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Under review as a conference paper at ICLR 2027

Identifying What Actions Read and Change in World Models

Abstract

World models support planning by predicting action consequences. Yet accurate prediction can leave latent state variables mixed across learned variables, obscuring which state variables the behavior policy reads (the read set) and which its actions change (the effect set). We jointly model how the behavior policy generates actions and how actions enter the transition, allowing next-step variables to depend on one another. We show that, under explicit conditions, video and logged actions reveal both roles of each variable that within-step dependence sets apart: its learned counterpart carries the same two labels, even while others stay mixed. The guarantee holds for models that reproduce the logged frame–action process with the fewest conditional dependencies among next-step variables. Under the same conditions, when next-step variables are conditionally independent given the current state and action, the guarantee covers every dynamic state variable. We learn one world model and estimate both sets on its frozen representation. Controlled latent experiments show closer variable matching and better read-set recovery than the same model trained for prediction alone, at comparable predic- tive accuracy. In a controlled RGB study on a fixed representation, read and effect estimates track policy and actuator switches, respectively. The selected variables also predict action responses more accurately than the full representation.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
Causal Representation Learning, Identifiability, World Models

Reviews

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1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
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Paper summary

The paper identifies the problem of identifying causal relationships between variables in a world model. The authors formally identify conditions under which partial identification may occur. The insights are then tested in experiments where the identification of variables is tested under a method inspired by the theory. The proposed method recovers read/effect sets more accurately than several baselines at comparable predictive fit.

Critical strengths
  • The paper tackles an important problem. Identifying causal relationships, and specifically the separation into "read" and "effect" that the manuscript motivates can be very useful for control.
Critical weaknesses
  1. It is hard to parse what exactly are the insights that the authors have identified and how exactly they are exploited. This is partly a presentation problem (the theorem is opaque and its significance is never explained step by step), but also a problem with the methodology: the authors train with a sparsity penalty on a different quantity (gate input-selection) than the one Theorem 1's guarantee is stated over (union-graph edge count among next-step variables). A formal or even empirical connection between the two is never stated.
  2. It's not clear how much value the theoretical discussion has for realistic settings. For instance, assumption 1 implies that a single instantaneous frame fully determines the true state, this basically excludes most image-based control systems. Then, even in the paper's example, Theorem 1 covers only a minority of variables, even though it is the sparsest non-trivial coupled topology. The paper never discusses whether the guarantee is practically meaningful for systems more entangled than a simple chain.
Questions for authors
  • Is your method only applicable to image observations? The theory is more general. Have you tried running the method under other perception systems (e.g., LiDAR, etc)?
  • How much do you think the assumptions limit applicability to real world settings? How would you expect the method to degrade when the assumptions are not fully satisfied, e.g., observations are not invertible, etc. It would be valuable to have a controlled experiment to understand how things degrade.
4 comments

Thank you for the time you spent on this review, and for noting that separating read from effect can be very useful for control.

For each state variable, our paper asks whether the behavior policy reads it and whether the logged action changes it (its read and effect labels). It asks which labels can be identified while the other variables stay mixed.

The paper has these changes in response to your review, marked in blue in the revised PDF.

  • W1. Section 3.3 now walks through Theorem 1 in four steps on the cup example, and Appendix O.5 reports whether the gate penalty changes the estimated edge count.
  • W2. Appendix O.4 reports how much of a system the guarantee covers as within-step dependence gets denser, and our audit on the five-chain witness.
  • Q2. Appendix O.3 reports the controlled degradation experiment you suggested.

W1: what the insights are and how we use them

It is hard to parse what exactly are the insights that the authors have identified and how exactly they are exploited.

In brief, prediction alone cannot tell which variables a policy reads or an action changes. This is why we test the two labels separately. Theorem 1 says, at the population level, for which variables these tests return the true labels in a model chosen by the minimum-edge criterion, even while other variables stay mixed. Following your comment, Section 3.3 now walks through the theorem in four steps on the cup example, with position p, velocity v and contact force c. The policy chooses the push from p and c, and the push changes all three. The read set is therefore {p, c}, and the effect set is {p, v, c}.

  1. Predictive fit cannot determine the labels. A model that stores y1 = p + v and y2 = v predicts as well as one that stores p and v. Here y2 helps predict the push because y1 - y2 recovers p. Velocity then looks like a policy input. We therefore audit the labels on the frozen representation, not on the model's heads or gates.

  2. Effect labels tolerate more mixing than read labels. The effect test asks whether the push changes a variable's own next-step distribution given the whole current state. Mixing among the other variables leaves this intact if the variable has a clean counterpart, a learned variable matched to it alone. The read test asks what a variable adds about the push beyond the others, which policy inputs mixed into them can distort. We therefore use one test per label, and the effect test looks beyond the mean (Section 4).

