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Under review as a conference paper at ICLR 2027

How a World Model Forms: Separating World Knowledge from Behavioral Competence in Sokoban Transformers

Abstract

Does teaching a policy to represent its environment more accurately make it better at acting? We study this question in Sokoban Transformers that receive an initial board and move history, without updated observations. Eight training conditions vary supervision of state, action effects, and goal occupancy while sharing the same action targets and trajectory corpus. We measure what probes recover, which state distinctions guide decisions, and whether the policy solves. Action prediction alone yields accurate action-effect readouts and decisions that distinguish remote states, despite incomplete state reconstruction. Across three seeds, supervising all three components raises complete-state recovery from 0.208 to 0.955, while solving on held-out puzzles with optimal distances of 32–60 changes from 0.745 to 0.735. Supervision does help when policies must continue from supplied detour histories, but doubling training in both conditions reduces this advantage, leaving training efficiency as a plausible contributor. Together, these results show why complete-state recovery cannot stand in for behaviorally useful world knowledge. Its value must be tested through the decisions and continuations it is intended to support.

Primary area:
interpretability and explainable AI
Keywords:
world models, world knowledge, interpretability, representation probing, behavioral competence, sequential decision-making

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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

This paper investigates the relationship between recoverable world knowledge and behavioral competence in Transformer-based Sokoban agents. The authors train decoder-only Transformers to predict optimal actions from an initial board and action history, comparing eight training conditions in a 232^3 factorial design that varies auxiliary supervision for state, action effects, and goal occupancy. They evaluate world-knowledge representations using linear, nonlinear, and attention-pooling probes, and assess behavioral competence through optimal-action prediction, matched-state decisions, and puzzle-solving rollouts under different trajectory conditions. The main finding is that explicitly supervising world knowledge substantially improves state recoverability without consistently improving solving performance from original states. Meanwhile, action-only models can distinguish states requiring different optimal actions despite incomplete state recovery, and explicit supervision provides benefits in some continuation settings involving non-optimal action histories. The authors also conduct activation interventions to investigate the behavioral relevance of decodable state representations. Overall, the paper highlights a substantial gap between explicitly recoverable world-state representations and downstream decision-making performance.

Critical strengths

1. Comprehensive experimental design and carefully controlled behavioral evaluations.

The paper presents a systematic (2^3) factorial comparison of state, action-effect, and goal-occupancy supervision, while keeping optimal-action prediction as the shared primary objective. This design allows the authors to examine how different components of world-knowledge supervision affect representation recoverability and downstream solving, including their combinations and interactions. The evaluation is also notably thorough. In particular, the matched-pair experiments control for initial boards, local observations, immediate action effects, and several action-history cues while requiring different optimal actions, providing strong evidence that the policies distinguish states beyond these local cues. The supplied-history experiments further distinguish on-plan states, detours with on-plan box configurations, and off-plan box configurations, enabling more targeted comparisons of state tracking and recovery after non-optimal histories. Together with the multiple random seeds, probe controls, and supplementary intervention analyses, these experiments provide a carefully controlled investigation of the relationship between world knowledge and behavior, while acknowledging the limits of causal attribution.

2. An informative empirical characterization of the gap between world-state recoverability and behavioral competence.

The paper investigates an important question concerning whether more explicitly recoverable world knowledge necessarily leads to better decision-making. Its results reveal a substantial dissociation, i.e. directly supervising the state representation increases complete-state recovery rate but does not improve original-start solving on the hardest puzzles. At the same time, action-only models can make accurate state-sensitive decisions despite relatively poor complete-state recovery, while explicit knowledge supervision improves continuation after certain supplied detour histories. These findings demonstrate that the relationship between recoverable world-state information and behavioral performance depends on the evaluation setting, rather than following a simple monotonic relationship. Although related distinctions between representation quality and downstream performance have been explored in earlier world-model research, this paper provides a particularly controlled analysis using exact environment states, solver-defined optimal actions, and component-specific supervision. The resulting observations are valuable for understanding both the capabilities and limitations of representation-based evaluations of learned world models.

Critical weaknesses

1. Insufficient mechanistic understanding of the dissociation between world-state recoverability and behavioral competence.

The paper provides extensive evidence that world-state recoverability and behavioral competence do not necessarily improve together, but offers limited mechanistic insight into why this dissociation occurs. Although the probing experiments identify decodable representations of player and box positions, action effects, and goal occupancy, the paper does not investigate how the Transformer computes and updates this information from action histories, or how it uses such information to select optimal actions. In particular, it remains unclear whether the model reconstructs the current state from the action history at each prediction position, reuses intermediate state representations through a state-transition-like computation, or relies on alternative task-relevant representations. Nor does the paper identify the attention heads, MLPs, or computational pathways responsible for state tracking and optimal-action selection. This limitation is particularly important given the paper's own findings: action-only models make accurate state-sensitive decisions despite incomplete state recovery, while Appendix F.2 shows that removing state-probe directions can nearly eliminate state decodability without comparably impairing solving performance in the action-only and all-component models. These results suggest that the policies may rely on representations or computational pathways not adequately characterized by the measured linear state codes, making a mechanistic investigation especially important.

The causal interventions also remain limited in scope. Although Appendix F examines state-probe direction ablations and selective box-code replacements, these experiments do not establish whether the policy actually uses the decoded world-state representations to compute optimal actions. Since Sokoban is a deterministic Markov environment in which the optimal action depends only on the current complete state and fixed board layout, a more direct test would be to intervene on the model's internal representation and examine whether its predictions change consistently with a counterfactual board state. For example, jointly replacing representations of player and box positions, action effects, and goal occupancy with those corresponding to another valid state requiring a different optimal action could test whether the policy follows the counterfactual state's optimal action. The existing box-code interventions do not establish such full-state causal consistency, leaving unresolved whether the recoverable world knowledge mediates the policy's decisions or whether alternative internal computations support its behavior.

2. Insufficient isolation of the functional effects of world-knowledge supervision.

Although the paper demonstrates that explicit world-knowledge supervision substantially improves complete-state recovery without consistently improving original-start solving, the experimental comparisons do not fully isolate the effects of the supervised information from changes in optimization and training resources. The conditions share the same training data, model architecture, and update counts, but the auxiliary objectives introduce additional computation and gradients. Moreover, the reduced advantage of all-component supervision under longer training suggests that differences in training efficiency may contribute to the observed behavioral effects. Without more closely matched computational budgets and auxiliary-objective controls, it remains unclear whether the differences between action-only and explicitly supervised models arise specifically from the additional world-knowledge targets or from more general changes in multitask optimization. This limits the interpretation of how explicit knowledge supervision affects behavioral competence.

