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Under review as a conference paper at ICLR 2027

Understanding the limits of latent world models

Abstract

World models are widely proposed as core components for enabling agents to reason over long temporal and spatial horizons. Yet current evaluations often emphasize task performance while providing limited insight into whether learned world models acquire predictive latent dynamics that reflect the underlying structure of the environment. Here we introduce the concept of faithful latent world models as an equivariance condition between the environment's transition map and the learned latent dynamics. We propose latent rollout consistency (LRC) as a metric to evaluate action-conditioned latent prediction. Strikingly, we find that across a range of state of the art latent world models, none solves the task by actually faithfully modeling the environment.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
latent world models, latent dynamics, evaluation, benchmarking

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_Qi7AOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
2
Soundness
3
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Paper summary

This paper studies the question of understanding the quality of world models. The authors argue that looking at the world model's agent score or reward alone is not sufficient to judge whether the world model accurately models the underlying environment. Instead, the authors propose to explicitly measure the faithfulness of world models. The authors propose two main metrics to assess the faithfulness: 1) latent rollout consistency (LRC) which is the coefficient of determination (R^2) between the distribution of encoded observations (with history of length h) into latents and the distribution of predicted latents after h prediction steps. 2) the ground-truth decoding quality. The motivation behind that is that LRC cannot capture collapsed latent vectors for which the correlation would be perfect.

The authors conduct a controlled study in three different environments (pendulum, cartpole and reacher) testing three different world model types (DreamerV3, TD-MPC2 and LeWM) from both pixel and state inputs. The authors find that none of the world models can model the underlying dynamics faithfully despite they work well for control. Throughout a series of studies the authors identify gaps in the baseline models.

Critical strengths
  • The authors study an important problem of whether the learned dynamics of world models is accurate.
  • The authors intentionally use simple and interpretable environments to make interpretable judgments about world models.
  • The authors present an in depth analysis of different aspects of world model faithfulness.
Critical weaknesses
  • poor motivation of the LRC metric. Despite this is a central part of the contribution, the paper presents only a very short justification of the metric choice. This is, in my opinion, an important missing point as it makes understanding of next sections much harder. The authors should add a more in-depth discussion that justifies the choice of it. For example, a simple L2 distance could be an alternative or a more advances distributional distance (for example, batch-wasserstein).
  • Specifically the authors should justify why does this metric provides a normalization (between 0 and 1) such that a fixed level of it means the same level of faithfulness (or not) regardless of other factors such as the dimensionality of the latent. Given that the authors use different latent dimensionality for different observation types and different models, this can be a confounding factor.
  • The space of tasks is a bit too small. I would agrue that tasks like ant or hopper are simple too since they are significantly more simple that dexterous manipulation for example. Those tasks (ant or hopper) could have been studied in this work too.
  • The writing makes a few parts of the paper a bit hard to follow.

I think that these weaknesses are not fatal and they can be addressed in during the rebuttal.

Questions for authors
  • minor error: Line 118 – I think the authors meant SIGReg instead of reconstruction loss.
  • why LeWM performs better on states and barely works on pixels? that model was originally proposed for pixel observations.
2 comments

We thank the reviewer for the positive review, and we agree that the weaknesses raised can be addressed. We have updated the manuscript (changes highlighted in blue) with new validation experiments and clarifications addressing each of your points.

Motivation and validation of LRC (W1/W2).

We agree that LRC needed a stronger motivation in the paper, which we also discussed with reviewer VtU7. We added Appendix B.1 and B.2 where we validate LRC against state prediction in physical space and comparing the R2R^2 in LRC it with L2 and cosine similarity.

Validation in physical space (Appendix B.2). We introduce physical rollout consistency (PRC), which decodes each predicted latent with the frozen state probes and computes R2R^2 against the true simulator state. PRC is computed in the same physical coordinates for every model, so it does not depend on latent dimensionality or scale. LRC and PRC are strongly correlated (ρ=0.81\rho = 0.81, p=2.53×10−46p = 2.53×10^{-46}, n=196n = 196, Fig. 12), and the main results are unchanged when PRC replaces LRC (Fig. 13). PRC needs the ground-truth state and an accurate probe, so we keep LRC as the primary metric and use PRC as a check.

