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Withdrawn from ICLR 2027

ACID: Action Consistency via Inverse Dynamics for Planning with World Models

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

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Abstract

Decision-time planning with action-conditioned world models has become a popular paradigm for embodied control. However, the standard planning cost judges a candidate solely by how close its predicted terminal state lies to the goal, leaving the realizability of the intermediate transitions unchecked—a predicted trajectory can look convincing while the environment rollout drifts away from it. In this paper, we propose ACID, a decision-time planning framework that introduces cycle action consistency: the action inferred backward from a predicted transition by an inverse dynamics model should recover the one that was conditioned on. We fold this per-step residual into the planning cost via a scale-invariant adaptive weight. Across four action-conditioned world models and eight tasks encompassing object manipulation and articulated control in simulation, visual navigation, alongside real-robot manipulation, ACID consistently improves planning and matches the baseline's accuracy with substantially less planning compute.

Primary area:
applications to robotics, autonomy, planning
Keywords:
world model, decision-time planning, cycle action consistency

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.80 over 5 reviews, above 27% of the others.
Reviewer_g9VhOpenReview ↗
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Paper summary

This paper addresses a limitation of world-model-based planning: candidate actions are evaluated solely by the distance between the predicted terminal state and the goal, with no check on whether the predicted transitions are actually consistent with the actions. To address this, the paper proposes ACID. The method uses a separately trained inverse dynamics model to infer actions from the state transitions predicted by the world model, and treats the discrepancy between these inferred actions and the original candidate actions as a consistency cost. This cost is combined with the goal cost through adaptive weighting to improve the selection of candidate action sequences, without any modification to the world model itself. Under a locally linear dynamics assumption, the paper analyzes the connection between this cost and a component of the prediction error. The approach is evaluated on simulated control and manipulation, visual navigation, and real-robot manipulation tasks. The experiments report performance gains across different world models, and ablation studies examine the effects of the adaptive weighting, the sampling budget, and errors in the inverse dynamics model.

Critical strengths
  1. The paper studies the use of world models as outcome predictors and selectors for a policy's candidate actions, and identifies an important gap in existing work: current world models tend to focus only on the generated goal image, potentially overlooking whether the actions can actually produce the predicted transitions. Building on this observation, the authors propose a cost targeting the consistency of intermediate actions, which effectively mitigates this issue.

  2. Unlike most prior work, which uses an inverse dynamics model (IDM) as an action generator or a pseudo-label generator, this paper employs the IDM as a verifier at the planning stage. It directly influences the selection of candidate actions and forms a closed loop with the world model's forward prediction. I find this idea quite interesting.

Critical weaknesses

1. The action-consistency criterion relies on a strong action-identifiability assumption, and its practical scope remains unclear.

The paper treats the discrepancy between the IDM-inferred action and the original action as a signal of inconsistent predicted transitions, but this interpretation holds only if the action is uniquely determined by the start and end states. Although the theoretical analysis makes this condition explicit through the locally linear dynamics assumption and the requirement that B has full column rank, the extent to which it holds in practical settings with visual latents and action chunks has not been sufficiently verified. Different actions or action sequences may produce identical or nearly identical observable transitions. In such cases, even if the world model's prediction is accurate, the IDM may return a different but equally valid action, causing the consistency cost to wrongly penalize a feasible candidate. The residual may therefore conflate world-model prediction error with the inherent ambiguity of inverse dynamics, and the paper should more explicitly qualify the conditions under which it serves as a valid feasibility signal.

2. The technical novelty is relatively limited and amounts mainly to an extension of an existing planning cost.

ACID retains the established pipeline of world-model prediction and CEM/MPC planning, and its main technical increment is an IDM-based action-consistency cost combined with the goal cost through adaptive weighting. It leaves CEM's candidate sampling, elite selection, and distribution update unchanged, so the contribution is essentially an improvement to the planning objective. While this design has practical value, the paper's emphasis on the overall framework should be commensurate with the scope of what is actually new. CEM is already introduced in §3.1 and the accompanying pseudocode, but the paper could more clearly distinguish the existing planning pipeline from the newly added module, so that the boundary of the contribution is easier to see.

3.The navigation experiments with video-generation world models provide limited support for the related performance claims.

