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Withdrawn from ICLR 2027

Building State v.s. Using State: Representation and Utilization in Multi-Step Tasks

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Multi-step tasks require a model to do two things well: maintain the state needed for future decisions and use that state when producing actions or answers. We study these problems separately in language models and partially observed reinforcement learning agents. In a controlled maze, map-related information becomes linearly decodable before strong task performance, and matched belief swaps show that this internal map content affects behavior. Yet a representation-targeted auxiliary that raises decodability leaves tight-horizon success essentially unchanged (0.093 to 0.094), while policy-level supervision raises it to 0.497. Craftax shows the same asymmetry at larger scale: recurrent state is necessary for strong performance and contains hidden spatial information, but substantially increasing position decodability does not improve reward. We then ask whether this diagnosis can be used to improve the models. It can. After informative state has formed, interventions aimed at the state-to-behavior mapping improve downstream performance in both domains. Post-convergence efficiency pressure raises Craftax score from 15.09 to 16.56, and latent-guided distillation raises low-data answer accuracy from 0.86 to 0.94 in the language setting. These results suggest that multi-step learning can be limited by state utilization even after useful internal state has already been learned.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
internal state representations, world models, representation learning, state utilization, multi-step reasoning, reinforcement learning, language models, partial observability

Reviews

Among:
Shape:
1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_LwFHOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
2
Soundness
2
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Paper summary

The authors claim that in sequential decision-making, models must both maintain a useful internal state and learn to predict behavior from that state. They find that a useful state can become available before behavior extracts its full value. This motivates intervention after the state is formed to improve downstream performance. They validate across a maze task, Craftax, and language.

Critical strengths
  • I appreciate multi-setting validation of the experimental findings.
Critical weaknesses
  • One weakness is that the scope is perhaps a bit small. The main conclusion is a validation that once state is formed, we should remove pressure for learning the internal state and focus optimization on fitting behavior from that state. This claim is a bit unsatisfying in that it may not provide much new insight to the community, and it’s not clear how this rule can be packaged well into an algorithm, even though the paper claims it is “operationalized”.
  • Another weakness is that the experiments aren’t thorough/promising enough. I would appreciate seeing better validation of this insight since it doesn’t seem like the improvements in Craftax are particularly significant.
  • Due to these weaknesses, I don’t think this paper is fully complete and for now has a bit of a narrow claim - with more algorithmic work and stronger empiricism, there could be a better submission.

Writing nitpicks:

  • What is a “matched belief swap”? It would be good to keep the abstract more high-level. Again, I see “Yet a representation-targeted auxiliary that raises decodability leaves tight-horizon success essentially unchanged” - I can use context clues to assume that training to explicitly decode state doesn’t improve performance? Maybe it’d be good to have examples of these “interventions” if they’re core to the paper’s key insights.
Questions for authors
  • Isn’t this addressable by classic loss scheduling? We can just weight down representation supervision when it’s converged and begin weighting up the behavioral loss. When attacking multi-objective systems and weighted losses, many folks can downweight based on the staleness of the objective (i.e. how converged it has become).
  • Also, what about cases where it’s unclear what internal state we are forming (i.e. no ground truth)? How do we supervise this or even gauge the convergence?
Reviewer_EXwDOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper investigates two distinguishable components of multi-step tasks: forming useful internal states and effectively using those states to produce behavior. It finds that decodable state information can emerge before reliable behavior, and that improvements in representation metrics do not necessarily translate into corresponding performance gains. Based on this observation, the authors propose a diagnosis-driven training approach: once useful state has formed, training can focus on improving the mapping from state to actions or answers. Through experiments on mazes, Craftax, and language-model state tracking, the authors examine this distinction and report performance gains from efficiency fine-tuning and latent-state-guided readouts, supporting its potential value for interpreting model behavior and selecting training objectives.

Critical strengths
  1. The perspective is insightful, and the decomposition has explanatory value. Distinguishing state formation from state utilization makes “accessible internal information but poor behavior” a problem that can be studied in its own right, rather than attributing every failure to insufficient memory or representation. This provides a valuable framework for interpreting the gap between a model’s internal information and its actual performance. (Sections 1 and 2)

  2. The central phenomenon is supported across tasks and through multiple approaches. The experiments cover controlled mazes, partially observed Craftax, and language-model counter tasks, combining training dynamics, probes, state interventions, and comparisons of training objectives. In particular, same-map and different-map belief swaps provide evidence beyond correlation alone (lines 207–213). These complementary results strengthen the limited conclusion that state accessibility and behavioral performance need not improve together. (Sections 3 and 4)

  3. The central conclusion is intuitive and can inform the choice of training objectives. The observation that forming useful state does not imply using it effectively, and that better representation metrics need not improve behavior, is clear and empirically grounded. It encourages researchers to examine the state-to-action or state-to-answer mapping rather than focusing exclusively on further representation learning. The reported gains from RL fine-tuning and language-model readouts extend this idea beyond a purely descriptive observation. (Sections 4 and 5; specific gains in lines 303–306 and 316–323)

Critical weaknesses

W1. The gains from policy supervision cannot yet be attributed solely to improved utilization. Policy supervision introduces action supervision during PPO training (lines 259–260), but it is unclear whether the representation is held fixed. Figure 3 also acknowledges that it changes “rollouts and state visitation” (lines 245–246). The gains in Table 1 (lines 221–224) may therefore reflect improvements in both task-relevant representations and the mapping to behavior, rather than solely better utilization of existing state. The authors should clarify whether the representation network is frozen, which parameters are updated by the supervision, and how they rule out improved task-relevant representations as an explanation.

