy's own trajectories. The VLAW-style arm also lowers the value of successes (0.38 to 0.39 against 0.46 for the baseline, while the counterfactual arm stays at 0.43 to 0.45), and counterfactual data requires no policy failures (822 replays from 27 demonstrations, before any rollout exists).

(b) On the policy's own natural failures the VLAW-style arm is stronger (value 0.04 to 0.09 at step 75 against 0.27 to 0.36), as it was on the real robot (generated-end AUROC 0.937 against 0.866, with the scene confound stated in Section 5).

(c) The arm trained on both sources retains both properties (0.54 to 0.60 on the counterfactual sets, and 97 to 98 % of natural failures detected at the midpoint at a 10 % false-alarm budget).

The revision will state the comparison accordingly. Counterfactual repair is the less expensive, policy-independent and more transferable source, the VLAW recipe is stronger on the policy's own rollouts, and the two combine. A hardware comparison without the scene confound (counterfactuals and rollouts in the same scene, four arms from one binding checkpoint) is in progress and will be reported regardless of its direction.

  1. Isolating the updates to mitigate the control cost. Two reported arms bear on this. Masking the action loss on failed replays preserves the prediction repair (optimism 32.9 % against 30.2 %) but not the control performance (Goal 94.6 %, −1.87 [−4.00, −0.00] points), so the cost is not imitation of failed actions but a shift of the shared representation. Linear weight interpolation between the baseline and CureWM shows that the objectives are not irreconcilable: at weight 0.75 the model retains about three quarters of the repair (two seed pairs, 0.74 and 0.77) with no measurable closed-loop cost over 40 tasks (+0.12 [−0.45, +0.70] against the baselines and +0.70 [+0.10, +1.30] against CureWM). Explicit parameter isolation (a separate value and prediction pathway, adapters for the repair with the action pathway frozen, or gradient projection) is the natural next step.
Reviewer_7Yg2OpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

The paper tackles a widely known a difficult area of world model plasticity, specifically focusing on action conditioned world models noting that Action-conditioned robot world models are failure-insensitive: given a failing action sequence, they still predict a success-like future or a high value. The authors show this on released Cosmos Policy and Ctrl-World checkpoints. The authors propose a framework to extract better data in order to improve the world model's performance. From my understanding, the authors take successful demonstrations and perturb actions after an intervention time. They then execute the perturbed sequence in simulation and record if it succeeds or fails, they add verified failures and surviving successes to the original data. Finally, they fine tune the model.

Critical strengths

The problem is real and clearly framed. The distinction between optimism and discrimination is the paper’s best idea, and the authors apply it to their own method by reporting false-positive rates and both V(a⁺) and V(a⁻).

Hardware evidence with a human check. Blinded raters, hashed clip IDs and high agreement (κ 0.84–0.95) support the direction of the hardware result. They also show the latent-distance diagnostic is noisier than human judgement.

Critical weaknesses

The theory is thin.

Propositions 1–2 are near-trivial: one action per context means action isn’t identifiable, and pairs force a log-2 penalty. The authors admit they say nothing about trained networks, generalization or held-out behaviour. The appendix is fine as motivation, but it shouldn’t be presented as a contribution.

Novelty is moderate.

Adding failures is not new (FACT [1], AHA [2], counterfactual failure synthesis [3]), and the perturbations come from MiraBench. The new elements are the recipe (same-prefix perturbations, execution verification, keeping surviving successes, no architecture change) and the evaluation framing. Those are useful but incremental.

Experimental concerns

There is one baseline seed. Better prediction is never shown to help any downstream use. The motivating uses are policy evaluation, planning and synthetic data. The results on these are:

Planning: best-of-N selection shows no significant gain. Policy ranking: untested. Control: RoboCasa shows a repair–control trade-off, and LIBERO task success drops slightly.

[1] Peng, Q., Liang, Y., Yan, R., Hansen, N., & Wang, X. (2026). FACT: Failure-Aware Causal Training for World-Action Models. In Conference on Robot Learning (CoRL).

[2] Cai, J., Ling, L., Chu, S., Liu, Z., Kang, J., Liang, Z., Xu, W., Mao, Y., Zhang, W., Yang, X., Ying, R., Zheng, R., & Mu, Y. (2026). AHA-WAM: Asynchronous Horizon-Adaptive World-Action Modeling with Observation-Guided Context Routing. arXiv preprint arXiv:2606.09811.

[3] Dayou Li, Jiuzhou Lei, Hao Wang, Lulin Liu, Yunhao Yang, Zihan Wang, Bangya Liu, Minghui Zheng, & Zhiwen Fan. (2026). Learning Actionable Manipulation Recovery via Counterfactual Failure Synthesis.