In the goal-conditioned visual navigation experiments with NWM/CompACT, ACID reduces ATE and RPE by only 2.3% and 1.5% relative to the baseline. These are modest gains, and describing them as a "notable performance improvement" in the main text is somewhat overstated. More importantly, these metrics measure how closely the planned trajectory matches the reference trajectory in the dataset, and this setting involves no closed-loop execution in an environment. Being closer to the reference trajectory does not directly translate into a higher goal-reaching success rate, nor does it fully capture obstacle avoidance or the ability to replan under execution errors. The current results therefore mainly show that the method reduces offline trajectory error in this setting, and are insufficient to demonstrate improved closed-loop navigation performance. The authors should either temper the corresponding claims or add closed-loop experiments with metrics such as navigation success rate that directly reflect task completion.

Questions for authors

1. What is the new contribution of this paper relative to existing IDM-based action-consistency metrics?

CompACT[1] already uses an IDM to infer actions from generated frames and evaluates the action consistency of the generated results via the error between the inferred and input actions. I would like the authors to clarify more explicitly how ACID relates to and differs from such existing methods. Beyond turning this signal from an evaluation metric into a planning cost and introducing adaptive weighting, what substantive technical contributions does the paper make? Clarifying this would help readers more accurately understand the scope of the novelty.

2. Does ACID detect world-model prediction errors, or deviations of candidate actions from the behavior patterns in the training data? Could this preference limit generalization?

Since the IDM is trained on offline data, a large action-reconstruction error may arise either from inaccurate world-model predictions or from candidate actions that lie outside the behavior distribution familiar to the IDM. Appendix J evaluates ranking ability using reference actions and their noise-perturbed versions, but the fact that the method tends to select the reference action does not seem sufficient to distinguish between these two explanations. Could the authors provide more direct evidence that the consistency cost indeed reflects the discrepancy between prediction and actual execution? Furthermore, when an action is not uniquely determined by the state transition, an action that differs from the training demonstrations may still produce a correct and valid transition. Would ACID wrongly penalize such an action because the IDM fails to reconstruct it, thereby biasing selection toward the behavior patterns in the training data? In policy-guided planning in particular, could this filtering suppress valid novel behaviors that the policy would otherwise generate, and thus limit generalization to new scenarios? I would appreciate it if the authors could discuss this risk, as well as how the method performs when the action-identifiability assumption does not hold.

3. Why do the standalone Diffusion Policy and the full system use different data budgets on PickPlace?

According to the appendix, the DP on PickPlace is trained on only 30 demonstrations, whereas the WM and IDM are trained on 200. The improvement of the full system over standalone DP therefore conflates the effect of additional training data with that of inference-time candidate search, making it difficult to disentangle their respective contributions. Why was the standalone DP not also trained on all 200 demonstrations, and what is its success rate in that setting? I would encourage the authors to add this comparison, so that readers can assess how much benefit planning and consistency-based filtering provide under the same data budget.

[1] Dongwon Kim, Gawon Seo, Jinsung Lee, Minsu Cho, and Suha Kwak. Planning in 8 Tokens: A Compact Discrete Tokenizer for Latent World Model. arXiv preprint arXiv:2603.05438, 2026.

Reviewer_Hzo4OpenReview ↗
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Paper summary

ACID augments goal-conditioned planning with an action-cycle consistency cost: an inverse dynamics model recovers actions from world-model-predicted transitions, and the squared discrepancy from the conditioning actions penalizes candidate plans. The method combines this residual with terminal goal distance using a weight proportional to the ratio of the costs’ standard deviations across candidates. The paper provides an oracle linear-dynamics analysis and reports improvements across three latent world models on five simulated tasks, an offline video-model navigation evaluation, and two real-robot tasks, together with reduced search budgets to reach baseline performance.

Critical strengths
  1. The controlled simulation results provide credible evidence that the added cost improves planning. For example, Section 4.2 keeps each world model and CEM configuration fixed, and Table 1 reports improvements across all 15 model–task combinations with three-seed statistics. Particularly meaningful effects include Le-WM on Cube, 68.0% → 79.3%, PLDM on Cube, 56.0% → 68.0%, and DINO-WM on Rope, 1.32 → 0.65 Chamfer distance. These demonstrate benefits beyond a single representation or small benchmark gain.