Questions for authors

Clarification Requests

1. Interpretation of state-direction ablation results.

Appendix F.2 shows that removing state-probe directions nearly eliminates state decodability while leaving solving performance largely unchanged in the action-only and all-component models, but produces a larger behavioral effect under latent prediction and state matching. How do the authors interpret these differences across training objectives? Could they reflect different internal representations or computational pathways, redundancy in state information, or limitations of the identified linear state codes? Clarifying what these interventions establish about the causal role of world-state representations would help interpret the central recoverability–competence dissociation.

2. Role of optimization and training budget.

The training conditions match architecture, data, and update counts but not auxiliary computation or gradient contributions, while longer training substantially reduces the advantage of all-component supervision on supplied-history continuation. How much of the observed behavioral difference do the authors attribute to explicit world-knowledge supervision, as opposed to changes in optimization dynamics or training efficiency?

Suggestions for Future Work

1. Mechanistic analysis of state tracking and optimal-action computation.

Could the authors investigate how the Transformer internally computes and uses world-state information, particularly in light of the dissociation between state decodability and solving performance? For example, it would be valuable to identify attention heads, MLP components, or computational pathways involved in tracking player and box positions, modeling action effects, and selecting optimal actions. An important question is whether the model reconstructs the current state by aggregating information from the full action history at each prediction position, reuses intermediate state representations through a state-transition-like computation, or employs more compressed task-relevant representations without explicitly reconstructing the full board. Comparing these mechanisms across action-only and explicitly supervised models could clarify whether similar behavioral competence emerges from different internal computations.

2. Counterfactual world-state interventions.

Since Sokoban has deterministic Markov dynamics, could the authors conduct interventions that replace the model's internal representation of the current board with that of another valid state requiring a different optimal action, and test whether its predictions become consistent with the counterfactual state's optimal policy? Beyond the existing box-code replacements, jointly manipulating player and box positions, action effects, and goal occupancy, while controlling for unintended changes to other representations, would provide a more direct test of whether the decoded world-state information causally determines action selection. Comparing counterfactual optimal-action accuracy and downstream solving under these interventions would help distinguish functional state representations from merely decodable information.

3. Representation redundancy, recovery, and robustness.

Given the limited behavioral effects of state-direction ablation in some models, could the authors examine whether task-relevant state information remains accessible through other residual-stream directions, token positions, or layers after intervention? Tracking component-specific probe accuracy and behavioral performance in subsequent layers could reveal whether state information is reconstructed or whether the policy relies on alternative representations. Comparing these effects across action-only and all-component models would also help determine whether explicit supervision improves the robustness of world-state representations to targeted perturbations.

4. Compute- and optimization-matched controls.

Could the authors introduce compute-matched action-only baselines and additional auxiliary-objective controls with comparable loss scales or gradient statistics to distinguish the specific effects of explicit world-knowledge supervision from generic multitask optimization and additional training resources?

5. Generalization across task complexity.

Could the authors examine whether the dissociation between state recoverability and behavioral competence persists as the Sokoban environment becomes more complex, for example with larger boards, more boxes, or longer planning horizons? This would help determine whether explicit state representations become more functionally important as state-tracking and planning demands increase.

2 comments
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Response to Reviewer pGTC (Part 1 of 2)

Part 1 of 2: the joint replacement and where the decision-relevant information is

Thank you for proposing the joint counterfactual replacement: it reveals a substantial but partial behavioural effect. In the all-component model, replacing the probe-defined code at every move position at block 8 (the supervised block) raises the rate of taking the donor's optimal action by 44 points, against 92 for the full residual swap and under 2 for random subspaces of the same rank. Its share of the full swap, 0.47 (seeds 0.46-0.48), is below the 0.5 that our criterion fixed in advance; the result shows neither full mediation nor necessity. A check added after these results removes four directions of the code that do not change the probes' outputs: the transfer is 36 points (share 0.39), still partial. After the edit the probes give the donor representation's predictions for the player and box cells at the current token in every case; this does not show that those predictions are correct. We also correct Appendix F.2, which you rightly questioned: freshly fitted probes still recover the state after its edit (complete state, action only: 0.167, unedited 0.208), so unchanged behaviour cannot show that the policy does not use state information.

Section numbers below refer to the revised PDF, which we have uploaded.

Weakness 1 and Suggestion 2, replacing the decoded state. On the paper's 7x7 two-box board (three seeds per objective, protocols fixed before the runs) we used 2,848 ordered pairs of histories that share the initial board, move count, player cell and local cues, differ in a remote box and have disjoint optimal actions. At each block from 8 to 16 we set the recipient's component in the span of the linear probes for player cell, box cells, goal occupancy and action effects (at most 64 directions) to the donor's, h' = h + UU^T(h_donor - h), where U is an orthonormal basis of the probe directions. Transfer is the rate at which the edited policy takes the donor's optimal action, minus that rate in the clean run. A code counts as carrying the decision-relevant state at a block only if, in every seed, its transfer is at least half that of the full residual swap and at least 10 points above the largest random subspace.

No block meets this in the absolute frame; in the action-only model the decoded code moves the decision by 6-8 points at blocks 8-11 (share at most 0.09; 2-3 points, the level of random subspaces, without the four directions). Replaced at the current token only, the code transfers within 0.5 points of random subspaces at blocks 8-14 in both models, and with same-state donors the current-token edit leaves the action unchanged in at least 95.9% of cases. With player-relative box directions in the action-only model (box positions are decoded more accurately in that frame), the result before the output block does not change. At the current token of block 16 the relative code met the criterion with the pre-specified code (60 points, share 0.68); without the four directions it transfers 0.2 points, like every code at the output block, so those transfers cannot be attributed to the decoded state alone, and without those directions no code meets the criterion at any block. No rollouts were run under the edit, so downstream solving under it is not measured.