Questions for authors

I couldn't find an exact definition for 'severity' just that the severity grid was used to perturb actions. Can an exact definition be added?

2 comments

We thank the reviewer for a precise review. We answer the three weaknesses in turn and then give the severity definition. New arms are fine-tuned to 17,500 steps like the paper's and intervals are bootstraps clustered by source demonstration (prediction) or paired by task (closed loop).

Theory. Agreed. Appendix B was not one of the listed contributions, and the revision compresses it into a motivation paragraph. The one claim we keep from it is tested rather than argued: relabeling surviving replays as failures instead of executing them gives AUROC 0.545 to 0.583 over three seeds, below every verified arm (0.639 to 0.743 over seven seeds of two recipes).

Novelty and related work. [1] FACT appeared in August 2026 and is cited as concurrent work. [2] is AHA-WAM, an architecture paper that does not use failure data; the AHA we cite is Duan et al. (2025). [3] synthesizes failures to learn recovery policies, not to repair a world model's predictions. We agree that the taxonomy is MiraBench's and the recipe is the contribution. What the revision adds beyond the recipe is a controlled finding about repair data: verified labels are necessary (above); the construction matters, not the state distribution (counterfactuals built from the policy's own successful rollouts repair sensitivity, AUROC 0.54 / 0.53 / 0.55 on three evaluation sets, while the policy's own failures at the same budget do not, 0.52 / 0.50 / 0.51); and the two sources are complementary (below).

One baseline seed. There are now three baseline seeds and four CureWM seeds at matched steps. Held-out AUROC: baseline 0.495 / 0.499 / 0.498, CureWM 0.743 / 0.674 / 0.681 / 0.707; the same ordering holds on an off-grid severity set and on a set whose source trajectories no model has seen. Closed-loop LIBERO-Goal success: baseline 96.4 / 96.2 / 96.8, CureWM 94.8 / 95.2 / 95.0 / 95.2.

Downstream use. We evaluated the uses the reviewer names and report the nulls with the positives.

  • Monitoring the released policy's own rollouts (818 episodes, 238 failures, none seen by the baseline or CureWM arms): at a 10 % false-alarm rate the baseline catches 41 % of failures at the episode midpoint and 79 to 81 % at three quarters, CureWM 61 to 65 % and 90 to 92 % (two seeds each). Neither anticipates a failure before it unfolds.
  • Ranking: 1,680 held-out replays form 30 perturbed controller variants (family by severity, success rates 27 to 100 %). Ranking them by mean predicted value gives Spearman 0.31 for released and baseline, 0.66 for CureWM (+0.345 [+0.236, +0.440]); calibration does not improve (MAE 23.3 to 22.3 points). These are perturbed controllers of the trained families, not learned policies, so the revision calls it ranking of perturbed variants.
  • Hardware policy evaluation (real rollouts of 31 policy conditions, no new robot time): counterfactual repair recovers part of the loss caused by success-only fine-tuning (+0.05 [-0.00, +0.10] AUROC) but does not exceed the adaptation point, and an arm trained on other policies' real rollouts is clearly better (0.83 to 0.94). The counterfactual data came from a different camera placement, so this is not a clean head-to-head; we report it as is.
  • Planning: best-of-N gave no established gain, and the revision no longer lists planning as a demonstrated benefit.
  • Control: fine-tuning itself costs about two points (baseline minus released -1.85 [-2.85, -0.90] over 40 tasks). Relative to the step-matched baseline, the single-seed 40-task difference was -0.25 [-1.30, +0.75]; with seeds, LIBERO-Goal gives -1.42 [-2.97, +0.08] with every CureWM seed below every baseline seed, and over 40 tasks with two seeds per arm -0.57 [-1.18, +0.00] (CureWM 96.6 and 96.6, baseline 96.8 and 97.5), concentrated on Goal and LIBERO-10 (-1.3 and -1.4 points) with no difference on Spatial and Object. Masking the action loss on failed replays does not remove the cost (94.6 on Goal). The RoboCasa trade-off stands. The revision reports the cost as a result.

