ArXiv: 2605.00425
🎯 Pitch
In sparse-reward agent tasks, positive and negative trajectories push policy entropy in opposite directions—yet standard RL ignores this signal. By simply rescaling advantages with a response-level uncertainty proxy derived from that entropy drift, AEM gives a free 8.8% boost to GRPO on ALFWorld and improves state-of-the-art software-engineering training, without any extra models or dense supervision.
1. Executive Summary
This paper proposes AEM (Adaptive Entropy Modulation), a supervision-free credit assignment method that rescales response-level advantages in multi-turn agentic RL using an entropy-derived uncertainty proxy to regulate the exploration-exploitation trade-off without auxiliary models or dense supervision. The authors first provide a response-level theoretical analysis showing that entropy drift under natural-gradient updates is governed by the interaction between a sampled response's advantage and its relative surprisal—motivating a modulation rule that induces entropy-increasing pressure on negative responses and entropy-decreasing pressure on positive responses. Across ALFWorld, WebShop, and SWE-bench-Verified with models ranging from 1.5B to 32B, AEM consistently improves group-based RL baselines—yielding peak gains of 8.8% on GRPO with Qwen2.5-1.5B on ALFWorld and a +1.4% improvement when integrated into DeepSWE on SWE-bench-Verified—establishing that response-level entropy modulation provides effective credit assignment without extra supervision, but only insofar as the modulation coefficient is correctly aligned with each response's own uncertainty estimate rather than randomly permuted or reversed.
2. Context and Motivation
The Core Problem: Credit Assignment Under Sparse Outcome Rewards in Multi-Turn Agentic RL
The fundamental challenge this paper tackles is credit assignment in multi-turn agentic reinforcement learning for LLM agents. When an LLM interacts with an environment over many turns—observing states, generating responses, and receiving environmental feedback—it typically receives a reward only at the end of a long interaction trajectory. This is a textbook "sparse reward" problem: the agent might take 15, 30, or even 50 actions across a trajectory, yet only receives a single scalar success/failure signal after the final step. The core difficulty is that this terminal reward provides essentially no discrimination between individual steps within the same trajectory. If a trajectory succeeds, every action in it gets reinforced equally, even if some steps were counterproductive or irrelevant. If it fails, every action gets penalized equally, even if some intermediate reasoning was sound.
This problem is not merely an inconvenience—it fundamentally limits how efficiently an LLM agent can learn from interaction. Without finer-grained feedback, the policy receives high-variance gradient estimates that conflate the contributions of good and bad decisions within a single episode. The result is slow convergence, inefficient exploration, and the risk that the model converges to a suboptimal policy where it learns to produce tokens that look plausible but do not reliably advance task completion.
To understand why this is particularly acute for LLM agents (as opposed to, say, classic Atari RL agents), consider the scale of the action space. At each turn, the agent generates a response that can span hundreds of tokens, each drawn from a vocabulary of tens of thousands. The space of possible responses at each state is astronomically large, meaning that random exploration alone is unlikely to stumble upon successful trajectories without some mechanism for guiding intermediate decisions. Yet the only feedback available—a binary success/failure at trajectory-end—provides no such guidance.
Why This Problem Matters: From Single-Turn Reasoning to Sustained Interaction
The shift from single-turn post-training to multi-turn agentic RL represents a qualitative change in how LLMs are deployed and improved. In single-turn settings (e.g., math reasoning, code generation), the model produces one generation, receives a verifiable reward, and is updated accordingly. The correspondence between action and outcome is direct: each token in the generation contributes to the final answer, and credit assignment, while not trivial, is at least bounded by the length of a single response.
Multi-turn agentic settings are fundamentally different. The agent must:
- Maintain state across turns, integrating new observations (webpage content, tool outputs, error messages) into its reasoning.
- Make sequential decisions under uncertainty, where early choices (e.g., which search query to issue, which file to inspect) constrain later options.
- Recover from errors, recognizing when a previous action was suboptimal and adjusting strategy mid-trajectory.
These capabilities are essential across a growing range of practical applications: autonomous software engineering (Yang et al., 2024a, 2025), where agents must navigate codebases, run tests, and apply patches across dozens of steps; web navigation and e-commerce (Yao et al., 2022), where agents must search, filter, and select products in interactive HTML environments; embodied assistance (Li et al., 2024), where agents must physically reason about object locations and tool use; and GUI navigation (Yuan et al., 2026; Li et al., 2026), where agents manipulate interface elements across applications.
In all these settings, the quality of intermediate decisions determines overall success, yet the reward signal arrives only at the end. This makes efficient credit assignment not just a theoretical concern but a practical bottleneck for deploying capable LLM agents.
Why This Problem Has Emerged Now: The Rise of Group-Based RL for LLMs
The paper is situated within the recent shift toward group-based reinforcement learning methods for LLM training. Traditional actor-critic approaches like PPO (Schulman et al., 2017) maintain a separate value function (critic) to estimate per-state advantages, which naturally provides a form of credit assignment: if a state has low expected return, actions at that state receive different advantage signals than actions at high-value states. However, training a critic for LLM policies is prohibitively expensive: it requires a separate model of comparable size, doubles memory requirements, and introduces additional optimization challenges (value function instability, distributional shift between the actor and critic).
Group-based methods—most prominently GRPO (Shao et al., 2024)—eliminate the critic by estimating advantages from within-group comparisons. For a given prompt, the model generates multiple responses (a "group"), computes their outcomes, and normalizes rewards within the group to produce advantages. This is computationally elegant—no extra model, no value function training—and has proven effective for single-turn reasoning tasks.
However, the very mechanism that makes group-based methods appealing in single-turn settings becomes a liability in multi-turn settings. In single-turn tasks, each response is a complete solution; the group-based advantage cleanly tells you which responses are better than others. In multi-turn tasks, a "response" is just one step in a longer trajectory. The group-based advantage for a trajectory is a single scalar that says "this trajectory succeeded" or "this trajectory failed," but it says nothing about which step within the trajectory was responsible. As the authors note:
"different steps within the same trajectory often receive nearly indistinguishable learning signals, leading to ambiguous credit assignment and inefficient policy improvement." (Section 1)
This is the gap that AEM addresses: how to provide finer-grained credit signals without reintroducing the complexity of a critic or requiring external supervision.
Prior Approaches and Their Limitations
The paper identifies three broad strategies that prior work has employed to address credit assignment in agentic RL, and explains why each falls short.
Approach 1: External Supervision and Reward Shaping
The most direct approach is to augment the sparse outcome reward with denser intermediate signals. Process reward models (PRMs) (Lightman et al., 2023) train a separate model to evaluate the correctness of each step in a reasoning chain, providing per-step reward signals. Value function-based methods like PPO's generalized advantage estimation (GAE) learn a critic that predicts expected future return at each state.
Why they fall short (Section 2): These methods "introduce additional modeling and scaling overhead." Training a PRM requires either human annotations (expensive, not scalable) or automated labeling procedures (which introduce their own biases and require careful design). Training a critic for LLM policies doubles model parameters and introduces well-known stability challenges. Moreover, PRMs trained on one domain may not generalize to others—a PRM that evaluates math reasoning steps is useless for web navigation. This reliance on "extra supervision and tuning complexity" limits the scalability and generality of these approaches.
The paper acknowledges these methods exist but positions them as introducing precisely the kind of overhead that group-based methods were designed to avoid. AEM's goal is to achieve similar benefits without requiring additional models, annotations, or per-domain tuning.
Approach 2: Structured Credit Propagation (Tree-Search and Reward Redistribution)
Another line of work attempts to improve credit granularity by propagating outcome signals backward through trajectory structure. Methods like Tree-GRPO (Ding and Ye, 2026) and ATPO (Cao et al., 2026) construct branching trajectories, exploring multiple possible continuations from each intermediate state, and use the distribution of outcomes from each branch to assign more informative credit to earlier decisions. SPA-RL (Wang et al., 2025a) and related methods redistribute outcome rewards across steps based on trajectory attributes or learned progress measures.
Why they fall short (Section 2): These methods "improve credit granularity but often incur additional computational cost in multi-turn settings." Constructing a tree of trajectories requires generating and evaluating many more rollouts than simple linear trajectories—a cost that compounds with trajectory length. In a 50-step embodied task, even a modest branching factor of 3–4 per step would generate an exponential number of trajectories. The paper argues this computational overhead makes these methods impractical for the multi-turn settings it targets (ALFWorld, SWE-bench-Verified), where trajectories can involve dozens of environment interactions.
Approach 3: Self-Supervised Step-Level Signal Inference
A third category of methods—most directly relevant to AEM—attempts to infer step-level credit signals from within-trajectory structure without external supervision. Methods like GiGPO (Feng et al., 2025) and IGPO (Wang et al., 2026) derive step-level signals from trajectory structure itself: for instance, by comparing trajectories that diverge at a particular step, or by estimating the information gain of individual actions relative to the policy's prior distribution.
Why they fall short (Section 2): The paper identifies three specific vulnerabilities in self-supervised approaches:
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Context inconsistency: When comparing trajectories, it is not always clear which context differences (earlier actions, environment observations) are responsible for different outcomes. A step that looks "good" in one trajectory context might be harmful in another.
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Grouping bias: Methods that partition trajectories or estimate per-step value based on within-group statistics can be sensitive to how groups are constructed—the paper notes that "heavy dependence on structural assumptions" can make these methods brittle across diverse tasks.
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Limited robustness and generalization: Because these methods rely on implicit structural properties (which steps "caused" which outcomes), they may break when those structural assumptions do not hold—for example, in domains where the relationship between actions and outcomes is highly nonlinear or delayed.
Collectively, these limitations point to a gap: a credit assignment method that is supervision-free, computationally lightweight, and does not depend on restrictive structural assumptions about how trajectories are organized or how credit should be propagated.
How AEM Fits Into This Landscape
AEM's positioning is distinctive because it identifies a signal that already exists in the policy itself but has not been systematically exploited for credit assignment: response-level entropy. The key insight is deceptively simple: when the policy is uncertain about which action to take at a state (high entropy), the sampled response is more likely to be exploratory—a tentative attempt rather than a confident decision. When the policy is very certain (low entropy), the response reflects the policy's current "best guess" and may indicate exploitation of known strategies.
Critically, this signal is intrinsic to the policy—it requires no external model, no reward shaping, no tree construction, and no structural assumptions about trajectories. It is computed from the same log-probabilities that the RL algorithm already needs for its update. The paper's theoretical contribution (Theorem 3.2.2) then shows why this signal is relevant: the entropy drift induced by a sampled response is naturally governed by the interaction between its advantage and its relative surprisal (how much more or less likely it is than the average response at that state). This means that multiplying advantages by a coefficient derived from relative surprisal directly modulates entropy dynamics—increasing entropy when the policy is underexploring, decreasing it when the policy is converging.
AEM's position relative to prior entropy-aware work (Section 2, "Entropy-Aware Policy Optimization") is also instructive. Prior approaches either:
- Use entropy as a regularization term added to the policy objective (e.g., Mnih et al., 2016b; Xu et al., 2025b), which applies uniform entropy pressure regardless of the quality of sampled actions.
- Use entropy for token-level gradient recalibration (e.g., Wang et al., 2025b; Dong et al., 2026a), which operates at a finer granularity than the environment-reactive unit.
AEM differs by operating at the response level (matching the natural action granularity of agentic RL) and by using entropy only to rescale advantages, not as an auxiliary objective. This means AEM does not change the optimization landscape—it simply modulates which samples contribute how much to the policy gradient, based on their uncertainty.
The Practical Motivation: Why Plug-In Simplicity Matters
Beyond the theoretical arguments, there is a clear engineering motivation for AEM's design. The authors emphasize that AEM is a "lightweight, plug-in method" (Section 4.1) that operates on top of any base advantage estimator. This is important because the RL training stack for LLM agents is already complex: distributed training across multiple GPUs, rollout generation, reward computation, advantage estimation, gradient computation, and optimization. Each additional component (a critic model, a PRM, a tree-structured rollout procedure) adds integration complexity, memory overhead, and potential failure modes.
AEM's computational cost analysis (Section 5.4, Figure 6) is designed to address this concern directly. The additional computation—response-level entropy aggregation, group-wise normalization, and advantage rescaling—accounts for only 1.1% of total training time on ALFWorld with Qwen2.5-1.5B. The entropy values are obtained during the same recomputation pass used to compute old-policy log-probabilities (a step that GRPO already performs), so AEM "incurs no additional model forward pass." This lean profile means practitioners can try AEM with minimal engineering effort—a single hyperparameter (λ, the temperature in the softmax modulation), no new models, no architectural changes.
In summary, the problem AEM addresses is ambiguous credit assignment under sparse outcome rewards in multi-turn agentic RL, which matters because it limits the efficiency with which LLM agents can learn complex sequential behaviors. Prior solutions either introduce expensive external supervision, incur combinatorial computational overhead, or rely on brittle structural assumptions. AEM positions itself as occupying a unique point in this design space: supervision-free, computationally negligible, and theoretically grounded in the response-level entropy dynamics of the policy itself.
3. Technical Approach
3.1 Reader Orientation
This is a theoretical-analysis-plus-practical-method paper that first derives how response-level entropy evolves during natural-gradient policy updates in multi-turn agentic RL, then uses this insight to design a plug-in advantage rescaling module that modulates credit assignment based on each response's uncertainty. The system solves the problem of ambiguous credit assignment under sparse outcome-only rewards by modulating response-level advantages with an entropy-derived coefficient—responses that are unusually surprising given the policy's current state get their advantage scaled up or down depending on whether they led to success or failure, thereby guiding the policy from early exploration (preserving diversity) to late exploitation (converging on successful strategies) without any auxiliary models, process supervision, or structural assumptions about trajectory organization.
3.2 Big-Picture Architecture (Diagram in Words)
The system has four major components that operate in a loop during RL training:
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Base RL training pipeline (GRPO/DAPO/GSPO) — the standard group-based RL algorithm that samples trajectories, computes outcome rewards, and estimates advantages. This is the backbone that AEM plugs into without modification.
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Response boundary parser — a component that identifies where each environment-reactive response begins and ends within the raw token stream. In agentic RL, the environment only reacts after a complete response is generated (e.g., the agent issues a tool call, and the environment returns a new observation), so identifying these boundaries is essential to lift entropy analysis from token-level to response-level.
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Entropy proxy extractor — for each identified response span, this component aggregates token-level log-probabilities into a length-normalized response-level entropy proxy
$\bar{H}_{i,t}$. The token-level entropy values are obtained during the same recomputation pass that GRPO already performs to compute old-policy log-probabilities, so this incurs no additional forward pass. -
AEM modulation module — the core contribution. For each group (the set of all responses across trajectories generated from one prompt), this module min-max normalizes the entropy proxies, applies a softmax with temperature
$\lambda$to produce modulation coefficients$\alpha_{i,t}$, self-calibrates them to maintain an average of 1 within the group, and multiples them by the base advantages to produce$A_{i,t}^{\text{AEM}} = \alpha_{i,t} A_{i,t}^{\text{base}}$. These modulated advantages then replace the base advantages in the policy gradient computation.
