- Rating
- 2(+1)
- Confidence
- 4(+1)
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 2(+1)
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Paper summary
This paper investigates the scaling relationship between training compute and prediction error in action-conditioned latent world models. To explore this, the authors developed the RoboJEPA model family, ranging from 22M to 8B parameters, by adapting the V-JEPA 2-AC architecture and training the predictors on large-scale, multi-embodiment robotic datasets. The authors then systematically analyzed prediction errors across different model sizes and training compute budgets and proposed a second-order power law as an empirical scaling function. Among the scaling functions evaluated, the second-order power law achieves lower extrapolation error when predicting the latent prediction error of larger models. Furthermore, the authors examined the relationship between model scale and downstream control performance through both simulated and real-world robotic planning experiments.
Critical strengths
S1: Building on the V-JEPA 2-AC architecture, this paper introduces the RoboJEPA model family, ranging from 22M to 8B parameters, and trains the predictors on large-scale, multi-embodiment robotic datasets.
S2: Leveraging RoboJEPA, the authors provide an analysis of the scaling relationship between training compute and prediction error and propose a second-order power law as an empirical scaling function. Among the evaluated scaling functions, it achieves lower extrapolation error when predicting the errors of larger models.
Critical weaknesses
W1: Overclaim. In the Introduction (L45–47), the authors state a problem that previous latent world models were typically trained at a single scale and that how model quality changes with data size, model parameters, and training compute has not been sufficiently characterized. And the problem is also the main research problem addressed in this paper. However, in the Related Work section, which is placed in the Appendix, the authors have already discussed prior studies [1]–[4] that investigate different aspects of world-model scaling. In particular, [2] explicitly investigated power-law relationships involving model size, data size, and compute in world modeling. Therefore, the Introduction overclaims the gap in existing research. Since the Related Work is placed in the Appendix, despite its importance for positioning the paper against existing studies, readers cannot clearly understand the actual novelty of this work from the main text alone. After considering the related work, the positioning of this paper differs substantially from that presented in the Introduction.
W2: Insufficient Positioning Against Prior Work. In the Introduction (L47–50), the authors mainly categorize existing scaling studies into two groups:
- Generative video models or interactive environments outside robotic control.
- Policy scaling rather than world-model scaling.
However, the Related Work in the Appendix shows that previous studies [1]–[4] have already investigated different aspects of world-model scaling, some of which are directly related to the research scope of this paper. Furthermore, other recent studies, such as WestWorld [5], have investigated world-model scalability across heterogeneous robotic systems, including how model performance changes with the number of robotic environments and generalization to unseen robotic systems. Therefore, the Introduction does not sufficiently position this work against existing studies. Related work on world-model scaling and multi-embodiment world models is not adequately discussed in the main text, although it is important for distinguishing the existing research from the contributions of this paper.
W3: Ambiguous Method Definition. The paper describes Eq. (5) as a per-token objective, but the equation uses summation without normalization, which is inconsistent with the description. According to L239–241, the complete loss definition, including per-frame masking and patch normalization, is provided in Appendix D. However, Appendix D (L1713–1717) states that the loss is only defined in Eq. (5), leaving the complete loss definition inconsistent between the main text and the Appendix. Furthermore, Appendix C.5 (Eq. (12), L1620–1627) defines and states that it is used in Eq. (5), but this mask does not appear in Eq. (5).
W4: Unreasonable Results.
- In L345–346, the authors claim that they verify that the improvement translates into a better success rate. However, the corresponding results in Fig. 2 report normalized cumulative reward rather than success rate. According to the definition in Appendix H.4, the reward is based on the distance to the goal, rather than binary task success. These two metrics are not interchangeable. Even if the reward reaches 0.9, the episode may still be unsuccessful if the goal has not been reached.
- Fig. 4 and Table 3 report the scaling of success rates in real-world experiments. However, according to the evaluation protocol in Appendix H.2, each RoboJEPA model–task combination is evaluated over 30 episodes. If each episode is classified as either successful or unsuccessful, the success rate should change in increments of approximately . Similarly, each VLA model–task combination is evaluated over 50 episodes, so the success rate should change in increments of . However, why does RoboJEPA-4B report a success rate of , while reports in Table 3 and Table 12? These experimental results require clarification, as the reported success rates are inconsistent with the stated evaluation protocol.
[1] Terver, B., et al. What Drives Success in Physical Planning with Joint-Embedding Predictive World Models? (TMLR 2026)
[2] Pearce, T., et al. Scaling Laws for Pre-training Agents and World Models. (ICML 2025)
[3] Baldassarre, F., et al. Back to the Features: DINO as a Foundation for Video World Models. (arXiv 2025)
[4] Huang, W., et al. PointWorld: Scaling 3D World Models for In-The-Wild Robotic Manipulation. (CVPR 2026)
[5] Wang, Y., et al. WestWorld: A Knowledge-Encoded Scalable Trajectory World Model for Diverse Robotic Systems. (ICML 2026)
Questions for authors
Q1: How is the loss normalized in Eq. (5)? How is the mask defined in Appendix C.5 incorporated into Eq. (5)?