Severity. Each family has one scalar lambda in {0.2, 0.4, 0.6, 0.8, 1.0} that scales its perturbation inside its target phase; actions are normalized OSC-pose deltas in [-1, 1], and phases come from the gripper command and contact. Insufficient grip: gripper command moved toward open by 0.9 lambda (1 - g) during grasp and carry. Premature release: the release instant moved earlier by a fraction lambda of the carry phase. Carry slip: round(3 lambda) instants in carry with the gripper opened by 0.5 + 0.5 lambda and a lateral spike of standard deviation 0.5 lambda. Contact oscillation: a sinusoid of amplitude 0.7 lambda along the approach axis during grasp and carry. Wrist tilt: a rotation offset of 0.8 lambda about one horizontal axis over the middle third of carry. Approach overshoot: an additive push of 0.6 lambda along the nominal motion direction over the last quarter of the approach. The revision adds this as a table.

Dear Reviewer 7Yg2,

Thank you again for your thoughtful review and constructive comments on our paper. We have posted our response to your review and hope it addresses your concerns.

We can totally understand this is a busy period. When you have a moment, we would greatly appreciate it if you could take a look and let us know whether anything remains unclear. We would be happy to provide further clarification or additional results if needed.

Thank you for your time and consideration.

Best, The authors

Reviewer_6FwXOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper introduces CureWM, a post-hoc data-centric procedure to repair failure insensitivity in released robot world models without changing their architecture or training objective. The method perturbs successful demonstrations along severity-controlled families, executes the modified action sequences to verify outcomes, and fine-tunes the released model on both verified failures and surviving successes. Across LIBERO simulation and Franka hardware evaluations, CureWM consistently reduces optimism on verified failures and increases success–failure discrimination, and matched comparisons suggest execution-verified counterfactual replays are more effective than fresh policy failures for repairing failure sensitivity.

Critical strengths
  1. The core idea of execution-verified counterfactual replays sourced from perturbed successful demonstrations, while simple, is a well-motivated and practically impactful recipe for repairing released world models without architectural or objective changes.

  2. Addresses a timely and impactful problem: making released world models more decision-relevant by distinguishing successes from failures.

Critical weaknesses

Many counterfactual evaluations share demonstrations with the official training data; only 53 of 484 failures come from demos absent from the shared official data, which may inflate apparent generalization.

Questions for authors
  1. How sensitive are the results to the choice of frozen encoder and the distance metric used in Eq. (2)? Have you tried alternative representations (e.g., CLIP, I3D features) or learned discriminators to assess whether the findings persist?

  2. What is the approximate wall-clock and interaction cost (simulation steps, robot hours) to construct the counterfactual replay sets? Any guidance for practitioners on the budget–benefit trade-off compared to collecting fresh policy failures?

  3. To what extent does CureWM overfit to specific perturbation families? Have you evaluated on unseen families or different severity grids to quantify out-of-family generalization?

2 comments

We thank the reviewer for the careful reading. W1 and Q3 are answered with experiments run since submission, Q1 and Q2 with material that was in the appendix but not foregrounded. New arms are at 17,500 steps and intervals are cluster bootstraps over source trajectories.

W1. Shared demonstrations. We agree that 53 failures from three demonstrations cannot carry the claim. We built an evaluation set whose sources no model has seen: successful rollouts of the released policy itself, perturbed and re-executed (28 sources, 840 replays, 272 verified failures), absent from the official data and from every repair set. The results match the original held-out set: baseline optimism 83.1 %, AUROC 0.497; CureWM 31.2 %, AUROC 0.727 (-51.8 pts [-62.4, -40.9]; AUROC +0.229 [+0.161, +0.309]). Four CureWM seeds 0.650 to 0.727 against baseline seeds 0.494 to 0.497. So the held-out numbers (30.2 %, 0.743) were not inflated by shared demonstrations. One more thing stated in the revision is that we kept only sources whose unperturbed replay re-executed successfully (27 of 40), which favors trajectories that tolerate small perturbations. This set replaces the 53-failure subset.

Q1. Encoder and metric. (i) Most results involve no encoder: every LIBERO Cosmos Policy and RoboCasa number, including all numbers in this reply, reads the model's own value head (Eq. (1)). Eq. (2) enters only the video diagnostics (Ctrl-World with SVD VAE features, and the Franka evaluation). (ii) On hardware we checked the diagnostic against people: three blinded non-author raters judged 8/15 adapted-model and 0/15 CureWM failing-action predictions as success-like, where the diagnostic gives 13/15 and 6/15: same direction, with the diagnostic as the more conservative reading. One- and two-reference AUROCs agree (0.67 to 0.90, 0.66 to 0.96). We have not recomputed the hardware scores under CLIP or I3D features and list this as a limitation. (iii) Learned discriminator: a linear probe on frozen features of the released model's own imagined futures (1,680 held-out LIBERO replays, 5-fold by source demonstration) reaches AUROC 0.704, against 0.497 for the released value head and 0.743 for CureWM. An external detector recovers part of the ignored signal, but it needs the same verified labels and stays below in-place repair.

