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- Informativeness
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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
- 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.
- 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
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 degree | Share with a guaranteed read label | Share with a guaranteed effect label |
|---|---|---|
| 0 (no within-step dependence) | 1.00 | 1.00 |
| 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 |
| 4.0-7.3 | at most .06 | 0, .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):
| Condition | Level | Measure | Change in our model | Our Read F1 minus the backbone's |
|---|---|---|---|---|
| Observation noise τ | 0.1 | MCC | -.008 | +.221* |
| 0.3 | -.036* | +.234* | ||
| 0.5 | -.089* | +.174* | ||
| Occlusion p | 0.1 | MCC | -.028* | +.144* |
| 0.25 | -.051* | +.219* | ||
| 0.5 | -.098* | +.220* | ||
| Policy noise, from 0.55 | 0.3 | Effect F1 | +.064 | +.224* |
| 0.15 | -.063 | +.138* | ||
| 0.05 | -.276* | +.003 | ||
| Logged action delayed with probability p | 0.25 | Effect 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.
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: what the insights are and how we use them
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}.
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.
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).
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.
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).