  2. The integration is practical. The verifier reuses existing offline data and predicted trajectories without retraining the world model. On Reacher, ACID with 30 candidates exceeds the goal-only baseline with 300 candidates for both Le-WM and PLDM (Table 3: 82% and 78% versus 76%). The policy-guided robot experimen improves from 11/15 to 14/15 successes on each task with the same policy and world model, supporting feasibility in physical manipulation, although these small trials do not establish a precise effect size.

Critical weaknesses
  1. The oracle results do not establish that an IDM trained on real transitions extrapolates correctly to model-generated transitions: the candidate-dependent error and cross term in Eq. (15) can alter rankings, and independent training does not rule this out. Section 4.6 tests injected Gaussian offsets, while Appendix J ranks a recorded action chunk against Gaussian perturbations using distance from that recorded action. Neither directly tests whether the residual ranks actual dynamics errors among CEM candidates. This substantial but fixable gap is especially relevant to Appendix F, where different action chunks can produce similar endpoint observations, so disagreement with one inferred chunk need not indicate an unrealizable transition. Executed-candidate error measurements and a matched action-prior control are needed to distinguish verification from preference for familiar actions.

  2. The originality of inverse-based verification is insufficient. RLIR (Ye et al., 2025), Sec. 4.1, already compares actions recovered from generated videos with their conditioning actions, using discrete agreement as a reward for world-model post-training. WAV (Liu et al., 2026), Sec. 2.3, uses an inverse–forward cycle from proposed subgoals to identify model errors for exploration.

  3. Some Table 1 changes are small relative to reported variation, such as DINO-WM on Reacher, 67.3 ± 3.1% → 68.0 ± 5.3%. Appendix D.2 evaluates each deformable-object task on only 10 instances, and the physical experiments have only 15 trials per task. The navigation extension reports ATE −2.3% and RPE −1.5% without uncertainty and explicitly lacks environment rollouts (Appendix E), so it supports offline trajectory matching rather than demonstrated closed-loop navigation improvement. These limitations do not negate the larger simulation gains, but they narrow the claimed breadth; the paper should also specify what the three seeds vary and the episode counts for the other simulated tasks.

  4. Table 9 measures separate network forward times only at 300 candidates and horizon 5, finding 11.8–14.5% verifier overhead, while Sec. 4.5 infers savings from fewer candidates or planning steps. This suggests useful computational savings, but does not establish the actual latency reduction at 30 candidates, since batching and fixed planner costs need not scale linearly, and the video-model extension also uses ten IDM integration steps (Appendix E).

  5. Section 4.4 says no constant weight improves all three Le-WM tasks, but Table 4 shows that wa=10w_a=10 improves Cube, PushT, and Reacher by 2, 2, and 6 percentage points, respectively. Adaptive weighting still achieves the larger total gain, but the result establishes an advantage for the tested configuration, not the claimed failure of every fixed weight. Moreover, the λ\lambda sweep in Table 3 covers only Reacher and does not establish cross-task insensitivity.

Questions for authors
  1. On actual CEM candidates, how well does the consistency residual rank simulator-measured prediction error and true goal outcomes, including candidates with low residual but large rollout error? Does it outperform a learned action-prior penalty with the world model, data, and search budget held fixed?

  2. In the robot setting, how does recovering an entire action chunk from a pair of latent observations handle multiple valid chunks with similar endpoints?

  3. What do the three seeds in Table 1 randomize, how many evaluation episodes are used for Cube, Reacher, and PushT, and are the reported improvements stable under paired evaluation on the same initial states?

  4. Please provide end-to-end planning time at matched quality for the 30-versus-300-candidate comparison, and clarify how the per-model λ\lambda values were selected without task-specific test tuning.

Reviewer_4821OpenReview ↗
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Paper summary

The paper proposes ACID for decision-time planning with action-conditioned world models. A separately trained flow-matching inverse dynamics model (IDM) maps each predicted transition back to an action, and the residuals to the conditioning actions are averaged into a consistency cost c_a, which is added to the terminal goal cost c_g. The weight is set adaptively at every CEM iteration as w_a = λ·σ_g/σ_a, and the world model itself is not retrained. Under locally linear latent dynamics and an ideal IDM, the authors show that the residual equals the action-explainable part of the world model's one-step error, and that the augmented cost upper-bounds the true goal distance. Experiments cover Le-WM, PLDM, and DINO-WM on five simulated tasks, visual navigation with NWM, and two real-robot tasks. The paper claims that ACID consistently improves planning in all settings and matches the baseline's accuracy with substantially less planning compute.

