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Under review as a conference paper at ICLR 2027

Correlation Does Not Certify Reliable Evaluation: Identifiability Limits of World-Model-Based Robot Policy Selection

Abstract

Policy evaluation with world-model rollouts and a VLM judge has been reported to correlate strongly with real-world success rates. We ask whether this correlation certifies sensitivity to the consequences of actions. Empirically, it does not. The evaluator's scores track simulator success rates, yet barely change under interventions that make the task fail in the simulator, and rise under a perturbation that lowers success rates. Most of the score variance across candidates is instead explained by similarity to the world model's training demonstrations. We then prove that, without additional real-world trials, no evaluation procedure can reliably identify the better of two candidates that differ only in an action unsupported by the demonstrations, even given a pretrained world model, the candidates' weights, and a perfect judge. Identifiability depends on , the expected number of demonstrations containing that action, rather than on , and perfect rank correlation can coexist with no response to such interventions. Finally, we propose ResGap, a coarse screening metric that needs neither world-model rollouts nor a VLM judge, ranks candidates more accurately than the world-model evaluator, and allows real-world trials to be concentrated on the top-ranked candidates. Correlation with success rates therefore does not certify reliable evaluation for world-model-based robot policy selection.

Primary area:
applications to robotics, autonomy, planning
Keywords:
World Models, Robot Policy Evaluation, Robot Manipulation, Identifiability

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_heR3OpenReview ↗
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Paper summary

Action-conditioned video world models coupled with vision-language model (VLM) judges are increasingly used to evaluate robot policies without physical trials. While prior benchmarks validate these evaluators via high correlation with real success rates, the paper investigates whether statistical correlation genuinely certifies sensitivity to action consequences.

Empirical results show that auditing a state-of-the-art evaluator (Wan2.1 video model + Qwen2.5-VL judge on LIBERO) across 31 policies reveals critical failure modes:

(1) Intervention Insensitivity: Despite showing r=0.72r = 0.72 correlation across 24 chunked action policies, the evaluator altered its judgment in only 0.060.06 of cases under interventions designed to cause guaranteed physical task failure.

(2) Perturbation Blindness: A test-time grasp-delay perturbation dropped simulator success from 0.910.91 to 0.370.37 while counterintuitively raising the evaluator score from 0.740.74 to 0.840.84.

(3) Demonstration Bias: Evaluator scores correlate strongly (r=−0.86r = -0.86) with how closely generated rollouts resemble the training demonstrations, rewarding memorization rather than physical correctness.

The authors prove that without additional environment interactions, no evaluator can reliably rank two candidate policies whose distinction depends on actions unsupported by demonstrations. This fundamental unidentifiability holds even assuming candidate weights, an optimal pretrained world model, and an error-free judge. Controlled experiments verify that scaling demonstrations without coverage of the critical action fails to decrease error.

Critical strengths

(1) The phenomenon identified in the paper is interesting and worth exploring, which will inspire new research effort on rethinking the role of action-conditioned generative model in robotics.

(2) The experiments are extensive and findings in the experiments including Perturbation Blindness and Demonstration Bias demonstrate the meaningfulness of this problem.

(3) The authors provide theoretical analysis on the findings.

Critical weaknesses

(1) Most of the experiments focus on simulation environment. Results can be more supportive if there is real-world experiments.

(2) The proposed ResGap can only serve as coarse-screening. Is it possible for us to find a space that can well describe the relationship between the rollouts of generative model and success rate in target environment? Or does it stem from the ability of current generative model?

Questions for authors

Please refer to the critical weakness part.

2 comments

Thank you for reviewing our paper. We agree that real-world experiments would further strengthen our findings, and we consider them a top priority for future work. Although our experiments are conducted entirely in simulation, they demonstrate that correlation with success rate does not guarantee sensitivity to action consequences, consistent with our theoretical results.

Your question about which space could capture the relationship between generative-model rollouts and success rates in the target environment is precisely what we are currently investigating. Our results show that even when generated videos resemble successful demonstrations, they do not necessarily reflect the consequences of the given actions accurately. This motivates us to investigate how the relationship between observations and actions is reflected in policy parameter adaptation, in addition to video similarity. Inspired by ProjNorm and MAML, we believe that capturing the relationship between parameter changes and success rates in the target environment could lead to a useful evaluation metric. ResGap is a first step toward exploring this possibility.

