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Under review as a conference paper at ICLR 2027

Enhancing Large Language Models with Decision-Relevant Knowledge for Reinforcement Learning Tasks

Abstract

Large language models (LLMs) have demonstrated strong language understanding and reasoning capabilities through large-scale pretraining, motivating their increasing use in reinforcement learning and sequential decision-making. However, pretrained LLMs lack sufficient understanding of task-specific decision-relevant knowledge, including critical state information and task rules that directly guide action selection. While such knowledge is essential for effective decision-making, general-purpose LLMs often fail to correctly interpret and leverage it in domain-specific reinforcement learning tasks. To address this gap, we propose a two-stage training framework that explicitly teaches LLMs task-specific decision-relevant knowledge before policy optimization. In Stage-A, we construct supervision signals from structured-state definitions and task rules to train the LLM to recognize key environmental facts and infer the current decision objective, yielding a decision representation . In Stage-B, a lightweight policy is optimized with PPO on top of through online interaction. Under the same online interaction budget, our method achieves better overall performance than the compared baselines on Atari and Crafter and also shows applicability to additional environments.

Primary area:
reinforcement learning
Keywords:
Large Language Models, Reinforcement Learning, Decision-Relevant Knowledge, Representation Learning, Domain-Specific Knowledge

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
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Paper summary

The paper proposes a two-stage framework for using a pretrained LLM (Qwen3-1.7B; Qwen2.5-3B for Sokoban/FrozenLake) as the backbone of an RL policy. In Stage-A, GPT-5.5 is prompted with the environment description, the structured-state definition and hand-written task rules. It produces discrete label fields (“state-fact” and “rule-conditioned”, including a high-level goal field) and a deterministic Python labeler. The LLM receives encoded structured-state and rule tokens and is trained with LoRA so that linear heads can predict these labels from its representation hth_t. In Stage-B, the heads are discarded, and the same LoRA and encoders, together with a new policy head and critic, are trained with PPO for ~1M environment steps. The method reports large gains over PPO, LLM-Explorer, LaRe and SR on five Atari games and Crafter, and over PPO on Sokoban/FrozenLake.

Critical strengths
  1. The pipeline clearly described. The full labeler-generation prompt and most hyperparameters are provided.
  2. Ablation study is informative. Random Label shows that correct labels matter, not just an extra supervised stage. Single-Stage compares sequential and joint training at a matched budget.
  3. The gains over the identical model without Stage-A are consistent across environments. On Sokoban this holds even with Stage-A data from a random policy.
Critical weaknesses
  1. By construction, the Stage-A labels are a deterministic function of the pre-decision structured state and the task rules, which is exactly the policy input at every step. The labeler can therefore be run at test time at negligible cost. Stage-A trains a 1.7B model to approximately reproduce this function (92–97% all-field accuracy, Table 3), and the LLM then runs at every environment step in Stage-B. In my view, the key missing comparison is a non-LLM policy with the same access to the rule-derived knowledge: an MLP-PPO policy whose input is the structured state concatenated with the exact labeler outputs. The rule-conditioned labels already incorporate the thresholds. Together with a tuned MLP-PPO on the structured state alone, this would compare LLM and MLP backbones both with and without the rule-derived knowledge, and directly isolate the contribution of the LLM. Without it, I do not think the central claim that the LLM acquires decision-relevant knowledge is supported.
  2. Contribution 1 is “formulating decision-relevant knowledge as an explicit learning objective before policy optimization”. It is seemed like auxiliary supervision of the representation followed by RL. This is a well-established line: auxiliary tasks for RL (e.g., UNREAL, Jaderberg et al., 2017), which the paper does not discuss, and representation fine-tuning before value or policy learning (e.g., Digi-Q, which the authors cite). The potentially novel element is that an LLM designs the auxiliary tasks and writes the labeler from rule text. However, this element is not evaluated enough. Moreover, a separate model is trained for each environment, with environment-specific rules, labeler and data. There are no experiments on unseen rules, rephrased rules or multi-environment training. These are the settings where I would expect an LLM backbone and the natural-language rule interface to pay off. The per-task setup cost makes the approach hard to scale beyond the evaluated games.
  3. The PPO baseline puts a 1.7B LoRA backbone under PPO from scratch, which is known to be hard to optimize. Its numbers fall well below standard references: Crafter: PPO here reaches 4.82, whereas a tuned pixel-based PPO with a ResNet encoder reaches 15.6 on the official leaderboard at the same 1M-step budget. The proposed method (21.99) is on par with Achievement Distillation (21.8) and below SPRING (27.3). Atari: the reported scores are of the same order as standard pixel-based PPO at 40M frames (Schulman et al., 2017). OCAtari (Delfosse et al., 2024) reports that PPO on object-centric states performs on par with or better than pixel-based PPO. So I consider a properly tuned non-LLM PPO on the same structured states as a strong and necessary reference.
Questions for authors
  1. How do the following perform: a tuned MLP-PPO on the structured state, and an MLP-PPO on the structured state concatenated with the exact labeler outputs?
  2. What happens if the goal field is removed from Stage-A supervision? Since this field encodes the hand-designed rule priorities, the answer would show how much of the gain comes from the rules themselves.
  3. What is the score of the CleanRL expert used to collect Atari Stage-A data, and how do the results change if Stage-A data come from a random policy, as for Sokoban?
4 comments