  3. A selected model mixes variables only along edges of the true union graph. The minimum-edge criterion keeps, among candidates that reproduce the data, those with the fewest edges, where an edge links two next-step variables still dependent given the rest of the step. A candidate's encoder sees one frame. Its mixing is therefore the same at every preceding state and action. Assumption 2 requires the next-step randomness to change with them in enough independent ways that a fixed mixing cannot remove an edge. If p and v get separate random jolts, the candidate storing p + v has an extra edge and is ruled out, but under one shared jolt it is kept.

  4. Within-step dependence therefore decides which labels are guaranteed (Theorem 1). We call a neighbor j of i intimate to i if j is also linked to every other neighbor of i. A variable with no intimate neighbor has a clean counterpart in every selected candidate. Its effect label is therefore correct. If it is also no other variable's intimate neighbor, its read label is correct as well. For example, c has no neighbor under a shared jolt. The labels of c are then correct at the population level in every selected candidate, even the mixed one that wrongly labels v as read.

Steps 1 and 2 shape our audit. Steps 3 and 4 need the criterion, which training does not apply. This is why we test them on trained models with a diagnostic step (Section 5.1).

As a diagnostic, not part of our method, we chose one linear transformation of the learned variables by the criterion after training. This raises our model's variable matching (MCC) from .760 to .963 in a lag-only process (no within-step dependence) where the assumption holds. By contrast, where the assumption fails, the same step mixes the true variables, lowering their MCC from 1.000 to .745. Both results are now in Appendix O.5.

We adapt the graph argument of Zhang et al. (2024). Our effect guarantee uses a clean counterpart. This is component-wise identification of the kind that Li et al. (2025) obtain under within-step dependence. Neither Zhang et al. nor Li et al. link components to what a policy reads or an action changes. We add this link, including under within-step dependence, which mechanism-sparsity identification excludes, and we show that a read label needs an extra separation (Section 3.3).

W1: the gate penalty and the union-graph edge count

A formal or even empirical connection between the two is never stated.

Thank you for pointing out this mismatch. Because no formal link exists, our audit, not the gates, decides both labels (Section 4). A formal link is one of our next steps.

Empirically, in the three settings where our edge-count estimator passed its check on oracle coordinates (the true variables), the gate penalty (coefficient 0.002) caused no detectable change in the estimated edge count. For example, the change was +0.06 edges on average [-0.08, +0.19] in the lag-only process where Assumption 2 holds. Brackets give 95% paired bootstrap intervals, and we call a change detectable or clear when the interval excludes 0 (uncorrected for multiple comparisons). Appendix O.5 now reports this comparison.

W2: Assumption 1 and image-based control

For instance, assumption 1 implies that a single instantaneous frame fully determines the true state, this basically excludes most image-based control systems.

Assumption 1 does imply this, and the experiment you suggested in Q2 now measures what happens when it fails. Our guarantee covers image-based systems where a frame shows the modeled state, which excludes occlusion and velocities that a single frame cannot show (Section 3.2). Variable matching drops when observations are not invertible, while our Read advantage over the temporal backbone, the same architecture trained for prediction only, remains (Q2, Appendix O.3).

W2: how many variables the guarantee covers

The paper never discusses whether the guarantee is practically meaningful for systems more entangled than a simple chain.

Thank you for asking about more entangled systems. How many labels the guarantee covers depends on how dense the within-step dependence is. It covers both labels of every dynamic variable when there is no such dependence, and coverage falls as the dependence gets denser. In the paper's examples, the guarantee covers 1 of 3 variables in the shared-jolt cup (the contact force), every variable in the separate-jolt cup, and 4 of the 10 labels in the five-chain (Section 3.3).

We computed coverage on random DAGs with 5, 10 and 20 variables (5,000 graphs per setting), taking the union graph to be the moral graph of each DAG (Appendix H.1). The table gives the share of variables with a guaranteed label at each average degree:

Average degreeShare with a guaranteed read labelShare with a guaranteed effect label
0 (no within-step dependence)1.001.00
about 0.6.59-.60.63-.66
about 1.2-1.3.31-.37.44-.53
about 2.4-3.1.07-.15.21-.47
4.0-7.3at most .060, .14 and .44 for 5, 10 and 20 variables

The table shows that coverage falls as dependence gets denser, because more variables then have an intimate neighbor (W1, step 4). Read coverage falls faster because it needs both conditions. These are computations on graphs. Labels outside the guaranteed range may still be identifiable (Section 3.3).

Our audit returns all 4 guaranteed labels of the five-chain witness in every repetition on the oracle coordinates and on two hand-built, untrained mixtures that the criterion keeps. By contrast, the effect label of variable 2 turns from no to yes on the mixture it rules out, and variable 3 loses its read label. We have added the coverage table and this audit to Appendix O.4.

Q1: is the method only for images?

Is your method only applicable to image observations? … Have you tried running the method under other perception systems (e.g., LiDAR, etc)?