Choice of R2R^2 (Appendix B.1–B.2). Variance-weighted R2R^2 normalizes prediction error by target variance, giving a fixed scale across latent dimensionalities (11 is perfect prediction, 00 corresponds to predicting the mean) and invariance to translations, global rescaling, and orthogonal transformations. In Appendix B.2, LRC, cosine similarity, and L2L_2 distance all correlate well with PRC (ρ=0.81\rho = 0.81, 0.780.78, and 0.710.71; Fig. 14). However, raw L2L_2 distance lies on an arbitrary model-specific scale and grows with latent dimensionality, and cosine similarity has no fixed reference point.

Adding new environments (W3).

We chose three simple systems on purpose, because they let us compare each model against the true state and dynamics, and our claims are counterexamples to the assumption that high reward implies an accurate model. However, we agree that expanding the range of tasks helps show how far these failure modes extend. We added Appendix H (Fig. 27; also referenced in Section 5.1), evaluating the 317M-parameter multi-task TD-MPC2 model trained from states across 30 DMControl tasks spanning 11 environments (including locomotion tasks such as hopper and walker). Our core finding holds: task reward and LRC remain uncorrelated across the 30 tasks (Spearman ρ=−0.11\rho = -0.11, p=0.56p = 0.56), with many locomotion tasks reaching almost perfect reward despite very low LRC.

Clarity of writing (W4).

We revised the theoretical formulation and Definition 1 in Section 2, clarified the LRC evaluation protocol in Section 4.2, and added self-contained details on LRC computation and validation (Appendix B.1–B.2) and own-policy trajectory evaluation (Appendix C). If specific passages were still hard to follow, please let us know and we will gladly revise them.

Answer to Questions:

Q1: Line 118. Thank you for catching this. The sentence now lists SIGReg regularization separately from reconstruction losses.

Q2: Why does LeWM work from states but barely from pixels? Our pixel LeWM matches the original results under their original evaluation protocol (Fig. 20). The original evaluation is goal reaching, where the model must reach a goal state that is close to the start state. Our tasks are more complex (e.g. reach over longer distances, swing-up) with nontrivial unforced dynamics. Solving them requires accurately predicting how positions and velocities evolve over many steps, where pixel-based LeWM breaks down.

We hope these additions address your concerns, and we would be glad to discuss any remaining points.

Thank you for the detailed feedback. My concerns are resolved now. I will reflect the rebuttal and my resolved concerns in my final assessment.

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

The paper studies the problem of faithfulness of language models. It correctly points out that a lot of work limit their analysis to the downstream utility of world models, or otherwise neglect fine-grained analysis into the capabilities of world models. To tackle this gap, the manuscript proposes two mechanisms to quantify the faithfulness of a world model and performs analysis on world models on classic environments. Among their conclusions is that high planning performance does not imply accurate world modelling.

Critical strengths
  • The core question that the manuscript attempts to answer ("Do successful latent world models actually learn representations and dynamics that model their environment?") is very important and scientific in nature, even if limited in scope. A lot of contemporary works focus only on downstream metrics of the world models and neglect this issue.
  • The manuscript is well-written and the claims are generally supported by the evidence.
Critical weaknesses
  • The proposed definition of faithfulness is substantially limited, and the implications of the core question are. (1) It is well known that next-observation prediction accuracy is insufficient to capture quality of a world model. This is due to issues like error accumulation, robustness to noise, etc. (2) As the manuscript points out, imperfect world models are still useful for planning in practice, why and how does this happen? (In my opinion) A discussion of how to quantify the extent to which a model is faithful should incorporate some consideration for downstream utility. Everyone agrees that a perfect model is great, but the usefulness of an imperfect model depends on the application.
  • There are limited insights that one can derive from the coarse analysis done in the manuscript that would directly inform development of world models. The main experiment compares different world models from the literature. This is valuable, but they are treated essentially as black boxes, and thus we can't tell e.g., whether there are specific architectural components, etc., to which we could attribute different forms of robustness, etc. A more granular analysis of how architectural decisions relate to different forms of faithfulness would strengthen the work a lot. This is aggravated by the fact that "world modelling" is a very, very well studied field (which includes adjacent problems like time-series modeling), and so the bar for the significance of the insights that an analysis provides is high.
Questions for authors