We thank the reviewer for the constructive feedback and valuable suggestions. In response, we conducted additional experiments to further examine the role of the policy backbone and the impact of Stage-A data collection policies. We present our responses and the corresponding experimental results below.

Question 1: Comparison with MLP-PPO Baselines and the Role of Stage-A

Thank you for raising this important question. Following your suggestion, we conducted additional experiments with two MLP-PPO baselines: MLP-PPO using only structured states as input and MLP-PPO using structured states concatenated with the exact labels generated by the deterministic annotation program.

Both MLP-PPO baselines use the same structured-state interface and approximately 1 million online environment interactions.

The MLP policy backbone has approximately 25.2 million parameters, with a backbone learning rate of 1e-4. PPO (LLM) uses Qwen3-1.7B and updates its parameters through LoRA, with a LoRA learning rate of 5e-6. The results are shown below.

EnvironmentOursPPO (LLM)MLP-PPO (Structured State)MLP-PPO (Structured State + Exact Labels)
Alien1362.0 ± 157.280.0 ± 86.6066.67 ± 63.51535.03 ± 327.62
SeaQuest1618.6 ± 113.7621.13 ± 31.00153.33 ± 46.19634.40 ± 101.55
Assault5188.8 ± 807.5623.98 ± 9.85505.75 ± 118.02574.42 ± 145.03
BeamRider5182.91 ± 1217.25246.0 ± 77.83677.28 ± 2510.10741.32 ± 0.00
DemonAttack8112.3 ± 758.4502.1 ± 27.9390.75 ± 444.06562.68 ± 406.65
Crafter21.99 ± 0.964.82 ± 0.433.7452 ± 0.073910.18 ± 0.59

As shown in the table, providing exact rule-derived labels to MLP-PPO improves performance in five of the six environments. This indicates that these labels contain useful decision-relevant information. However, even with direct access to the exact labels generated by the annotation program, MLP-PPO still performs below our full method in all six environments. These results show that simply concatenating rule-derived labels with structured states as policy inputs is not sufficient to achieve the performance of our method.

The comparison with the PPO (LLM) baseline provides further evidence. With the same LLM backbone and online training settings, Stage-A supervised learning effectively improves subsequent policy performance.

Question 3: CleanRL Expert Performance and the Impact of Random-Policy Data on Stage-B

Thank you for raising this question. First, we report the performance of the CleanRL expert policies used to collect Atari Stage-A data. The following results show the mean scores and standard deviations over 100 episodes. The expert policies were trained using the same PPO configuration as CleanRL PPO, with an online interaction budget of 20 million steps.

EnvironmentExpert Policy
Assault8,040.85 ± 2,854.50
BeamRider3,885.68 ± 1,440.66
DemonAttack55,720.10 ± 28,722.96
SeaQuest2,073.42 ± 113.26
Alien2,664.12 ± 445.27

These results characterize the performance of the expert policies used for data collection. We further examine how replacing expert-policy or human-collected Stage-A data with random-policy data affects subsequent Stage-B performance.

Following your suggestion, we conducted additional experiments to investigate the impact of Stage-A data collection policies on subsequent Stage-B performance. Specifically, we replaced the original expert-policy or human-collected data with random-policy data, while keeping all other training settings unchanged. We evaluated this setting on SeaQuest, Assault, and Crafter. The results are shown below.