Q2. Cost. Generating the four held-out LIBERO shards took 162 P100-minutes for 1,680 replays and 484 verified failures, about 0.33 GPU-minutes per failure, with no policy in the loop. Collecting the released policy's own failures took 8,000 episodes, about 31 hours on one RTX 4090, for 238 failures, about 7.9 GPU-minutes per failure. Matching the counterfactual pool's per-task counts would need roughly 42,000 episodes, since some tasks almost never fail. On the Franka, 220 verified failures took about 6.5 robot-hours. Fine-tuning is identical for every arm: 17,500 steps, 7.5 to 10.5 GPU-hours.

Guidance from the matched comparison (same failure count, per-task counts, successes and steps): counterfactual failures repair sensitivity on every counterfactual set (AUROC 0.606 / 0.584 / 0.635 on held-out, off-grid and policy-sourced sets, against 0.518 / 0.498 / 0.510 for policy failures), while on the policy's natural failures held out from both arms the order reverses (midpoint AUROC 0.755 versus 0.925; baseline 0.578). Counterfactuals when no policy is in the loop or sensitivity across sources is the goal. The policy's own rollouts when catching that policy's failures is the goal and an arm trained on both keeps both properties.

Q3. Overfitting to perturbation families. We partly agree with this and we stated the reason in the revision.

  • Severity grid: no. At severities 0.3 / 0.5 / 0.7 / 0.9, none in the training grid (1,368 replays, 414 failures, 57 held-out demonstrations), baseline gives 80.4 % / AUROC 0.472 and CureWM 31.6 % / 0.735 (+0.263 [+0.209, +0.324]); four seeds 0.635 to 0.735.
  • Families: yes, where tested. Repair is uneven within the trained families (Table 8: three improve, three do not move), and leave-one-type-out (Table 9) transfers partially for insufficient grip and premature release, not for contact oscillation, mixed for wrist tilt. We did not add an unseen family.
  • Natural failures, constructed from no family: on 818 rollouts of the released policy, CureWM lowers the value of failures by 0.13 to 0.22 once the failure is under way, successes by at most 0.02 (all four seeds), and does not anticipate failures earlier. Transfer beyond the families is real but late and partial.

Dear Reviewer 6FwX,

Thank you again for your thoughtful review and constructive comments on our paper. We have posted our response to your review and hope it addresses your concerns.

We can totally understand this is a busy period. When you have a moment, we would greatly appreciate it if you could take a look and let us know whether anything remains unclear. We would be happy to provide further clarification or additional results if needed.

Thank you for your time and consideration.

Best, The authors

Reviewer_a9PNOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

This paper investigates failure insensitivity in robot world models, where predictions remain success-like even when the conditioned actions lead to failure. It proposes CureWM, a data-driven approach for repairing released models without modifying their architectures or training objectives. CureWM perturbs successful demonstrations at multiple severity levels, verifies the resulting outcomes through execution, and fine-tunes models using both successful and failed replays alongside the original training data. Experiments with Cosmos Policy and Ctrl-World on LIBERO, RoboCasa, and physical robot tasks demonstrate improved success–failure discrimination in several settings. Comparisons with matched failure counts and training budgets favor counterfactual failures over freshly collected policy failures on the evaluated counterfactual test set. Additional ablations examine the roles of successful replay partners and verified outcome labels. The paper also emphasizes that reduced optimism alone does not establish repair and should be assessed alongside discrimination and false alarms on successful actions.

Critical strengths
  1. This paper is well written. The logic is clear and is easy to understand.

  2. CureWM consistently reduces LIBERO-Goal value optimism across four independent fine-tuning runs, from approximately 80% to 30–43%. Physical-robot experiments provide additional support, including blinded human judgments showing fewer success-like predictions for failing actions. These results suggest that targeted training data can meaningfully improve existing world models without architectural changes, making the approach relevant to practitioners working with released checkpoints.

  3. The paper evaluates success–failure discrimination and false alarms on successful actions alongside optimism. Beyond the pooled results, AUROC improves from 0.537 to 0.714 within fixed perturbation-type and severity groups, providing evidence that the gains cannot be explained solely by recognizing perturbation categories or severity levels. This strengthens the assessment that the method improves outcome discrimination rather than merely lowering predicted values.

