acceptodds
Withdrawn from ICLR 2027

A Perfect Model Is Not Enough: A case study on long horizon planning in LeWorldModel

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

We study what limits long-horizon planning in JEPA world models through a case study on LeWorldModel (LeWM), a compact world model trained end-to-end offline on pixels whose evaluation protocol has become standard in subsequent work. Several of LeWM’s successors attribute its failures at long horizons to compounding rollout error. We first show that extensions of the standard protocol that simply increase the goal offset cannot test this claim: seemingly minor details of several environments and datasets make them poor tests of long-horizon planning at larger goal offsets. On environments that avoid these pitfalls, we evaluate LeWM on held out episodes across increasing start-goal offsets, varying its rollout source and terminal cost separately. Our results show that (a) planning with a perfect model (by executing each candidate in the simulator) improves long horizon success only modestly, while (b) replacing only the Euclidean terminal cost with a cost-to-go learned on frozen embeddings can achieve similar or greater outcomes without retraining the world model. These insights suggest that evaluation protocol and planner costs inherited by follow up work deserve as much scrutiny as the predictive world model itself.

Primary area:
applications to robotics, autonomy, planning
Keywords:
JEPA, representation learning, world models, goal-conditioned rl, planning, temporal distance

Reviews

Among:
Shape:
1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_BCBNOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper investigates the rationale behind the LeWM’s struggles under long-horizon scenarios. Main argument of the investigation is that the accumulated errors during the rollout is not the main bottleneck of this struggle, and rather the metric (L2 distance) that evaluates the action sequence candidates is very misleading.

Critical strengths
  • The way authors tackle the evaluation protocol of the LeWM makes a good sense. The edge cases authors insisted; tasks solved at start, number of tasks, held-out episodes all reveal vulnerability of the current protocol, and sound critical.
  • Cost being more critical factor than the rollout error makes sense, and many studies to add or modify the L2 cost of the planner support the claim as well.
  • Table 8 that tries to ablate the effect of rollout error and erroneous cost is helpful, although in appendix.
Critical weaknesses
  • Paper may be undone at this stage: L104: appendix zyz, L130: appendix abc, L172: (cite), L215: see appendix and also cite that point this out, L432: (a,b,c,d,e,g,…), L433: Appendix ??, … etc.
  • To make this paper’s claim firm, it would have been better if authors come up with better benchmark that covers the aforementioned vulnerability of the current protocol, not insisting that PointMaze-giant is the only environment that suffices the conditions that authors’ checklist. PointMaze cannot cover diverse scenarios that world model has to handle, and analysis only on it may be constrained to a single environment.
  • From Table 2, using true dynamics also gives Push-T and Cube-play a huge improvement over each counterpart. The author’s claim may come from the easier action space that PointMaze has: it’s an environment where the 2D point never interacts with surroundings, and it just takes velocity command.
Questions for authors
  • Fig.3 demonstrates that increasing the lookahead results in performance degradation, and this effect is confounded with search difficulty and accumulated rollout error. What happens if you sweep this lookahead range under true dynamics? Solely attributing its degradation to CEM’s sample efficiency (Pinneri et al., 2020) is not sufficient.
  • The learned cost-to-go is learned by TD on the demonstrator’s own trajectories. The gain obtained from using the cost-to-go to make the demonstration go over similar trajectory pattern that it has shown in the training dataset. Can the authors evaluate the cost-to-go condition on goals not tied to the same-episode construction (the random-goal mode of stable-worldmodel (Maes et al., 2026), or OGBench’s official PointMaze-giant tasks) and report whether the cost’s advantage over L2 (and over the perfect predictor) persists there?
Reviewer_NJCgOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
1
Soundness
1
Read review
Paper summary

This study looks at why goal-conditioned planning can fail with LeWorldModel. The authors first check the evaluation setup and question whether sampling demonstration frames further apart in time actually gives tasks that need longer plans. They then compare four combinations: rollouts from either learned dynamics or the true simulator, each paired with either Euclidean distance in latent space or a learned cost-to-go as the terminal objective. The encoder and predictor are kept fixed while the cost-to-go is trained. Across seven simulated environments, changing the objective often gives a larger gain in success than using the simulator in place of the learned model. The work is an empirical examination of an existing planner and its evaluation procedure, with no new planning algorithm. I am less convinced that the findings go far enough beyond the limitations discussed in the paper's related work.

Critical strengths

Comparing both objectives under both sources of dynamics is a useful experiment. Since the backbone is unchanged and all four variants are tested on the same tasks, the effect of the terminal objective is easier to assess than it would be from separate aggregate results. The evaluation check also finds a problem worth reporting. In Cube (expert), 83 out of 200 sampled tasks satisfy the goal before the agent takes any action; removing them lowers success from 66.0% to 41.9%. This changes how the reported performance should be read. I think these results give good reason to examine the released LeWM planner and evaluation more carefully, though they do not yet amount to a sufficiently new or general finding for acceptance.