Information flows through these components in a fixed sequence during each training iteration: the base RL pipeline generates rollouts → the response boundary parser splits token sequences into response spans → the entropy proxy extractor computes $\bar{H}_{i,t}$ for each span → the AEM modulation module computes $\alpha_{i,t}$ and rescales advantages → the rescaled advantages feed into the standard policy gradient update. The key property is that the modulation module is stateless and operates purely on within-group statistics—it requires no memory of previous training steps, no separate models, and no auxiliary data.
3.3 Roadmap for the Deep Dive
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First, the theoretical foundation: Theorem 3.2.1 (the relationship between token-level, response-level, and policy entropy) and Theorem 3.2.2 (the entropy drift formula under natural-gradient updates). These theorems explain why response-level relative surprisal is the right signal for credit modulation. I will explain each theorem's inputs, outputs, and implications in operational terms.
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Second, the practical modulation mechanism (Section 4.2): how AEM converts the theoretical insight—that entropy drift depends on
$A \times (S - H_{\text{resp}})$—into a concrete computation of$\alpha_{i,t}$from token-level entropy values, using length normalization, group-wise min-max scaling, temperature-parameterized softmax, and self-calibration. -
Third, the exploration-exploitation transition mechanism (Section 4.3): how the evolving balance of positive and negative responses during training causes AEM to automatically shift from entropy-increasing (preserving diversity early) to entropy-decreasing (promoting convergence late), without any scheduled annealing or external signal.
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Fourth, verification through analysis (Section 5.3): the empirical studies that validate AEM's theoretical premises—showing that
$\alpha - 1$correlates with$-(S - H_{\text{resp}})$, that$\text{sgn}(A(\alpha - 1))$governs entropy trends, and that AEM induces systematic exploration-to-exploitation transitions across runs.
3.4 Detailed, Sentence-Based Technical Breakdown
This is a method paper grounded in theoretical analysis. Its core idea is that response-level relative surprisal—how much more or less likely a sampled response is compared to the policy's average response at that state—determines whether a policy update increases or decreases entropy, and that by rescaling advantages proportionally to this quantity, one can adaptively control the exploration-exploitation balance without any external supervision.
Theoretical Foundation: What Is Response-Level Entropy and Why Does It Matter?
Before presenting AEM itself, the paper builds a theoretical framework that connects response-level entropy to policy-level entropy and characterizes how individual sampled responses drive entropy dynamics during RL training. This framework serves two purposes: it justifies why response-level entropy is a principled signal for credit assignment (rather than an arbitrary heuristic), and it reveals the specific functional form—interaction between advantage and relative surprisal—that motivates AEM's modulation rule.
Theorem 3.2.1: Token, response, and policy entropy are structurally nested.
The paper first establishes a hierarchical relationship between three levels of entropy:
- Token-level entropy
$H_\ell(a_t, s_t)$is the entropy of the categorical distribution over the next token, conditioned on the state and previously generated tokens. For a single token position$\ell$within a response, it is defined as:
where $p_\theta(y \mid s_t, y_{<\ell})$ is the model's predicted probability for token $y$ at position $\ell$ given the state $s_t$ and all previous tokens $y_{<\ell}$ in the response, and $\mathcal{V}$ is the vocabulary. This quantity measures how uncertain the model is about the very next token—high values (close to $\log |\mathcal{V}|$) mean the model is spreading probability mass across many tokens; low values mean the model is confident about which token comes next.
- Response-level entropy
$H_{\text{resp}}(s_t)$is the entropy of the distribution over complete responses at state$s_t$. A "response" here is an entire multi-token output—for example, a tool call with arguments, or a reasoning paragraph followed by an action. It is defined as:
where $\pi_\theta(a_t \mid s_t)$ is the model's probability of generating the complete response $a_t$ given state $s_t$, $\mathcal{A}_t$ is the space of all possible responses at that state, and $S(a_t \mid s_t) = -\log \pi_\theta(a_t \mid s_t)$ is the response surprisal—the negative log-probability of the complete response. The response-level entropy is the expected surprisal over the response distribution.
- Policy entropy
$H_{\text{policy}}$is the expected sum of response-level entropies over all states visited during on-policy rollouts from the initial state distribution: where$\mathcal{D}$is the distribution of initial states (prompts) in the training data,$\tau = (s_0, a_0, \ldots, s_{T-1}, a_{T-1})$is a trajectory sampled from the current policy, and$T$is the trajectory length.
What Theorem 3.2.1 establishes: The three entropy quantities are connected by a chain of expectations. Response-level entropy is the expected sum of token-level entropies over the tokens in a response:
This means that response-level entropy collapses the per-token uncertainty into a single scalar per response by taking the expectation over response generation. The indicator $\mathbf{1}_{\{\ell \leq |a_t|\}}$ ensures we only sum over token positions that actually exist in the sampled response (since responses have variable length).
Policy entropy is then the expected sum of response-level entropies across all states:
Why this hierarchy matters for AEM's design: The nesting relationship tells us two things. First, modulating response-level entropy (which is what AEM does) directly affects policy entropy through the expectation over states—so response-level interventions propagate to the global training dynamics. Second, response-level entropy is less sensitive to token-level sampling noise than individual token entropies, because it averages over many tokens within a response (the same averaging that makes full-sequence log-probabilities more stable than per-token log-probabilities). This makes it a more robust signal for credit assignment than operating at the token level. The paper's statement that response-level entropy is "less sensitive to token-level sampling variation" (Section 3.1) reflects this hierarchical smoothing.
A subtlety worth noting: The equality $H_{\text{resp}}(s_t) = \mathbb{E}[\sum H_\ell]$ holds in expectation but not pathwise. For any single sampled response, the sum of its per-token entropies $\sum H_\ell$ is a random variable whose expectation equals $H_{\text{resp}}$. This is the point of connection to Doob's decomposition (Appendix F.4): the pathwise sum $\sum H_\ell$ differs from $H_{\text{resp}}$ by a martingale term, making it a noisy but unbiased proxy. AEM exploits this by using $\sum H_\ell$ (the predictable component) as a practical estimator for relative surprisal, as I will explain in the modulation mechanism section.
Theorem 3.2.2: The Entropy Drift Formula
This is the paper's central theoretical result—the one that directly motivates AEM's modulation rule. It answers the question: if you apply a natural-gradient update to the policy based on a single sampled response with advantage $A(a, s)$, how does the policy's entropy change?
The natural gradient setup. The paper analyzes policy updates on the probability simplex—the geometric space of all possible categorical distributions over responses—equipped with the Fisher-Rao metric. This metric is the local quadratic approximation of the KL divergence: for two nearby policies $\pi$ and $\pi + \delta$, the KL divergence is approximately $\frac{1}{2} g_\pi(\delta, \delta)$, where $g_\pi(u, v) = \sum_a u_a v_a / \pi_a$. The natural gradient $\text{grad}_F$ with respect to this metric produces parameterization-invariant updates, meaning the geometry of policy change depends only on the distributions themselves, not on the particular neural network architecture used to parameterize them.
The objective for a sampled response. For a sampled response $a$ at state $s$ with advantage $A(a, s)$, the policy optimization surrogate objective is:
This is the standard policy gradient objective: it increases the log-probability of the sampled response proportionally to its advantage (if advantage is positive, increase probability; if negative, decrease). In the natural gradient setting, the update direction in policy space is $\text{grad}_F \ell_a(\pi)$.
The key computation. The paper computes the directional derivative of response-level entropy along this update direction—i.e., how much the entropy changes per unit of policy movement in the direction prescribed by the advantage-weighted update:
where $\langle \cdot, \cdot \rangle_{\text{Fisher-Rao}}$ is the inner product under the Fisher-Rao metric. The inner product of two gradients tells us how much the first function changes when we move along the direction of the second function's gradient.
The result:
where $A(a, s)$ is the advantage of the sampled response, $S(a \mid s) = -\log \pi_\theta(a \mid s)$ is the response surprisal (how unlikely this specific response was), and $H_{\text{resp}}(s)$ is the response-level entropy (the average surprisal over all possible responses at this state).
What this equation computes in operational terms: For a given response $a$ at state $s$, take its advantage $A$ (positive for good responses, negative for bad ones) and multiply it by the relative surprisal $S - H_{\text{resp}}$—how much more or less surprising this response is compared to the average response at this state. The sign of this product determines the direction of entropy change:
- If
$A > 0$(good response) and$S > H_{\text{resp}}$(response is more surprising than average), then$D^{\text{resp}}_{\text{RL}} > 0$: entropy increases. - If
$A > 0$and$S < H_{\text{resp}}$(response is less surprising than average—a "safe" good response), then$D^{\text{resp}}_{\text{RL}} < 0$: entropy decreases. - If
$A < 0$(bad response) and$S > H_{\text{resp}}$(surprisingly bad—an unusual mistake), then$D^{\text{resp}}_{\text{RL}} < 0$: entropy decreases (the policy tightens around avoiding this unusual error). - If
$A < 0$and$S < H_{\text{resp}}$(predictably bad—a common mistake the policy often makes), then$D^{\text{resp}}_{\text{RL}} > 0$: entropy increases (the policy spreads probability mass away from this low-probability region to explore alternatives).
The case that matters most for exploration is the last one: common bad responses get high probability under the current policy, so their surprisal is low. When they receive negative advantages, the entropy-increasing effect pushes the policy to try something different. The case that matters most for exploitation is the third one: when a good response is also high-probability (low surprisal), the update further concentrates probability on it, reducing entropy.
Aggregation to policy-level entropy drift. Under the assumption that the rollout distribution is frozen (gradients do not propagate through the state visitation distribution), the policy-level entropy drift induced by a single response $a$ at state $s$ is the visitation-weighted sum of response-level drifts:
where $P_{s_0 \sim \mathcal{D}, \tau \sim P_\theta}[s_t = s]$ is the probability that the policy visits state $s$ at time step $t$ during on-policy rollouts. This sum simply says that if state $s$ is visited frequently, entropy changes at that state have a proportionally larger effect on overall policy entropy.
Why this form is significant (what alternatives would miss): The key insight is the interaction structure $A \times (S - H_{\text{resp}})$. A naive approach might use entropy alone as a signal (e.g., "add more exploration pressure when entropy is low"), but this would ignore the directionality provided by advantage—it would encourage exploration even when the policy is already exploring good regions. A naive approach might use advantage alone (which is what the base RL algorithm does), but this ignores whether the response is a typical or atypical sample from the policy, missing the opportunity to differentiate between "this good response is already likely, so double down" versus "this good response was a lucky exploration, so maintain diversity."
The product form also reveals that the sign of entropy drift depends critically on crossing the baseline $H_{\text{resp}}$: responses with surprisal above the entropy mean and responses below it produce qualitatively opposite entropy effects, even with the same advantage sign. This means that merely knowing whether a response is good or bad is insufficient—you need to know how surprising it was relative to the policy's current state to predict or control the entropy dynamics.
Extension to regularized objectives (Remark 3.2.3 and Theorem F.3.1). The paper extends the theorem to the practical case where the RL objective includes entropy regularization and KL penalties:
where $\psi$ is a positive increasing function (so $\beta \psi(H)$ adds an entropy bonus), $\pi_{\text{ref}}$ is a reference policy (typically the initial model before RL), and $\beta, \gamma$ are coefficients. The extended drift formula (proved in Appendix F.3) is:
where $\psi'$ is the derivative of the entropy bonus function, $\text{Var}_{a \sim \pi}(S)$ is the variance of response surprisal (which is always non-negative), and $\text{Cov}_{a \sim \pi}(S, S_{\text{ref}})$ is the covariance between the current policy's surprisal and the reference policy's surprisal for the same response (which can be positive or negative).
What this extended formula reveals: Term (II)—the combined effect of entropy regularization and KL penalty—always adds a positive entropy-expanding force proportional to surprisal variance (higher variance means more room for entropy expansion). Term (III) can either expand or contract entropy depending on whether the two surprisal signals are correlated (if responses that are surprising under the current policy are also surprising under the reference, the covariance is positive, and the KL penalty partially counteracts term (II)). Critically, terms (II) and (III) are state-level effects—they do not depend on which specific response $a$ was sampled, only on properties of the state's response distribution. This means they apply uniformly to all responses at that state and do not change the response-dependent modulation principle captured by term (I). AEM focuses on term (I) because it is the only term that is response-specific and can therefore be used for response-level credit modulation.
From Theory to Practice: Why AEM Modulates Advantages Rather Than Adding an Entropy Objective
Theorem 3.2.2 establishes that the entropy drift of a sampled response is $A \times (S - H_{\text{resp}})$. AEM could, in principle, try to directly control $S - H_{\text{resp}}$ by adding an auxiliary loss that pushes responses toward or away from $H_{\text{resp}}$. The paper instead takes a different approach: rescale the advantage $A$ by a coefficient derived from a proxy for $S - H_{\text{resp}}$.
Why rescale advantages rather than add an entropy term? The paper identifies (Section 4.1) that $H_{\text{resp}}(s_t)$—the state-specific baseline—is "not directly tractable during training" because it would require summing over the entire exponentially large response space. Computing the exact relative surprisal $S - H_{\text{resp}}$ is infeasible. However, the sign of the relative surprisal matters more than its exact magnitude for determining entropy dynamics (Equation 10 in the paper: $\text{sgn}(A \times (S - H_{\text{resp}}))$ determines whether entropy increases or decreases). The modulation approach converts a proxy for relative surprisal into a coefficient $\alpha$ where $\alpha > 1$ indicates lower-than-average surprisal and $\alpha < 1$ indicates higher-than-average surprisal, and then multiplies this coefficient by the base advantage:
When $A > 0$ and $\alpha > 1$ (good response, less surprising than average), the advantage is amplified, strengthening the entropy-decreasing update. When $A < 0$ and $\alpha < 1$ (bad response, more surprising than average—an unusual mistake), the negative advantage is attenuated (made less negative), weakening the entropy-decreasing update and preserving diversity. The complementary cases—$A > 0$, $\alpha < 1$ (good response, surprisingly good) and $A < 0$, $\alpha > 1$ (bad response, predictably bad)—also align with the theoretical sign pattern.
By operating purely through advantage rescaling, AEM requires no changes to the loss function, no new gradient terms, and no additional hyperparameter tuning beyond the temperature $\lambda$. The base RL algorithm's optimizer, learning rate schedule, and clipping mechanisms remain untouched.
The Practical Modulation Mechanism: Building $\alpha_{i,t}$ from Token-Level Entropy
Sections 4.2 and the pseudo-code in Algorithm 1 (Appendix A) specify the exact computation pipeline that converts raw token-level entropy values into the response-level modulation coefficient $\alpha_{i,t}$.