EnvironmentOriginal DataRandom-Policy DataPerformance Drop
SeaQuest1618.6 ± 113.71446.40 ± 56.6910.6%
Assault5188.8 ± 807.54217.85 ± 1996.8918.7%
Crafter21.99 ± 0.9613.04 ± 0.1440.7%

The results show that our method maintains effective performance across all three environments when using random-policy data. In particular, SeaQuest and Assault retain 89.4% and 81.3% of their original mean performance, respectively. This suggests that our method does not necessarily rely on expert-collected states to learn effectively.

To better understand these performance differences, we further analyzed the distributions of task-related events in the two datasets.

In SeaQuest, random-policy data covers 6 out of 7 event categories, compared with 7 out of 7 for expert-policy data. The proportion of states requiring the agent to surface for oxygen decreases from 31.29% to 1.35%, while states involving the delivery of a full load of divers are entirely absent. Meanwhile, random-policy data contains more states involving collision threats and nearby divers. These results indicate clear differences in both event coverage and the distribution of decision-making situations.

In Crafter, achievement-event coverage decreases from 22/22 to 8/22, while the number of unique achievement combinations drops from 530 to 25. This indicates that random policies have difficulty reaching states associated with more advanced task progress, which is consistent with the larger performance drop observed in this environment.

In Assault, both datasets cover 5 out of 6 decision-goal event categories, although the final performance still decreases.

Importantly, Stage-A does not use expert actions or policy outputs as supervision targets. As described in Section 3.2 and Appendix A.2, all supervision labels are generated from structured states and task rules through deterministic annotation programs. The LLM learns environmental facts and rule-conditioned decision-relevant knowledge rather than directly imitating expert actions.

Overall, these additional experiments show that expert-collected data is not a necessary condition for our method to achieve performance improvements. The differences in Stage-B performance are closely related to the event categories and state distributions covered by the two data collection policies. In complex environments such as Crafter, random policies have difficulty collecting states associated with advanced task progress. Consequently, the LLM receives fewer training examples for learning decision-relevant knowledge in these situations, leading to a larger performance drop in Stage-B. In contrast, the random and expert policies cover nearly the same event categories in the two Atari environments, where the performance drops are relatively smaller.

Question 2 Ablation Study on the Goal Field in Stage-A

Thank you for raising this question. To further investigate the impact of the Goal field on Stage-A training and final policy performance, we conducted an additional No Goal ablation experiment. We removed the Goal field from Stage-A supervision and compared the final policy performance across three Atari environments.

First, the Goal field in our paper represents a high-level decision objective. It indicates what the agent should prioritize based on the current environment state and task rules. Specifically, the model needs to combine environmental facts and task rules to determine the decision objective associated with the current state. For example, in SeaQuest, when oxygen is low, the current objective should be to return to the surface to replenish oxygen, rather than continue exploring or collecting divers. Therefore, the Goal field provides supervision that connects environmental facts and rule conditions to the current decision objective.

We conducted the No Goal ablation experiments in Assault, Alien, and SeaQuest. The results are shown below:

EnvironmentFull MethodNo Goal
Assault3679.68 ± 501.94200.6 ± 376.0
Alien1520.70 ± 13.11494.0 ± 274.0
SeaQuest1339.77 ± 47.66417.93 ± 38.51

The results show that the contribution of the Goal field varies across environments.

In Assault, removing Goal leads to a higher mean score. However, given the variability in both results, we do not interpret this change as a performance improvement. This may be related to redundancy in the Goal labels in Assault. For example, track_attack_target accounts for 74.9% of the training data. Some of the other decision-related fields already contain information needed to infer the current goal. Therefore, explicitly supervising the Goal field may provide limited additional benefits.

In Alien, the mean score after removing Goal remains close to that of the Full Method. This suggests that, under the current experimental setting, the additional contribution of the Goal field is not pronounced.

In contrast, SeaQuest shows a much stronger dependence on Goal supervision. After removing Goal, the mean score drops from 1339.77 to 417.93, a decrease of approximately 68.8%. We believe this is related to the decision-related information contained in different high-level goals in SeaQuest. For example, return_for_air and collect_diver represent different objectives: returning to the surface to replenish oxygen and collecting divers, respectively. In addition, oxygen management is critical to survival and score accumulation in SeaQuest. If the agent fails to return to the surface in time to replenish oxygen, it may run out of oxygen and lose the opportunity to continue accumulating scores. Therefore, the model needs to determine which objective should take priority between survival and other task goals based on the current environment state and task rules. This makes the Goal field an important source of high-level decision supervision, helping the model understand which objective should be prioritized in the current state.