Q2: Why does the last input column in Fig. 1 contain , while the corresponding output is still ?
Q3: Appendix B.4 states that the maximum action input width is 64 and explains that the largest DROID joint-velocity action-key chunk is 8 × 8, indicating that each joint-velocity command is 8-dimensional. However, Appendix C.6 states that when DROID is downsampled from 60 Hz to 5 Hz, 12 controller commands are concatenated into a single world-model action. If each joint-velocity command is 8-dimensional, the resulting action dimension would be 12 × 8 > 64, which contradicts the definition in Appendix B.4. Is there an additional downsampling step?
Q4: The main experiment supporting the claimed understanding of object dynamics is the Object Push task in Fig. 3(d), which reports success rate. However, the main text defines task success as moving the object toward a target position, while Appendix H.4 specifies the initial distance between the object and its target. Does any movement toward the target count as success, regardless of the distance moved, or must the object reach a specified distance threshold? If success only requires movement in the correct direction, the results provide limited evidence for the claimed understanding of object dynamics.
Q5: The start-goal definitions for ObstacleReach are inconsistent between Appendix H.4 and Table 14. Which definition was actually used in the evaluation?
3 comments
Thank you for the detailed response and the revised manuscript. I appreciate the improvements to the Related Work and the clarification of the implementation details. The new episode counts and confidence intervals also resolve my earlier concern about the numerical consistency of the reported success rates.
However, I remain concerned about the main contribution and its supporting evidence.
First, Section 3 states that the scaling-law candidates are fitted on compute-optimal frontier points, whereas Appendix K describes fitting BNSL and UNSL on 47 small-model checkpoints and evaluating them on 33 large-model checkpoints. It is still unclear how these checkpoints relate to the frontier points and whether all candidate functions are compared under the same protocol. Furthermore, the 4B and 8B models are used to select the best functional form, so the selected scaling law has not been independently validated beyond this selection.
Second, I appreciate that the authors have revised the claim about imagination error being a reliable proxy for planning performance. However, this also limits the practical implications of the main result. The paper establishes an empirical scaling relationship for latent prediction error within a specific predictor family, but does not show that the resulting law can reliably predict downstream robot control performance or guide broader world-model training decisions.
Finally, the comparison between short- and long-horizon training changes both the rollout horizon and input resolution. Without separating these factors, it is difficult to determine how much of the improvement comes specifically from longer-horizon training.
I recognize the scale of the experiments and the improvements made during rebuttal. Nevertheless, I remain unconvinced that the current evidence establishes a sufficiently general or practically significant scaling-law contribution. These concerns continue to affect my overall assessment.
Thanks for the revised assessment and for increasing the score. Let us elaborate the new concerns below:
1.1 We thank the reviewer for finding a reporting gap. All four candidates use the same protocol (fit on 47 checkpoints and extrapolate to larger 33 frontier checkpoints). We updated the Appendix Section K to properly reflect that.
1.2 Please note that training world models beyond 8B parameters would require a substantial amount of the training compute, on the scale of training large language models of similar size (e.g., Qwen3 [1]). We believe validating the selected scaling law at those scales is a valuable direction for future work. As outlined in the paper, our current data setting is approaching saturation at the largest scale, so this would also require a substantially larger training dataset.
- We would like to point the Reviewer’s attention to the fact that all scaling laws are specific to not only their domain but also to parameterization, and individual architecture choices [2]. For example, the diffusion world modeling formulation yields scaling that is specific to that formulation and, to the best of our knowledge, it is not known to transfer to other formulations. At the same time, predicting the planning performance across world model architectures, training formulations (e.g. stochastic diffusion-based or deterministic feedforward), or other broad world modeling decisions is a highly non-trivial problem that is beyond the scope of this work. In this work we only focus on bridging the planning performance to the world model quality measured by the prediction error or the training compute within the same model family.
The paper establishes an empirical scaling relationship for latent prediction error within a specific predictor family, but does not show that the resulting law can reliably predict downstream robot control performance.
We would like to clarify that the widely accepted view in the scaling laws community is that downstream performance metrics do not extrapolate reliably for large-scale models [3, 4] (as we discussed it in the response to the Reviewer 6KGA). In the revised version of the paper we showed that our domain is similar as it has several phase transitions of the downstream performance. To this reason, we decided to not fit the scaling laws for downstream performance and only qualitatively predict that the downstream performance improves (in the form of the correlation trend between downstream performance and compute or downstream performance and prediction error).
We believe this places only a minimal limitation on the practical implications of the main result, since prediction error is strongly linked to training compute, which deterministically predicts prediction error for compute-optimal models.
- As described in Section 3.2, long-horizon rollouts are introduced only during the cooldown phase; the main training stage always uses short-horizon training. Depending on total training compute, long-horizon training accounts for between 33% and 2% of training compute, since the number of cooldown steps is fixed while the main training stage varies in duration. Despite this variation, we observe a consistent improvement across scales (Figure 35), suggesting that the long-horizon cooldown amplifies capabilities developed during the main training stage. Although our final experiments change both input resolution and rollout horizon during cooldown, in earlier experiments we did not observe improvements in long-horizon prediction from higher resolution alone. In other words, we believe the long-horizon, multi-resolution cooldown is too short to develop long-horizon prediction as an entirely new capability.