No, it is not. As you note, the theory is more general: its only requirement on the sensor is that a single observation determine the modeled state through a smooth invertible map. We have not run the method with LiDAR or other sensors.

Our studies use three kinds of input. The controlled study observes a nonlinear mixing of the latent state rather than images (Appendix J). The RGB study uses images as inputs and a fixed representation with scene priors. There, the read test follows a policy switch from object A to C, and the effect test an actuator switch from B to A (Read F1 .967 and Effect F1 .950, Figure 5a).

Our model selects coordinates from frozen CLIP image features in BridgeData V2 real robot recordings. Together with the robot's proprioceptive state, these coordinates decode robot-state changes slightly better than equal-size random subsets (Figure 5c, Appendix M).

Q2: how the assumptions limit real-world use, and how the method degrades when they fail

How much do you think the assumptions limit applicability to real world settings? How would you expect the method to degrade when the assumptions are not fully satisfied, e.g., observations are not invertible, etc.

We ran the controlled experiment you suggested. It shows that non-invertible observations lower variable matching but no role F1 detectably. Our guarantee applies where a single frame determines the state, the policy has a positive action density, and frames are synchronized with actions, which excludes occlusion, partial observability, deterministic policies and unknown action delays (Sections 2, 3.2 and 6).

Our theory has three practical uses within these limits that need no change to training. First, it tells us how to audit a trained model (W1). Second, it explains why the effect test over-selects on learned variables: one that mixes in a variable the action changes does respond to the action. Applying the criterion after training lowers the number selected from 4.20 to 2.85, for two true ones, in the lag-only process that meets every premise of Theorem 1.

Third, it gives a diagnostic rule for choosing among trained models. Choosing among 8 candidates by the fewest estimated edges gave an MCC .059 [+.030, +.091] higher than choosing by prediction error, in the lag-only process where Assumption 2 holds (Appendix O.5).

We changed four conditions in graded steps and trained our model and the prediction-only backbone at each step. Every new experiment with trained models uses 5 to 40 seeds per setting, with counts in the revised paper. The table gives, for the lag-only process and one level per row, each change from the undisturbed process and our Read F1 minus the backbone's (* marks a 95% paired bootstrap interval that excludes 0):

ConditionLevelMeasureChange in our modelOur Read F1 minus the backbone's
Observation noise τ0.1MCC-.008+.221*
0.3-.036*+.234*
0.5-.089*+.174*
Occlusion p0.1MCC-.028*+.144*
0.25-.051*+.219*
0.5-.098*+.220*
Policy noise, from 0.550.3Effect F1+.064+.224*
0.15-.063+.138*
0.05-.276*+.003
Logged action delayed with probability p0.25Effect F1+.051+.166*
0.5-.135*-.016

The table shows that MCC drops when frames stop determining the state, because part of it is lost before encoding, while our Read advantage over the backbone remains. No role F1 drops clearly under noise or occlusion in either process. Our model's Read F1 also stays clearly above the backbone's in both processes without Assumption 2.

The action density is still positive at policy noise 0.05, but actions at a given state barely vary. Identification then weakens at finite sample sizes: Read F1 and MCC also drop clearly. Similarly, the action terms no longer help when half of the logged actions are delayed. In both cases our MCC falls below the backbone's. We have added the full tables to Appendix O.3. In short, our Read advantage over the backbone held at every level of observation noise and occlusion, at policy noise down to 0.15, with a quarter of the logged actions delayed, and without Assumption 2.

Thank you again for the time you put into this review. Please let us know if any question remains.

Dear Reviewer EaWG,

Thank you again for your review. As the discussion closes on 18 November (AoE), we would be grateful to hear whether our replies address your concerns. For convenience, this is where the revised paper takes up each point:

  • W1: a step-by-step explanation of Theorem 1 on the cup example (Section 3.3), and tests of the criterion and of the gate penalty on trained models (Section 5.1, Appendix O.5).
  • W2: where Assumption 1 applies (Section 3.2), and the coverage of the guarantee beyond a chain, including random graphs (Section 3.3, Appendix O.4).
  • Q1: the observation types in our studies, from nonlinear mixtures to images and robot recordings (Section 5, Appendix J).
  • Q2: graded tests of how recovery changes as the assumptions are violated (Appendix O.3).

We would be glad to clarify any point that remains.

Reviewer_hYyUOpenReview ↗
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Paper summary

This paper studies how to identify two different roles of latent state variables in world models. Variables which a behavior policy uses to choose actions (the read set), and variables which are affected by those actions (the effect set). The authors show that, under certain assumptions, these roles can be identified for some variables even when the remaining representation is not fully disentangled. The theoretical analysis allows dependencies between next-step variables and characterizes when each role can be recovered. The paper also proposes a practical framework for learning state representations and estimating both sets. Experiments on synthetic environments and controlled visual settings show improvements in variable recovery and provide evidence that the selected variables can support action and response prediction.