Overall, we conclude that the contribution of the Goal field depends on the task characteristics of each environment and the decision-related information it contains. In Assault and Alien, some Goal information may already be captured by other supervision fields, resulting in relatively small performance changes after removing Goal. In SeaQuest, however, Goal provides more important supervision for high-level decision objectives.

Reviewer_mR5YOpenReview ↗

Response to Rebuttal

I thank the authors for the detailed rebuttal and the additional experiments. The new MLP-PPO baselines, the random-policy Stage-A data and the goal ablation address part of my concerns. However, not all of my points were answered. In particular, my concern about the limited generalization and applicability of the method remains: a separate model is still trained per environment, with environment-specific rules, labeler and data, and there is no evaluation on unseen or rephrased rules, nor any transfer across environments. I therefore keep my original score.

Reviewer_aEWkOpenReview ↗
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Paper summary

The paper argues that pretrained LLMs lack decision-relevant knowledge for RL tasks and proposes to teach it explicitly before policy learning. In Stage A, a LoRA-adapted Qwen3-1.7B is supervised to predict field-level environment facts and rule-conditioned goals — including paired samples where the same state with perturbed rule thresholds yields different labels; in Stage B, standard PPO is run on top of the resulting representation. Under a 1M-frame online budget the method outperforms PPO and several LLM-based baselines on five Atari games (OCAtari structured states) and Crafter, with additional results on Sokoban/FrozenLake.

Critical strengths

The decomposition — learn the knowledge first, then the policy — is clean, and the paired-sample construction is a clever way to force genuine rule grounding rather than state-label memorization. The random-label ablation (performance collapses) does support that the gains come from the semantics of the supervision rather than from an extra training phase per se.

The headline improvements are large and consistent across environments, and the representation analysis is more careful than the usual probing exercise — the Procrustes/affine alignment controls are a nice touch that most papers in this space skip.

Critical weaknesses

The "same online interaction budget" framing is misleading. Stage A consumes substantial privileged offline resources: 200K states per game collected by a fully trained PPO agent (itself trained on far more than 1M frames), 100 human trajectories for Crafter, and hand-written rules with tuned thresholds — in effect Stage A partly distills a handcrafted rule policy. There is no comparison against simply executing that rule script, against BlendRL (which the paper cites and whose state interface it reuses), or against a plain MLP-PPO on the same structured states, so the contribution of the LLM itself is never isolated. The 1M-frame budget is also very small for Atari, and the low baseline scores partly reflect that.

The representation analysis misses the standard control: a fresh linear probe trained on the frozen pre-Stage-A features. Without it, the claim that Stage A encodes the knowledge into the representation (as opposed to the knowledge simply not being linearly decodable beforehand) is not fully established. The inconsistent evaluation protocols between Table 1 and Table 4 add avoidable confusion.

Questions for authors
  1. If Stage-A data is collected by a random or weak, unconverged policy instead of a trained PPO agent, how much does Stage-B performance drop? And how does the method compare to directly executing the hand-written rules?
  2. Can you add BlendRL and an MLP-PPO baseline on the same OCAtari structured states under the same budget?
  3. What does a fresh probe on the frozen pre-Stage-A representation achieve? How sensitive is the pipeline to noisy or incomplete rule specifications?
3 comments

Thank you for the highly detailed review and constructive feedback about this work. We especially appreciate your questions about the role of Stage-A in our framework, for which we conducted additional experiments. Please find our responses below.

Question 1 Impact of Stage-A Data Collection and the Role of Task Rules

1. Impact of Random-Policy Data on Stage-B Performance

Following your suggestion, we conducted additional experiments to investigate the impact of Stage-A data collection policies on subsequent Stage-B performance. Specifically, we replaced the original expert-policy or human-collected data with random-policy data, while keeping all other training settings unchanged. We evaluated this setting on SeaQuest, Assault, and Crafter. The results are shown below.

EnvironmentOriginal DataRandom-Policy DataPerformance Drop
SeaQuest1618.6 ± 113.71446.40 ± 56.6910.6%
Assault5188.8 ± 807.54217.85 ± 1996.8918.7%
Crafter21.99 ± 0.9613.04 ± 0.1440.7%

The results show that our method maintains effective performance across all three environments when using random-policy data. In particular, SeaQuest and Assault retain 89.4% and 81.3% of their original mean performance, respectively. This suggests that our method does not necessarily rely on expert-collected states to learn effectively.