Weakness 1 and Suggestion 1, where the decision-relevant information is. In full residual swaps on the same cases, swapping the current token alone first yields the donor's optimal action in at least half the cases at block 15, while swapping all other move positions still does so through block 14, in both models:

Positions swappedAction only, block 14block 15All-component, block 14block 15
Current token only22.4%71.0%33.9%78.7%
All move positions but the current one76.0%27.7%65.6%20.6%

At block 8, swapping only the last eight positions gives 31.9% for action only (all positions: 93.7%) and 63.0% with all-component supervision: supervision makes recent positions more informative. Restricting the current token's attention to the board and its last 15 moves lowers the optimal-action rate from 94-96% to 78-80% in action only, latent prediction and all-component supervision, so in every model the current token draws directly on positions more than 15 moves back. These interventions show that the decision depends on representations at older history positions; they do not distinguish aggregating the history at each prediction position from reusing intermediate state computed at earlier positions, two of the alternatives in your review. A residual swap moves state and plan alike, so it locates this information without separating the two; none of these analyses identifies heads or MLPs or explains the dissociation itself (Appendix N).

AuthorsOpenReview ↗

Response to Reviewer pGTC (Part 2 of 2)

Part 2 of 2: optimisation, budget, Appendix F.2 and the suggestions

Weakness 2 and Clarification 2, optimisation and budget. On the 7x7 two-box board supervision raised complete-state recovery (all-component: 0.208 to 0.955), but our controls do not separate every optimisation effect from the supervised information. The cost of state supervision reported in the submission was largely a loss-balance effect: at coefficient 0.1, where gradient statistics are close to action only, state supervision solves +4.9 percentage points (pp) [+2.5, +7.4] more 32-60 puzzles (optimal length 32-60 moves) than at 1.0 (all three seeds; a descriptive comparison). Our rule for an improvement, fixed after the reviews and before the new runs and applied unchanged to the submission's runs, needs every seed positive and a mean of at least +2 points. No tested coefficient (0.03-1.0), site (block 8, 12 or 16) or budget (1x, 2x and 4x the 51,360 updates) meets it, and a small gain is not excluded: with six seeds at 0.1 the difference from action only is +1.6 pp [-0.2, +3.4] for state and +1.2 pp [-0.4, +2.9] for all-component supervision (Sections 4.3 and 6, Appendix K). Part of the advantage after supplied detours may be training efficiency: its point estimates are smaller at 2x and 4x (three seeds, Appendix H.4).

After supplied detours, supervised minus action only, pp1x2x4x
All-component 1.0+4.7+0.7+0.6
State 0.1+2.6+1.0+1.5

With six seeds at 4x, all-component 1.0 is -0.2 pp [-2.0, +1.6], and +2.3 pp [+0.4, +4.2] on a second set of such histories, the development panel's (Appendix H.4).

Clarification 1, Appendix F.2. Its "after" column read the removed probe on its own removed directions, which gives near zero by construction. Complete-state recovery with freshly fitted probes, three seeds:

ObjectiveLinear, cleanLinear, afterMLP, cleanMLP, afterLinear, removed at every later block
Action only0.2080.1670.4220.3790.172
Latent prediction + state matching0.3170.2360.6190.5340.238
All-component0.9550.9130.9570.9320.913

The edit removes one linear code but not the state information, which fits your redundancy and linear-code alternatives; across objectives we can only describe the differences, with three seeds. After the edit, matched-neighborhood accuracy (both members optimal; pairs share the current neighborhood) is below the random-control range in every seed for latent prediction and all-component supervision, and within it for action only (revised Appendix F.2).

Suggestion 3. We tested this for the complete state only, not by token position: it stays recoverable after every later block's code is also removed (last column above), and supervision does not make behaviour more robust to the edit.

Suggestion 4. We did not match compute or gradients exactly. Besides coefficient 0.1 and action-only runs trained 2x and 4x as long (more compute than any supervised 1x run), we trained a control target of the same form: the state head at 0.1 tracking a different world, the real moves replayed under a fixed action permutation. It costs 32-60 solving, -5.7 pp [-8.3, -3.1] against action only (every seed), and the true-state target solves +7.2 pp [+4.7, +9.7] more: the outcome depends on the target, not only on adding an auxiliary loss. With one permutation at one site, this comparison does not isolate the information in the target from its optimisation effects, and its cost does not show that the true-state target helps (Appendix K).

Suggestion 5. At 51,360 updates, on 7x7 with three boxes recovery rises (0.047 to 0.921-0.944) and no supervised condition improves 32-60 solving, so the dissociation holds (state 1.0 is negative in every seed, mean -1.93 pp, under the 2 points a cost needs); on each two-box board from 8x8 to 11x11 at least two of the four supervised conditions improve it by the rule fixed in advance; at twice the budget the gain of all-component supervision at 0.1 persisted on 9x9 and was not shown to persist on 8x8 and 11x11, nor was that of state supervision at 0.1 on 8x8 and 9x9. We designed the 8x8, 10x10 and 11x11 boards and the budget controls after the 9x9 result was known and fixed their analysis before their runs. Lookahead difficulty, box density, prefix length and corpus change with the board, so we claim no trend or effect of board size and cannot say whether the benefit tracks planning demand (our comments to all reviewers; Appendices P and R).

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Paper summary

The paper discusses the knowledge and action performance link in models and, specifically, whether forcing the policy to learn specific environment information improves action performance. Specifically, whether adding explicit environment supervision to a policy that already performs well in its actions, results in improving its behaviour.

The world-model decomposition they adopt is: State: current player and box positions Action effects: the effect (push, walk or stay) for each of the four possible current action Goal occupancy: 0 (not covered) and 1 (covered) for each goal position. A position counts as correct only if both bits are correct.

and their design investigates which parts of the world-model, when supervised, improve the behaviour.

The policy sees only the moves and the initial board, and not the current board state, thus to get the state it has to apply the actions internally. The state knowledge, even though not explicitly trained for, is consequential (for example a box pushed into a corner can make the puzzle unsolvable many moves before failure becomes visible) and thus should be learnt at least partially. Detours are 50% of the trajectories and as they are longer, they make up approximately 80% of the supervised positions. The detour inputs push the policy to track the state, so it cannot just memorize a usual sequence of moves.

Finding 1: the action-only model performs well despite the complete state (player and box position right) being decodable from its activations by a linear probe with rate 0.208. Specifically, player-cell accuracy is 0.949, whereas both-box accuracy is 0.213. Joint goal-occupancy accuracy is 0.622. Stronger probes, e.g., MLP, almost double complete-state recovery (0.427).