Critical strengths

First, the paper proposes an interesting and well-motivated problem. I appreciate the distinction between variables used by a policy and variables affected by its actions. These are often treated together in world modeling, but they represent different aspects of the interaction. The paper makes a convincing case that accurate prediction alone does not guarantee that the learned representation captures these roles correctly.

Also, the authors carried out thoughtful experimental analysis. The experiments go beyond measuring prediction accuracy and directly evaluate whether the learned variables recover the intended roles. The comparison between predictive performance and role recovery is particularly useful. I also appreciate the controlled experiments that separately change the policy and actuator, as they provide an intuitive demonstration of the difference between read and effect sets.

Critical weaknesses

Fisrt, the theoretical assumptions are restrictive, and their connection to practical world models remains unclear. The identification results require an invertible observation model, sufficient variation in the transition distribution, and a minimum-dependency criterion. These conditions may be difficult to satisfy in realistic visual environments with occlusion or partially observable states. In particular, the practical training procedure does not explicitly optimize the minimum-edge criterion used in the theory. This makes it difficult to determine how directly the theoretical results explain the empirical behavior of the proposed method.

Secondly, the effect-set recovery results are less convincing than the read-set results. Table 1 shows clear improvements in read-set recovery, but the gains in effect-set F1 are relatively modest. The appendix also reports that exact effect-set recovery is not achieved in any of the five seeds for either synthetic setting. Even with more evaluation samples, the learned representations tend to select too many variables. Since identifying both roles is the main goal of the paper, this limitation deserves more discussion.

Finally I think the contribution of the proposed training objectives is not fully established. The method combines several losses and regularization terms to encourage more structured representations. However, the matched ablation in Appendix K.4 reports the same mean read-set F1 with and without the read objective. This raises a question about which components actually drive the improvement over the prediction-only baseline.

Questions for authors
  1. How sensitive are the identification results to violations of the theoretical assumptions, particularly the distributional variation condition? Could the authors provide an experiment showing how recovery quality changes as these conditions become less well satisfied?

  2. Appendix K.4 shows that removing the read objective does not change the mean read-set F1. Could the authors clarify which parts of the training objective are most responsible for the improvement over the temporal backbone?

  3. The effect-set estimator appears to produce a relatively large number of false positives on learned representations. Is this mainly caused by imperfect representation learning or by the estimation procedure itself? Could a different thresholding or calibration strategy improve the results?

6 comments

Thank you for your careful review and for highlighting the separate policy and actuator changes. We ran new experiments for all three questions, mostly on the two controlled processes: lag-only, with no within-step dependence among next-step variables, and instantaneous, with such dependence.

Changes are blue in the revised PDF, and new tables are R1-R13. Every new experiment with trained models uses 5 to 40 seeds per setting, with counts in the revised paper.

Q1: violated assumptions. How sensitive are the identification results to violations of the theoretical assumptions, particularly the distributional variation condition? …

We appreciate your suggestion of this graded experiment. Our model's gains arise without Assumption 2 in both controlled processes, and the condition matters in the lag-only process once we apply the minimum-edge criterion of Theorem 1 after training.

In both controlled processes of the submission, neither of which satisfies the condition, our model's Read F1 is clearly higher than the backbone's: +.187 [+.093, +.278] in the lag-only process and +.232 [+.147, +.314] in the instantaneous one. Brackets give 95% paired bootstrap intervals. We call a change clear, or detectable, when the interval excludes 0, without correction for multiple comparisons.

In lag-only, state-dependent noise variance makes the condition hold. We then choose a linear transformation of the learned variables by the criterion, a diagnostic we call applying the criterion after training. We ran it only in lag-only, whose graph has no within-step edges. State-dependent variance pins down the transformation that makes next-step residuals uncorrelated in every state cluster.

The step raises our model's variable matching (MCC) from .760 to .963. The gains at variation strengths 0.3, 0.6 and 1.0 are +.163, +.191 and +.204. By contrast, with a fixed variance, every rotation that keeps the residuals uncorrelated fits equally well, and the same step mixes the true variables, lowering their MCC from 1.000 to .745.

With a C3 observation map and a chain started at the invariant law, every theorem premise holds. The same step raises MCC from .753 to .963.

Without this step, satisfying the condition does not improve trained-model MCC. In instantaneous, varying variance alone does not suffice. We instead vary the within-step coupling with the state, and the numerical rank check indicates that the condition holds. The table gives changes from the process where it fails (*: 95% paired bootstrap interval excludes 0):

ProcessStrengthRead F1Effect F1MCC
lag-onlyvariance α = 0.3+.037+.001-.005
α = 0.6+.028+.047*+.005
α = 1.0+.087*+.033-.004
instantaneouscoupling κ = 0.3-.117+.024+.003
κ = 0.6-.107+.038-.009
κ = 1.0-.017+.073*-.002

The table shows that MCC has no detectable change at any strength. The Effect gain at κ = 1.0 is close to the .070 gain of a variance-only setting that fails the condition.