To better understand these performance differences, we further analyzed the distributions of task-related events in the two datasets.

In SeaQuest, random-policy data covers 6 out of 7 event categories, compared with 7 out of 7 for expert-policy data. The proportion of states requiring the agent to surface for oxygen decreases from 31.29% to 1.35%, while states involving the delivery of a full load of divers are entirely absent. Meanwhile, random-policy data contains more states involving collision threats and nearby divers. These results indicate clear differences in both event coverage and the distribution of decision-making situations.

In Crafter, achievement-event coverage decreases from 22/22 to 8/22, while the number of unique achievement combinations drops from 530 to 25. This indicates that random policies have difficulty reaching states associated with more advanced task progress, which is consistent with the larger performance drop observed in this environment.

In Assault, both datasets cover 5 out of 6 decision-goal event categories, although the final performance still decreases.

Importantly, Stage-A does not use expert actions or policy outputs as supervision targets. As described in Section 3.2 and Appendix A.2, all supervision labels are generated from structured states and task rules through deterministic annotation programs. The LLM learns environmental facts and rule-conditioned decision-relevant knowledge rather than directly imitating expert actions.

Overall, these additional experiments show that expert-collected data is not a necessary condition for our method to achieve performance improvements. The differences in Stage-B performance are closely related to the event categories and state distributions covered by the two data collection policies. In complex environments such as Crafter, random policies have difficulty collecting states associated with advanced task progress. Consequently, the LLM receives fewer training examples for learning decision-relevant knowledge in these situations, leading to a larger performance drop in Stage-B. In contrast, the random and expert policies cover nearly the same event categories in the two Atari environments, where the performance drops are relatively smaller.

2. Comparison with Direct Execution of Handcrafted Task Rules

Regarding the suggested comparison with directly executing the handcrafted rules, we would like to clarify the role of task rules in our framework.

The task rules are primarily used to define rule-conditioned fields and generate Stage-A supervision labels, rather than to specify a complete action policy. Our objective is to enable the LLM to understand environmental facts and the current decision objective through rule-based supervision, instead of directly teaching it which actions to take.

Specifically, the annotation programs produce state-fact and rule-conditioned labels, but do not output environment actions. Therefore, directly executing these programs cannot produce a complete control policy. An additional mapping from rule-conditioned information to specific environment actions would be required.

For this reason, directly executing the annotation programs does not constitute an equivalent policy baseline for comparison with our method.

Beyond the role of Stage-A data and task rules, we further examine whether the observed performance gains also hold when using a different policy backbone.

Question 2 Comparison with MLP-PPO and PPO (LLM) Baselines

EnvironmentOursPPO (LLM)MLP-PPO
Alien1,362.0 ± 157.280.0 ± 86.6066.67 ± 63.51
SeaQuest1,618.6 ± 113.7621.13 ± 31.00153.33 ± 46.19
Assault5,188.8 ± 807.5623.98 ± 9.85505.75 ± 118.02
BeamRider5,182.91 ± 1,217.25246.0 ± 77.83,677.28 ± 2,510.10
DemonAttack8,112.3 ± 758.4502.1 ± 27.9390.75 ± 444.06
Crafter21.99 ± 0.964.82 ± 0.433.7452 ± 0.0739

To further examine the effect of the policy backbone, we conducted an additional MLP-PPO experiment and compared it with the PPO (LLM) baseline reported in the paper.

To ensure a fair comparison, we kept the online interaction budget, input information, and main PPO training settings consistent with those of the PPO (LLM) baseline. The main differences between the two baselines lie in their policy backbones and optimization settings. PPO (LLM) uses a pretrained Qwen3-1.7B backbone and applies LoRA for parameter updates, with a LoRA learning rate of 5e-6. MLP-PPO uses an MLP backbone with approximately 25.2M parameters and a backbone learning rate of 1e-4. Since the two backbones have different architectures and parameter update methods, we used different backbone learning rates while keeping the other main PPO hyperparameters unchanged.

The results show that our full method outperforms both MLP-PPO and PPO (LLM), neither of which uses Stage-A training, across all six environments.