Finding 2: all-component supervision (board + action effect + goal occupancy) makes the board almost perfectly decodable (recovery for action-only → all-component: 0.208 → 0.955), but it doesn’t detectably improve performance (hard-bin solving 0.745 → 0.735). Board state supervision alone hurts slightly, while training on action effect helps slightly.

Finding 3: the action-only policy uses information about distant boxes, even though probes can’t read the full board. The paper tests pairs that look similar (same starting board, move count, player position and nearby box, outcome of all four moves, last two moves, and push count) but still have different optimal moves, because a distant box is in a different place. The action-only policy picks a best move in both situations 89.2% of the time, and all-component supervision raises this to 93.1%.

Finding 4: the all-component supervised model does better at continuing from a supplied detour history that pushed boxes off every shortest path (optimal solution). Performance increases 0.814 action-only vs. 0.876 all-component. However, that advantage shrinks a lot with longer training.

Finding 5: erasing the decodable complete state in one layer doesn’t hurt performance, so the model isn’t relying on that decodable information in that layer.

Critical strengths
  1. The paper connects two directions, the learned environment models (trained to predict what happens next and used for control) and the sequence models (trained purely on move sequences) and investigates how the supervision of world knowledge affects performance. Auxiliary losses that predict the environment are widely used and probe decodability is commonly used as evidence that the model has a world-model. So the paper is well-motivated.

  2. Sokoban is a good game to explore this question, because specific boxes location can result in dead game positions, so state recovery is motivated.

  3. Good design. i) matched conditions on action-only and all other types of supervision with the inclusion of auxiliary targets ii) Use of a variety of decoding probes: linear, MLP, attention pooling. Random-network controls test for what the probe can reconstruct itself iii) 3 seeds per condition, with seed variation reported separately from group-level bootstrap intervals.

  4. Behavioural tests of knowledge beyond solving, e.g., detour continuation.

  5. Authors are openly stating results that weaken their positive findings, e.g., in detour continuation experiment, training for double the time shrinks the continuation gap (between full-state and action-only supervision) from 4.7 to 0.7.

Critical weaknesses
  1. The authors acknowledge in the Limitations that matching updates does not match the auxiliary computation or gradients but the main interpretation depends on exactly this. State supervision alone lowers 32–60-step solving relative to action-only in every seed (Table 15) and all-component supervision doesn’t improve it. These results cannot distinguish the conclusion of the paper that state information does not help the policy from a large auxiliary gradient interfering with the action objective. The effect of state supervision should be explored, i.e., sweep for different smaller values for the state supervision coefficients across all three seeds.

  2. My understanding is that the supervision site is also fixed (full-state supervision is applied with a linear head on block 8 outputs). The action-only model’s full-state information peaks later (according to Table 5 around layer 12) so supervising at block 8 forces the computation earlier. So, could attaching a strong full-state supervision at block 8 be the reason why full-state supervision does not improve performance? A variation of the supervision site to later layers (block 12 or final) should be done.

  3. No analyses regarding how the decodability, e.g., of boxes changes based on how relevant they are. Specifically, can it be that the decision-making only requires the “relevant” part of the board and not the full state, so, the model encodes what is sufficient for the task? To explore this, I suggest the following analyses: i) Take the “relevant” boxes, as these are already defined in the paper (i.e., if changing its position would change the best move) and compare decodability for “relevant” vs “irrelevant” boxes ii) Check if box’s decodability changes with the player moving, e.g., improving as the player approaches it iii) Explore if box positions are encoded relative to the player instead of absolute grid cells.

  4. Balogh, and Jelasity (ICLR 2026) is a very close prior work in chess that is not cited. Their results also highlight that decodable world-state information does not necessarily affect model behaviour. It should be cited and the current work’s contribution should be positioned relative to that work.

  5. A lot of analyses are in the Appendices. It would be helpful to bring some of this into the main text, is space allows.

Questions for authors
  1. In Section 5 the authors state that the action-only performance (0.745) vs. full state supervision performance (0.735) measurements use different populations and that their difference is not a numerical knowledge deficit. What does this mean exactly, and why do they use different populations? Can’t they be tested in the same population?

  2. Please see Weaknesses.

2 comments
AuthorsOpenReview ↗

Response to Reviewer EZtm (Part 1 of 2)

Part 1 of 2: loss balance, supervision site and training budget

You were right about loss balance, and it changes our interpretation of the original cost. On the paper's 7x7 two-box board, lowering the state-loss coefficient from 1.0 to 0.1 improves 32-60 solving by +4.9 percentage points (pp) [+2.5, +7.4], in every seed (a descriptive comparison), while complete-state recovery stays high (0.958 at 1.0; 0.947 at 0.1 over six seeds). Across six seeds, state supervision at 0.1 differs from action only by +1.6 pp [-0.2, +3.4]: a two-point benefit remains possible; we claim no equivalence. Below we report the coefficient, site and budget controls, then the relevance and reference-frame analyses (Part 2).

Section numbers below refer to the revised PDF, which we have uploaded.

W1, "a large auxiliary gradient interfering with the action objective". Besides the paper's 1.0, we trained state supervision at coefficients 0.3, 0.1 and 0.03 and all-component supervision at 1/3 and 0.1 (block 8; three seeds, six at 0.1). At 1.0 every update after warm-up of the state runs was clipped (median pre-clip norm 6.6-6.9, against 0.8-1.4 for action only), and at update 1,202 the auxiliary gradient norm was on average 7.3 times the action gradient norm; at 0.1 norms and clipping are close to the action-only range and that ratio is at most 0.76 as a seed mean. By our rule, fixed after the reviews and before the new runs and applied unchanged to the submission's runs, a row improves on action only if every seed is positive and the mean at least +2 points on 32-60 puzzles, and costs in the reverse case; otherwise the outcome is "neither" (the paper's "no consistent change"), whatever the signs of the seeds. Comparisons between coefficients or sites are descriptive and were added after the coefficient-1.0 results were known.