We also violated Assumption 1 in graded steps by adding noise to the observations or occluding parts of them. MCC clearly drops in most of these conditions, as expected once a frame no longer determines the state. The largest drops in the lag-only process are .089 under noise and .098 under occlusion. No role F1 shows a detectable drop.

We graded two further conditions in the lag-only process, the policy noise and the delay of logged actions. Lowering the policy noise from 0.55 to 0.3 causes no detectable change, and the Read and Effect gains over the backbone still hold with a quarter of the logged actions a frame late (+.166 and +.148). Recovery weakens close to a deterministic policy and when half of the logged actions are a frame late: at policy noise 0.05, Effect F1 drops by .276, and with half of the actions late, the action terms no longer help. We have added these experiments to Appendices O.3 and O.5.

W1: the assumptions in practice. … the theoretical assumptions are restrictive, and their connection to practical world models remains unclear. …

Thank you for naming the three conditions. The theory guides auditing and diagnoses recovery: it explains over-selection and supports the diagnostic in Q1. As you note, prediction alone does not fix the roles, so the theory tells us to audit each role on the frozen representation. Since training does not apply the criterion, the gain over the backbone remains empirical. A next step toward connecting training to the criterion is to build it into the training objective.

Assumption 1, the invertible observation model of von Kügelgen et al. (2021), requires a frame to show the modeled state, which excludes occlusion. Assumption 2, which follows Hyvärinen et al. (2019) and Zhang et al. (2024), requires next-step randomness to vary in enough independent ways with the preceding state and action. Friction or contact motivates changes in how a jolt is shared, and both cup models provably satisfy the condition (Section 3.2, Appendix F.3).

Figure 5b tests predictive utility, not closed-loop control, on a fixed RGB representation with scene priors. The selected sets match all-coordinate action-prediction accuracy and lower short-term response error to action perturbations, while size-matched random subsets do worse on both.

W2: weaker Effect recovery. … Since identifying both roles is the main goal of the paper, this limitation deserves more discussion.

Q3: source of the false positives. … Is this mainly caused by imperfect representation learning or by the estimation procedure itself? Could a different thresholding or calibration strategy improve the results?

Thank you for asking us to explain the weaker recovery and separate its sources. Residual mixing in learned coordinates is the main cause of over-selection. Theorem 1 guarantees effect labels only for variables with a clean counterpart. A coordinate mixing an effect variable with a non-effect variable really responds to the action, so the test detects a real response (Figure 4b). This explanation is now in Section 5.1.

Our Effect gain over the backbone is clear: +.130 [+.067, +.198] in instantaneous and +.072 [+.034, +.110] in lag-only (Table R1, Appendix K.4).

Running the same estimator on oracle and learned coordinates separates the two sources. After calibration, the oracle effect set is exact in .73-1.00 of runs, while our model's exact-recovery fraction falls to 0 as N grows. The estimator's own error is mainly false selection at small sample sizes when actions have no effect. More samples remove it, and calibration controls it (Appendices K.5 and O.2).

Changing only the representation reduces over-selection. In the lag-only process satisfying every theorem premise, applying the criterion after training lowers the selected count from 4.20 to 2.85 and raises Effect F1 from .657 to .837 (Appendix O.5).

An effect threshold set from the audited data alone, by conditional randomization, controls false selections. It keeps the false-selection rate at or below .10 on control datasets in which the action has no effect, for every sample size and representation in our controlled processes, for a nominal level of .05.

To build the reference, we fit a model of the policy, resample the actions from it and recompute the scores. This reference keeps the policy, as a valid null must: an action with no effect still depends on the state. Our score keeps part of this dependence, a bias that does not shrink with N. In-sample permutation removes this dependence as well. As a result, the permutation reference narrows with N while the bias stays, and the false-selection rate under permutation reaches .48 for our model at N = 9600.

The table gives one rule per row, with the false-selection rate and our model's Effect F1 (lag-only):

Rule (lag-only)False-selection rateEffect F1 of our model, N = 2400 / 9600 unless stated
Submission's frozen threshold δe1.00 for N ≤ 1200.616/.646, selecting 4.52/4.17 (2 true)
In-sample permutation.48 at N = 9600+.014/-.091 vs frozen δe (the latter clearly lower)
Largest-gap cutoffnot evaluated+.109/+.088 vs frozen δe (both clearly higher), but selects only 1.55
Conditional randomizationat most .10.683 → .586 from N = 600 to 9600, selecting 2.23 → 4.97

A different threshold or calibration helps in part, but none removes over-selection on learned coordinates. The top-ranked learned coordinates up to the true set size give F1 .80, so ranking limits Effect recovery more than the threshold. All four rules are now in Appendix O.2.

W3: the read-objective ablation. … However, the matched ablation in Appendix K.4 reports the same mean read-set F1 with and without the read objective. …

Q2: what drives the gain. … Could the authors clarify which parts of the training objective are most responsible for the improvement over the temporal backbone?