The additional MLP-PPO results further demonstrate the performance advantage of our method over a conventional MLP policy. Together with the comparison against PPO (LLM), these results support our main argument: under a limited online interaction budget, first teaching the LLM decision-relevant knowledge through supervised learning and then optimizing the policy with PPO can effectively improve subsequent policy learning.

While these comparisons demonstrate the performance benefits of our method, we further examine whether Stage-A actually improves the decision-relevant knowledge encoded in the LLM representations.

Question 3 Linear Probing on Frozen Pre-Stage-A Representations

Thank you for raising this question. Our goal is to enable the pretrained LLM to learn task-relevant decision knowledge before policy optimization and encode this knowledge into the decision representation (h_t). To further examine whether Stage-A improves the LLM's ability to represent decision-relevant knowledge, we conducted an additional Linear Probe experiment following your suggestion.

In our framework, decision-relevant knowledge refers to the model's ability to identify facts about the current environment state and determine the decision objective associated with that state based on these facts and the task rules. As described in Section 3.2 of our paper, the readout heads are used to examine whether the LLM has encoded decision-relevant knowledge in its decision representation. After training, the decision representation (h_t) produced by the LLM is a latent vector. Its numerical values do not directly reveal the specific facts and decision-related information it contains. Therefore, a readout head is needed to decode this representation and map the encoded information to interpretable supervision fields. Predictions on these fields allow us to assess whether the LLM has encoded the relevant knowledge in its decision representation.

Specifically, we compared two model representations: Pre-Stage-A and After Stage-A. For Pre-Stage-A, we used the pretrained Qwen3-1.7B with randomly initialized adapters. For After Stage-A, we used the LoRA, state encoder, and rule encoder trained through supervised learning. The model parameters used to produce the representations were kept frozen during probe training in both conditions. We trained a separate Linear Probe for each representation, rather than using the original Readout Heads from Stage-A. Both probes followed the same architecture and training setup.

We conducted the experiments in Assault and Crafter. Assault used 4,096 held-out test samples with 16 supervised fields, while Crafter used 2,048 held-out test samples with 12 supervised fields. We report two metrics: the average accuracy across individual fields and the all-field accuracy, which requires all supervised fields to be predicted correctly for a sample. The results are shown below.

EnvironmentRepresentationAll-field CorrectAll-field AccuracyAverage Single-field Accuracy
AssaultPre-Stage-A128/40963.12%66.81%
AssaultAfter Stage-A2091/409651.05%94.91%
CrafterPre-Stage-A314/204815.33%75.79%
CrafterAfter Stage-A967/204847.22%92.39%

Note: All-field accuracy measures the proportion of samples for which every supervised field is predicted correctly. Each sample contains 16 supervised fields in Assault and 12 in Crafter.

The results show that after Stage-A training, the Linear Probe can predict environmental facts and decision-relevant fields more accurately from the model representations in both environments. This indicates that decision-relevant information is more fully encoded in the representations and provides evidence that the LLM has indeed learned decision-relevant knowledge. In Assault, the all-field accuracy increases from 3.12% to 51.05%, while the average single-field accuracy increases from 66.81% to 94.91%. In Crafter, these two metrics increase from 15.33% to 47.22% and from 75.79% to 92.39%, respectively.

These results further support our central claim: through state-fact supervision and rule-conditioned decision supervision, Stage-A enables the LLM to better understand structured environmental information and the corresponding decision goals, and to encode this information into the decision representation (h_t).

Reviewer_75j4OpenReview ↗
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Paper summary

This work focuses on the problem that LLMs lack decision-relevant knowledge and thus perform poorly on decision-making tasks. It proposes a two-stage training method for LLMs. In Stage-A, it constructs supervision signals from structured-state definitions and task rules to train the LLM to recognize key environmental facts and infer the current decision objective, yielding a decision representation hth_t. In Stage-B, a lightweight policy is optimized with PPO on top of hth_t through online interaction.

Critical strengths

This paper argues that LLMs struggle to directly solve decision-making tasks and attempts to inject task-relevant knowledge into them. This is well-motivated and makes sense. This work aims to teach LLMs structured-state information and task rules; in particular, the task-rule supervision is interesting and novel.

Critical weaknesses

However, constructing supervision signals is challenging, requiring a large amount of task-specific labeling design and validation. Although the paper uses GPT-generated annotation programs, how are these supervision signals and the underlying task rules obtained and validated? Especially for some tasks, the decision objective is hard to define, and the task rules are unknown, while structured-state is comparatively easier to obtain than them. This limits the generality and practicality of this work. I think injecting task rules is a good idea, but how to obtain these rules is itself an interesting problem.