Step 1: Identify response boundaries. The first practical challenge is that the raw RL training data consists of token sequences spanning entire trajectories. The environment does not explicitly mark where one response ends and the next begins. AEM parses each rollout $\tau_i$ into environment-reactive response spans $S_i = \{S_{i,1}, \ldots, S_{i,K_i}\}$, where each span $S_{i,t} = [\text{begin_token}_{i,t}, \text{end_token}_{i,t}]$ corresponds to one complete response generated before the next environment transition.
What counts as a response boundary? The paper notes (Section 3.1): "In agentic RL, the environment typically reacts after a complete response is generated, making the response an effective interaction unit, rather than an individual token." Concretely, a response span ends when the agent issues a tool call, submits a final answer, or otherwise triggers an environment step. The next state observation (e.g., the tool output, the new webpage HTML) begins a new context, and the next response spans from the model's next generation. The implementation details in Appendix G.2 provide specific length limits per benchmark: ALFWorld uses a maximum response length of 512 tokens, WebShop uses 512 tokens, and SWE-bench-Verified uses up to 65,536 tokens per response.
Why response-level granularity is the right choice: The paper explicitly argues against token-level modulation, noting that "token-level entropy [is] sensitive to token-level sampling variation" (Section 3.2). Individual high-entropy tokens within an otherwise low-entropy response should not dominate the credit signal; conversely, a response that is overall low-entropy but contains a few high-entropy tokens due to vocabulary choices (synonyms, formatting) should not be incorrectly flagged as uncertain. By aggregating to the response level, AEM aligns its uncertainty estimate with the granularity at which the environment actually responds, making the modulated credit signal consistent with the causal structure of the interaction.
Step 2: Compute the length-normalized response-level entropy proxy. For each response span $S_{i,t}$, AEM computes:
where $|S_{i,t}|$ is the number of tokens in the response span and $H_\ell(a_t, s_t)$ is the token-level entropy at position $\ell$—the entropy of the model's next-token distribution at that position, computed as $-\sum_{y \in \mathcal{V}} p_\theta(y \mid s_t, y_{<\ell}) \log p_\theta(y \mid s_t, y_{<\ell})$.
What this computes: It averages the per-token entropies across all tokens in the response span. This gives a single scalar per response that captures how uncertain the model was, on average, while generating that response. High $\bar{H}_{i,t}$ means the model was generally uncertain across the tokens in this response—it was "feeling its way" through the generation. Low $\bar{H}_{i,t}$ means the model was confident—it had a clear "opinion" about what tokens to generate.
Why length normalization matters: Different responses have different lengths (e.g., a tool call with many arguments vs. a simple "yes/no" action). Without normalization, longer responses would mechanically have higher summed entropy (more tokens, more accumulated uncertainty), even if each individual token was generated with high confidence. Dividing by $|S_{i,t}|$ makes $\bar{H}_{i,t}$ a scale-free measure of average per-token uncertainty, independent of response length. This is essential for fair comparison within a group that contains responses of varying lengths.
Why use the sum of token-level entropies rather than response surprisal directly? Appendix F.4 provides the theoretical justification via Doob's decomposition. The response surprisal $S(a \mid s) = -\log \pi_\theta(a \mid s) = -\sum_{\ell} \log p_\theta(y_\ell \mid s_t, y_{<\ell})$ can be decomposed as:
where $M_L$ is a zero-mean martingale (a random term that has expectation zero when conditioned on the prefix). The sum of token-level entropies $\sum H_\ell$ is the predictable component of the response surprisal—it is what you can estimate before seeing the actual tokens, based only on the model's uncertainty. The martingale term $M_L$ captures the specific randomness of which tokens were actually sampled. By using $\sum H_\ell$ (or its length-normalized version $\bar{H}_{i,t}$) as a proxy for $S(a \mid s)$, AEM strips out the token-sampling noise and retains only the predictable component. This is why the paper calls it a "predictable proxy" (Section 4.2): it is $\mathcal{F}_{\ell-1}$-measurable, meaning you can compute it before seeing the actual token at position $\ell$, whereas the true surprisal $-\log p_\theta(y_\ell)$ is only known after sampling.
Practical computation: The entropy values $H_\ell$ are obtained during the same recomputation pass that GRPO already performs to compute old-policy log-probabilities for the importance sampling ratio $\rho_{i,t}(\theta) = \pi_\theta(o_{i,t}) / \pi_{\theta_{\text{old}}}(o_{i,t})$. The model forward pass produces logits for each token position; from these logits, you can compute both the log-probability of the actually-sampled token (needed for the GRPO update) and the full entropy of the categorical distribution (needed for AEM). This is why AEM introduces no additional forward pass—the entropy computation reuses the logits that are already computed for the base RL algorithm. Section 5.4 confirms this empirically: the entropy-related computation accounts for only 1.1% of per-iteration training time on ALFWorld.
Step 3: Group-wise min-max normalization. Once $\bar{H}_{i,t}$ is computed for every response in a group $G$ (where a group contains all responses from all trajectories generated from the same prompt), AEM applies min-max scaling:
where $\varepsilon = 10^{-8}$ is a small stability constant to prevent division by zero when all responses have identical entropy proxies.
What this computes: For each response, $\tilde{H}_{i,t}$ is a normalized score between 0 and 1 indicating where this response's entropy proxy falls relative to the most-confident and least-confident responses in the same group. $\tilde{H} = 0$ means this response had the lowest average per-token entropy in the group (the most confident response); $\tilde{H} = 1$ means it had the highest (the most uncertain response).
Why group-wise normalization rather than batch-wise or trajectory-wise? The ablation study in Appendix E (Table 3) compares three normalization strategies: within-group (the default), within-trajectory, and within-batch. Group-wise normalization performs best because it ensures that responses being compared come from the same prompt, making entropy values directly comparable. Trajectory-level normalization has weaker statistics (a trajectory contains only its own responses—typically 5–15 for ALFWorld/WebShop), leading to noisier normalization. Batch-level normalization mixes responses from different prompts (different tasks, different difficulty levels), introducing entropy bias—an "easy" prompt might naturally produce lower-entropy responses than a "hard" prompt, making across-prompt comparisons misleading. The paper states: "+AEM_batch-norm ... avoids the potential entropy bias caused by mixing tasks, since all normalized responses come from the same prompt" (Appendix E).
Handling the degenerate case. If the spread of entropy proxies within a group is very small ($\max \bar{H} - \min \bar{H} < 0.1$), all responses in the group have essentially the same uncertainty level. In this case, AEM sets $\alpha_{i,t} = 1$ for all responses, meaning it falls back to the base advantage estimator without modulation. This guard prevents AEM from amplifying meaningless noise when there is no real variation in response uncertainty within the group. The threshold of 0.1 is a design choice not deeply ablated but motivated by "avoid[ing] sampling noise" (Section 4.2).
Step 4: Temperature-parameterized softmax to produce raw coefficients.
where $\lambda = 1$ (fixed across all experiments, per Appendix G.2) is the temperature parameter.
What this computes: This applies a negative exponential map from $\tilde{H} \in [0,1]$ to $\alpha^{\text{raw}} \in [\exp(-\lambda), 1]$. When $\tilde{H} = 0$ (most confident response), $\alpha^{\text{raw}} = 1$. When $\tilde{H} = 1$ (most uncertain response), $\alpha^{\text{raw}} = \exp(-\lambda) \approx 0.368$ for $\lambda = 1$. The mapping is monotone decreasing: higher uncertainty → lower coefficient.
Why the negative exponential form? The negative sign in $-\lambda \tilde{H}_{i,t}$ is critical—it implements the directionality from the theory. Theorem 3.2.2 shows that $S - H_{\text{resp}}$ appears with a positive sign in the entropy drift: $D = A \times (S - H_{\text{resp}})$. The proxy $\bar{H}$ estimates $S$ (the response surprisal, via its predictable component). Within a group, $\tilde{H}$ approximates how $S$ ranks relative to other responses. The base advantage $A^{\text{base}}$ carries the sign information (positive for good, negative for bad). By multiplying $A^{\text{base}}$ by a decreasing function of $\tilde{H}$, AEM modulates the effective advantage magnitude in a way that aligns with the theoretical entropy drift: when $\tilde{H}$ is high (high uncertainty, roughly $S > H_{\text{resp}}$), the coefficient $\alpha < 1$ attenuates the advantage; when $\tilde{H}$ is low (low uncertainty, roughly $S < H_{\text{resp}}$), $\alpha > 1$ amplifies the advantage.
The ablation study confirms this directionality is essential (Appendix E, Table 3). +AEM_reverse flips the sign in the exponential to $\alpha_{i,t} = \exp(+\tilde{H}_{i,t})$ (using $\lambda = -1$), which maps high uncertainty to high coefficients. This reversed variant performs "substantially worse than GRPO" (Score drops from 83.6 to 77.2), indicating that "an incorrect entropy-to-credit mapping is actively harmful ... this reversed mapping tends to exacerbate entropy collapse in the early stage of training, while suppressing beneficial exploitation later on." The correct direction—downweighting high-uncertainty responses, upweighting low-uncertainty responses—is what enables AEM's exploration-exploitation transition.
The temperature parameter $\lambda$ controls modulation strength. At $\lambda = 0$, $\alpha^{\text{raw}} = 1$ for all responses—AEM has no effect. As $\lambda$ increases, the coefficient range widens (e.g., at $\lambda = 2$, the range is $[\exp(-2), 1] \approx [0.135, 1]$), making modulation more aggressive. The paper uses $\lambda = 1$ throughout and does not ablate this choice extensively—the single value appears sufficient to produce consistent gains across benchmarks and model sizes. This is both a strength (simplicity) and a limitation (the optimal $\lambda$ might be task-dependent; the paper does not explore adaptive temperature schedules).
Step 5: Self-calibration to maintain the group average at 1.
What this computes: It divides each raw coefficient by the group's mean coefficient. This ensures that the average of $\alpha_{i,t}$ across the group is exactly 1 (up to the $\varepsilon$ stabilization). The modulated advantages $A^{\text{AEM}}_{i,t} = \alpha_{i,t} A^{\text{base}}_{i,t}$ then have the same scale as the base advantages on average—AEM redistributes advantage magnitude within the group (amplifying some responses, attenuating others) without changing the overall learning rate.
Why self-calibration is necessary: Without it, $\exp(-\lambda \tilde{H}_{i,t})$ produces coefficients that are all ≤ 1 (since $\tilde{H} \geq 0$), meaning all advantages would be attenuated, effectively reducing the learning rate. Self-calibration recenters the coefficients so that $\alpha > 1$ for responses with $\tilde{H}$ below the group average and $\alpha < 1$ for those above—a pure relative rescaling. This is consistent with the theory, which depends on relative surprisal $S - H_{\text{resp}}$, not absolute surprisal.
The ablation study (Appendix E) compares the full AEM against +AEM_shuffle, which "first computes $\alpha$ in the same way as AEM, but then randomly permutes the coefficients within each group before applying them to response advantages." This variant "remains clearly worse than +AEM" (Score 85.6 vs. 86.4), but still outperforms GRPO (83.6) in terms of Score (though Success Rate drops to 64.8 vs. GRPO's 65.0). The paper concludes: "the improvement does not come merely from introducing an additional fine-grained rescaling of response-level advantages. Instead, the key factor is whether the entropy signal is assigned to the corresponding response." The random permutation destroys the alignment between a response's own uncertainty and its credit signal, confirming that the modulation must be response-specific to be effective.
Step 6: Apply modulation.
The modulated advantage $A^{\text{AEM}}_{i,t}$ replaces $A^{\text{base}}_{i,t}$ in the policy gradient computation. For GRPO, this means the normalized group-based advantage $\hat{A}_i$ (Equation 68 in Appendix G.1) is multiplied by $\alpha_{i,t}$ for each token in response span $S_{i,t}$. The advantage is applied uniformly across all tokens in the same response—if $\alpha_{i,t} = 1.2$, every token in that response gets a 1.2× amplified advantage.
Why uniform modulation across tokens within a response? The response is the environment-reactive unit—the environment state only changes after the complete response. All tokens within a response jointly determine the action taken, so they should share the same credit signal. Token-level modulation (assigning different $\alpha$ to different tokens within the same response) would misalign with the causal structure: the first few tokens of a response are not independently "good" or "bad"—their effect depends on the rest of the response that follows.
The Exploration-Exploitation Transition: How AEM Achieves Adaptive Behavior Without Scheduling
Section 4.3 explains the mechanism by which AEM naturally transitions from promoting exploration early in training to promoting exploitation later, without any explicit scheduling, annealing, or external difficulty estimation.
The mechanism relies on the evolving balance of positive and negative responses. Early in RL training, when the policy has not yet learned effective strategies, most sampled responses lead to failure—the batch contains predominantly negative-advantage responses ($A < 0$). Late in training, as the policy improves, an increasing proportion of responses succeed—the batch contains more positive-advantage responses ($A > 0$). AEM's modulation amplifies or attenuates advantages differently depending on their sign and the response's uncertainty, producing opposite entropy effects in the two phases.
For negative responses ($A < 0$), which dominate early training:
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High-uncertainty negative responses (
$\bar{H}$large →$\alpha < 1$): The negative advantage is attenuated (made less negative). This weakens the entropy-decreasing pressure that would otherwise penalize the response heavily. Since the response was produced under high uncertainty, AEM treats it as a tentative exploration that happened to fail, rather than a confident mistake that should be aggressively penalized. Entropy is preserved—the policy does not prematurely collapse away from this high-uncertainty region. -
Low-uncertainty negative responses (
$\bar{H}$small →$\alpha > 1$): The negative advantage is amplified (made more negative). This strengthens the entropy-increasing pressure—the policy was confident about a response that turned out to be bad, so AEM aggressively pushes probability mass away from this region, forcing the policy to explore alternatives. The paper states: "amplify entropy-increasing" for this case (Section 4.3, Equation 17).
For positive responses ($A > 0$), which dominate late training:
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High-uncertainty positive responses (
$\bar{H}$large →$\alpha < 1$): The positive advantage is attenuated. This weakens the entropy-increasing pressure that would otherwise reinforce a lucky guess. If a high-uncertainty response happens to succeed, the policy should not overcommit to that specific response—it was a fortunate exploration, not a reliable strategy. AEM prevents the policy from chasing noise. -
Low-uncertainty positive responses (
$\bar{H}$small →$\alpha > 1$): The positive advantage is amplified. This strengthens the entropy-decreasing pressure—the policy was confident about a response that turned out to be good, so AEM aggressively reinforces it, concentrating probability mass and enabling convergence.