Head (block 8, 1x unless stated)Recovery32-60 minus action only, ppOutcome
State 1.0 (paper)0.958-3.5 (seeds -5.6, -1.2, -3.6)costs
All-component 1.0 (paper)0.955-1.1 [-3.5, +1.5]neither
State 0.1, six seeds0.947+1.6 [-0.2, +3.4]neither
All-component 0.1, six seeds0.951+1.2 [-0.4, +2.9]neither
State 0.1, block 120.971-1.5 [-4.1, +1.1]neither
State 0.1, block 160.979-4.2 [-6.8, -1.5]costs
State 0.1, 2x0.964-2.0 [-4.1, +0.2]neither
State 0.1, 4x0.969+0.2 [-2.0, +2.4]neither

Three seeds unless stated; 95% intervals over structural groups, conditional on seeds; complete-state linear recovery in absolute cells (action only: 0.208). 1x is 51,360 updates; 2x and 4x are compared with action only trained as long. State 0.3 and 0.03, all-component 1/3, and all-component 0.1 at 2x and 4x (Appendix H.4) are also "neither".

What remains open. No tested coefficient, site or budget meets the rule for a consistent improvement, but at 0.1 a small gain is not excluded. After a supplied detour history (your Finding 4), supervision at 0.1 exceeds action only by +2.8 pp [+0.5, +5.1] for state and +3.3 pp [+1.6, +5.2] for all-component supervision (six seeds, 1x; the point estimates are smaller at 2x and 4x, Appendix H.4). Similar gradient statistics and action-only runs trained two and four times as long are not an exact match of gradients or compute. On a new 9x9 board the coefficient-1.0 runs were also clipped at every update after warm-up, yet supervision improves 32-60 solving there at 51,360 updates (at twice the budget the gain persists for all-component supervision at 0.1 and was not shown to persist for state supervision at 0.1), so these runs do not tell us what role clipping plays (our comments to all reviewers).

W2, "could attaching a strong full-state supervision at block 8 be the reason". Not in the tested range: a later head raises recovery but not solving, and block 8 is the least costly site. We put the state head on block 12 and on the last block (16) and tested both coefficients at each site. At 1.0 the later heads cost 32-60 solving, -9.2 pp [-12.0, -6.4] at block 12 and -23.1 pp [-26.3, -19.9] at block 16; at 0.1 they solve 7.7 and 18.9 points more than at 1.0, but 2.9 and 5.7 points less than the block-8 head, in every seed. Supervision at block 8 also does not make the decision-relevant information reach the current token earlier by our measure: swapping the current token's residual stream with that of a paired history that needs a different move (a full residual swap) first yields the donor's optimal action in at least half the cases at block 15, with all-component supervision as with action only (at block 14: 33.9% and 22.4%; Appendix N).

Section 6 now states the loss-balance result and Section 4.3 the rule. Appendix K gives the coefficient and site runs with their gradient statistics, and Appendix H.4 the budget series.

AuthorsOpenReview ↗

Response to Reviewer EZtm (Part 2 of 2)

Part 2 of 2: which boxes are decoded, prior work and the two populations

W3, "the model encodes what is sufficient for the task". Partly: in the action-only model, box positions are decoded more accurately in player-relative coordinates and better as the player approaches a box, but decoding is not limited to the box that decides the move. Values are for action only; we ran the three analyses on all nine conditions, three seeds each.

(i) On cue-matched pairs the probe scores the true cell of a box that decides the move above its cell in the paired state in 81.0% of cases, against 78.0% for a box that does not change the optimal move (chance: 50%; both unadjusted). Reweighting the irrelevant boxes to the relevant boxes' mix of player distance and moves since the box last moved gives a difference of +2.4 pp [+1.3, +3.4], and +3.0 pp with an MLP probe.

(ii) Decoding of a moved box improves as the player approaches it: the MLP probe decodes it at 81.3% at player-box distance 1-2 against 30.0% at 5 or more, and decoding 1-2 moves before its next push exceeds decoding 9 or more moves before it by 15-16 points (MLP) and 4.5-7.7 points (linear). All-component supervision stays at 96-98% throughout.

(iii) A linear probe for box offsets relative to the player recovers both boxes at 56.1%, against 21.3% in absolute cells, 33-36 points more in every seed (55.7% with the decoded rather than the true player cell). For all-component supervision the absolute frame is better (96.8% against 69.6%); with a linear probe, in every condition and seed the better frame follows the supervision target. Section 5 now reports both frames (Appendix M).

W4, Balogh & Jelasity (ICLR 2026). Thank you; we were not aware of it, and Section 7 now cites it. They verify chess sequence models with adversarial move sequences and infer from indirect evidence that "the extracted board states have no causal role in next token prediction in most of the models" (their abstract). Their variants trained with a joint board-state probe raise probe accuracy with a negligible effect on soundness (legal moves under attack), a pattern close to ours on the 7x7 boards. Our study differs in what its controls separate: supervision of three environment components with action targets, corpus and updates held fixed; task success rather than move legality, from the original start and when continuing supplied histories; and tests across boards and training budgets.

W5, main text. Section 5 now gives both frames and the recovery on each policy's own evaluation rollouts (Q1), Section 6 the coefficient and site results with the results on the other boards beside them, and Section 4.3 the rule; a guide at the start of the appendix says where each analysis is.

Q1, "different populations". The sentence meant only that the probe numbers (0.208, 0.955) come from the probe set and the solve rates from the evaluation panel, so one should not be subtracted from the other; the two solve rates (0.745, 0.735) are on the same 500 puzzles and differ by -1.1 pp [-3.5, +1.5]. We also measured recovery on each policy's own evaluation rollouts, pooled over the three distance bins: 0.212 for action only and 0.924 for all-component supervision (three seeds). Solved 32-60 episodes decode better than failed ones in both (0.266 against 0.136, and 0.998 against 0.730), a correlation within each policy's rollouts. Section 5 now states the contrast this way (Appendix F).

Finding 5 of your summary. It follows our Appendix F.2, which read the removed probe on its own removed directions. The revision corrects it: freshly fitted probes still recover the state after the edit (0.167 for action only, 0.208 unedited), so unchanged behaviour cannot show that the policy does not use state information.

Reviewer_m9mJOpenReview ↗
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Paper summary

The paper studies 50M-parameter transformer networks trained on the 7x7 grid size version of the game of Sokoban. The networks are trained on initial board and move history sequences to predict the next move. The authors train probes on the residual stream to compute three metrics: 1) state reconstruction, 2) effect of each action, and 3) goal occupancy. The authors also study the effects of supervising for these metrics during training. They find that with additional supervision using these metrics, the trained networks do well on these metrics but that doesn't improve the held out solve rate of the networks.