Beyond the weaknesses outlined above:

  1. Do you think your work could be developed into a framework for evaluating world models more generally?
  2. Would you consider expanding the related work discussion to include time-series modeling literature? Please elaborate on why the techniques developed in these mature fields are insufficient and why a new definition of faithfulness is required.
  3. Do you think different control policies could lead to different conclusions, given that they supply the data used to train the world model (and presumably also could supply different test distributions)?
3 comments

Thank you for the positive review of our paper, we appreciate the time you put into the paper. We have updated the manuscript (changes highlighted in blue) with new validation experiments and clarifications addressing each of your points.

Limitation of definition of faithful world model (W1).

It is well known that next-observation prediction accuracy is insufficient to capture quality of a world model. This is due to issues like error accumulation, robustness to noise, etc.

Indeed, error accumulation and noise make it harder to evaluate prediction accuracy of the dynamics model. However, in some environments long-horizon planning is crucial (see the new results on Pendulum + Cartpole in Figure 22, where the optimal planning horizon is >= 20-50), which means that it is actually desired to measure the effects of error accumulation, which is what LRC does. Regarding noise robustness, this is an interesting angle to study in future work but does not apply to the environments studied here (or in dm_control more broadly).

"Imperfect world models are still useful for planning in practice, why and how does this happen?". We would like to clarify the paper's position. We do not claim that imperfect world models are useful for planning in practice. We rather state that in world models that are jointly trained within an RL context (TD-MPC2, DreamerV3), it is possible that the full model setup achieves high task reward without faithfully modeling the environment.

To sharpen the manuscript and make this point more prominent, we extracted the latent dynamics model from TD-MPC2 and disregard the reward model, terminal value function, and policy prior for planning. Using the dynamics model, we plan with its frozen latent dynamics model using MPC, following LeWM setup. This makes the evaluation setting more comparable to LeWM, and with a faithful world model, this would yield successful control (see Fig. 2).

Since the world model is frozen, LRC stays the same while we re-measure return using the latent dynamics alone (Fig. 5). LRC is now predictive of reward. State-based TD-MPC2 matches the native controller (≈900\approx 900 return across tasks), whereas pixel-based TD-MPC2 drops from ≈900\approx 900 to ≈550\approx 550 (with large variance) on Pendulum and from ≈750\approx 750 to ≈400\approx 400 on CartPole. We sweep the planning horizon in Fig. 22 to see why. Without a terminal value function, swing-up requires long-horizon rollouts (H≥20–50H \ge 20\text{--}50), where pixel-based predictions drift. In contrast, Reacher is solved even at H=1H=1 (a greedy step toward the target) and retains much higher pixel LRC (≈0.55\approx 0.55; Fig. 18), so both modalities still succeed.

In summary, once the learned value and policy heads are removed, TD-MPC2 behaves like LeWM: solving tasks that require multi-step planning depends directly on accurate latent rollouts as measured by LRC. In pixel-based TD-MPC2, high reward is due to the reward-trained policy and value heads compensating for inaccurate latent dynamics rather than from a faithful world model.

W2: Insights for developing world models.

We see the main insight of the paper as a problem with evaluation. Latent world models are judged mainly by reward, and we show that reward can report success for models that have not learned the dynamics. As in generative modeling [Theis et al., 2016], progress depends on metrics that measure what the models are meant to learn, and LRC and state decoding are a step in that direction.