Critical strengths
  1. The method is simple and plugs directly into existing pipelines. It leaves the world model untouched and changes only the planning cost, so it applies to any sampling-based planner. If the gains hold, the method could be used in many existing systems, and this is where the main value of the paper lies.
  2. Proposition 1 makes clear what the residual measures, namely the action-explainable part of the world model's error. The authors are also candid about the blind spot of the method, and they acknowledge that the IDM error not masking world-model errors is only an assumption. This makes the scope of the method fairly clear.
Critical weaknesses
  1. The reproduced baselines are clearly below the values reported in the original papers, which contradicts the authors' own statements, and several core claims rest precisely on these under-performing baselines. Appendices C.2, D.2, and D.3 state that the Le-WM protocol and planning configuration are followed without modification, that Le-WM uses the official checkpoints, and that DINO-WM is trained until it reaches the performance reported by Le-WM. Yet under the same protocol, the Original rows of Table 1 are clearly lower. Le-WM with the official checkpoint gets 75.3 on Reacher (reported 86) and 68.0 on Cube (reported 74). PLDM gets 56.0 on Cube (reported 65). DINO-WM gets 76.7 on Cube (reported 86) and 67.3 on Reacher (reported 79), and 1.32 and 0.46 on Rope and Granular, versus 0.41 and 0.26 with MPC in the original DINO-WM paper. In four of the nine success-rate cells, ACID with the consistency cost is still below the published baseline without it. The paper never acknowledges these gaps. The compute-efficiency claim (82 at N=30 on Reacher exceeding 76 at N=300), the λ-robustness claim (Table 3, right), and the adaptive-weight claim (+12 of the total +20 in Table 4 comes from Reacher) all rely on a Reacher baseline of about 76, and most of them no longer hold against the reported 86. In addition, Tables 3 and 4 do not state the number of seeds or how they relate to Table 1. Working backward from the means and standard deviations in Table 1, they are not any of its three seeds and are most likely a separate single run (for the same configuration, Ours is 82.0 in Table 1 and 88 in Table 3, and the Ours values for Cube and PushT in Table 4 are not among the seeds of Table 1 either). The compute-efficiency, λ-robustness, and adaptive-weight arguments all depend on this undisclosed single run.

  2. The ablation does not support the adaptive weight as a contribution. Sec. 4.4 states that no single constant improves all three tasks, yet in Table 4 w_a = 10 improves all three (+2, +2, +6). The constants tested only go up to 10, whereas according to Fig. 10 the adaptive weight with λ = 0.07 actually lies roughly between 4 and 40, so the comparison cannot distinguish "adaptive is better" from "larger is better". The cross-world-model variation in Fig. 10 is confounded with the task, since the DINO-WM row shows only Rope and Granular, and λ has to be tuned per world model anyway. Table 3 shows that the results are insensitive to a 20× change in λ, which further weakens the premise that the two scales must be matched precisely at every iteration. Moreover, Table 4 appears to use a single seed with 50 start–goal pairs per cell (one success equals 2 points), so the differences in the Cube and PushT rows amount to only one or two successes.

Questions for authors

Clarifications:

  1. Reproduction of Le-WM. Please evaluate Le-WM repeatedly using the official released weights, the official evaluation code, and the original protocol (including the start–goal sampling and random seeds). Please report the result of each run and the code version used, and confirm that Le-WM indeed yields the low scores reported in the paper (75.3 on Reacher and 68.0 on Cube, versus 86 and 74 reported by Maes et al., 2026). If the authors can show this, I will raise my rating.
  2. How many seeds are used in Tables 3 and 4, and do they share seeds with Table 1? Judging from the means and standard deviations in Table 1, they appear to come from a separate single run. Please clarify, and rerun these two tables over multiple seeds with standard deviations. In addition, how many start–goal pairs per seed are evaluated in Tables 1, 3, and 4, and which λ is used in Tables 1 and 4?
  3. What explains the gaps of PLDM and DINO-WM on Cube and Reacher relative to the reported values, and the 3.2× and 1.8× gaps of DINO-WM on Rope and Granular relative to the original paper? Were DINO-WM's proprioceptive inputs disabled on Rope and Granular?