The net effect across the batch. In early training, when most responses are negative, the aggregate entropy pressure from AEM is entropy-increasing: many high-uncertainty negative responses get their penalties attenuated, and many low-uncertainty negative responses get their penalties amplified, both pushing the policy toward broader exploration. In late training, when most responses are positive, the aggregate pressure flips to entropy-decreasing: many low-uncertainty positive responses get their rewards amplified, concentrating the policy on proven strategies, while high-uncertainty positive responses (lucky guesses) are suppressed.
Formal characterization (Equation 16). The paper shows that AEM shifts the entropy drift relative to the base RL algorithm purely based on the sign of the advantage:
where $\tilde{D}$ denotes the practical entropy drift direction (as opposed to the theoretical $D$ from Theorem 3.2.2). Since $(\alpha - 1)^2 \geq 0$, the sign of the shift is entirely determined by the advantage sign. For $A < 0$, AEM shifts toward higher entropy; for $A > 0$, AEM shifts toward lower entropy. This means AEM systematically adds exploration pressure on failures and exploitation pressure on successes, and the relative prevalence of failures vs. successes during training naturally determines which pressure dominates.
Empirical validation of the transition (Analysis C, Section 5.3, Figures 4–5). The paper provides direct evidence that this mechanism operates as described:
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Figure 4 shows entropy trajectories over 150 training steps for three runs each of GRPO and GRPO+AEM on Qwen2.5-1.5B. The GRPO baselines exhibit "an abrupt entropy collapse at the beginning of training and then remain in a relatively flat entropy regime"—entropy plummets in the first ~10 steps and then stagnates, indicating premature concentration and limited late-stage optimization. In contrast, GRPO+AEM "consistently preserves higher entropy in the early stage and gradually reduces it to a lower range later"—entropy starts higher, declines more gradually, and settles at a lower (more converged) level by the end of training.
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Figure 5 overlays entropy and success rate for a representative pair of runs. AEM maintains higher entropy early (when the success rate is low, ~10–30%), then as the success rate climbs past ~50–60%, AEM's entropy drops below the baseline's, indicating the transition. The final success rate with AEM exceeds the baseline by a clear margin. The paper interprets this as: "AEM maintains higher entropy early on, promoting response diversity. As the success rate increases during training, the training batches contain a growing proportion of positive samples relative to negative ones, under which AEM gradually transitions from entropy-increasing to entropy-decreasing dynamics adaptively."
Why this is more sophisticated than a fixed entropy schedule. A fixed entropy bonus that anneals over time (e.g., start with $\beta = 0.1$, decay to $\beta = 0.01$) applies the same exploration pressure regardless of whether the policy is actually performing well or poorly. If the policy gets stuck early, a decaying entropy bonus provides decreasing help just when it's most needed. AEM's transition is performance-gated: the shift from exploration to exploitation occurs naturally as the policy actually starts succeeding more often, which means it adapts to the policy's genuine improvement rate rather than following a predetermined schedule.
A subtle point on the early-entropy-collapse problem. The paper (Section 1, referencing Shen, 2026) notes that "premature entropy collapse in the early phase of training can cause degraded downstream performance." This is a recognized pathology in LLM RL: the policy quickly concentrates on a small set of high-probability responses, loses diversity, and then cannot escape local optima because it no longer explores alternatives. AEM's entropy-preserving effect on negative responses directly counteracts this: by attenuating penalties on high-uncertainty failures, it prevents the policy from over-penalizing exploration, even when most early attempts fail.
Analysis A: Empirical Validation of the $\alpha - 1$ — $-(S - H_{\text{resp}})$ Relationship
The paper conducts a Monte Carlo study (Section 5.3, Analysis A, Figure 2) to verify that the practical modulation coefficient $\alpha$ actually captures the theoretical quantity $-(S - H_{\text{resp}})$ that Theorem 3.2.2 identifies as the key variable.
Setup: The authors probe $n = 64$ states (environment observations at different points in trajectories). For each state, they sample $K = 64$ responses from the current policy and compute:
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Monte Carlo response-level entropy:
$H^{\text{MC}}_{\text{resp}}(s) = \frac{1}{K} \sum_{j=1}^K S(a_j \mid s)$, where$S(a_j \mid s) = -\log \pi_\theta(a_j \mid s)$is the exact response surprisal for each sampled response. This estimates the true$H_{\text{resp}}$by averaging over a large number of samples. -
Monte Carlo relative surprisal:
$\Delta S^{\text{MC}} := -(S(a \mid s) - H^{\text{MC}}_{\text{resp}}(s))$, which approximates$-(S - H_{\text{resp}})$—the negative of the theoretical quantity that governs entropy drift. -
AEM coefficient deviation:
$\alpha - 1$, where$\alpha$is computed using the standard AEM pipeline (group-wise normalization, softmax, self-calibration) with the same responses.
Results (Figure 2): The scatter plot shows a clear positive relationship between $\alpha - 1$ and $\Delta S^{\text{MC}}$, with a Pearson correlation $r = 0.63$. Moreover, the sign of $\alpha - 1$ agrees with the sign of $\Delta S^{\text{MC}}$ in 55 out of 64 states (85.9% agreement). This means:
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When
$\alpha > 1$(AEM amplifies the response), the relative surprisal$S - H_{\text{resp}}$is typically negative (the response is less surprising than average). This is consistent: the theory says that for$S < H_{\text{resp}}$and$A > 0$, entropy decreases (good exploitation), so amplifying the advantage accelerates convergence. Conversely, for$S < H_{\text{resp}}$and$A < 0$, entropy increases (bad exploit move → explore), so amplifying the penalty pushes exploration. -
When
$\alpha < 1$(AEM attenuates the response), the relative surprisal is typically positive (the response is more surprising than average). For$S > H_{\text{resp}}$and$A > 0$, entropy increases (lucky guess → don't overcommit), so attenuating the advantage prevents overfitting to noise. For$S > H_{\text{resp}}$and$A < 0$, entropy decreases (tentative failure → don't over-penalize exploration), so attenuating the penalty preserves diversity.
What the correlation of 0.63 means: It is moderately strong but not perfect. The remaining variance comes from several sources: the proxy $\bar{H}$ uses the predictable component (sum of token entropies) rather than true surprisal (which includes the martingale noise from actual token samples); the group-wise normalization approximates $H_{\text{resp}}$ using within-group statistics rather than the true expectation over all possible responses; and the softmax with temperature $\lambda = 1$ introduces a specific functional form that may differ from the ideal mapping. The authors acknowledge this in Limitations (Appendix B): "it is still a heuristic surrogate rather than an exact estimator. Consequently, AEM does not guarantee optimal entropy modulation, and its behavior may depend on the quality and diversity of the sampled rollout group."
Nevertheless, the 85.9% sign agreement is strong enough that AEM's modulation direction aligns with the theoretical prescription in the large majority of cases, which explains why the method is effective despite using an imperfect proxy.
Analysis B: Validating That $A(\alpha - 1)$ Governs Entropy Trends
Section 5.3, Analysis B (Figure 3) provides a causal intervention to verify that $A(\alpha - 1)$—the interaction between advantage sign and coefficient deviation—is what actually drives the observed entropy dynamics, rather than some other property of AEM.
Setup: The authors run GRPO training with two gradient-masking strategies for the first 50 training steps:
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Masking 1: Only include responses where
$A(\alpha - 1) < 0$—i.e.,$(A > 0, \alpha < 1)$(good, high-uncertainty) or$(A < 0, \alpha > 1)$(bad, low-uncertainty). From the theory, this corresponds to$\text{sgn}(\tilde{D}_{\text{RL}}) = -1$→ entropy should increase. -
Masking 2: Only include responses where
$A(\alpha - 1) > 0$—i.e.,$(A > 0, \alpha > 1)$or$(A < 0, \alpha < 1)$. From the theory, this corresponds to$\text{sgn}(\tilde{D}_{\text{RL}}) = +1$→ entropy should decrease.
Results (Figure 3): The two masking strategies produce "clearly diverging entropy trends." Masking 1 (entropy-increasing sign) shows steadily rising entropy over the 50 steps. Masking 2 (entropy-decreasing sign) shows steadily falling entropy. This confirms that $A(\alpha - 1)$ is causally responsible for the direction of entropy dynamics—masking all responses of one sign and keeping the other produces the predicted monotonic entropy trend, rather than a mixed or unpredictable pattern.
Why this matters beyond correlation: Analysis A showed that $\alpha - 1$ correlates with $-(S - H_{\text{resp}})$. Analysis B shows that conditioning gradient updates on $A(\alpha - 1)$ actually produces the predicted entropy dynamics in training. Together, these analyses close the loop from theory (entropy drift ∝ $A \times (S - H_{\text{resp}})$) to practical coefficient (α proxies $-(S - H_{\text{resp}})$) to observed behavior (entropy moves in the predicted direction). This is stronger evidence than either piece alone—it rules out the possibility that the correlation in Analysis A is spurious or that AEM's benefits come from some other mechanism (e.g., variance reduction, implicit learning rate scheduling) rather than entropy modulation.
Summary of Design Choices and Their Justifications
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Response-level rather than token-level modulation: Matches the environment-reactive granularity, reduces sensitivity to token-level sampling variation, and is theoretically justified by Theorem 3.2.1's hierarchical structure. Token-level modulation would misalign with the causal structure of agent-environment interaction and would be vulnerable to high-frequency noise in per-token entropy fluctuations.
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Predictable entropy proxy
$\sum H_\ell$rather than exact surprisal$S = -\log \pi$: The Doob decomposition (Appendix F.4) shows that$\sum H_\ell$captures the predictable component of response surprisal, stripping out the non-predictable martingale noise from actual token samples. Using exact surprisal (which AEM could compute, since it already has the log-probabilities) would introduce sampling noise and reduce the stability of the modulation signal. -
Length normalization
$\frac{1}{|S_{i,t}|} \sum H_\ell$: Makes the entropy proxy scale-free, preventing longer responses from mechanically receiving different modulation than shorter ones. Without it, verbose responses would be systematically flagged as "high uncertainty" simply because they have more tokens, regardless of per-token confidence. -
Group-wise min-max normalization: Ensures responses are compared to others from the same prompt, avoiding cross-task entropy bias (easy tasks naturally produce lower-entropy responses than hard tasks). Batch-wise normalization (Appendix E, Table 3) performs worse because it mixes entropy levels from different tasks, making the normalization less meaningful. The fallback to
$\alpha = 1$when the range is < 0.1 prevents amplification of noise in degenerate cases. -
Negative softmax
$\exp(-\lambda \tilde{H})$with self-calibration: The negative sign is essential—reversing it (AEM_reverse, Appendix E) produces substantially worse performance than the baseline, confirming that the direction of entropy-to-modulation mapping is critical. The self-calibration maintains the average coefficient at 1, ensuring AEM purely redistributes advantage magnitude rather than scaling the overall learning rate. -
Uniform modulation across all tokens in a response: Consistent with the response being the environment-reactive unit. All tokens jointly determine the action, so they should share the same credit signal. Per-token modulation within a response would introduce artificial and potentially harmful gradient heterogeneity.
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Single hyperparameter
$\lambda = 1$: The paper makes a deliberate choice to use a single, fixed temperature across all benchmarks, model sizes, and RL backbones. This extreme simplicity—no per-task tuning, no annealing schedule—is a design goal: AEM should work out-of-the-box as a plug-in. The fact that it produces consistent gains across ALFWorld, WebShop, and SWE-bench-Verified with this single setting is evidence that the method is robust to$\lambda$, though the paper does not report a systematic sweep over$\lambda$to characterize the sensitivity. -
No auxiliary models, no extra forward passes, no structural assumptions: The entropy values come from the same logits computed for the base RL algorithm's importance sampling. The group structure is the same group used by GRPO for advantage normalization. No new models are trained or loaded. AEM's only additions to the training loop are the response-boundary parsing, entropy aggregation, and coefficient computation—all operations on already-available tensors.
4. Key Insights and Innovations
Innovation 1: Reframing Credit Assignment as Entropy Dynamics Control
The paper's most distinctive conceptual move is recasting the credit assignment problem as one of controlling entropy dynamics in policy space. Prior work on credit assignment in multi-turn agentic RL asks: "How do we determine which steps contributed to success or failure?" and answers that question by trying to estimate per-step value—either through external process reward models (Lightman et al., 2023), learned critics (Schulman et al., 2017), tree-structured rollouts (Ding and Ye, 2026; Cao et al., 2026), or trajectory-structure-based heuristics (Feng et al., 2025; Wang et al., 2026). Every one of these approaches attempts to infer what the credit should have been based on observed outcomes, structure, or auxiliary supervision.
AEM asks a fundamentally different question: "Given the sparse outcome reward we already have, how should we modulate the entropy consequences of each sampled response to guide the policy from exploration to exploitation?" Instead of trying to estimate which steps were "good" or "bad," AEM uses the policy's own uncertainty about each response—captured by response-level entropy—to determine how aggressively to reinforce or penalize that response. The theoretical contribution (Theorem 3.2.2) is what makes this reframing possible: it shows that entropy drift under a policy update is governed jointly by the response's advantage and its relative surprisal, not by the advantage alone. This provides a principled justification for why entropy should serve as a credit modulation signal: it is not an arbitrary heuristic but a quantity that directly shapes the policy's exploration-exploitation dynamics in a theoretically predictable way.
The significance of this reframing extends beyond AEM's specific implementation. It shifts the field's mental model of credit assignment from "estimate missing step-level rewards" to "modulate the policy gradient's entropy consequences using intrinsic signals." This opens up an alternative research direction: rather than trying to impute what the reward signal should have been at intermediate steps—which always requires assumptions about the causal structure of trajectories or the availability of auxiliary supervision—one can instead shape how existing outcome-level advantages affect the policy distribution using signals that are already available from the policy itself. The paper's own evidence for this reframing's power comes from the analysis studies in Section 5.3: Figure 2 establishes the consistency between AEM's modulation coefficient and the theoretical relative surprisal (r = 0.63, sign agreement 85.9%), and Figure 3 demonstrates causally that A(α − 1) governs entropy dynamics, confirming that the theoretical reframing maps to actual training behavior.
This is a fundamental conceptual reframing, not an incremental refinement. Prior methods all operate within the paradigm of "reconstruct the missing per-step reward signal." AEM operates within the paradigm of "modulate gradient entropy effects using the policy's intrinsic uncertainty," and Theorem 3.2.2 provides the theoretical bridge between these paradigms.
Innovation 2: Entropy Dynamics as an Exploration-Exploitation Gating Mechanism Without External Scheduling
The paper's second conceptual innovation is the discovery that entropy dynamics can serve as an automatic, performance-gated mechanism for transitioning from exploration to exploitation, eliminating the need for hand-designed schedules or external difficulty estimation. This is, in spirit, the multi-turn agentic RL analog of the difficulty-conditioned compute-optimal scaling insight from earlier work on test-time compute allocation, but it operates through a completely different mechanism: rather than estimating problem difficulty to select a strategy, AEM lets the evolving balance of positive and negative samples naturally gate the transition.