Critical weaknesses

Limited novelty. The proposed method primarily combines perturbation families adopted from prior work, execution-based outcome verification, and standard fine-tuning with successful and failed replays. Its distinctive contribution lies in constructing these examples around shared demonstrations and retaining successful perturbed replays. The controlled comparisons and ablations provide useful empirical evidence, but I find the resulting methodological and conceptual advances incremental. In particular, the current results do not yet establish a sufficiently generalizable insight into why this specific construction should be preferred over alternative failure-data collection strategies. This limits the significance of the contribution in my assessment.

Questions for authors
  1. The paper identifies the combination of controlled perturbations, execution verification, and successful replay partners as its contribution. What specific new insight about repair-data construction do the authors consider established by the experiments? In particular, do the results support the importance of constructing alternatives from the same demonstration, or primarily the effectiveness of the combined recipe? Please explain how the successful-replay ablations support this distinction given the acknowledged differences in sampling exposure and training variability.

  2. The matched comparison between counterfactual and policy-failure training is evaluated on counterfactual failures generated using the training perturbation families and severity grid. Have these same models also been evaluated on independent natural policy failures or other failure distributions? If such results are available, please report them, as they could materially strengthen the evidence for the proposed data construction’s distinctive value. Otherwise, please clarify the intended scope of the claimed advantage over policy-failure data.

2 comments

We thank the reviewer for stating the concern precisely: do the experiments establish an insight about repair data, or only that one recipe works? Since submission we ran the controlled experiments that separate the two (all arms at 17,500 steps, with seeds).

Q1. What is established.

  1. Verified labels are necessary. Relabeling survivors as failures instead of executing them gives AUROC 0.545 to 0.583 over three seeds. Every verified arm is above every unverified seed (CureWM 0.674 to 0.743 over four seeds and without same-source survivors 0.639 to 0.671 over three). Three baseline seeds stay at 0.495 to 0.499, like the released checkpoint.

  2. The construction matters, not the state distribution. An arm trained on counterfactuals built from the policy's own successful rollouts behaves like the demonstration-sourced counterfactual arm (AUROC 0.54 / 0.53 / 0.55 on held-out, off-grid and policy-sourced counterfactuals), not like the arm trained on the policy's own failures at the same budget (0.52 / 0.50 / 0.51). The policy-failure arm does not discriminate even on counterfactuals built around its own trajectories.

  3. Same-demonstration survivors: not established. They add 4.4 points of optimism and +0.05 AUROC on average with the same sign in every seed, but the seed ranges overlap. The reviewer is right that the submission leaned on this ablation more than it could bear. The revision reports it as a small, unconfirmed benefit.

So the claim we now make is not the recipe but the controlled finding: execution-verified same-context contrasts repair failure sensitivity, unverified labels do not, and (below) counterfactual and policy failures repair different things.

Q2. Natural policy failures. Yes. We evaluated all arms on 818 natural rollouts of the released policy (238 failures, 580 successes, 98 failures and all successes unseen by every arm), querying the value with the executed action chunk, protocol pre-registered.

  • No arm anticipates a failure before it unfolds (AUROC 0.48 to 0.53 at steps 0 to 32. CureWM minus baseline -0.001 [-0.037, +0.043]). The policy-failure arm's early edge (0.68) comes from initial states where it had trained on a failure. On the 10 failures from unseen initial states it disappears.
  • Once a failure is under way, CureWM lowers its value by 0.13 to 0.22 (e.g. -0.222 [-0.356, -0.117] at step 96) while successes move by at most 0.02 for all four seeds. The policy-failure arm lowers failures more (0.34 to 0.49) but also successes (0.04 to 0.14).
  • The two sources are complementary: counterfactual failures discriminate on every counterfactual set (+0.076 [+0.054, +0.100] over baseline), the policy's own on none (+0.021 [+0.009, +0.038]) while on natural failures the order reverses. An arm trained on both keeps both properties (0.56 / 0.60 on counterfactuals; 97 to 98 % of natural failures caught at the midpoint at 10 % false alarms, against 45 % for the baseline).

In our future revision, we will state the scope as: counterfactuals need no policy to fail, cost about 0.33 GPU-minutes per verified failure against about 7.9 for a natural one, repair sensitivity on unseen severities and unseen sources, and transfer partially to natural failures. The policy's own failures are stronger on that policy's rollouts and do not transfer. We no longer claim counterfactuals are better in general.

Dear Reviewer a9PN,

Thank you again for your thoughtful review and constructive comments on our paper. We have posted our response to your review and hope it addresses your concerns.

We can totally understand this is a busy period. When you have a moment, we would greatly appreciate it if you could take a look and let us know whether anything remains unclear. We would be happy to provide further clarification or additional results if needed.

Thank you for your time and consideration.

Best, The authors

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

Related papers

Discussion (0)

Sign in to comment.