Critical weaknesses

I had difficulty identifying what this study adds to the existing account of the problem. Section 5 notes that accurate prediction does not guarantee good control, and credits Li et al. (2026a) with using temporal-distance scores in a frozen LeWM planner. The probe itself is trained through a familiar temporal-difference procedure. A new algorithm is not necessary for an empirical contribution, but the experiments still need to establish something new that matters. The claim that rollout error is not the bottleneck seems too broad for results from one backbone with one CEM configuration. They show which component limits this particular setup, without showing whether the conclusion holds with stronger search or a different representation. I also do not see how the PointMaze SHORT gain, from 2.5% to 76.8%, fits the explanation in terms of long-horizon failure. That result needs further discussion.

Several parts of the manuscript still contain unfinished text, including references needed to follow the experimental details: “appendix zyz” on p. 2, “appendix abc” and “to = direct temporal distance” on p. 3, and “Appendix ??” together with “(a,b,c,d,e,f,g....)” in the reproducibility statement. More substantively, I could not determine the number of environment steps between replanning calls from Section 2 and Tables 9–10. There is also a discrepancy in Appendix C: the stated checkpoint rule would select 5,000 updates, but the experiments use 25,000. Taken together, these leave parts of the setup uncertain and make the main comparison harder to trust.

Questions for authors
  1. Which result here answers a question left open by the temporal-distance scoring work of Li et al. (2026a)? Beyond substituting simulator rollouts into the existing LeWM pipeline, I would like to understand what new conclusion is established and which experiment supports it.

  2. How many environment steps are executed before the next planning call: 25 or five? Please clarify why Section 2 and Tables 9 and 10 seem to give different accounts, and state which setting produced the main results. The answer matters for understanding the source of the planning failures.

  3. Appendix C gives 692/800 successes at 5,000 updates and 677/800 at 25,000, yet chooses the latter checkpoint. Why was the stated selection rule not followed? Would using the checkpoint selected by that rule change the comparison between improving the cost and improving the dynamics?

  4. Among the actual evaluation tasks verified to need more than one planning horizon, how much of the reported long-horizon effect remains? Could the authors connect the protocol analysis to the success comparisons for those same tasks? I am asking for evidence behind the present claims, rather than additional experiments on unrelated extensions.

Reviewer_nwW2OpenReview ↗
Rating
1
Confidence
4
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

The paper claims that the most accepted explanation for why world models fail is that world model errors compound over time. It claims to present a counter-argument to this by showing that improving the cost-to-go estimator from Euclidean distance in pixel space to a learned cost-to-go function based on temporal differences improves coverage (percentage of problems solved). The results show that, as the number of steps between the start and goal state increases, the positive impact of the quality of the cost-to-go function (where the learned cost-to-go function is of higher quality) and the fidelity of the world model increases.

Critical strengths

The paper reinforces the known result that cost-to-go function quality can significantly impact search performance. Some literature in that focuses on learning world models may overlook this fact.

The paper has a direct comparison to learned and true world models. This simple study may also be overlooked by some modern world model literature.

Critical weaknesses

The results of the paper are known. It is known that the quality of cost-to-go (or heuristic) function significantly impacts the performance of search [1,2]. The results in Figure 2 support these results.

The results in Figure 2 also directly contradict the authors’ claim that world model fidelity is not the bottleneck. Switching from a learned to the true world model helps significantly in most cases for both the Euclidean distance and learned heuristic functions. It is also known that world models of higher fidelity result in better coverage [3].

[1] Korf, Richard E. "Finding optimal solutions to Rubik's Cube using pattern databases." AAAI/IAAI. 1997. [2] Brewka, Gerd. "Artificial intelligence—a modern approach by Stuart Russell and Peter Norvig, Prentice Hall. Series in Artificial Intelligence, Englewood Cliffs, NJ." The Knowledge Engineering Review 11.1 (1996): 78-79. [3] Sutton, Richard S., Andrew G. Barto, and Andrew Barto. Reinforcement learning: An introduction. Vol. 1. No. 1. Cambridge: MIT press, 1998.

Questions for authors

The text has “appendix zyz” and “appendix abc”. What is this?

Are there any images of the problems being solved that support the authors claims? For example, areas where the world model is incorrect, yet the better heuristic function somehow overcomes this? This sounds contradictory as the heuristic function takes the state the world model gives it as input. If the world model is significantly incorrect, then solving the problem is just a matter of luck.

The paper can be improved by a better description of the environments that are being used, for those that are unfamiliar with Mujoco (it appears these are Mujoco environments or, at least, based on them.)

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

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