W2. Craftax: the effects of additional training, reward modification, and improved utilization remain unresolved. Section 5.1 reports an increase in score from 15.09 to 16.56 after 200 additional fine-tuning updates (lines 303–306), but does not report a budget-matched continued-PPO control using the original reward. The contribution of additional training therefore remains unresolved. The per-step cost could also alter preferences concerning survival or early termination, so its handling of termination and truncation needs clarification. More importantly, the authors explicitly acknowledge that sensitivity to spatial codes has not been measured on the same pre- and post-fine-tuning checkpoints (lines 309–312). Thus, the performance gains have not yet been linked to the earlier diagnosis of state utilization through corresponding measurements.

W3. Unclear supervision budgets and insufficient statistical support limit the interpretation of gains and null results. Although the language experiment freezes the base model, the improvement from 0.86 to 0.94 uses a teacher probe that predicts the counter state (lines 316–322). The teacher’s labeling budget, its performance when used directly as the answer predictor, and comparisons under the same total supervision budget remain unclear. Consequently, the 32 labeled student examples cannot be treated as the total supervision cost. Meanwhile, Table 1 lacks results for individual training seeds and intervals for performance differences: the representation auxiliary provides almost no gain at a 12-step horizon, but improves success from 0.822 to 0.870 at a 60-step horizon (lines 221–222). The claim that the Craftax auxiliary leaves the score essentially unchanged (lines 267–269) also lacks corresponding seed-level statistical support. The positive gains therefore still require controls for additional supervision, while the null results require clarification of their statistical precision and the horizons over which they hold.

Questions for authors
  1. Regarding W1: Which parameters does policy supervision update in Table 1, and is the representation network frozen? What information is available when constructing the belief-optimal labels? What existing evidence distinguishes “utilizing existing state” from “learning representations better suited to decision-making”?
  2. Regarding W2: Is there a paired control starting from the same checkpoint and continuing training for 200 updates with the original reward? Are there state-utilization measurements on the same pre- and post-fine-tuning checkpoints? If not, how should the scope of this result’s support for the utilization diagnosis be characterized?
  3. Regarding W3: How many labels are used to train the teacher probe, and how do the direct-teacher and total-supervision-budget-matched baselines perform? Could the authors provide seed-level intervals for performance differences in Table 1 and the Craftax representation-auxiliary experiment, and explain the dependence of the auxiliary’s gains on the rollout horizon?
Reviewer_rbEtOpenReview ↗
Rating
1
Confidence
2
Informativeness
1
Presentation
1
Soundness
1
Read review
Paper summary

This paper analyzes split of representation and utilization in multi-step tasks. Authors assert that two abilities are seperately improved, and measure representation by learnable linear probe with frozen hidden state, and utilization by accuracy with hidden state change. In experiments, they use 7*7 partial observable maze, craftax-symbolic with more restriction, mod-10 counter. Each experiments, they use causal transformer, GRU, light transformers respectively. With their experiments result, representation is learned first, and utilization is later. By fine tuning representation, result accuracy can be improved.

Critical strengths

There exists some strength in the idea of ​​distinguishing between not knowing the state and knowing the state but failing to use it effectively.

The paper combines linear probes with belief interventions and goes beyond diagnosis by testing representation-targeted and policy-targeted training.

Critical weaknesses

The representation analysis does not establish that the model has learned useful internal representation:

  • The paper measures how much representation has been learned by fitting a linear probe on a hidden layer to predict distance-to-goal. However, there is no baseline showing that the hidden representation is more informative than the raw input itself. The only comparison offered is with early training checkpoints (update 25), which shows that the representation is better than that of an essentially untrained network, not that it encodes hidden map state.
  • Moreover, Appendix B.4 reports that the distance-probe direction is nearly orthogonal to the subspace that predicts the optimal action. In other words, the distance information extracted by the probe is not what the policy relies on. The same problem affects the claim about improving utilization improves downstream performance. The paper concludes that utilization improved because performance rose while the distance probe did not. Since this probe does not track what the policy uses, probe score does not show that the representation was unchanged. The networks appear to be fine-tuned end-to-end, and no direct measure of utilization is reported before and after fine-tuning.