Additional experiments that would affect my assessment:

  1. Please add constant weights covering the actual range of the adaptive weight (e.g., 20–50), a variant that computes the ratio only once, and per-task tuned constants, with multiple seeds. Please also reconcile the statement in Sec. 4.4 with the w_a = 10 column of Table 4.
Reviewer_fBbyOpenReview ↗
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Paper summary

The paper introduces ACID, a decision-time trajectory selection method for action-conditioned world models. During planning, a separately trained inverse dynamics model infers the action corresponding to each imagined transition (s^t,s^t+1)(\hat{s}_t, \hat{s}_{t+1}). The discrepancy between this reconstructed action and the actual candidate action passed to the world model is averaged over the planning horizon and added to the nominal goal cost. To combine these terms without manual weight tuning, the authors use an adaptive weighting scheme based on the ratio of standard deviations of the two costs across the candidate population. Under ideal assumptions (e.g. linear dynamics, perfect inverse model), the authors link this consistency residual to the action-explainable subspace of prediction error and derive an error bound on goal distance.The empirical evaluation is broad, testing three latent world models across five simulated benchmarks, an offline video-generative navigation task, and two real-robot manipulation setups using policy-guided planning. The authors report consistent gains across these environments, alongside reduced planning sample budgets needed to match baseline success rates in certain regimes.

Critical strengths
  • A clean, modular intervention with minimal computational overhead. ACID requires zero structural changes to the forward world model, latent space, or proposal policy. The verifier reuses the offline training data and scores rollouts already generated by the planner. In practice, this makes the method exceptionally easy to drop into existing model-based pipelines.

  • Broad, consistent empirical gains across disparate backbones. The empirical evidence is broad. Table 1 shows solid, consistent improvements across Le-WM, PLDM, and DINO-WM (e.g., boosting Cube from 68.0% to 79.3% on Le-WM, and cutting Rope Chamfer distance from 1.32 to 0.65 on DINO-WM). The physical robot trials (14/15 vs. 11/15) further indicate that the approach transfers beyond idealized simulation.

Critical weaknesses

Limited methodological novelty relative to existing inverse-dynamics planning objectives.

I am not fully convinced that the methodological novelty is sufficiently distinct from existing literature. In particular, Wang et al. [1] already propose an inverse-dynamics-based action consistency penalty as a planning-time objective, evaluating essentially the same discrepancy between candidate actions and actions inferred from predicted transitions. ACID applies this concept to action-conditioned rollouts using CEM, but I can hardly see what constitutes a fundamental algorithmic leap beyond porting this penalty into a different planning framework.

Furthermore, Paster et al. [2] had already shown how an inverse dynamics model can guide and filter action-sequence selection at planning time, which directly challenges how Section 2.2 characterizes prior work on IDMs. While the empirical improvements are solid, the paper does not adequately delineate its algorithmic novelty from [1] and [2], leaving me unsure how much new technical ground is actually broken here.

The learned score is not convincingly validated as a measure of physical realizability or true prediction error.

The theory relies on an ideal inverse model, but in practice, the inverse network is trained on real transitions and then evaluated on out-of-distribution, potentially unphysical transitions imagined by the forward model. Appendix A.5 notes that inverse-model errors could theoretically cancel or mask forward errors, arguing that separate training reduces systematic correlation. However, sharing the same latent representation and training data creates shared inductive biases, making correlated blind spots very possible.Furthermore, I am not convinced that the ranking diagnostic in Appendix J isolates realizability. The benchmark ranking uses L2L_2 distance to a ground-truth action chunk with Gaussian noise added. A plan that deviates from an offline demonstration action isn't necessarily unfeasible or physically inaccurat - it might just be an alternative valid route. Consequently, this experiment doesn't distinguish between a verifier that spots model hallucinations and one that simply acts as an in-distribution action density filter. A direct comparison between the consistency score and the actual rollout error when executed in the simulator would make this claim much more credible.

The experiments do not isolate cycle consistency from simpler action-prior baselines.

Because all main baselines rely on a goal-only planning objective, it is hard to tell whether the forward-inverse loop (ŝ_{t+1} → â_t) is doing the work, or if the planner simply benefits from regularizing actions toward the training distribution. To really convince me of the mechanism, the authors need a control baseline: for instance, a matched-capacity behavior-cloning prior π(a | s_t) penalizing candidates that stray from likely actions, without looking at the predicted next state ŝ_{t+1}. If a simple state-conditional action prior yields comparable gains, then the cycle-consistency framing is mostly incidental. Adding basic penalties like action-rate limits or smoothness would also help eliminate simple regularization as the primary driver.