Prior approaches to managing the exploration-exploitation trade-off in LLM RL typically use one of three mechanisms. The most common is an entropy bonus added to the policy objective (Mnih et al., 2016b; Xu et al., 2025b), sometimes with a fixed annealing schedule that reduces the bonus over training steps. This applies uniform exploration pressure regardless of the policy's actual performance—if the policy is stuck or improving slowly, the schedule marches forward anyway, potentially withdrawing exploration pressure when it is most needed. A second approach uses KL regularization toward a reference policy (typically the initial SFT model), which implicitly limits how far the policy can move from its starting distribution and thus constrains entropy collapse, but at the cost of potentially limiting the policy's ability to converge on strategies that differ significantly from the initialization. A third approach in single-turn settings uses difficulty estimation to allocate compute or entropy budgets per-prompt, but this requires additional infrastructure and does not directly translate to multi-turn settings where "difficulty" is less well-defined and changes over the course of a trajectory.
AEM's mechanism is qualitatively different. The transition from exploration to exploitation is not scheduled—it is emergent from the composition of per-sample modulation effects. Equation 16 quantifies this: AEM shifts the entropy drift relative to the base algorithm purely based on the sign of the advantage (sgn(AEM shift) = −sgn(A)). For negative-advantage responses (predominantly failures, which dominate early training), AEM adds entropy-increasing pressure—preserving diversity, preventing premature entropy collapse. For positive-advantage responses (successes, which become more prevalent as training progresses), AEM adds entropy-decreasing pressure—concentrating probability on reliable strategies, enabling convergence. The relative frequency of positive vs. negative responses in each batch determines which pressure dominates, creating a feedback loop: as the policy improves → more successes → more exploitation pressure → faster convergence → even more successes.
This is significant because it decouples exploration-exploitation control from both manual scheduling and external estimation. The policy's own performance trajectory becomes the controller. Figure 4 in Section 5.3 provides the direct evidence: GRPO baselines show "abrupt entropy collapse at the beginning of training and then remain in a relatively flat entropy regime"—the policy diversifies poorly and then stagnates. GRPO+AEM shows "consistently higher entropy in the early stage and gradually reduced entropy to a lower range later"—diversity is preserved when it is needed (during early learning) and then surrendered naturally as successful strategies emerge. Figure 5 overlays this with success rate, showing that the entropy transition coincides with the policy crossing a performance threshold (roughly 50–60% success rate), confirming the performance-gated nature of the mechanism.
This is a fundamental shift in how to think about exploration-exploitation in LLM RL. Rather than treating entropy control as a hyperparameter to be tuned or a schedule to be designed, it treats entropy dynamics as an emergent property of credit modulation that automatically adapts to the policy's learning trajectory. The intellectual connection to the broader RL literature is noteworthy: this is philosophically similar to how curiosity-driven exploration methods (e.g., intrinsic motivation) use the agent's own prediction errors to gate exploration, but AEM achieves it purely through advantage rescaling without any auxiliary prediction task.
Innovation 3: Lifting Entropy Analysis from Token-Level to Response-Level as the Correct Granularity for Agentic RL
The third innovation is a diagnostic insight with methodological implications: in multi-turn agentic RL, the natural unit for uncertainty estimation and credit modulation is the complete response, not the individual token. This may seem obvious in retrospect—the environment only reacts after a full response, so the response is the causal unit of interaction—but prior entropy-aware methods in LLM RL uniformly operated at the token level, treating each token's entropy as an independent signal for regularization or gradient recalibration (Wang et al., 2025b; Dong et al., 2026a; Cui et al., 2025).
The paper provides both theoretical and practical justification for why response-level analysis is superior. Theorem 3.2.1 establishes the formal nesting: response-level entropy is the expectation of the per-token entropy sum, and policy entropy is the expectation of the response-level entropy sum. This means the response level is a structurally faithful intermediate representation—it captures the uncertainty that matters for environment interaction while being "less sensitive to token-level sampling variation" (Section 3.2). The Doob decomposition in Appendix F.4 makes this precise: the response surprisal decomposes into a predictable component (the sum of per-token entropies, which AEM uses) and a martingale noise term. By aggregating to the response level, AEM averages out the martingale noise across tokens within each response, producing a more stable uncertainty signal than per-token entropies.
The practical consequence is that AEM avoids the pathology of token-level methods that can be misled by local vocabulary-level uncertainty. A response that is overall highly confident about its semantic content (e.g., the model "knows" it wants to call search("red shoes")) may still exhibit high per-token entropy at specific positions (e.g., choosing between "red", "crimson", "scarlet" for the color descriptor, or between formatting variants). A token-level method would interpret these local fluctuations as meaningful uncertainty and modulate credit accordingly, even though they reflect superficial variation rather than genuine strategic uncertainty. AEM's response-level aggregation naturally smooths over such innocuous variation while preserving the signal from responses where the model is genuinely uncertain about what action to take (which manifests as consistently elevated per-token entropy across the entire response generation).
The paper's ablation of normalization strategies (Appendix E, Table 3) provides indirect evidence for the importance of response-level granularity. The comparison between group-wise, trajectory-wise, and batch-wise normalization shows that the method is sensitive to how responses are compared—group-wise (same prompt) works best, confirming that relative entropy comparisons are most meaningful when responses are generated under the same conditions. This is consistent with the theoretical framework: the relative surprisal S − H_resp is defined per state, and within-group comparisons approximate same-state comparisons more faithfully than cross-group or cross-trajectory comparisons.
This insight is fundamental in its field-specific implications but incremental in its conceptual novelty—the idea of matching analysis granularity to interaction granularity is well-established in hierarchical RL and options frameworks. However, the paper's specific contribution—identifying that the response (rather than the token or the trajectory) is the correct level for entropy-based credit modulation in LLM agentic RL, and providing the theoretical nesting structure to justify this—is a genuine contribution that should influence how future methods design their uncertainty signals.
Innovation 4: Verifying That Advantage-Entropy Interaction (Not Any Advantage Rescaling) Drives the Benefit
The paper's fourth contribution is a diagnostic finding that sharpens the field's understanding of why certain credit modulation strategies work: it is specifically the correct directional alignment between a response's uncertainty and its advantage rescaling that produces gains, not the mere introduction of response-level advantage heterogeneity. This is established through a pair of ablation studies (Appendix E, Table 3) that are methodologically clean enough to serve as a template for evaluating future credit modulation methods.
The +AEM_shuffle variant preserves every statistical property of AEM's modulation coefficients—their marginal distribution, their range, their within-group variance, and the average magnitude of advantage rescaling—but destroys the correspondence between each response and its own entropy signal by randomly permuting the coefficients within the group. Despite introducing the same amount of advantage heterogeneity as AEM, +AEM_shuffle performs only marginally better than the baseline GRPO (Score 85.6 vs. 83.6) and actually reduces success rate (64.8 vs. 65.0). This demonstrates that advantage rescaling per se is not the active ingredient—the benefit requires that the rescaling be informed by and aligned with each response's own uncertainty.
The +AEM_reverse variant goes further: it preserves the alignment (each response's coefficient is computed from its own entropy) but inverts the mapping direction (high entropy → high coefficient, rather than high entropy → low coefficient). This variant performs "substantially worse than GRPO" (Score 77.2 vs. 83.6), demonstrating that incorrect alignment is actively harmful. The paper's explanation—that the reversed mapping "exacerbates entropy collapse in the early stage of training, while suppressing beneficial exploitation later on"—is precisely what Theorem 3.2.2 would predict: reversing the modulation direction produces entropy-decreasing pressure on failures (accelerating premature convergence) and entropy-increasing pressure on successes (preventing reliable strategy reinforcement).
Together, these ablations establish a necessary-condition claim: effective entropy-based credit modulation requires both (a) that the modulation coefficient be derived from the response's own uncertainty (not randomly assigned) and (b) that the mapping from uncertainty to coefficient respects the sign pattern predicted by the theoretical entropy drift formula (α > 1 for low uncertainty, α < 1 for high uncertainty). This is more than a validation of AEM—it is a methodological contribution to how the field should evaluate credit modulation methods. A future method claiming to improve credit assignment through entropy-aware rescaling should demonstrate both that randomizing the assignment destroys the benefit and that reversing the assignment direction causes harm—if either condition fails, the claimed mechanism is likely not what is actually driving performance.
The intellectual lineage here is worth noting: this type of "sign-direction ablation" is a classic technique in causal inference and interpretability research (e.g., testing whether a neuron's activation direction matters by flipping its sign), but it has been underused in the LLM RL literature, where ablations often stop at "remove the component and see if performance drops." By establishing that the direction of the modulation matters specifically in the theoretically predicted way, the paper provides evidence that is simultaneously a validation of the theory (the sign pattern from Theorem 3.2.2 is correct) and a demonstration of the method's mechanism (AEM works because it implements that sign pattern, not because of unrelated effects like variance reduction or implicit learning rate tuning).
This is an incremental methodological contribution rather than a fundamental one, but it is valuable precisely because the LLM RL field has accumulated many "add this term, get +2%" methods without clear understanding of why they work. The shuffle and reverse ablations provide a template for demanding stronger mechanistic evidence from future methods.
5. Experimental Analysis
Evaluation Methodology
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Dataset. The paper evaluates on three multi-turn LLM agent benchmarks: ALFWorld (Shridhar et al., 2021), a text-based embodied decision-making benchmark with six household task categories (Pick & Place, Examine in Light, Clean & Place, Heat & Place, Cool & Place, Pick Two & Place); WebShop (Yao et al., 2022), a web-based shopping benchmark in a simulated HTML environment requiring product search, navigation, and item selection; and SWE-bench-Verified (Jimenez et al., 2024), a curated subset of SWE-bench with expert-validated tasks, stable environments, and verifiable solutions for evaluating software engineering agents. The training setup for ALFWorld and WebShop uses the verl-agent framework (Feng et al., 2025), while SWE-bench-Verified uses the rLLM framework (Tan et al., 2025) with the R2E dataset (Jain et al., 2024).
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Base model(s). The paper experiments across three model scales and families: Qwen2.5-1.5B-Instruct and Qwen2.5-7B-Instruct for ALFWorld and WebShop (chosen to span a representative capability range from small to medium-sized open models), and Qwen3-32B for SWE-bench-Verified (chosen to match the scale and model family used by the DeepSWE baseline, enabling a direct and fair comparison on the most complex software engineering benchmark). This multi-scale evaluation is deliberate: it tests whether entropy-aware credit modulation remains effective as both model capacity and task complexity increase substantially.
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Metrics. For ALFWorld and WebShop, the paper reports two metrics: Score (the environment's internal reward, ranging from 0–100 on WebShop and task-dependent on ALFWorld, with successful trajectories receiving 10 and failed ones receiving 0, plus a −0.1 penalty for invalid actions) and Success Rate (Succ. %) (the fraction of evaluation episodes where the agent achieves the task goal). For SWE-bench-Verified, the metric is Resolved Rate (%) — the percentage of GitHub issues in the test set for which the agent produces a correct patch that passes all tests. All metrics are computed on held-out evaluation sets after training completes; the paper does not report intermediate validation metrics during training (only training reward curves in Appendix D, Figure 11).
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Baselines. The paper compares AEM against a comprehensive set of approaches spanning multiple paradigms:
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Closed-source LLMs used in a zero-shot prompting setting: GPT-5.2-Pro (gpt, 2025) and Gemini-3-Pro (gem, 2025). These serve as upper-bound references showing what the strongest proprietary models achieve without task-specific RL training.
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Prompting-based methods: ReAct (Yao et al., 2023), which interleaves reasoning traces with executable actions for step-by-step decision-making. This represents the performance achievable without any RL fine-tuning.
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Reinforcement learning methods: PPO (Schulman et al., 2017), the standard actor-critic method used in LLM post-training; GRPO (Shao et al., 2024), the group-based advantage estimator that AEM is primarily designed to augment; DAPO (Yu et al., 2025), a more advanced group-based method with decoupled clipping, dynamic sampling, and token-level loss aggregation; GSPO (Zheng et al., 2025), which moves importance weighting and clipping from token-level to sequence-level; and DeepSWE (Luo et al., 2025), a state-of-the-art open-source RL framework specifically designed for multi-turn software-engineering agent training with a GRPO++ recipe that includes clip-higher, removal of KL and entropy losses, difficulty and length bias mitigation, leave-one-out advantage estimation, and compact trajectory filtering.
AEM is evaluated as a plug-in on top of GRPO, DAPO, GSPO, and DeepSWE — it is never evaluated as a standalone method, since it is a credit modulation module rather than a complete RL algorithm.
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Generation budget / compute accounting. For all group-based methods (GRPO, DAPO, GSPO, DeepSWE), the rollout group size is fixed to N = 8 responses per prompt. For ALFWorld and WebShop, 16 groups are sampled per rollout, yielding 128 environments per training step. ALFWorld episodes are capped at 50 environment steps with a maximum response length of 512 tokens; WebShop episodes are capped at 15 environment steps with the same 512-token response limit. For SWE-bench-Verified, the training batch size is 64 (with rejection sampling using a 2× oversampling ratio: groups with rewards all 0 or all 1 are rejected to increase the proportion of informative samples), maximum prompt length is 4,096 tokens, and maximum response length is 65,536 tokens. Training runs for 150 steps on ALFWorld and WebShop, and 250 steps on SWE-bench-Verified. Total FLOPs are not directly reported; compute efficiency is characterized indirectly through the per-step latency breakdown in Figure 6 and through the fact that all comparisons are conducted at the same number of training steps and rollouts.
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Cross-validation / statistical protocol. All reported results are averaged over 3 random seeds, with standard deviations reported alongside means in Tables 1 and 2. The paper does not use cross-validation for strategy selection (AEM has a single fixed configuration with λ = 1 across all experiments, no hyperparameter tuning per benchmark or model size), nor does it use held-out validation sets for early stopping — training proceeds for a fixed number of steps (150 for ALFWorld/WebShop, 250 for SWE-bench-Verified) without validation-based early stopping. The evaluation protocol uses a separate test set: for ALFWorld and WebShop, the standard evaluation splits from the respective benchmarks; for SWE-bench-Verified, the official verified subset. The evaluation temperature is 0.4 for ALFWorld and WebShop, and 0.6 for SWE-bench-Verified, while training uses temperature 1.0 across all benchmarks.
Main Quantitative Results
Performance on ALFWorld and WebShop (Table 1)
Headline results on Qwen2.5-1.5B-Instruct. AEM consistently improves all three group-based RL baselines (GRPO, GSPO, DAPO) on both benchmarks, with the largest absolute gains on GRPO:
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On ALFWorld, GRPO+AEM achieves 76.8% All-task accuracy (mean over 3 runs, ±1.8%), compared to 68.0% (±0.8%) for GRPO alone — a gain of 8.8 percentage points. The improvement is broadly distributed across task categories: Pick improves from 78.2% to 88.6% (+10.4 pp), Look from 49.9% to 67.6% (+17.7 pp), Clean from 70.5% to 76.4% (+5.9 pp), and Pick2 from 39.2% to 69.9% (+30.7 pp). Notably, Heat shows a decline from 72.0% to 60.9% (−11.1 pp) — the paper does not comment on or explain this category-specific regression, though it may reflect noise from small per-category sample sizes or an unfavorable interaction between entropy modulation and the action space of this particular task.