[1] Yang, A., et al. (2025). Qwen3 Technical Report. arXiv preprint arXiv:2505.09388. https://arxiv.org/abs/2505.09388
[2] Everett, K. E., Xiao, L., Wortsman, M., Alemi, A. A., Novak, R., Liu, P. J., Gur, I., Sohl-Dickstein, J., Kaelbling, L. P., Lee, J., & Pennington, J. (2024). Scaling Exponents Across Parameterizations and Optimizers. ICML 2024.
[3] Lourie, N., Hu, M. Y., & Cho, K. (2025). Scaling Laws Are Unreliable for Downstream Tasks: A Reality Check. Findings of the Association for Computational Linguistics: EMNLP 2025
[4] Schaeffer, R., Schoelkopf, H., Miranda, B., Mukobi, G., Madan, V., Ibrahim, A., Bradley, H., Biderman, S., & Koyejo, S. (2025). Why Has Predicting Downstream Capabilities of Frontier AI Models with Scale Remained Elusive? ICML 2025
We thank the reviewer for a detailed review. We would like to address some of the concerns:
W1&W2. We would like to clarify that the novelty we are claiming is that our work is the first one to build a scaling law for multiembodiment world models. We agree that the specific wording that we used in L45-L47 does not exclude unambiguous interpretation, therefore, we updated the paper with an unambiguous wording.
We would like to highlight that neither works [1-5], nor any prior work which we know builds extrapolatable scaling laws for multiembodiment robotics. The closest work to ours is [2] (Pearce et al. 2024) which presents an extrapolatable single embodiment scaling law in their Appendix and connects it to pixel generation quality of their robotic world model (but not to the planning performance of the WM). Please note that going from single embodiment to multiembodiment training is highly non-trivial.
Additionally, we would like to emphasize the difference between a scaling law and an empirical scaling trend, where the former fits a parametric curve on the latter and it ensures that the fitted curve extrapolates (potentially redefining the scaling recipe toward an extrapolatable one). We believe the empirical trend is a prerequisite for the scaling law and an extrapolating scaling law requires a more rigorous study that finds optimal hyperparameters for compute-optimal scaling. Works [1,3-5] build empirical scaling trends for single or multiembodiment robotics while our work builds world model scaling law for multiembodiment robotics for the first time.
On related work. We agree that having a discussion of related works in the main text rather than the appendix would help the readers better understand the positioning of our work. Since our related work section is almost 2 pages long, we updated the main text with a shorter version of the related works section that discusses critical works (such as [1-5] and more) and refers to the longer related works section in the appendix.
To summarize, our main contribution is the first scaling law for multiembodiment robotics while past works only either do single embodiment scaling laws, build single or multiembodiment scaling trends, or build world models at single scale.
W3&Q1&Q2. We would like to correct the reviewer regarding the validity of the Equation (5). Since zt(v) is defined as a tensor of size [Hp,Wp,De] (see L161), therefore, for example ∣∣z^t(v)−zt(v)∣∣1 becomes the sum of all absolute elementwise differences between two tensors containing the sum over patches. This means that Equation (5) is consistent with respect to its definition in L233-241. The lines L1620–1627 describe the loss masking that is used in the implementation of the loss from Equation (5). The loss masking is needed since different training sequences may have different lengths so masking each sequence is necessary because it is padded. We believe this is a full definition of the loss so we removed the reference to the expanded loss We updated the section C.5 to properly refer to Eq (5). We thank the reviewer for spotting a typo in Fig. 1 which we fixed.
W4. 1. We would like to provide clarification regarding the planning result in RoboCasa. Each of the 4 tasks we test, we use the success metric (either discounted return, final reward, or success rate) that most faithfully reflects the progress toward the goal. In the reaching task with the perfect match success criterion, the optimal agent would be unsuccessful because of physical limitations of RoboCasa’s simulated franka robot that only drives it 5mm to 1cm from the goal. We updated the paper motivating the choice of each performance metric used for each RoboCasa task.
W4. 2. Fig. 4, and Tables 3 and 12 provide real world evaluation results. However, sometimes these evaluations fail due to external reasons such as hardware errors. Due to a significant cost of real world evaluation, we ran the full benchmark (8 models, 3 tasks, 30 episodes) only once. We updated the paper with the new table with valid episode count.
Q3. Appendix C.6 contains a mistake which we corrected. For droid commanded actions we use 7.5Hz control and 5Hz control for droid state-delta action formulation (see Appendix C.5, C.6). The original description of B.4 is correct.
Q4. We use the threshold-based success criterion where success = final_reward > 0.1. We believe that our conclusion stands for this definition, since models under 1e22 FLOPS mostly keep the robot at init (for push, init and goal have the same robot pose) and only start moving the object and returning after that amount of compute.
Q5. We thank the reviewer for pointing this out. Table 14 is correct, and we have corrected the inconsistency stated in Appendix H.4.
We hope that we have resolved the reviewer’s concerns. If that is the case, we are kindly asking the reviewer x8Rr to increase the score of our work.