Critical strengths

None

Critical weaknesses
  • It's not clear to me and written in the paper when the specific training strategy was adopted as compared to training the network with RL, as is standard in the literature for such game-playing networks. The main networks analyzed also seem undertrained given more training improves performance. There is no reported performance over training step to confirm this in the paper. The paper also uses 7x7 grid size with maximum two boxes in which case the game becomes trivial and doesn't require any planning aspects.
  • The paper doesn't add anything novel. It check whether the network trained to predict the action only also computes auxiliary metrics that could be helpful for performance and find that the network doesn't. The paper then trains network by supervising with these metrics and finds that those metrics improve but not the solve rate of the model which seems like a trivial result. This result has no relevance outside the specific setup, since the setup itself is not a common way to train game-playing networks so the result is very specific to the particular setup and the game of Sokoban.
  • The paper is also written badly and is very terse to understand.
    • Nowhere in the main text are the supervision loss for various components they add is properly defined.
    • The paper uses terms like physical context, frozen panel, handover, numerical knowledge deficit, etc. that are either defined nowhere and are not standard or not defined before they are used in the main text.
    • Training of the probe itself is not clearly written in the main text. Information like where is the activations used for the probe collected from, the exact target for the probe, etc. needs to be clearly written in the main text.
Questions for authors

How is goal-occupancy supervision done? I see that two logits are computed for the two goals, but how is the ordering of the goal itself decided given that goals can be on random cells in a board position? Are you using some permutation invariant way to represent the goal state? This detail should be clearly written in the paper.

2 comments
AuthorsOpenReview ↗

Response to Reviewer m9mJ (Part 1 of 2)

Part 1 of 2: solver labels, training amount, task difficulty and what is new

We train on solver-labelled trajectories so that every condition learns its actions from the same data and targets and only the auxiliary supervision varies. Our question is what sequence policies learn from such move histories and whether explicitly teaching them environment components improves their behaviour. We added training at four times the updates, true-state planner baselines (the best depth-4 planner solves 12.4% of the puzzles with 32-60 optimal moves, the action-only policy 74.5%) and new boards, and the main text now defines the losses, probes and terms.

Section numbers below refer to the revised PDF, which we have uploaded.

"compared to training the network with RL". On-policy RL would let each condition visit its own states and mix the effect of supervision with a difference in data. Training on solver actions follows Lehnert et al. (2024), who train Transformers on optimal plans, with or without A* traces, for 7x7 Sokoban. Our PPO agent solved none of the 500 32-60 puzzles in any of three seeds (action only: 74.5%). As fixed before the runs, this is a budget-limited negative result: it does not show whether the dissociation (supervision raising state recovery without consistently improving 32-60 solving) depends on supervised action targets, and a different reward, curriculum or budget could change the outcome (Appendix Q).

"seem undertrained"; "no reported performance over training step". The submission's Figure 6(b) (Figure 5(b) in the revision) plots solving and 8-step optimal-path retention at all 28 checkpoints of seed 1, within 51,360 updates. You were right that the policies are not converged, so besides twice the updates (2x) we trained with four times (4x, 205,440 updates):

32-60 solving1x (51,360)2x4x
Action only74.5%81.9%82.3%
All-component supervision73.5%79.5%81.6%
Difference, percentage points (pp)-1.1-2.4-0.7 [-2.4, +0.9]

Three seeds at 1x and 2x, six at 4x. By our rule, fixed after the reviews and before the new runs and applied unchanged to the submission's runs, a difference from action only is an improvement if every seed is positive and the mean at least +2 points, and a cost if every seed is negative and the mean at most -2. At 2x every seed is negative, a cost, and on a second held-out panel (Appendix L) the 4x difference is a cost too, -4.1 pp [-5.9, -2.3]. A larger budget could still move the difference either way; we claim no asymptote (Appendix H.4).

"the game becomes trivial and doesn't require any planning aspects". These puzzles cannot be solved by looking a few moves ahead. We gave planners the exact engine and the true current state and let them search up to 16 moves ahead under the same 64-action cap: the best depth-4 planner solves 12.4% of the 32-60 puzzles, and none reaches the action-only policy's 74.5% even at depth 16 (these planners are baselines; the training labels come from an exact solver). On optimal paths 96.7% of states have a unique optimal action, and 95.3% of the policies' 32-60 failures are irreversible dead ends (Appendices O and D.2). At 51,360 updates no supervised condition improves 32-60 solving with three boxes on 7x7 (depth-4 planner: 7.0%), while on each two-box board from 8x8 to 11x11 (planner: 34.8% to 77.2%) at least two of the four supervised conditions do (our comments to all reviewers; Appendices P and R).

"doesn't add anything novel". Whether a model should be taught an explicit world model is a central question: model-based agents plan with learned models (Ha & Schmidhuber, 2018), and sequence models trained only on moves form board-state representations (Li et al., 2023; Karvonen, 2024). Studies that add explicit state information in training report benefits in particular settings: with little chess data (Toshniwal et al., 2022) and for RL post-training on a cube task ("Better World Models Can Lead to Better Post-Training Performance", arXiv:2512.03400); Balogh & Jelasity (2026) find higher probe accuracy with nearly unchanged move soundness. Our contribution is a controlled test of when such supervision improves the behaviour of a policy that already acts well: the action targets, corpus and number of updates are held fixed, so a change in solving is attributable to the supervision; each component (state, action effects, goal occupancy) is supervised separately; and each result is followed across coefficients, sites, budgets and boards, from the original start and after supplied histories. Supervision raised state recoverability on every board, but solving improved only on some boards at 51,360 updates and most of these gains were not shown to persist with longer training. Making the world state recoverable is therefore not the same as making it useful to the policy, and world-model supervision has to be judged by the behaviour it is meant to improve.

AuthorsOpenReview ↗

Response to Reviewer m9mJ (Part 2 of 2)

Part 2 of 2: what the policy knows, relevance, definitions and the goal order

"find that the network doesn't". The action-only policy does form part of this knowledge (Section 5; Appendix M for the frame):

Action-only policy, paper's 7x7 board
Action effects (walk, push or stay for each move), linear probe98.1%
Optimal move in both members of cue-matched pairs that differ in a remote box and need different moves89.2%
Both boxes, decoded in player-relative coordinates (in absolute cells: 21.3%)56.1%

What the tested linear probe recovers at only 20.8% of positions is the complete state in absolute cells.