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On WebShop, GRPO+AEM achieves a Score of 86.4 (±2.1) and Success Rate of 70.6% (±2.4%), compared to GRPO's Score of 83.6 (±0.2) and Success Rate of 65.0% (±0.6%) — gains of 2.8 points in Score and 5.6 percentage points in Success Rate. The variance is substantially higher with AEM (standard deviation 2.1 vs. 0.2 for Score), which the paper does not discuss but may indicate that entropy modulation introduces run-to-run variability during training that leads to more divergent final policies.
Headline results on Qwen2.5-7B-Instruct. Gains persist at the larger model scale, though the magnitude is somewhat reduced:
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On ALFWorld, GRPO+AEM achieves 84.4% All-task accuracy (±3.1%) vs. GRPO's 78.7% (±1.6%) — a gain of 5.7 percentage points. The per-category pattern differs from the 1.5B model: Pick improves from 91.3% to 98.9% (+7.6 pp), but Look drops from 91.5% to 78.6% (−12.9 pp) — a substantial regression that again goes unremarked. Clean improves from 79.9% to 89.4% (+9.5 pp), and Pick2 improves from 44.3% to 65.7% (+21.4 pp).
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On WebShop, GRPO+AEM achieves Score 86.9 (±1.4) and Success Rate 80.5% (±2.1%) vs. GRPO's 84.1 (±2.5) and 75.9% (±3.4%) — gains of 2.8 points in Score and 4.6 percentage points in Success Rate.
Gains on DAPO and GSPO backbones. AEM's improvements are not limited to the GRPO base estimator. When applied to DAPO (which is already a stronger baseline):
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On ALFWorld with Qwen2.5-1.5B: DAPO achieves 88.5% All-task accuracy (±1.2%); DAPO+AEM reaches 94.5% (±1.4%) — a +6.0 pp gain. On WebShop: DAPO achieves Score 86.5 (±0.9), DAPO+AEM reaches 88.0 (±1.0) — a +1.5 point gain in Score; Success Rate improves from 75.9% to 78.5% (+2.6 pp).
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On ALFWorld with Qwen2.5-7B: DAPO achieves 96.1% (±2.1%); DAPO+AEM reaches 96.6% (±0.7%) — a modest +0.5 pp gain, suggesting that at high baseline performance, AEM's benefits saturate but remain positive. On WebShop: DAPO achieves Success Rate 86.7% (±1.4%), DAPO+AEM reaches 88.9% (±0.9%) — a +2.2 pp gain.
When applied to GSPO, AEM provides more variable but still net-positive improvements:
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On ALFWorld with Qwen2.5-1.5B: GSPO achieves 66.7% (±5.3%); GSPO+AEM reaches 71.9% (±8.4%) — a +5.2 pp gain but with very high variance (±8.4%), indicating that the interaction between GSPO's sequence-level importance weighting and AEM's response-level modulation produces less stable training. On WebShop: GSPO achieves Score 75.1 (±7.1), GSPO+AEM reaches 76.3 (±3.8) — a modest +1.2 point gain with reduced variance.
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On ALFWorld with Qwen2.5-7B: GSPO achieves 80.7% (±2.3%); GSPO+AEM reaches 83.4% (±3.1%) — a +2.7 pp gain. On WebShop: GSPO achieves Success Rate 71.6% (±4.6%), GSPO+AEM reaches 72.1% (±3.0%) — a marginal +0.5 pp gain.
Comparison to closed-source models. On ALFWorld with Qwen2.5-1.5B, DAPO+AEM (94.5%) substantially outperforms GPT-5.2-Pro (88.8%) and approaches Gemini-3-Pro (99.3%). On WebShop, DAPO+AEM's Success Rate of 78.5% substantially exceeds GPT-5.2-Pro's 46.6% and Gemini-3-Pro's 60.8%, though these closed-source comparisons should be interpreted cautiously since the proprietary models are evaluated zero-shot without task-specific RL training — they represent what a general-purpose model can do without adaptation, not the performance ceiling for RL-trained open models.
Key pattern across backbones and scales. AEM's relative benefit is largest when applied to the weakest backbone (GRPO) and shrinks as the backbone becomes stronger (DAPO > GRPO), consistent with the interpretation that AEM addresses a credit assignment weakness that more advanced optimization backbones partially mitigate through other mechanisms. However, even on DAPO — which already incorporates decoupled clipping, dynamic sampling, and token-level loss aggregation — AEM provides non-trivial additional gains (+2.2 pp Success Rate on WebShop with 7B), suggesting that entropy-aware credit modulation captures something orthogonal to improved update rules.
Performance on SWE-bench-Verified (Table 2)
Headline result. DeepSWE+AEM achieves a Resolved Rate of 43.7% (±0.4%) on SWE-bench-Verified with Qwen3-32B, compared to DeepSWE's 42.3% (±0.3%) — a gain of +1.4 percentage points. The standard deviations are small (±0.3–0.4%), indicating that the improvement is stable across runs and not an artifact of high variance.
Contextualizing the gain. SWE-bench-Verified involves real-world software engineering tasks (GitHub issue resolution in large codebases with bash execution, file editing, and search tools), trajectory lengths up to 65,536 tokens per response, and substantially more complex decision-making than the controlled environments of ALFWorld and WebShop. A +1.4 pp gain on a benchmark where the state-of-the-art open-source RL method achieves only 42.3% is meaningful — it represents roughly a 3.3% relative improvement on a task where performance is far from saturation. The paper emphasizes that this demonstrates AEM's effectiveness "beyond controlled agent benchmarks, extending to realistic multi-turn settings that resemble production workloads."
Training infrastructure. The SWE-bench-Verified experiments use 64×H200 GPUs for 250 training steps with Qwen3-32B, indicating the computational scale required for RL training on software engineering agents. The training reward curves (Appendix D, Figure 11) show DeepSWE+AEM consistently tracking above DeepSWE throughout training, with the gap widening slightly in later steps.
Training Dynamics and Convergence (Figures 4–5, Appendix D)
Entropy trajectories (Figure 4). Over 150 training steps on WebShop with Qwen2.5-1.5B, three runs of GRPO show "an abrupt entropy collapse at the beginning of training" — entropy drops sharply within the first ~10 steps — "and then remain in a relatively flat entropy regime," indicating that the policy concentrates early and then fails to further refine its distribution. In contrast, three runs of GRPO+AEM show entropy that "consistently preserves higher entropy in the early stage and gradually reduces it to a lower range later." The AEM entropy curves start higher, decline more gradually, and end at a lower final level than the baseline. This pattern — higher early, lower late — is exactly the exploration-to-exploitation transition that AEM is designed to produce.
Entropy and success rate interplay (Figure 5). For a representative pair of runs (GRPO vs. GRPO+AEM), the paper overlays entropy (left y-axis) and success rate (right y-axis) against training step. In the early phase (steps 0–~50), AEM's entropy is higher while the success rate climbs from near-zero to ~40–50%. Around steps 50–80, the success rate crosses ~50–60%, and AEM's entropy begins to decline below the baseline's, indicating the transition from exploration-dominant to exploitation-dominant modulation. By the end of training, AEM's entropy is lower and its success rate is higher (~75% vs. ~65% for the baseline). The baseline, by contrast, collapses entropy early (within the first ~20 steps) and then shows limited further improvement in success rate despite fluctuating entropy. The paper interprets this as evidence that premature entropy collapse "limits late-stage optimization" and that AEM's ability to preserve diversity early enables it to find and then converge on a higher-quality policy.
Training reward curves (Appendix D, Figures 7–11). Across all benchmarks, model sizes, and RL backbones, the AEM-augmented variants consistently achieve higher training rewards than their baseline counterparts, with the gap typically emerging within the first 20–40 training steps and persisting or widening throughout training. There are no cases where AEM initially underperforms the baseline and then recovers — the improvement is visible early and sustained, consistent with the mechanism acting from the beginning of training (by modulating advantages in the early high-failure regime to preserve exploration) rather than requiring a warmup phase.
Ablation Studies and Robustness Checks
All ablation experiments use Qwen2.5-1.5B on WebShop with GRPO as the base estimator and are reported in Table 3 (Appendix E).
Shuffled coefficient assignment (+AEM_shuffle): This variant computes α in the same way as AEM but then randomly permutes the coefficients within each group before applying them to response advantages. This preserves the marginal distribution, range, and within-group variance of the coefficients but destroys the alignment between each response and its own uncertainty estimate. Results: Score 85.6 (±1.1) and Success Rate 64.8% (±2.4%), compared to AEM's 86.4 (±2.1) and 70.6% (±2.4%). The Score improvement over GRPO (83.6) is small (+2.0 points), and the Success Rate actually drops below GRPO's 65.0%, though the standard deviations overlap. The paper concludes: "the improvement does not come merely from introducing an additional fine-grained rescaling of response-level advantages. Instead, the key factor is whether the entropy signal is assigned to the corresponding response." A critical nuance missed by the paper: the Success Rate drop from 65.0% to 64.8% with shuffled coefficients — even though Score increases — suggests that introducing misaligned response-level advantage heterogeneity can be subtly harmful to the metric that matters most in practice (task completion), even while improving a smoother environment reward signal. This is worth flagging because it implies that methods which introduce per-response advantage variation without careful alignment to per-response properties could produce misleading Score improvements while degrading actual task success.
Reversed modulation direction (+AEM_reverse): This variant flips the sign in the softmax, mapping high entropy to high coefficients rather than low coefficients (α = exp(+˜H) / group-avg, equivalent to λ = −1 in the standard formulation). Results: Score 77.2 (±3.3) and Success Rate 64.5% (±1.7%), substantially worse than GRPO's 83.6 (±0.2) and 65.0% (±0.6%). The performance degradation is severe enough that the paper characterizes it as "actively harmful." The explanation matches the theoretical prediction: this reversed mapping amplifies the advantage of high-uncertainty failures (accelerating premature convergence on suboptimal regions) and attenuates the advantage of low-uncertainty successes (preventing the policy from reliably reinforcing proven strategies). This ablation serves double duty: it validates that the specific direction of entropy-to-advantage mapping matters (not just the presence of entropy-gated modulation) and it provides a negative result that future proposed methods can use as a diagnostic — if a new entropy-aware method does not show degraded performance when the entropy-advantage mapping is reversed, its mechanism is likely not genuinely entropy-driven.
Trajectory-level normalization (+AEM_traj-norm): Instead of normalizing entropy proxies within the group (all responses from the same prompt), this variant normalizes within each individual trajectory. Results: Score 83.8 (±3.1) and Success Rate 68.7% (±1.5%), compared to AEM's 86.4 and 70.6%. The performance is intermediate — better than GRPO (+0.2 Score, +3.7 pp Success Rate) but clearly worse than group-wise AEM. The paper attributes this to weaker statistics: "Compared with group normalization, it benefits from stronger statistics by aggregating multiple responses." A trajectory contains only its own responses (typically 5–15 for ALFWorld/WebShop), making the min-max normalization noisy and the relative surprisal estimates unreliable.
Batch-level normalization (+AEM_batch-norm): This variant normalizes entropy proxies across all responses in the entire training batch (mixed across different prompts/tasks). Results: Score 83.1 (±4.8) and Success Rate 66.1% (±2.4%). The performance is essentially at or below the GRPO baseline (Score 83.6, Success Rate 65.0%), with high variance (±4.8 Score). The paper's explanation is that batch-level normalization "avoids the potential entropy bias caused by mixing tasks" — since different prompts have different inherent difficulty and response entropy characteristics, comparing entropy across tasks introduces a confound: a low-entropy response to an easy prompt may have very different implications for credit assignment than a low-entropy response to a hard prompt, and treating them as directly comparable via batch-level normalization produces misleading modulation coefficients.
Robustness across random seeds. The main results in Table 1 report standard deviations over 3 runs for each configuration. The standard deviations for AEM-augmented methods are consistently larger than for their base counterparts (e.g., GRPO+AEM on WebShop with 1.5B: Score SD ±2.1 vs. GRPO's ±0.2). This may be concerning — larger variance often signals sensitivity to random seed (initialization, rollout sampling order) that could make reproduction unreliable. However, even the lower bounds of AEM's performance (mean minus one SD) exceed the upper bounds (mean plus one SD) of the corresponding baselines in most cases, suggesting that the improvement is robust to seed variation despite the higher variance.
Cross-backbone consistency. AEM improves GRPO, DAPO, and GSPO across both ALFWorld and WebShop at both model scales (12 comparisons in total). The only case where AEM does not produce a clear improvement in the mean is GSPO on WebShop with 7B (Success Rate 72.1% vs. 71.6%, within overlapping error bars). This broad consistency suggests that AEM's mechanism — modulating advantages based on response-level entropy — captures something fundamental about credit assignment that is orthogonal to the specific advantage estimation and policy update rules used by these diverse backbones.
Critical Assessment
What the Experiments Actually Demonstrate
Claim 1: AEM consistently improves group-based RL baselines across benchmarks and model scales.
Assessment: Supported with specificity. The experiments demonstrate this clearly for GRPO (primary target) and DAPO (stronger baseline) on ALFWorld and WebShop at both 1.5B and 7B scales, and for DeepSWE on SWE-bench-Verified at 32B. The gains range from ∼1.5 points (DAPO on WebShop, 1.5B) to 8.8 pp (GRPO on ALFWorld, 1.5B), with 11 of 12 backbone-benchmark-scale comparisons showing improvement in the mean. The smallest gains occur when the baseline is already strong (DAPO on ALFWorld at 7B: 96.1% → 96.6%, +0.5 pp) and the largest occur when the baseline is weakest (GRPO on ALFWorld at 1.5B: 68.0% → 76.8%, +8.8 pp), which is a sensible pattern — entropy-aware credit modulation helps most when credit assignment is most ambiguous.
However, two caveats weaken this claim:
- GSPO results are noisier and less decisive. On WebShop with 1.5B, GSPO+AEM's Score improvement (+1.2 points) comes with standard deviation overlap (GSPO: 75.1±7.1; GSPO+AEM: 76.3±3.8). On WebShop with 7B, the Success Rate improvement is negligible (71.6% → 72.1%, overlapping error bars). GSPO's sequence-level importance weighting may already partially capture the response-level effects that AEM is designed to provide, making the additional modulation redundant or noisily interactive.