Improvements in generative models may also mitigate the failure patterns observed in this study. However, parameter-based evaluation is also subject to the limitations of Theorem 1 when the available information is the same. Clarifying the conditions under which such metrics can predict success rates therefore remains an important direction for future work.

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Reviewer heR3 please respond to author comments

Reviewer heR3 please respond to author comments

Reviewer_vuETOpenReview ↗
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Paper summary

The paper empirically identifies that robot manipulation policy evaluation in world models can be insensitive to important yet subtle action changes and give falsely positive evaluation results. Based on the observation, the paper questions if the correlation between the evaluation results in a source and a target environment is a reliable metric to reflect the faithfulness of a world model for evaluation.

Critical strengths
  1. The observation made in this work is good, and the authors conduct good amount of experiments to try to isolate the reason causing the false positive evaluation from world models.
Critical weaknesses

Despite the efforts made, I don’t think the core claim is sufficiently supported with the existing evidence.

  1. I think the results in Figure 1(a) is not sufficient as is to support the claim “correlation is not a reliable metric for policy evaluation”. The world model judge is not in itself uniformly accurate across the state-action space. Evaluating it for heterogeneous policy classes might just pushes the judge to less accurate areas and causes the correlation drop. Existing evidence in the paper is not sufficiently ruling this possibility out.
  2. Error decomposition: the error decomposition and characterization in Eq. (1) is not quite rigorous. Does the decomposition assume the underlying policy is a deterministic one? If not, as in the evaluated policy classes, even rolling out the same policy in the simulator twice can and normally will generate two different sequences of actions. Currently the decomposition is not distinguishing whether the behavior changes come from different environments or just the underlying randomness of a policy itself.
  3. Section 3.3: I think this section is not serving its purpose:
    1. First, playing the same sequence of action in open-loop across simulation and a world model is not evaluating the same policy due to the dynamics difference between the two environments.
    2. Second, the evidence given in this section only proves the point that the world model becomes invalid after action modification and gives wrong judgement, cf. my point 1 above. The simulator still gives the correct results that the modified action sequences will fail. In this case, the correlation is a reliable metric and becomes low between a correct simulator and an incorrect world model.
  4. Small things:
    1. Some notations are not defined properly before being used - for example, the Pearson correlation coefficient in the abstract, the epsilon in the Introduction.
Questions for authors

N/A

6 comments

Thank you for reviewing our paper.

1. Correlation and action sensitivity

For the first point, your explanation is plausible. That is, the decrease in correlation when including different policies can be caused by these policies visiting state-action regions where the world model cannot predict accurately. Moreover, we confirmed that differences in action-update frequency for single-action policies contributed to the performance decrease in the additional experiments conducted to address the second point.

However, although the evaluation scores for the 24 ACT and Diffusion Policy candidates showed a high correlation with simulator success rates, the evaluator's judgments barely changed even when the simulator outcomes changed from success to failure under the grasp-release intervention.

This shows that high correlation in the original candidate set and insensitivity to important action changes can coexist. Our claim is that high correlation alone cannot guarantee sensitivity to action consequences. We will clarify this claim and its supporting evidence in the manuscript.

2. Error decomposition and stochastic policies

Thank you for raising this concern. Our explanation of how Eq. (1) handles stochastic policies and how its terms should be interpreted was insufficient. We have re-examined the implementation and saved data, reanalyzed the results using matched episode sets, and conducted additional experiments on action-update frequency.

First, Eq. (1) is an algebraic identity obtained by adding and subtracting intermediate success rates; it does not assume deterministic policies. Although stochastic policies can produce different action sequences and outcomes from the same initial state, the expected success rates under each evaluation condition, and their difference, remain well-defined. Our analysis estimates this average difference. However, the identity alone does not establish how precisely the difference is estimated from finite trials or which factors cause it. We therefore performed the following checks.

Regarding Table 1, we recalculated all four quantities using the same 100 conditions (10 tasks with 10 initial states each, using only the first world-model generation). By resampling the matched results for each initial state within each task using a paired bootstrap (10,000 resamples), we obtained the following behavior-change estimates and 95% confidence intervals: ACT: −0.16 [−0.18, −0.14], Diffusion Policy: −0.06 [−0.08, −0.04], and BC-RNN: −0.30 [−0.34, −0.26]. Therefore, we confirmed that the average differences remained nonzero in the reanalysis.