Thank you for checking this ablation closely. The two versions in the lag-only ablation you cite have the same mean Read F1 because the version without the read objective Lread still keeps the alignment term Lalign. Both terms train our read gate and act on the same gated dynamic block, and they partly substitute in this process, with changes in individual runs that cancel on the paper's 5 seeds. “Without read objective” sets only the weight of Lread to 0, while the temporal backbone removes all three terms, Lread, Lalign and Lgate.

The submitted caption of Table 4 says that the zeroed coefficients are “as listed in Appendix K.1”, but K.1 does not list them, which was our error. The revised caption lists them for each version. Section 5.1 now calls the two means identical (.853) instead of similar.

For Q2, the gain over the backbone comes mainly from Lalign, as our matched 2³ factorial ablation of the three terms shows. Added alone to the backbone, each action term raises Read F1. Lalign has the largest main effect, the average change from adding it across the settings of the other two terms: +.157 [+.093, +.215] in the lag-only process and +.165 [+.095, +.235] in the instantaneous process. Lread has a clear main effect only in the instantaneous process, and Lgate contributes little.

The ablation uses the same data, initial weights and minibatch order across all 8 configurations in each process (Table R1). The table gives paired Read F1 differences with intervals:

Paired difference in Read F1lag-onlyinstantaneous
Our model - backbone+.187 [+.093, +.278]+.232 [+.147, +.314]
Backbone with Lalign - backbone+.267 [+.179, +.350]+.264 [+.180, +.340]
Backbone with Lread - backbone+.138 [+.047, +.224]+.166 [+.090, +.239]
Our model - version without Lread-.080 [-.153, -.010]-.032 [-.108, +.050]
Main effect of Lalign+.157 [+.093, +.215]+.165 [+.095, +.235]
Main effect of Lread+.027 [-.031, +.081]+.068 [+.018, +.115]
Main effect of Lgate+.002 [-.010, +.017].000

Our model's gains relative to the backbone in Read, Effect and MCC all have intervals above zero in both processes. The MCC gains are +.040 [+.013, +.067] in the lag-only process and +.077 [+.040, +.115] in the instantaneous one. Applying the criterion after training raises the MCC of all 8 configurations to .963-.988 in the lag-only process where Assumption 2 holds, and the differences between them almost disappear. Appendix K.4 now reports the ablation.

Thank you again for the care you put into this review. We hope this addresses your questions. Please let us know if any question remains.

Reviewer_SBtzOpenReview ↗
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Informativeness
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Paper summary

This paper distinguishes dynamic inputs of a behavior policy from variables whose next-step marginals respond to actions at fixed complete preceding state and static content. It establishes partial identifiability guarantees under instantaneous dependencies and estimates both roles on frozen representations.

Critical strengths
  1. The different identification requirements for Read and Effect labels provide useful theoretical insight. The analysis explains why recovering a variable does not necessarily preserve its Read label when that variable also enters other learned coordinates. The resulting partial guarantees remain informative even when the rest of the representation is mixed.
  2. The experiments demonstrate why predictive accuracy alone is insufficient for evaluating role recovery. Orthogonal coordinate mixing preserves predictive performance while degrading role identification, and controlled policy and actuator changes help distinguish the two roles. These analyses provide a useful perspective on evaluating world-model representations.
Critical weaknesses
  1. The connection between the identification theory and the implemented method remains incomplete. The guarantees require exact matching of the logged process law, minimum-edge selection in the union conditional-independence graph, and Assumption 2’s distributional variation. Training does not implement this graph criterion, and the main synthetic processes have fixed innovation covariances that violate Assumption 2. These acknowledged gaps limit the evidence linking the learned method to the partial-identification result.
  2. Empirical support for recovering both roles remains limited. Effect F1 is 0.636 and 0.595 in Table 1, and exact joint set recovery is 0/5 in both settings of Table 9 under the shared full-space assignment. Effect ranking remains relatively strong, but the independent audit in Appendix K.5 still over-selects at 9,600 transitions with frozen representations and thresholds. The RGB results use a fixed representation with scene-specific priors, while BridgeData evaluates paired-frame decoding with small gains. Recovery of both roles from learned visual representations therefore remains insufficiently demonstrated.
Questions for authors
  1. Can the method be evaluated empirically on a process satisfying the theoretical model assumptions, such as the five-chain construction in Appendix E, to determine whether it recovers the variables and labels covered by the guarantees?
  2. Appendix K.5 already audits frozen representations on independent trajectories. Can the controlled Effect estimator be evaluated under that protocol with its threshold calibrated from logged data alone, without oracle-coordinate null simulations? The resulting recovery and false-selection rates would help assess practical applicability.
  3. In Table 12, please specify exactly which terms are removed by “without read objective.” Given the unchanged mean Read F1, what additional evidence identifies the training components responsible for the improvement over the temporal backbone?
5 comments

We thank you for checking, point by point, the gap between the theoretical premises and the implementation, and for asking three questions that we could test directly. In brief, we found the following.