"seems like a trivial result". This is not the outcome the field expects: auxiliary environment-prediction losses (for example DeepMDP and SPR, cited in Appendix J) are used because they are expected to help. In our runs the outcome is not uniform. On the paper's 7x7 board, supervising all three components raises complete-state recovery from 0.208 to 0.955 without consistently improving 32-60 solving: no tested loss coefficient (0.03 to 1.0) meets the improvement rule of Part 1, but a small gain is not excluded (six seeds at 0.1: +1.6 pp [-0.2, +3.4] for state and +1.2 pp [-0.4, +2.9] for all-component supervision). After a supplied detour history that moved boxes off every shortest path, all-component supervision at 1.0 does help, +4.7 pp at 51,360 updates, falling to -0.2 pp with six seeds at 4x (+2.3 pp [+0.4, +4.2] on a second set of such histories, the development panel's; Appendix H.4), and on the larger two-box boards at least two of the four supervised conditions improve original-start solving at 51,360 updates (Part 1).

"no relevance outside the specific setup". Next-move prediction from move histories is the setting in which Othello and chess Transformers are probed for world models, so our result bears on that probe evidence. The evidence is for Sokoban and for supervised policies, and Section 2 says so.

"properly defined": losses, probes and terms. Section 4.1 defines the three losses, each a linear head on the block-8 residual stream with coefficient 1: the player cross-entropy over the 25 interior cells plus 25 summed box binary cross-entropies (state), four three-way cross-entropies (action effects) and two binary cross-entropies (goal occupancy). Sections 2 and 4.2 describe the probes: they read the embeddings and each of the 16 block outputs at the token aligned with the current state (the last move, or the history marker before any move), are fitted on 32,000 trajectories from 2,000 layouts, and target the player cell, the two box cells, the effect of each move and the two goal bits. The main text now defines "physical context" (Section 2), the "frozen panel", now the evaluation panel (Section 4.3), and "handover" (Section 6), and replaces the sentence with "numerical knowledge deficit" (Section 5). Together with the new results, the main text now follows five steps (Sections 1, 2-4, 5, 6, 7-9): the question, the setup, what forms without supervision, what supervision changes, and related work, limits and conclusion.

"how is the ordering of the goal itself decided". The order is canonical: bit i refers to the i-th goal cell in row-major order, in the corpus, the head and the probe. The goal cells are part of the initial board and never move, so no permutation-invariant encoding is needed; a position counts as correct only if both bits are right (Sections 4.1 and 4.2).

Comments on the paper

3 comments
AuthorsOpenReview ↗

Summary of our response

Summary of our response

Thank you for the reviews, and we apologise for the late response. To address your concerns we trained and analysed 212 further runs: controls of the loss coefficient, supervision site, training budget and auxiliary target on the paper's board, five further boards up to 11x11, a PPO agent, and 63 runs at twice and four times the training budget; we also added planner baselines and new analyses of the existing checkpoints. Completing and validating these experiments with limited access to shared GPUs took longer than expected. They changed three conclusions of the submission:

  1. Optimisation. On the paper's 7x7 two-box board, the cost of state supervision reported in the submission was largely a loss-balance effect, as EZtm suggested: lowering the coefficient from 1.0 to 0.1 raises solving of 32-60 puzzles (32-60 optimal moves, the hardest bin) by +4.9 percentage points (pp) [+2.5, +7.4] (a descriptive comparison). Whether supervision then helps remains uncertain: over six seeds, state supervision at 0.1 differs from action only by +1.6 pp [-0.2, +3.4], short of our rule for an improvement (every seed positive, mean at least +2 points; fixed after the reviews, before the new runs), and a 2-point benefit is not excluded.
  2. Scope. Supervision does improve solving on other boards, so we do not claim that it never helps: at 51,360 updates, at least two of four supervised conditions improve 32-60 solving on each two-box board from 8x8 to 11x11. When the gains at coefficient 0.1 on 8x8, 9x9 and 11x11 were retested at twice the budget, that of all-component supervision on 9x9 persisted and the others (state supervision on 8x8 and 9x9, all-component supervision on 8x8 and 11x11) were not shown to persist; at four times the budget, the 9x9 gain of all-component supervision was not shown to persist. The 8x8, 10x10 and 11x11 boards and the budget controls were designed after the first 9x9 result was known (our two comments on the board-size series and the longer budgets).
  3. Causal reading. Appendix F.2 was wrong, and pGTC was right to question it: freshly fitted probes still recover the state after its edit (action only: 0.167, unedited 0.208), so unchanged behaviour cannot show that the policy does not use state information. The joint replacement of the probe-defined state code that pGTC proposed moves the all-component model's decision by 44 points, against 92 for a full residual swap, and by 36 once four directions that do not change the probes' outputs are removed from the code (a check added after the results): a partial effect, below the criterion we fixed in advance, which shows neither full mediation nor necessity.

Contribution. We test when explicit supervision of world knowledge improves behaviour under controlled action learning: component by component, with the action targets, corpus and number of updates held fixed; from the original start and when continuing supplied histories; and across training budgets and boards. On every board we evaluated, supervising the state raised state recoverability, whereas a behavioural benefit was observed only in some tests and, at 51,360 updates, on some boards.

Appendices K-R of the revised paper are new.

We have uploaded the revised PDF. Section numbers in our replies refer to that version.

Further experiments are in progress: the last 11x11 cell at four times the budget has finished training and is being analysed, and three more are being set up: an extension of the PPO comparison to a larger training budget, further control targets that separate the information in the supervision target from its optimisation effects, and a component-level analysis of which attention heads and MLPs carry the decision-relevant state. We will report them here.

AuthorsOpenReview ↗

Follow-up comment to all reviewers: the board-size series

Follow-up comment to all reviewers: the board-size series

On each two-box board from 8x8 to 11x11, at least two of the four supervised conditions improve solving of 32-60 puzzles at 51,360 updates. Whether these gains persist with longer training is the subject of our update comment.

We train action only and four supervised conditions (state or all-component supervision at coefficient 1.0 or 0.1; block 8, three seeds), each board with its own corpus and evaluation panel. A condition improves 32-60 solving if every seed is above action only and the mean at least 2 points above, and costs in the reverse case. We designed the 8x8, 10x10 and 11x11 boards after the 9x9 result was known and fixed their analysis before their runs, so only they test whether the benefit depends on the board.