Note that the ACT candidates do not sample actions at inference time. On the other hand, we do not interpret the individual differences in outcomes for stochastic policies solely as effects of the environment, because policy randomness affects episode-level differences.

Regarding our evaluator, single-action policies update their actions at each step in the simulator, but each action is held for 4 steps in the world model. To measure the effect of this difference in update frequency, we conducted additional experiments comparing updates at each step and every 4 steps in the simulator, using 3 BC-RNN, 3 BC-Transformer, and 1 OpenVLA candidates. For the experiment, we set the same initial states, horizon, and termination conditions and used actual simulator observations in both conditions. For BC, we repeated each condition with 3 policy random seeds.

The changes in success rate caused by holding each action for 4 steps were −0.19 [−0.22, −0.16] for BC-RNN, −0.61 [−0.64, −0.58] for BC-Transformer, and −0.20 [−0.30, −0.10] for OpenVLA. Especially for BC-Transformer, the success rates of all three candidates decreased to 0, reproducing nearly the same decrease as the original behavior-change term. For BC-RNN, the difference in update frequency explains a large part of the performance decrease.

For OpenVLA, action holding alone cannot explain the gap: the success rate under the holding condition was 0.66, while the success rate obtained by re-executing the world-model action sequences in the simulator was 0.10. However, we cannot say that this residual gap is caused solely by generated images.

Based on these results, we will revise the description that attributes behavior change to generated observations. This term is the gap in success rates between closed-loop execution in the simulator and re-execution in the simulator of action sequences produced by the policy in the world model. In addition to generated observations, it includes differences in execution conditions within the evaluator, such as action-update frequency and estimated gripper states. We will add the results of these additional experiments and the limitations of this interpretation to the main text and appendix.

Moreover, we found an error in the consequence error in the “All” row of Table 1. Previously, we reported +0.19, but after correcting the error and recalculating using matched episode sets, the updated value is +0.12. We will update Table 1 and clarify the experimental conditions in the manuscript.

3. Purpose of the experiment in Section 3.3

We're sorry that our explanation of the goal of the experiment in Section 3.3 was not sufficient.

In this experiment, we verified whether the world model can reproduce changes in outcomes when the action sequences are changed. Therefore, we kept all actions except the grasp-release action unchanged and compared the generated outcomes with the actual outcomes in the simulator for the action sequences before and after the change. We did not intend to evaluate the same policy in closed loop in two environments.

To use a world model for policy evaluation in the target environment, the world model needs to reflect the consequences of the given actions precisely. In the experiment, judgments changed from success to failure in only 4 of 69 episodes after the grasp-release action, and the generated videos remained almost unchanged, while the simulator outcomes changed from success to failure. This indicates that the world model did not adequately reflect the consequences of this important action change.

We understand your comment to mean that correlation works as a metric indicating the evaluator's inaccuracy, since the correlation between the simulator and the world model would decrease after intervention. Our claim does not deny the usefulness of correlation.

The issue we mentioned in the paper is that the evaluator does not always change its judgment properly in response to action changes that turn the outcome from success to failure, even though the evaluation scores are highly correlated with success rates in the original candidate set. In fact, the evaluator continued to judge almost all episodes as successful, even though they failed in the simulator after grasp release.

We will rewrite the description of the goal of this experiment and our claim more clearly in the manuscript.

4. Undefined notation

Thank you for pointing this out. We will define r as the Pearson correlation coefficient at its first use in the abstract. We will also define ε and n before their first use in the controlled-experiment paragraph of the Introduction: ε is the probability that the demonstration policy releases the object at the branch, and n is the number of demonstration episodes.

Reviewer_hq3uOpenReview ↗
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Paper summary

This paper analyzes learned world model based policy evaluators and finds that while it is indeed true that such world model based evaluation schemes can exhibit correlations in success rate between world model evaluations and the real world, the world model can remain highly insensitive to counterfactual actions. In particular, intentionally causing actions to differ substantially from policy produced actions can, in experiments run by the authors, hardly change the evaluation score under the world model compared to the original policy. The authors attribute this phenomenon to a generalization gap: the world model can reliably score policies when the actions fed into the world model are in-distribution, but if counterfactual, off-distribution actions are supplied, the world model cannot reliably predict the correct trajectory rollout and thus success. The authors prove that is is possible for a world model to have perfectly correlating evaluations of a policy with the real world, and still suffer from this generalization gap to out of distribution actions. The authors primarily test on a world model they train on LIBERO, running evaluations across ACT, diffusion policy, and OpenVLA policies. Finally the authors propose a screening procedure called ResGap, in which the authors can estimate how different a policy might behave in the real world versus in the world model by looking at the differences in model weights when the policy is finetuned on real world demos vs world model synthetic ones.