Rather than treating the models purely as black boxes, we chose three model families that vary in whether they reconstruct observations and whether they are trained with reward (Fig. 3b). Combined with LRC and state decoding, our controlled interventions separate representation failures from dynamics failures. State versus pixel inputs test the encoder, velocity injection and frame-stacking ablations test temporal state estimation (Section 5.3), and invertible nonlinear mixing tests inversion of the observation map (Section 5.4). Training with reward makes the clearest difference across families, and our new TD-MPC2 ablation (Fig. 5) isolates why within a single model. Removing the learned value, policy and reward heads removes pixel-based TD-MPC2's performance on Pendulum and CartPole, showing that these auxiliary heads compensate for inaccurate latent dynamics.

These results point to concrete directions. Velocity estimation from pixels is a bottleneck, and the objective matters even when no information is lost, which motivates objectives with identifiability guarantees [Reizinger et al., 2025]. A systematic ablation within each model family is beyond the scope of this paper, but combined with such ablations, our metrics could show which components cause these failures.

  • Theis, L., Oord, A.V.D. and Bethge, M., 2015. A note on the evaluation of generative models. arXiv preprint arXiv:1511.01844.
  • Patrik Reizinger, Randall Balestriero, David Klindt, and Wieland Brendel. Position: An empirically grounded identifiability theory will accelerate self supervised learning research. In International Conference on Machine Learning, 2025.

Answer to Questions:

  • Q1: A general framework for evaluating world models. We think the field needs to develop better, and more rigorous benchmarks to test world models, and our work contributes to this. We show that good latent prediction is useful and necessary, and that only looking at reward does not reveal issues specific to modeling latent dynamics.
  • Q2: Connection to time-series modeling. We thank the reviewer for this suggestion. We have expanded the Related Work section where we discuss classical state-space models, system identification, and modern time-series forecasting. While these fields provide well-established modeling and evaluation techniques, commonly used objectives and metrics primarily focus on predictive performance rather than evaluating whether the learned latent dynamics preserve the underlying system dynamics. This motivates our definition of faithfullness, which explicitly evaluates dynamics equivariance and state sufficiency providing a metric for assessing whether latent world models faithfully capture the underlying system dynamics.
  • Q3: Effect of the control policy on the conclusions. We checked this directly. In the new Appendix C, we evaluate every model on trajectories from its own controller and repeat the main analyses (Fig. 17). The conclusions do not change. Pixel-based TD-MPC2 and DreamerV3 still reach high reward with low LRC, and pixel-based models still decode velocities worse than state-based ones. We expected LRC to improve on own-policy data, since these trajectories are closer to the training data, but it stays the same or gets worse for almost every model and environment (Fig. 18).

We hope these additions address your concerns, and we would be glad to discuss any remaining points.

Dear reviewer QoKU, please let us know if our comments addressed your concerns or if there are any additional questions we can clarify in the remaining discussion time. Thanks again for your time!

Reviewer_VtU7OpenReview ↗
Rating
3(+1)
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper investigates whether high task returns imply that a latent world model has learned accurate environment dynamics. The authors define a faithful latent world model in terms of dynamical equivariance and state sufficiency, and evaluate DreamerV3, TD-MPC2, and LeWM using latent rollout consistency (LRC), state-decoding probes, and task returns. The experiments show that reward and LRC can be decoupled, with particularly poor latent prediction and velocity decoding under pixel-based observations. By incorporating ground-truth velocity and introducing invertible nonlinear observation transformations, the authors further investigate the challenges of state estimation and dynamics learning.

Critical strengths
  1. The paper shows that high task returns do not necessarily imply accurate learned dynamics. Evaluating latent prediction and state decoding alongside returns provides a useful complement to standard task-based evaluation.