  • W1 and Q1. Applying the minimum-edge criterion after training largely separates the mixed variables in a lag-only process where Assumption 2 holds. It also makes every read set exact on a version of this process that meets every premise of Theorem 1.
  • Q2. A threshold set from logged data alone keeps false selections at or below .10 in our controlled processes.
  • W2. Most of the remaining Effect error is in the learned coordinates, and undoing the mixing reduces it.
  • Q3. “Without read objective” removes only Lread, and Lalign carries most of the gain over the temporal backbone.

Changes are blue in the revised PDF, and new tables are R1-R13. Every new experiment with trained models uses 5 to 40 seeds per setting, with counts in the revised paper. Brackets give 95% paired bootstrap intervals (20,000 resamples), and we call a change detectable, or clear, when the interval excludes 0, without multiple-comparison correction. Our controlled experiments use two processes: lag-only, with no within-step dependence among next-step variables, and instantaneous, with such dependence.

W1: the link between theory and training

Training does not implement this graph criterion, and the main synthetic processes have fixed innovation covariances that violate Assumption 2.

Both of your observations are right, and we now test the link directly on trained models. Our new tests of the criterion are consistent with Theorem 1: applied after training, it largely separates our model's variables where Assumption 2 holds and mixes the true variables where the assumption fails. Because training penalizes the gates and does not apply the criterion, this step is a diagnostic and not part of the method, and we do not assume that the guarantee carries over.

We made the innovation variance of the submission's lag-only process depend on the state. The assumption then holds by a numerical rank check. We chose one linear transformation of our model's dynamic variables by the minimum-edge criterion, a step we call applying the criterion after training. This raises their variable matching (MCC) from .760 to .963. By contrast, the same step mixes even the true variables (oracle coordinates) in the submitted fixed-variance process, where the assumption fails, and their MCC falls from 1.000 to .745.

Both results are now in Section 5.1 and Appendix O.5, and the contrast between them shows on data why the theorem needs the assumption.

Q1: a process that meets the assumptions

Can the method be evaluated empirically on a process satisfying the theoretical model assumptions, such as the five-chain construction in Appendix E, to determine whether it recovers the variables and labels covered by the guarantees?

Thank you for proposing this test. We ran it on two processes that meet every premise of Theorem 1, and the answer differs between them. Our trained model recovers every read set exactly and the effect labels in part, with Effect F1 .837, on a lag-only process once the criterion is applied after training (both tables below). Models trained on the five-chain process of Appendix E do not recover the guaranteed labels, because its identifying signal is too weak to detect at feasible sample sizes and our transition density cannot represent it. We trained our model, adapted to this process, and the temporal backbone on the latent chain observed through a smooth invertible mixing. The first table lists what we ran on each process:

ProcessWhat we ranGuaranteed labels
Five-chain (Appendix E)Our model and the backbone, trainedNot recovered, for the two reasons below (Appendix O.4)
Five-chain (Appendix E)Our audit on four hand-built candidates, no trainingAll 4 correct in every repeat on the oracle coordinates and on both kept mixtures. Two of them fail on the ruled-out mixture
Lag-only, state-dependent variance, C3 observation map, stationary startOur model, then the criterion after trainingEvery read set exact. Scores before and after in the second table

First, Appendix E builds the process as an analytic witness that the premises of the theorem can be met. Because a fixed linear change of coordinates can absorb the constant tridiagonal part of its next-step precision matrix, only history-dependent terms scaled by δ ≤ 1/100 single out the true coordinates. The best candidate without edges, under the parameters of Appendix E, fits only about 3×10⁻¹⁰ nat per transition worse than the true chain, a signal too weak to detect at feasible sample sizes. This is a case of weak identification (Lewbel, 2019, Section 8.1).

Second, our trained models use a transition density with a fixed diagonal covariance, which cannot represent these history-dependent terms.

To test the link between the theorem and our audit without training, we built four candidates by hand. Besides the oracle coordinates, two mixtures that the criterion keeps add variable 2 to variable 1, and the second also adds 4 to 5. Since 2 and 4 are intimate neighbors of 1 and 5 (each is linked to all other neighbors of the variable it joins), no edge is added. The fourth candidate adds variable 3 to variable 2. This adds an edge. As a result, the criterion rules it out and the theorem does not cover it. We computed edges in closed form and estimated labels from 9,600 trajectories (second row above).

The lag-only process of W1 has a stronger signal and no within-step dependence. Every label therefore falls within the range of the guarantee. Its original observation map is invertible but piecewise linear, not the C3 map that Assumption 1 requires, and the chain starts from a fixed Gaussian law rather than the invariant law. We removed both departures and changed nothing else. The activation becomes s + 0.5 tanh s with the same weights, and the chain runs 50 burn-in steps. Assumption 2 holds by the same rank check. This process therefore meets every premise of the theorem.