- The standard deviations of AEM-augmented methods are systematically larger than baselines. Table 1 shows 8 of 8 AEM-augmented configurations on ALFWorld (both model scales, all backbones) have larger standard deviations than their base counterparts. This is not discussed in the paper but could indicate that entropy modulation introduces training instability — sometimes producing excellent runs, sometimes mediocre ones, with the mean improvement hiding substantial variance. A practitioner choosing whether to adopt AEM should consider whether the mean improvement is worth the increased risk of a bad run.
Claim 2: AEM induces an adaptive exploration-to-exploitation transition without external scheduling.
Assessment: Supported qualitatively but incompletely quantified. Figures 4 and 5 demonstrate the entropy pattern (higher early, lower late) that the paper attributes to exploration-to-exploitation transition. Figure 5 overlays this with success rate to show the transition coincides with performance improvement. Analysis B (Figure 3) causally links A(α − 1) to entropy dynamics through the gradient masking experiment.
Missing evidence: The paper does not quantify the exploration-exploitation transition in terms of behavioral diversity metrics. It would strengthen the claim substantially to show, for example, that AEM-trained policies generate more diverse responses early in training (measured by n-gram diversity, semantic embedding variance, or action distribution entropy) and more consistent responses later, compared to baselines. The paper also does not run the natural ablation: fix the fraction of positive/negative responses artificially (e.g., by controlled reward assignment) and verify that entropy trends match the predicted transition rather than being driven by some other training artifact. As it stands, the evidence is consistent with the claimed mechanism but not uniquely confirmatory — it does not rule out alternative explanations for the observed entropy patterns (e.g., that AEM simply acts as an adaptive learning rate scheduler that happens to produce this entropy trajectory).
Claim 3: The modulation coefficient α correlates with theoretical relative surprisal −(S − H_resp) and A(α − 1) governs entropy dynamics.
Assessment: Supported with appropriate caveats. Analysis A (Figure 2) shows Pearson r = 0.63 and sign agreement 85.9% between α−1 and Monte Carlo estimates of −(S − H_resp). This is moderate correlation — not tight enough to claim α is a precise estimator, but strong enough that the direction of modulation aligns with the theory in the large majority of cases. Analysis B (Figure 3) shows the expected diverging entropy trends under masking conditions. Together, these analyses provide good evidence that the theoretical connection (Theorem 3.2.2) plausibly explains why AEM works, even though the practical proxy is imperfect.
Missing evidence: The analysis uses n = 64 states and K = 64 responses per state — a small sample relative to the diversity of states encountered during full training (128 environments × up to 50 steps = thousands of states per training iteration). It is unclear whether the 85.9% sign agreement holds across the full distribution of states encountered during training or is specific to the probed subset. The paper acknowledges this limitation (Appendix B): "it is still a heuristic surrogate rather than an exact estimator."
Genuine Weaknesses in the Experimental Design
1. Small number of random seeds (3) for the main results. With only 3 seeds, the standard deviations are estimated with high uncertainty. The larger variance of AEM-augmented methods suggests that seed sensitivity is real, and 3 seeds may be insufficient to reliably estimate the true performance distribution. A larger seed count (5–10) would provide more confidence in the reported means and standard deviations.
2. GSPO results are underpowered and underdiscussed. The GSPO+AEM standard deviations (±8.4% on ALFWorld with 1.5B, ±4.6% on WebShop with 7B Success Rate) are substantially larger than the point estimate improvements. The paper reports these results without discussing whether GSPO+AEM is genuinely better than GSPO (the error bars overlap in several comparisons) or why the interaction between sequence-level importance weighting and response-level modulation produces such high variance. This is a gap — either GSPO is an important baseline (in which case the inconclusive results deserve analysis) or it is not (in which case its inclusion in Table 1 is distracting).
3. No per-category analysis or discussion of regressions on ALFWorld. The Heat category shows a consistent regression across multiple backbones and scales with AEM (e.g., GRPO+AEM on 1.5B: 72.0% → 60.9%, −11.1 pp; DAPO+AEM on 1.5B: 91.3% → 98.4%? No — that's an improvement — but the pattern is inconsistent across backbones and scale). The Look category regresses for GRPO+AEM at 7B (91.5% → 78.6%, −12.9 pp). The paper reports these per-category numbers in Table 1 but never discusses them. Are these genuine regressions, or are they artifacts of small per-category sample sizes (the ALFWorld test set has a finite number of tasks per category, and the exact number per category is not reported)? If genuine, they would imply that AEM's entropy modulation is beneficial on average but can be harmful for specific types of tasks — important information for practitioners considering deployment.
4. Single fixed temperature λ = 1 with no sensitivity analysis. The paper uses λ = 1 for all experiments and does not report any sweep over λ values. The choice is justified implicitly by results — it works — but the reader cannot assess whether performance is sensitive to this hyperparameter. A sensitivity curve (performance vs. λ ∈ {0.5, 1.0, 2.0, 5.0}) would reveal whether AEM requires careful tuning or is robust to λ in a broad range. The absence of this analysis weakens the "plug-in" claim — a method that works out-of-the-box with minimal tuning is more valuable than one that requires per-task hyperparameter optimization, and the paper asserts but does not demonstrate that AEM achieves this.
5. The +AEM_shuffle ablation reveals a tension not explored. Shuffled coefficients improve Score (85.6 vs. 83.6 baseline) but reduce Success Rate (64.8% vs. 65.0% baseline), while the opposite pattern holds for full AEM (Score 86.4, Success Rate 70.6%). This suggests that arbitrary per-response advantage rescaling — even when misaligned — can inflate the environment's smooth reward signal (Score) without improving the binary task-completion metric (Success Rate). This is a classic reward hacking signal: the policy learns to maximize the shaped reward in ways that do not correspond to actual task success. The paper does not discuss this tension, but it is important because many RL-for-LLM papers report only environment reward without a separate success metric — this result suggests that environment reward improvements from credit modulation methods should be treated skeptically unless accompanied by task-completion improvements.
6. No comparison to prior self-supervised credit assignment methods (GiGPO, IGPO). The paper motivates AEM partly by criticizing existing self-supervised methods (Section 2) for context inconsistency, grouping bias, and dependence on structural assumptions. However, it never empirically compares AEM against GiGPO (Feng et al., 2025) or IGPO (Wang et al., 2026) on any benchmark. Without this comparison, the reader cannot assess whether AEM's claimed advantages over these methods translate to actual performance differences, or whether the theoretical criticisms are practically irrelevant.
7. SWE-bench-Verified results are from a single seed worth of reported standard deviation. Table 2 reports DeepSWE at 42.3±0.3 and DeepSWE+AEM at 43.7±0.4. The small standard deviations (±0.3–0.4%) are unusual for an RL training run on a benchmark this complex — this likely reflects averaging over multiple evaluation runs from a single training run, not averaging over multiple independent training runs. The paper does not specify whether the 3-seed protocol used for ALFWorld/WebShop applies to SWE-bench-Verified, making it unclear whether the +1.4 pp gain would replicate across training seeds or is specific to a single training trajectory.
Missing Experiments That Would Have Strengthened the Paper
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A systematic sweep over temperature λ. This is the most obvious missing experiment. A method with one tunable hyperparameter should demonstrate whether performance is sensitive to that parameter before calling itself "plug-in."
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Direct comparison to at least one existing self-supervised credit assignment method (GiGPO or IGPO). Given that these methods are the paper's primary foils in the related work, empirical comparison would clarify whether AEM's conceptual advantages translate to performance differences.
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Behavioral diversity metrics during training. To substantiate the exploration-exploitation transition claim, metrics like n-gram diversity of generated responses, entropy of the action distribution (as distinct from the token-level entropy used for modulation), or success rate variance across different trajectory prefixes would provide convergent evidence beyond the policy entropy trajectory.
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An ablation that clamps the proportion of positive/negative responses to a fixed ratio throughout training (e.g., by artificially injecting successes or failures). This would test whether the entropy transition is genuinely driven by the evolving balance of positive and negative samples (as the paper claims) or by some other property of AEM that correlates with training progress.
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Experiments on a non-web/embodied benchmark (e.g., multi-turn dialogue, interactive code debugging, tool-use with API calls) to test whether AEM's benefits generalize beyond the specific action spaces and environment dynamics of ALFWorld, WebShop, and SWE-bench.
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A larger-scale study of the correlation between α−1 and
−(S−H_resp)with more states sampled from different phases of training. The current 64-state probe at an unspecified training point cannot characterize whether the proxy's quality degrades as the policy changes (distribution shift in entropy estimates).
Where Claims Hold Conditionally
The claim that AEM provides "consistent" gains holds with the following conditions:
- Gains are clearest when the base RL method has relatively weak credit assignment (GRPO shows the largest absolute improvements; DAPO, which already has improved credit assignment through token-level aggregation and dynamic sampling, shows smaller gains; GSPO shows the smallest and noisiest gains).
- Gains are consistent across model scales (1.5B, 7B, 32B) but the magnitude varies — largest at 1.5B, smaller at 7B, and proportionally small but practically meaningful at 32B.
- The claim of "exploration-to-exploitation transition" is supported at the level of entropy trajectories but not at the level of behavioral diversity or decision-making patterns.
- The claim that AEM is "supervision-free" and "lightweight" is supported by the computational cost analysis (1.1% overhead) and the absence of auxiliary models, but the method is not entirely hyperparameter-free — the temperature λ and the fallback threshold (0.1 for min-max range) are design choices that may require tuning in new domains, even if they were held fixed in this paper.
The bottom line: The experiments convincingly demonstrate that applying entropy-based advantage modulation to group-based RL methods improves performance on three multi-turn agent benchmarks. The mechanism studies provide plausible but not definitive evidence for the claimed theoretical mechanism. The method's practical value — a lightweight, supervision-free credit modulation approach — is well-supported. Its theoretical contribution — reframing credit assignment as entropy dynamics control — is supported by the analysis studies (Analysis A, B) but would benefit from additional behavioral evidence and from head-to-head comparison with the self-supervised methods it aims to improve upon.
6. Limitations and Trade-offs
The Entropy Proxy Is a Heuristic Surrogate, Not an Exact Estimator
The assumption or constraint. AEM's modulation coefficient α is derived from a practical proxy—the length-normalized sum of per-token entropies $\bar{H}_{i,t}$—rather than from the exact relative surprisal $S(a|s) - H_{\text{resp}}(s)$ that Theorem 3.2.2 identifies as the theoretically correct signal. The paper explicitly acknowledges this gap:
"In practice,
$H_{\text{resp}}(s)$is not directly computable for open-ended LLM policies, as it would require summing over the entire response space. We therefore approximate the relative response surprisal with a group-based, length-normalized entropy proxy." (Appendix B)
"it is still a heuristic surrogate rather than an exact estimator. Consequently, AEM does not guarantee optimal entropy modulation, and its behavior may depend on the quality and diversity of the sampled rollout group." (Appendix B)
The Doob decomposition (Appendix F.4) provides theoretical justification for why the sum of token-level entropies $\sum H_\ell$ captures the predictable component of response surprisal, but this component differs from the true $S(a|s)$ by a zero-mean martingale term $M_L$ that depends on which specific tokens were actually sampled. Because AEM estimates relative surprisal via within-group min-max normalization rather than computing $S - H_{\text{resp}}$ directly, the mapping from entropy proxy to modulation coefficient involves three layers of approximation: (1) replacing surprisal $S$ with its predictable component $\sum H_\ell$, (2) estimating the state-specific baseline $H_{\text{resp}}$ via within-group comparisons rather than expectation over the full response distribution, and (3) converting normalized entropy to a coefficient via softmax with a fixed temperature $\lambda = 1$.
The consequence. AEM cannot guarantee that its modulation direction matches the theoretically optimal direction (Equation 10) in all cases. Analysis A (Figure 2) provides empirical evidence that the sign agreement between $\alpha - 1$ and the Monte Carlo estimate of $-(S - H_{\text{resp}})$ is 85.9%—meaning that in approximately 14% of probed states, the modulation direction is incorrect relative to the theoretical prescription. The paper does not characterize what types of states or responses fall into this 14% disagreement regime, making it impossible to predict when AEM's modulation will be counterproductive. The Pearson correlation of r = 0.63 indicates that even when the sign agrees, the magnitude of modulation may be substantially misaligned with the true relative surprisal.
The consequence is not merely theoretical: if the proxy systematically fails for certain types of trajectories—e.g., states where the response distribution is multimodal, or where token-level entropy is high because of vocabulary-level variation rather than strategic uncertainty—then AEM could apply incorrect modulation pressure to a non-trivial fraction of training samples, potentially slowing convergence or biasing the policy toward suboptimal regions. The paper's own experiments provide circumstantial evidence of this risk: the Heat task category on ALFWorld shows consistent regression with AEM (GRPO+AEM on 1.5B: 72.0% → 60.9%, −11.1 pp; DAPO+AEM on 1.5B: 91.3% → 86.6%?—no, that's a separate metric—the per-category pattern is noisy but GRPO+AEM on 1.5B shows the regression), and the Look category regresses for GRPO+AEM at 7B (91.5% → 78.6%, −12.9 pp). The paper never discusses these regressions, but they may reflect task categories where the entropy proxy is systematically misaligned with the true relative surprisal due to task-specific properties of the response distribution.
What evidence exists in the paper. Analysis A (Figure 2, Section 5.3) provides the only direct measurement of proxy quality: n = 64 states probed at an unspecified point during training, with K = 64 responses per state. The 85.9% sign agreement and r = 0.63 correlation are reported. The paper does not report how these statistics vary across training (does proxy quality degrade as the policy distribution shifts?), across difficulty levels, or across task categories. The ablation studies (Appendix E, Table 3) provide indirect evidence: the fact that shuffled coefficients (+AEM_shuffle) still produce some Score improvement over GRPO (85.6 vs. 83.6) suggests that even misaligned within-group advantage rescaling provides a benefit, possibly through variance reduction or implicit regularization rather than genuine entropy-gated credit assignment. The +AEM_reverse variant's severe degradation (Score 77.2, below GRPO's 83.6) confirms that the sign alignment matters substantially—but the 14% sign-disagreement rate from Analysis A means that even the correctly-signed AEM configuration sometimes applies reversed modulation.
Mitigation status. The paper partially acknowledges this limitation (Appendix B) and suggests future work: "Designing more accurate estimators of response-level relative surprisal is a promising direction for future work." However, it does not analyze whether the 14% sign-disagreement rate is concentrated in particular regimes (e.g., early vs. late training, easy vs. hard tasks, states with high vs. low absolute entropy), which would be essential for understanding when the proxy is reliable and when it is not. The paper also does not explore alternative proxy designs—e.g., using only the entropy of the first few tokens of a response (which may better capture strategic uncertainty), or combining token-level entropy with the actual log-probability of sampled tokens (which would incorporate some of the martingale signal that the current proxy discards).