Critical strengths

(1) The authors observe that even with world model based evaluation systems that demonstrate good ranking correlation, when very counterfactual (i.e., OOD) actions are supplied, the world model cannot reliably predict the correct consequences of these bad actions, which is an interesting observation.

Critical weaknesses

(1) The primary weakness is that the final takeaway is an obvious one, and therefore the novelty of the paper is limited. Concretely, the takeaway is that world models perform badly when given out-of-distribution actions, which given the world models are learned neural networks, is not surprising. The paper includes a proof of the fact that even with a world model that produces evaluations that perfectly correlate with real world evaluations, the world model can mis-generalize to OOD actions. However in a similar vein, this statement is somewhat obvious.

(2) Sufficient experimental results are lacking. The authors train their own world model on LIBERO and do experiments solely with that. It would have been nice to see experiments with world models trained in prior works, including ones that try to get their model to have good action sensitivity. The only experiments being on LIBERO is also a downside: it would be nice to see experiments on multiple robot platforms including real-robot platforms.

(3) While the writing is understandable, the clarity of flow could be improved.

Questions for authors

(1) Indeed as the authors point out, if an action is unsupported in the training set of the world model, the world model cannot generalize to correctly predicting its consequences. However if the world model, on the distribution of actions the policies it evaluates produces, is able to generalize, and therefore is able to get good rank correlation, does it matter that in very OOD actions it does not generalize?

(2) The ResGap procedure it quite involved, as it requires doing gradient updates. So it feels to me it is not as quite lightweight as the authors make it out to be. What is the point of the ResGap procedure, especially given it's heavy weight nature?

(3) For world model trained seemingly only on successful demonstrations, the authors find a correlation between distance to these success training demonstrations and world model success. However isn't this expected? I.e., if a policy in the middle of its trajectory happens to be in a state close to a training demonstration, then it is likely it remained in distribution and therefore will succeed. So such a correlation seems expected. What is the main purpose of this experiment?

3 comments

Thank you for reviewing our paper. We answer your points and questions below.

1. Novelty and why failures on OOD actions become a problem in policy evaluation

If the world model can precisely predict the consequences of actions generated by the policy being evaluated, prediction failures for other actions do not immediately invalidate the policy evaluation.

The issue we mentioned in the paper is whether, when choosing policy candidates before deployment, we can judge that this condition is satisfied based only on correlation with success rate.

The purpose of our study is to verify whether the evaluator can distinguish action differences that are significant to the outcomes of candidate policies.

For example, in the grasp-delay experiment, the evaluation score did not decrease, although the actual success rate decreased largely when shifting the timing of the grasp while keeping the arm action sequence the same. We want to distinguish such differences before deployment.

Therefore, our findings are not limited to the general statement that neural networks may fail on OOD inputs.

Even if the evaluation scores are highly correlated with success rates for the evaluated candidates, we cannot say that the evaluator correctly predicts the consequences of action changes significant to policy selection. This indicates that we need other verification methods in addition to correlation.

Of course, improving the performance of the world model may improve its predictions, but our Theorem 1 still shows limits on guaranteeing a correct ranking of candidates from the available information when the distinguishing actions are insufficiently supported by demonstrations.

2. Range of target world models and robot platforms

There are many world models that can be used for policy evaluation, but it is not straightforward to judge which world model is suitable for this purpose.

In this paper, we target only one evaluation system. However, we need to expand our methods to other world models, including those designed to improve action sensitivity, and investigate their sensitivity to action consequences. Moreover, we're planning to apply our methods to real robots in the future.

3. The significance of ResGap

Regarding your point, ResGap requires additional policy training and therefore has a computational cost. The significance of ResGap is obtaining information to screen multiple candidates and select which policy candidates should be evaluated in the target environment with higher priority.

ResGap does not require candidate-specific world-model rollouts or VLM judgments, and the regenerated demonstrations can be shared across candidates. We will rewrite the description of ResGap to clarify what computation is required and which steps can be omitted, rather than simply describing it as a “lightweight” method.