  2. Combining LRC with physical state decoding helps distinguish missing information in the representation from errors in dynamics prediction, rather than treating all failures as having the same cause.

  3. Injecting ground-truth velocity and applying invertible nonlinear observation transformations helps isolate possible sources of failure. The results suggest that improving observability or preserving all state information does not necessarily lead to accurate latent rollouts or successful control.

Critical weaknesses
  1. Different models may use latent representations with different scales and structures, which can affect LRC values. More validation is needed before interpreting differences in LRC as differences in dynamics prediction quality.

  2. Task returns are measured under each model’s own policy, while LRC is mainly evaluated on random-policy trajectories. Low LRC may partly reflect distribution shift.

  3. The encoder depends on observation and action histories, but the theoretical definition assumes a mapping from physical states to latent states. How this definition applies to recurrent models remains unclear.

  4. The experiments cover three simple environments and include changes to LeWM’s planner, with some configurations differing between state and pixel inputs.

Questions for authors
  1. Does the gap between high returns and low LRC remain when each model is evaluated on its own policy’s trajectories?

  2. How sensitive are the LRC rankings to changes in latent scaling? Do physical state prediction errors show the same pattern?

  3. How does the definition of faithfulness apply to encoders that depend on past observations and actions?

  4. Does the gap between state and pixel inputs remain when both use the same planner and compute budget?

4 comments

Thank you for your review, we appreciate the time you took to go through our paper. We updated the manuscript (changes highlighted in blue) with new validation experiments and clarifications to address each of your points.

Sensitivity of LRC to latent scale and structure (W1/Q2).

Validation in physical space (new Appendix B.2). To check whether LRC reflects actual state prediction error rather than differences between latent spaces, we now evaluate every model in the shared physical state space. To this end, we decode each imagined latent z^H\hat z_H with the frozen nonlinear state probes and compute R2R^2 against the true simulator state. We denote this metric as physical rollout consistency (PRC). Across models, modalities, and environments, LRC and PRC are significantly correlated (Spearman ρ=0.81\rho = 0.81, p=2.53×10−46p = 2.53×10^{-46}, n=196n = 196, Fig. 12).

Do physical state prediction errors show the same pattern? Yes. Replacing LRC with PRC does not affect any main finding (Fig. 13). Pixel-based TD-MPC2 and DreamerV3 still reach high reward with inaccurate rollouts, and pixel-based models still degrade faster over the horizon than state-based models. The ordering of models and modalities is preserved.

Alternative latent metrics. We considered various choices when designing LRC, which we now compare quantitatively in the paper: On top of R2 as used currently, we added comparisons to cosine similarity and L2L_2 distance (Fig. 14). All three correlate well with PRC (ρ=0.81\rho = 0.81 for LRC, 0.780.78 for cosine similarity, and 0.710.71 for L2L_2 distance). The reason why we picked R2 originally is that raw L2L_2 distance lies on an arbitrary scale specific to each model's latent space and grows with latent dimensionality, and cosine similarity lacks a fixed reference point. By contrast, variance-weighted R2R^2 gives a shared baseline (LRC=0\mathrm{LRC}=0 means predicting the mean) and is invariant to translations, global rescaling, and orthogonal transformations of the latent space.

We keep LRC as the primary metric because it requires neither the ground-truth state nor a trained probe, so it remains applicable where the physical state is unavailable. However, we believe that it added a lot of value to the paper to making these choices explicit and benchmark them, so thank you for your suggestions!

Evaluation on each model's own trajectories (W2/Q1).

Yes, the gap between high reward and low LRC remain when evaluating on each model's own policy data. In the new Appendix C, we collect an evaluation set of the same size as the random dataset using each model's own controller, and repeat all main analyses (Fig. 17). Pixel-based TD-MPC2 and DreamerV3 still reach high reward with low LRC at H=30H=30. Pixel-based models still decode velocities less accurately than state-based models, and position errors remain small for both.