Terminology:

  • Terms are used throughout the paper without rigorous definitions and are often used interchangeably.
  • The interventions are described as following a task-agnostic principle. In practice, however, they are standard task-specific fine-tuning of an already-trained model (step-penalty reward shaping in RL and supervised readout distillation in language). Calling this a task-agnostic principle seems to give a new name to ordinary post-hoc fine-tuning rather than introduce a new method.

Each section:

  • Section 2 should specify the target variable and score for each probe and explain how the probes are fitted and evaluated on held-out data. * Section 3.1 needs more explanation of each measurement before presenting results. Terminology should be consistent between the text and figures. Table 1 and Figure 3 also present largely the same results.
  • The utilization measurements need clearer explanation. Showing that behavior depends on internal state does not establish that the policy uses that state effectively. Reporting how often the probe predicts the reference optimal action while the policy does not would help explain their disagreement. The reference optimal action and belief-optimal action also need clear definitions.
  • Section 4.2 should explain why the next-view prediction auxiliary was chosen and specify its inputs, prediction target, loss, and weight.
Questions for authors
  1. The hidden layer used for the belief swaps and probes is not clearly specified. For each experiment, which layer provides the representation used for linear probing and for belief swaps?
  2. The use of Craftax-Symbolic is non-standard. Is there reason for removing the inventory, using only 9x9 terrain view instead of 9×11, and using a 17-action subset?
  3. Could you report the result of predicting distance with linear probe on the input alone, i.e., the current observation (position, goal, and the 3×3 wall window)?
  4. Why were the thresholds r>0.4r > 0.4 and development success 0.5 selected? Does the reported temporal ordering hold with different thresholds?
  5. Why are per-step penalties expected to improve utilization? Do the maze penalties replace or add to the original per-step penalty? Which penalty produces the reported Craftax improvement? Please clarify the training reward and evaluation score.
  6. How many training seeds are used for Table 1 and the low-data answer readout?

Comments on the paper

1 comment

The revised paper asks how useful historical state develops during learning and what downstream behavior can be recovered from it. The new navigation study connects the measurement to ordinary-start task performance with the encoder fixed.

Fifteen independent replication agents reach 69.60% success within 18 actions from ordinary starts, versus 37.28% for their original policies.

Matched controlSuccess (%)Learned-history advantage
Current view64.545.05 pp [3.49,6.61]
Paired initial random67.342.25 pp [1.13,3.38]
Same head, history erased63.506.09 pp [3.90,8.29]

These three co-primary intervals are 99.17% paired-model intervals (df 14), accounting for all six co-primary contrasts across both studies at simultaneous 95% coverage. All three prespecified lower bounds are positive; the joint criterion is met.

The initial five-agent joint test failed and remains separate. This fixed 15-agent replication keeps the method unchanged and accounts for both studies.

The training choice follows a separate development diagnosis. Remembered history changes the fixed controller's action on 188/2,039 validation decisions. We crossed gap/action prediction with uniform/balanced exposure, giving learned/current/random features every choice. Only balanced gap fitting qualified in both development agents. We then fixed it before training or evaluating any confirmation agents. Balanced versus uniform fitting changes final navigation by 4.62 pp [3.44,5.80], descriptive 95% model interval.

Encoder, embeddings and normalization stay frozen, hash-checked. Readouts share 4,096 histories, observed-candidate labels and 500 updates, with no unseen passage labels. Current/random controls share the planner's geometry and computation. The native-policy gain includes added controller resources; matched contrasts estimate learned history. Erasure removes the whole history channel.

The new results and every fresh agent appear in Section 4.2, Table 1; Appendix K. All 242 replication rollout arms were independently replayed on CPU. Earlier unsuccessful map/candidate readouts and the complete development comparison remain in the appendix; they are not pooled with confirmation.

The counter changes only ten native answer rows (970 parameters): five models improve 85.60% to 93.31%; ten separate models improve 84.93% to 92.82% primary and 73.50% to 88.04% strict. Native state sequences, hidden inputs and capacity stay identical. In the ten-model cohort, state-target fitting exceeds supervised/self-distilled heads in every model on both banks. Cohorts and test populations stay separate. The counter controls and label access are in Section 5.2, Table 2. Its direct teacher reaches 98.79%, above the student; symbolic targets work equally well. Prior state supervision and known dynamics remain required, with no overall annotation-efficiency claim.

Craftax's complete five-model continuation gives +.753 full-model/+.571 frozen-body original-reward window return over continued PPO. First-episode returns fall and endings increase, so the result does not identify improved spatial utilization (Section 6, Table 3). The separate full-model retention study fails its joint criterion: the late-strict 97.5% interval includes zero. Ordinary state supervision is comparable; no general scheduling advantage follows.

The manuscript separates decodability, behavioral dependence and recovered performance. Distance thresholds no longer establish state formation; contaminated operations-only results are withdrawn. Probe targets, intervention sites, splits, budgets, all model-level intervals and the independent tests are explicit. We cite concurrent He et al. on readout development. Readout fitting and reweighting are established tools; our contribution is the developmental evidence and the controlled task consequence.

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

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