At the same time, we have not shown that ResGap reduces the total cost of evaluation. At present, ResGap is an empirical screening method before final evaluation in the target environment. An important direction for future work is to investigate whether it can narrow down the candidates enough to justify the cost of additional training across a wider range of settings.

4. The purpose of investigating the correlation between distance to demonstrations and evaluation scores

Your comment that policies that act similarly to demonstrations tend to succeed is reasonable.

The purpose of the experiment is to reveal what high evaluator scores reflect, not to show the correlation itself as a surprising phenomenon.

Concretely, the scores might be highly correlated with actual success rates because the generated rollouts are close to demonstrations, even if the evaluator does not predict action consequences precisely. We conducted the distance analysis to consider this possibility.

However, we do not think that correlation with distance alone can identify what determines the evaluation scores. Therefore, we combined this analysis with experiments perturbing the same policy.

In the grasp-delay experiment, the actual success rate decreased, while the distance to demonstrations remained almost unchanged and the evaluation score did not decrease. Together, these results show that high scores associated with proximity to demonstrations do not necessarily reflect important changes in action consequences. We will clarify the purpose of this analysis and the scope of its conclusions in the manuscript.

5. Clarity and organization

Thank you also for your comment on the organization of the paper. We will improve the structure and explanations to make the connection between our goal of policy selection before deployment and the roles of the experiments, theoretical results, and ResGap clearer.

"The issue we mentioned in the paper is whether, when choosing policy candidates before deployment, we can judge that this condition is satisfied based only on correlation with success rate.

The purpose of our study is to verify whether the evaluator can distinguish action differences that are significant to the outcomes of candidate policies.

For example, in the grasp-delay experiment, the evaluation score did not decrease, although the actual success rate decreased largely when shifting the timing of the grasp while keeping the arm action sequence the same. We want to distinguish such differences before deployment."

----> Right, but to experiment on whether correlation can be insufficient of a guarantee, it only makes sense if the counterfactual actions are sampled from policies being evaluated. I think the authors picked counterfactual actions that did not come from the policies, and so what the authors are testing is just a failure of the world model to generalize to OOD inputs. The idea with sampling actions from the policy is that the world model might've been trained on rollout data, and so might actually generalize to these counterfactual actions, and success rate correlations might therefore be a sufficient metric.

Overall, I continue to agree with my original assessment of the paper.

Thank you for clarifying your point. Following your comment, we conducted two additional experiments to see whether the same problem occurs when the target policies generate the actions themselves.

In the first experiment, we ran the same Diffusion Policy several times from each initial state in the simulator. We chose seven initial states where the policy produced both a success and a failure. For each pair, we gave the world model the same initial frame and the two original action sequences, without changing any actions.

Based on the generated videos, the evaluator correctly distinguished success from failure in three pairs and judged both sequences as failures in three other pairs. In the remaining pair, it judged the failed sequence as a success and the successful sequence as a failure. The same judge correctly judged both original simulator videos for this pair. For ACT, we compared different checkpoints starting from the same initial state, and the evaluator correctly distinguished success from failure in 9 of 12 pairs. We cannot estimate how often these errors occur, since we selected pairs where one sequence succeeded and the other failed in the simulator.

In the second experiment, we investigated what happens if we choose a policy based on its evaluation score. Across the 24 ACT and Diffusion Policy candidates, the correlation between evaluation scores and simulator success rates was 0.73. We chose two ACT candidates for which the evaluator had ranked the weaker candidate higher. We evaluated both again under the same 100 initial conditions. We had already checked the simulator results for these conditions, but this was the first time we ran either policy in closed loop in the world model under these conditions.

The first ACT candidate succeeded only once in 100 simulator episodes, but its evaluation score was 0.90. The second ACT candidate succeeded in 93 of 100 episodes, but its score was 0.82. If we chose the policy based on its evaluation score, we would again choose the first candidate, which succeeded only once.

The second candidate had a much higher simulator success rate (difference +0.92, 95% CI [0.88, 0.96]). Its evaluation score was lower (difference −0.08, 95% CI [−0.16, 0.00]), although the interval for the score difference included zero.

We also checked how the same judge evaluated the original simulator videos. For the first candidate, it judged 65 of the 99 failed episodes as successful. This shows that the judge itself had difficulty recognizing this policy’s failures.

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