One could expect that LRC improves on own-policy trajectories, since they cover a narrower part of the state space and are closer to the data the task-trained models were trained on. Instead, LRC stays the same or gets worse for almost every model and environment (Fig. 18) which speaks to the robustness of the metric for assessing world modeling performance.

Faithfulness on observation and action histories (W3/Q3).

We agree that defining faithful world models through r=h∘g:S→Zr = h \circ g : \mathcal{S} \to \mathcal{Z} only covered the simplified case of memoryless encoders, whereas TD-MPC2 and LeWM stack frames and DreamerV3 uses a recurrent state.

Based on your feedback, we now revised Definition 1 to define latents directly along trajectories via zt=h(g(s0),…,g(st),a<t)z_t = h(g(s_0), \dots, g(s_t), a_{<t}). A world model is faithful if, after a context length k0∈Nk_0 \in \mathbb{N} (e.g., enough steps to infer velocities from frames), any two trajectories (st,zt)(s_t, z_t) and (st′′,zt′′)(s_{t^{\prime}}^{\prime}, z_{t^{\prime}}^{\prime}) satisfy for all t,t′≥k0t, t^{\prime} \ge k_0: (1) dynamics equivariance, f^(zt,at)=zt+1\hat{f}(z_t, a_t) = z_{t+1}, and (2) state sufficiency, zt=zt′′  ⟹  st=st′′z_t = z_{t^{\prime}}^{\prime} \implies s_t = s_{t^{\prime}}^{\prime}. For a memoryless encoder (k0=0k_0 = 0), this reduces to the original definition with r=h∘gr = h \circ g.

For recurrent models, requiring zt=zt′′  ⟹  st=st′′z_t = z_{t^{\prime}}^{\prime} \implies s_t = s_{t^{\prime}}^{\prime} means ztz_t uniquely determines the current state, while allowing extra history in ztz_t so two trajectories ending in the same sts_t need not map to the exact same latent. Our empirical metrics already test this trajectory-level definition directly: LRC compares imagined rollouts z^H\hat{z}_H against h(x≤H,a<H)h(x_{\le H}, a_{ < H}), and the probes decode sts_t from those same history-based latents.

Matched planners/compute budgets, state vs. pixel configurations (W4, Q4)

Yes, the gap remains under the same planner and compute budget. The state–pixel gaps in LRC (Fig. 4b) and velocity decoding (Fig. 4d) are measured on the world model alone, so they do not depend on the planner. TD-MPC2 and DreamerV3 use their own controllers, unchanged between modalities. For LeWM, Fig. 21 shows state and pixel models through the same planners (random shooting and CEM) and both costs: the original latent cost and our decoded state cost, which gives higher returns for both modalities. With the state cost, state-based LeWM solves every task with every planner, while pixel-based LeWM solves none under any planner or cost. The velocity and nonlinear-mixing experiments show the same pattern (Fig. 26).

Scaling to 30 environments with multi-task TD-MPC2 (W4).

We deliberately chose three low-dimensional systems where ground-truth states and transitions are simple and available, since failure to learn faithful dynamics in simple settings already serves as a clean counterexample. To test how far our findings extend, we added Appendix H (Fig. 27; also referenced in Section 5.1), evaluating the 317M-parameter multi-task TD-MPC2 model trained from states across 30 DMControl tasks spanning 11 environments. Our core finding holds: task reward and LRC remain uncorrelated across the 30 tasks (Spearman ρ=−0.11\rho = -0.11, p=0.56p = 0.56), with many locomotion tasks (e.g., walker) reaching almost perfect reward despite zero LRC.

We hope these additions address your concerns, and we would be glad to discuss any remaining points.

Dear reviewer VtU7, please let us know if our comments addressed your concerns or if there are any additional questions we can clarify in the remaining discussion time. Thanks again for your time!

Reviewer_VtU7OpenReview ↗

Official Comment by Reviewer VtU7

Thank you for your detailed response. My concerns are resolved now. As a result, I will raise my score.

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

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