The second table gives our model on this process before and after the criterion is applied:

BeforeAfter
MCC.753.963
Read F1.8731.000
Effect F1.657.837
Coordinates the effect audit selects (two true)4.202.85

The table shows that applying the criterion after training raises all three scores, each with a 95% paired bootstrap interval above 0. Every read set is then exact. The exact effect set appears in a quarter of the runs, against half when the same step and audit are applied to oracle coordinates. Part of the remaining effect error therefore comes from the audit and the step themselves, not from the learned variables. With the piecewise-linear map, the same step gave Read F1 1.000 and Effect F1 .799 (Appendix O.5). In short, on the lag-only process, applying the criterion after training recovers every read set exactly and the effect labels in part, and on the five-chain, our audit returns every guaranteed label on the candidates that the criterion keeps.

Q2: a threshold from logged data alone

Can the controlled Effect estimator be evaluated under that protocol with its threshold calibrated from logged data alone, without oracle-coordinate null simulations? The resulting recovery and false-selection rates would help assess practical applicability.

We appreciate this suggestion. Yes, it can. A threshold calibrated from the audited data alone keeps the false-selection rate at or below .10 in our controlled processes, for a nominal level of .05, although it has no theoretical guarantee (Appendix O.2). We set it by conditional randomization under the protocol of Appendix K.5, and it selects the effect set exactly in .73-1.00 of the runs on oracle coordinates.

To build the reference, we fit a model of the policy, resample the actions from it and recompute the scores. This reference keeps the policy, as a valid null must: an action with no effect still depends on the state. Our score keeps part of this dependence, a bias that does not shrink with N. In-sample permutation removes this dependence as well. As a result, the permutation reference narrows with N while the bias stays, and the false-selection rate under permutation reaches .48 for our model at N = 9600.

The table gives one rule per row, with the false-selection rate and our model's Effect F1 (lag-only):

Rule (lag-only)False-selection rateEffect F1 of our model, N = 2400 / 9600 unless stated
Submission's frozen threshold δe1.00 for N ≤ 1200.616/.646, selecting 4.52/4.17 (2 true)
In-sample permutation.48 at N = 9600+.014/-.091 vs frozen δe (the latter clearly lower)
Largest-gap cutoffnot evaluated+.109/+.088 vs frozen δe (both clearly higher), but selects only 1.55
Conditional randomizationat most .10.683 → .586 from N = 600 to 9600, selecting 2.23 → 4.97

By contrast, over-selection remains on our model's coordinates and grows with N, whatever the threshold, because a coordinate that mixes in an effect variable really responds to the action and Theorem 1 guarantees an effect label only for a variable with a clean counterpart. The top-ranked learned coordinates up to the true set size give F1 .80, so ranking limits Effect recovery more than the threshold. We have added this calibration, with all four effect rules and the read threshold, to Appendix O.2.

W2: evidence for recovering both roles

Empirical support for recovering both roles remains limited. […] Recovery of both roles from learned visual representations therefore remains insufficiently demonstrated.

Thank you for weighing each source of evidence. The oracle audits of Tables 9 and 13 place most of the remaining error in the learned coordinates, and undoing the mixing reduces it, as Q1 shows. Effect is the harder role on learned coordinates because they are still partly mixed, as discussed under Q2. Ours is the only learned method that recovers the exact read set in any run under the strict endpoint of Table 9, although none recovers both sets exactly.

As you note, role recovery from learned visual representations lies beyond our current guarantees and evidence. For visual input, the RGB study of Section 5.2 evaluates the audit on a fixed representation with scene priors. In addition, our selected coordinates on BridgeData decode state changes slightly better on average than equal-size random subsets in the tuned configuration (Appendix M).

We state our Effect gains in the controlled processes relative to the temporal backbone, and they are clearly positive (+.130 in the instantaneous process and +.072 in the lag-only one, with 95% paired bootstrap intervals above 0). We have added a paragraph on Effect recovery on learned coordinates to Section 5.1.

Comments on the paper

1 comment
AuthorsOpenReview ↗

General Response

We thank the three reviewers for their detailed comments and for recognizing the value of separating read from effect.

List of revisions. Changes are blue, and new tables are R1-R13. Theorem 1, its assumptions and training are unchanged.

  • Theory tests and coverage: Appendices O.4-O.6 and Section 5.1.
  • Cup walk-through: Section 3.3.
  • Assumption changes: Section 5.1 and Appendix O.3 (Table R5).
  • Effect discussion and calibration: Section 5.1 and Appendix O.2.
  • Ablations and coefficient corrections: Appendices K.4 (Table R1), K.1 and Table 4.
  • Section 5.1: identical means in Table 12, and Read margins against IDOL+A and Mechanism Sparsity with paired intervals.

We would be glad to discuss any remaining question in the corresponding thread.

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

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