Board, two boxesRecovery, action only to supervisedAction only, 32-60State 1.0State 0.1All-comp. 1.0All-comp. 0.1ImproveMean of the four, m
7x70.208 to 0.948-0.95874.53%-3.47+1.47-1.07+1.330 of 4 (state 1.0 costs)-0.43 (no interval)
8x80.092 to 0.935-0.94278.67%+3.33+3.67+4.00+3.474 of 4+3.62 [+1.48, +5.87]
9x90.049 to 0.920-0.93582.60%+2.27+3.40+4.47+3.604 of 4+3.43 [+1.72, +5.18]
10x100.026 to 0.931-0.93987.80%+2.13+1.87+2.33+4.272 of 4+2.65 [+1.08, +4.25]
11x110.017 to 0.932-0.95289.33%+0.73+2.27+2.47+3.602 of 4+2.27 [+1.07, +3.58]

Supervised minus action only on 32-60 puzzles, in percentage points (pp), at 51,360 updates; 95% intervals conditional on seeds. Recovery: complete state, linear probe, absolute cells. The table is descriptive, and m is not monotone non-decreasing over the boards.

By the rule fixed in advance for each board, the dissociation (a recovery gain without an improvement in 32-60 solving) does not hold on 8x8, 10x10 and 11x11 at 51,360 updates. Two means above 2 points are not improvements, since one seed is negative: state 0.1 on 11x11 and all-component 1.0 on 10x10 (+4.4, +3.0, -0.4). The one comparison between boards fixed in advance, m on 11x11 minus m on 9x9 at 51,360 updates, is -1.17 pp [-3.38, +0.92], so the benefit on 11x11 is not shown to be larger than on 9x9.

Limits:

  • This comment covers 51,360 updates; the runs at twice and four times the budget are in our update comment.
  • No claim beyond 11x11, no trend and no claim that board size causes a difference: lookahead difficulty, box density, prefix length, corpus size and passes over it, the budget relative to the board and the action-only baseline all change with it.
  • Three seeds, so no equivalence is inferred; the four contrasts of a board share its three action-only runs. Recovery is not compared across boards. 0 of 4 does not mean that the effect is zero.
AuthorsOpenReview ↗

Update to all reviewers: the runs at twice and four times the budget

Update to all reviewers: the runs at twice and four times the budget

On 9x9, all-component supervision at 0.1 still improves at twice the budget: its benefit persists there; at four times the budget it was not shown to persist. The other benefits at 51,360 updates retested so far were not shown to persist where a reading is made: state supervision at 0.1 on 8x8 and 9x9 (twice and four times the budget), and all-component supervision at 0.1 on 8x8 (twice and four times) and 11x11 (twice). The 11x11 all-component cell at four times the budget is still training.

As in our comment on the board-size series, a condition "improves" at a budget if every seed is above action only and the mean difference on 32-60 puzzles is at least +2 points; short of this (and of the mirror rule for a cost) the label is "no consistent change", whatever the signs of the seeds. A benefit at 51,360 updates "persists" at a longer budget if the condition still improves there; if it shows no consistent change, it is "not shown to persist", which does not show that it is absent. A reading is made only where action only solves between 10% and 95% of the 32-60 puzzles at that budget; otherwise the board is "not informative" there (n.i.): no reading is made, whatever the differences. These readings were fixed before the runs.

Board, condition51,360 updates102,720 updates205,440 updates
8x8, state 0.1+3.67-1.40 [-3.20, +0.40] (0.0, -0.8, -3.4)-0.07 [-1.80, +1.73] (+0.6, -0.8, 0.0)
8x8, all-component 0.1+3.47+0.67 [-1.20, +2.53] (+1.4, +2.0, -1.4)+0.40 [-1.20, +2.00] (+1.4, -0.8, +0.6)
9x9, state 0.1+3.40+0.73 [-1.00, +2.47] (+1.2, -1.0, +2.0)-1.00 [-2.47, +0.47] (+0.8, -3.4, -0.4)
9x9, all-component 0.1+3.60+2.33 [+0.67, +4.07] (+3.0, +1.2, +2.8)-0.47 [-1.67, +0.80] (+0.2, -0.8, -0.8)
10x10, state 0.1+1.87+0.60 [-0.67, +1.93] (-0.2, +0.6, +1.4) n.i.+0.60 [-0.20, +1.47] (+0.2, +0.8, +0.8) n.i.
10x10, all-component 0.1+4.27+0.73 [-0.53, +2.00] (+0.6, -0.2, +1.8) n.i.+0.73 [-0.20, +1.73] (-0.4, +0.4, +2.2) n.i.
11x11, state 0.1+2.27+1.47 [+0.33, +2.60] (+0.2, +2.2, +2.0)+0.07 [-0.80, +1.00] (+0.2, +0.4, -0.4) n.i.
11x11, all-component 0.1+3.60+0.87 [-0.33, +2.00] (-0.8, +2.2, +1.2)under way

Supervised minus action only on 32-60 puzzles in percentage points, both trained equally long, three seeds per cell: the mean at 51,360 updates, and at the longer budgets the mean [95% interval] (seeds 1, 2, 3). Bold: the condition improves; every other number is "no consistent change"; n.i. as defined above. The table of budgets in Appendix R adds the solve rates, the intervals and seeds at 51,360 updates and the t intervals over seeds, which at the longer budgets include zero in every cell.

All-component supervision at 0.1 improves at 51,360 updates on all four boards; on 9x9 at twice the budget its t interval over seeds, [-0.12, +4.78], includes zero.

On 10x10 at twice and four times the budget and on 11x11 at four times, action only solves more than 95% of the 32-60 puzzles (95.33%, 97.40% and 97.73%): these boards are not informative there, and no reading of persistence is made for either condition.

The limits stated in our comment on the series apply: these runs were designed after the results of the series were known (for them hypothesis-generating; the 9x9 state row at twice the budget is the series' own control, designed after the 9x9 result at 51,360 updates); three seeds, so no equivalence is inferred; no trend in board size; no claim about why a benefit does or does not persist. Where a reading is made, action only solves 88.93% to 94.73% at the longer budget; the highest are close to the 95% limit. Table 2 and Appendices P and R carry these results.

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

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