The evaluated tasks are relatively simple. Harder tasks could be considered to provide stronger evidence.

Although the methods use the same online interaction budget, the proposed method additionally requires pre-collected supervision data and task-specific rules. Matching only the online interaction budget seems unfair.

In addition, a baseline that directly uses the LLM to generate actions from the same structured-state and task-rule inputs[1] would be useful, since this method's Stage-B also queries the LLM at every state. [1]Grounding Large Language Models in Interactive Environments with Online Reinforcement Learning

Questions for authors

What are the model backbone and model size of the policy in Stage 2, and what is the model backbone of the PPO baseline? How are the same structured-state and task-rule inputs injected in PPO baseline? How can such a significant improvement of the method over the baselines be explained?

2 comments

Thank you for the highly detailed review and constructive feedback about this work. We especially appreciate your question about the significant performance improvements over the baselines, for which we provide further evidence from the ablation studies and representation analysis in Tables 3 and 4. Please find our response below.

Question 1: Policy Backbone and Model Size

The backbone architecture and model size used in Stage-B and the PPO baseline are explicitly specified in the manuscript.

Specifically, Section 4 (Training Configuration, Page 6) states that all LLM-based methods except LaRe use Qwen3-1.7B for the Atari and Crafter experiments. Thus, the policy backbone used in Stage-B is Qwen3-1.7B.

For the PPO baseline, Section 4 (Baselines, Page 7) and Appendix A.6 further clarify that it uses the same policy architecture and Qwen3-1.7B backbone as our method.

Question 2: Structured-State and Task-Rule Inputs for the PPO Baseline

The PPO baseline uses the same structured-state and task-rule inputs as our method. This is clearly stated in Section 4 (Baselines, Page 7) and Appendix A.6.

Both methods use the same policy and value network architectures, as well as the same encoders for structured states and task rules. The encoders convert the structured states and task rules into tokens. These tokens are then used as inputs to Qwen3-1.7B.

The configurations are summarized below.

ComponentOur MethodPPO Baseline
Policy backboneQwen3-1.7BQwen3-1.7B
Structured-state inputState encoder → State tokensSame
Task-rule inputRule encoder → Rule tokensSame

Question 3: Explanation for the Significant Performance Improvements

Following your valuable feedback on the significant performance improvements over the baselines, we further examine the contribution of field-level supervision in Stage-A using the ablation results in Table 4.

We compare three settings: Full Method, No Stage-A, and Random Label. The results are shown below.

EnvironmentFull MethodNo Stage-ARandom Label
SeaQuest1339.77479.0538.2
Assault3679.68564.61855.8
Alien1520.70298.8656.4
Crafter21.994.826.47

First, in the No Stage-A ablation, removing field-level supervision leads to a substantial performance drop across all environments, with the largest decrease reaching 84.7%.

Regarding fairness, we clarify that all methods use the same online environment interaction budget, but not the same total training resources. As stated in Section 4 (Page 6), our method uses additional supervision data in Stage-A.

In the Random Label ablation, we keep the same Stage-A data and training configuration as our full method, but randomly shuffle the supervision labels across samples. Performance also drops significantly across all environments, with the largest decrease reaching 70.6%. Since the additional Stage-A data and training are kept unchanged, these results suggest that most of the performance gains come from learning decision-relevant knowledge with correct supervision labels, rather than from additional training alone.

Finally, we use classification heads to examine whether decision-relevant knowledge can be recovered from the LLM representations before and after Stage-A. As shown in Table 3, the all-field prediction accuracy reaches 92.20% on SeaQuest and 97.20% on Assault after Stage-A, indicating that decision-relevant information can be accurately recovered from the learned representations.

Together, these results support our explanation that field-level supervision helps the LLM learn decision-relevant knowledge and use it during subsequent environment interactions, leading to substantial improvements in policy performance.

Thank you for the clarification. My main concern remains that constructing the supervision signal for Stage A is challenging, and limit the method’s generalizability. The evaluation is limited to the Atari benchmark. I therefore tend to maintain my original score.

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Area_Chair_gDdKOpenReview ↗

Please engage in the last-day discussion

Dear reviewers,

We have less than one day left for the discussion period, and the authors have provided their response to all reviewer comments. Could you read the authors' rebuttal and reply accordingly?

Many thanks, AC

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