References: [1] Wang, Z., Jiang, K., & Tan, X. (2026). Dynamics-Aligned Diffusion Planning for Offline RL: A Unified Framework with Forward and Inverse Guidance. Transactions on Machine Learning Research (TMLR).

[2] Paster, K., McIlraith, S. A., & Ba, J. (2021). Planning from Pixels using Inverse Dynamics Models. International Conference on Learning Representations (ICLR).

Questions for authors

Methodological distinction from Wang et al. [1] and Paster et al. [2]:

How does ACID fundamentally differ from the inverse-dynamics consistency objective introduced by Wang et al. [1]? Beyond swapping the trajectory generation and optimizer framework (e.g., diffusion vs. action-conditioned world models + CEM), what is the key conceptual advance? I would appreciate a direct, explicit comparison against both [1] and Paster et al. [2] clarifying exactly which mathematical or algorithmic components of ACID constitute novel contributions.

Physical validation of the consistency metric:

What is the inverse model’s held-out action-prediction error on genuine offline transitions? More critically, for candidate trajectories generated by the planner from the same initial state, how strongly does the consistency score correlate with the actual executed simulator error (∥ssim−s^model∥\Vert{}s_{\mathrm{sim}} - \hat{s}_{\mathrm{model}}\Vert{})? Can the score reliably identify faithful predictions among candidate plans that achieve similar goal costs?

Disentangling cycle consistency from action priors:

How does ACID perform against a matched-capacity action-prior baseline π(a∣st)\pi(a \mid s_t) trained on the exact same offline transitions? Showing that conditioning on s^t+1\hat{s}_{t+1} provides a statistically meaningful advantage over a current-state prior is essential to prove that cycle consistency—not just offline action regularization—is driving the performance gains.

Clarification of tuning and experimental setup:

Could you list the exact hyperparameter values (λ\lambda or scaling factors) used across the environments in Table 1, and describe the exact validation split used to select them? Additionally, please specify the exact episode counts for the Cube, Reacher, and PushT benchmarks, and clarify what changes across the three reported random seeds (e.g., world-model weights, inverse-model weights, planner sampling seeds, or reset state distributions).

Reviewer_478ZOpenReview ↗
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Paper summary

The paper studies planning with action-conditioned world models. In current methods, candidate action sequences are ranked by the predicted final state's distance to the goal. This cost does not check whether the actions could actually produce the intermediate transitions. The authors train an inverse dynamics model IDM on the world model's latents and penalize the mean squared difference between the actions it recovers from predicted transitions and the conditioning actions. Tests cover three latent world models in simulation, with additional navigation and real-arm experiments, and show mostly positive gains at modest overhead.

Critical strengths

I think the method has some merits.

  • First, I believe that training is necessary to solve the current WM's physical awareness limitations.
  • Training an IDM to predict action can be an easier task than finetuning a WM to better predict next state. Hence the proposed approach can be more efficient.
Critical weaknesses
  • While it makes sense that training IDM could be easier than tuning the WM itself, how it may help planning is not well justified, especially given the current training methods in the paper. The IDM is trained on real latents and actions, and may not extrapolate to latents in inference time, which are predicted instead of real. If the WM predicts a resulting state that is physically unrealizable, it is unclear if IDM will necessarily produce large errors in action prediction.
  • Furthermore, even if IDM is correctly trained to predict actions given observations, the pipeline could still be problematic when WM is not very physical aware. For example, a robot moves its gripper towards a ball. Let's say the WM predicts the gripper movement correctly, but incorrectly predicts that the ball moves, despite the gripper and ball never touches. The IDM may still correctly identifies the action from moving gripper. But the incorrect state prediction will cause problems for future moves (e.g., moving gripper to a wrong location).
Questions for authors
  • Is it possible to use WM to generate predicted trajectories, isolate problematic ones, and incorporate them to train IDM to predict an "invalid" action? Would this improve your current IDM? This is essentially training an open-set action predictor that accepts invalid state pairs.
  • The DINO-WM baseline seems to have lower numbers compared to its published paper. Any explanation?

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