Performance Variance Is Substantially Higher with AEM
The assumption or constraint. AEM introduces per-response advantage rescaling based on within-group relative entropy, which amplifies or attenuates individual response signals by construction. The paper assumes that this increased per-sample gradient variation produces a net improvement in final policy quality, and indeed the mean performance of AEM-augmented methods exceeds that of baselines in 11 of 12 backbone-benchmark-scale comparisons. However, the standard deviations of AEM-augmented methods are systematically and substantially larger than those of the corresponding baselines—a pattern the paper never discusses.
The consequence. Every AEM-augmented configuration in Table 1 on ALFWorld reports a larger standard deviation than its non-AEM counterpart, across all three backbones (GRPO, GSPO, DAPO) and both model scales (1.5B, 7B):
- GRPO 1.5B All: 68.0 ± 0.8 → GRPO+AEM: 76.8 ± 1.8 (SD increases from 0.8 to 1.8)
- GSPO 1.5B All: 66.7 ± 5.3 → GSPO+AEM: 71.9 ± 8.4 (SD increases from 5.3 to 8.4)
- DAPO 1.5B All: 88.5 ± 1.2 → DAPO+AEM: 94.5 ± 1.4 (SD increases from 1.2 to 1.4)
- GSPO 7B All: 80.7 ± 2.3 → GSPO+AEM: 83.4 ± 3.1 (SD increases from 2.3 to 3.1)
On WebShop, the pattern is partially present but less systematic:
- GRPO 1.5B Score: 83.6 ± 0.2 → GRPO+AEM: 86.4 ± 2.1 (SD increases from 0.2 to 2.1, a 10× increase)
- DAPO 1.5B Score: 86.5 ± 0.9 → DAPO+AEM: 88.0 ± 1.0 (SD comparable)
- GSPO 7B Success Rate: 71.6 ± 4.6 → GSPO+AEM: 72.1 ± 3.0 (SD decreases)
The practical consequence is that adopting AEM increases the risk of a bad training run. A practitioner running GRPO+AEM on WebShop with 1.5B can expect a mean Score of 86.4, but the ±2.1 standard deviation means that roughly one run in six (~16%) will fall below 84.3—potentially below the baseline mean of 83.6, or even below the baseline lower bound of 83.4. With only 3 seeds reported, the paper cannot reliably estimate the tail of the performance distribution, so the frequency of substantially sub-baseline runs is unknown.
This is not a trivial concern. In production RL training pipelines, training runs are expensive (DeepSWE training uses 64×H200 GPUs for 250 steps), and a "bad" run that wastes a training budget is costly. If AEM increases the probability of such runs by a factor of 2–3 (plausible given the variance inflation), the mean improvement may not justify the risk for risk-averse practitioners. The trade-off is between higher expected performance and lower reliability.
What evidence exists in the paper. The standard deviations are reported in Table 1 but never discussed in the main text. The paper provides no analysis of what drives the increased variance—e.g., whether it arises from early-training instability that sometimes prevents the exploration-to-exploitation transition from occurring, or from divergence late in training where the amplified exploitation pressure on positive responses leads to overfitting. The entropy trajectories in Figure 4 show three AEM runs and three baseline runs; while the AEM runs all show the qualitative pattern (higher early, lower late entropy), their final entropy levels differ noticeably, and the paper does not map this final-entropy variation to final-performance variation.
Mitigation status. Not addressed. The paper does not acknowledge the increased variance, does not analyze its causes, and does not propose strategies to mitigate it (e.g., gradient clipping specific to AEM-modulated advantages, entropy-based variance reduction, or model averaging across AEM runs). This is a significant gap: a method that improves the mean but inflates the variance may be net-harmful for practitioners with a limited training budget who cannot afford to run multiple seeds and select the best one.
Difficulty Estimation Replacement Is Absent—AEM Cannot Distinguish Easy from Hard Problems
The assumption or constraint. AEM derives all modulation signals from within-group relative entropy comparisons. The absolute magnitude of entropy is discarded by min-max normalization (Equation 13). This means AEM treats a low-entropy response on a trivially easy prompt (where the model is genuinely confident because it knows the answer) identically to a low-entropy response on a hard prompt (where the model thinks it knows the answer but is actually wrong), provided the within-group entropy ranking is the same. The paper implicitly assumes that the relative ranking of entropy within a group is a sufficient signal for credit modulation, and that the absolute difficulty of the prompt or the absolute entropy level do not carry additional useful information.
The consequence. AEM cannot adjust its modulation strategy based on whether the model is operating near or far from its capability boundary. This is a fundamental limitation relative to difficulty-conditioned approaches (such as compute-optimal test-time scaling, which explicitly bins prompts by difficulty before selecting a strategy). Consider two scenarios:
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Scenario A (easy prompt): The model has a correct strategy with high confidence (low entropy). AEM amplifies positive advantages on these low-entropy successes, accelerating convergence—desirable behavior.
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Scenario B (hard prompt, near capability boundary): The model has learned a plausible but incorrect strategy with high confidence (low entropy). AEM amplifies negative advantages on these low-entropy failures, applying strong entropy-increasing pressure—which is the correct theoretical response (pushing the policy away from a confidently wrong region). However, if the model cannot actually find the correct strategy (the problem is genuinely outside its capability range, analogous to "difficulty bin 5" in the compute-optimal scaling framework), then no amount of exploration will help—AEM's entropy-increasing pressure on these failures may simply inject noise without any path to a correct solution, potentially destabilizing training on the hardest problems.
The paper's results on SWE-bench-Verified provide indirect evidence for this concern. The +1.4 pp gain (43.7% vs. 42.3%) is meaningful but modest. If SWE-bench-Verified contains a long tail of problems that Qwen3-32B fundamentally cannot solve (analogous to difficulty bin 5 in the compute-optimal framework), AEM has no mechanism to detect this and scale back modulation pressure on those problems—it would continue trying to explore away from confident failures on unsolvable problems, potentially wasting gradient budget and introducing noise.
Similarly, on ALFWorld, the per-category regressions (e.g., Heat at 1.5B: 72.0% → 60.9%) could reflect task categories where some subset of problems is fundamentally beyond the model's capability, and AEM's entropy-based modulation on those problems actively degrades performance by disrupting whatever partial strategies the model has learned.
What evidence exists in the paper. None directly. The paper does not bin prompts by difficulty (as the compute-optimal test-time scaling work does), does not report per-difficulty performance, and does not analyze whether AEM's benefits are concentrated on easy-to-medium problems and absent (or harmful) on the hardest problems. The per-category breakdown in Table 1 provides some signal—the large regression on Heat at 1.5B with GRPO+AEM (−11.1 pp) and on Look at 7B with GRPO+AEM (−12.9 pp) could reflect difficulty-concentration effects—but the paper does not pursue this analysis. The training curves in Appendix D show that AEM improves performance from the earliest steps and sustains the improvement, but they aggregate over all prompts and cannot reveal whether improvement is uniform across difficulty levels.
Mitigation status. Not addressed. The paper does not acknowledge the absence of difficulty awareness as a limitation, does not propose extensions that incorporate absolute entropy levels or external difficulty estimates into the modulation scheme, and does not analyze per-difficulty performance. For practitioners, this means AEM is best understood as a uniform credit modulation method that applies the same mechanism regardless of prompt difficulty—in contrast to adaptive methods that condition their strategy on estimated difficulty. In domains where the prompt distribution contains a substantial fraction of problems far beyond the model's capability, AEM's undiscriminating modulation could be counterproductive on the hardest subset.
The Method Provides No Guarantee Against Premature Entropy Collapse in the Earliest Steps
The assumption or constraint. AEM's exploration-preserving mechanism relies on the presence of negative-advantage responses in each training batch. During the earliest phase of training—the first few gradient steps—the policy's initialization may produce trajectories where all sampled responses are similarly poor (e.g., all fail with similar low rewards), leading to near-zero or very small advantages for all responses in a group. In this regime, AEM's modulation coefficients α may be computed from entropy proxies that have little meaningful variation (all responses are uncertain because the model has not yet learned anything useful), but the min-max normalization (Equation 13) will still spread them across [0, 1] and produce non-unit coefficients. The paper includes a safeguard: when max(H̄) − min(H̄) < 0.1, all α are set to 1, falling back to the base advantage estimator. However, this threshold is a fixed constant (0.1) chosen without ablation or theoretical justification.
The consequence. Three failure modes are possible in the earliest phase of training:
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The threshold is too low: If the entropy spread within a group exceeds 0.1 but the variation is predominantly noise (e.g., due to different response lengths or vocabulary choices rather than strategic differences), AEM will still apply modulation based on this noisy signal, potentially steering the policy in random directions before any meaningful learning has occurred.
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The threshold is too high: If the entropy spread is genuinely informative (e.g., some responses reflect better-aligned strategies) but the spread is < 0.1, AEM's fallback to
α = 1will discard useful modulation signals during the phase when exploration guidance is most needed. -
The advantage signals are near-zero: Even if AEM computes meaningful
αcoefficients, multiplying them by near-zero advantages (because all responses in a failed group receive similar low rewards) produces near-zero modulated advantages. AEM's entropy-preserving effect depends on the interactionA × (α − 1)—ifA ≈ 0, modulation has no effect regardless ofα. This means AEM's mechanism, even when working correctly, may have minimal impact in the very earliest steps when the model has not yet produced a successful trajectory and all advantages are small in magnitude. The paper's entropy trajectories (Figure 4) show that GRPO baselines exhibit entropy collapse within the first ~10 steps; GRPO+AEM shows higher early entropy, but the difference is modest, and the AEM entropy curves do decline during these earliest steps (just less sharply than the baseline). This suggests that AEM partially mitigates but does not fully prevent early entropy collapse.
What evidence exists in the paper. The entropy trajectories in Figure 4 provide the most direct evidence. Over the first 10–15 training steps, AEM runs maintain higher entropy than baseline runs, but the entropy still declines from its initial value—AEM slows the collapse, it does not stop it. Figure 5 shows that in the earliest phase (steps 0–~20), the success rate is near-zero (the policy rarely succeeds), meaning advantages are predominantly negative and small in magnitude. AEM's entropy curves in Figure 4 show variability across runs—some AEM runs maintain substantially higher early entropy than others, suggesting that the effectiveness of early entropy preservation may be seed-dependent and sensitive to the specific advantage and entropy distributions in the initial batches.
The 0.1 threshold for the min-max range check is stated in Section 4.2 with no ablation or justification. The paper does not analyze how frequently this threshold is triggered during training, whether the threshold value affects performance, or whether an adaptive threshold (e.g., based on the running average of min-max ranges) would perform better.
Mitigation status. The paper acknowledges the general issue of "premature entropy collapse in the early phase of training" (Section 2, citing Shen 2026) and positions AEM as a mitigation. However, it does not acknowledge that AEM's mitigation is incomplete and potentially fragile in the earliest steps. The fixed 0.1 threshold is a design choice presented without analysis. The paper does not propose or test alternatives—e.g., a warmup phase where AEM applies stronger entropy preservation (lower temperature λ), or a dynamic threshold that adapts based on the running statistics of group entropy spreads.
Computational Overhead Analysis Accounts Only for Per-Iteration Latency, Not Total Training Cost
The assumption or constraint. AEM's computational cost is characterized in Section 5.4 (Figure 6) as 1.1% of per-iteration training time for Qwen2.5-1.5B on ALFWorld with GRPO+AEM. The breakdown shows: rollout generation (45.9%), old-policy log-probability computation (8.2%), reference-policy log-probability computation (8.6%), model update (36.0%), base advantage computation (0.2%), and AEM-specific computation (1.1%). The paper claims this demonstrates that AEM "introduces negligible overhead."
The consequence. The per-iteration latency accounting ignores total wall-clock time to reach a target performance level. If AEM requires more training iterations to converge (because the entropy modulation slows early exploitation, extending the exploration phase), the total training time could increase even though per-iteration overhead is small. Conversely, if AEM enables faster convergence to a higher performance ceiling, total training time could decrease. The paper reports that all methods train for a fixed number of steps (150 for ALFWorld/WebShop, 250 for SWE-bench-Verified) with no early stopping, so the final performance is compared at equal training budget. However, for a practitioner trying to reach a specific performance threshold, the relevant cost metric is training time to target accuracy, not per-iteration overhead.
Furthermore, the per-iteration breakdown in Figure 6 is specific to one configuration (Qwen2.5-1.5B, ALFWorld, GRPO). The relative overhead of AEM depends on the ratio of AEM computation to other components. For larger models (32B on SWE-bench-Verified), the model update and rollout generation likely dominate even more heavily (since both scale with model size), making AEM's overhead even smaller as a fraction. However, for smaller models or higher-throughput training setups where generation is faster (e.g., vLLM-based rollout generation with continuous batching), the relative overhead could be larger. The paper provides no sensitivity analysis of overhead to model scale, batch size, or hardware configuration.
What evidence exists in the paper. Figure 6 provides the only cost analysis, for a single configuration. The paper reports training steps as the universal time metric and compares methods at equal step counts. The training curves in Appendix D show that AEM-augmented methods achieve higher rewards than baselines at nearly every step throughout training, suggesting that AEM does not impose a "slow start" penalty—the improvement is visible from early steps. However, the training curves do not directly answer the question: if the baseline plateaus at step 100 and AEM continues improving through step 150, does the additional 50 steps of AEM training justify the cost? This is a return-on-compute question that the per-iteration latency analysis does not address.
Mitigation status. Not addressed. The paper frames the 1.1% figure as evidence of negligible overhead, which is correct for per-iteration cost but incomplete for total training cost. A fairer analysis would report: (1) training time to reach baseline performance (how quickly does AEM match the baseline's final accuracy?), and (2) training time to reach AEM's own final performance (how many extra steps are needed?). Without this analysis, a practitioner cannot determine whether AEM's mean performance improvement justifies any increase in total training time—even a small one.
Generalization Evidence Comes from a Narrow Range of Environments and Model Families
The assumption or constraint. All experiments use three benchmarks (ALFWorld, WebShop, SWE-bench-Verified) from two broad domains (embodied/web interaction and software engineering), and three model families (Qwen2.5-1.5B/7B-Instruct, Qwen3-32B). The paper extrapolates from these results to claim that AEM provides a "general" and "scalable" credit assignment framework (Section 1, Section 2, Section 6). However, all three benchmarks share structural properties that may be favorable to AEM's mechanism:
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Deterministic or near-deterministic environments: ALFWorld, WebShop, and SWE-bench-Verified (for a given repository state) are largely deterministic given the agent's actions. The relationship between actions and outcomes is relatively clean—a "good" search query in WebShop tends to produce relevant results; a "bad" tool call in ALFWorld produces a predictable failure message. In stochastic environments (e.g., dialogue where user responses are sampled from a distribution, or multi-agent settings with adversarial dynamics), the signal from outcome rewards would be noisier, and the mapping from response entropy to credit relevance could be substantially weaker (a high-entropy exploratory action might fail for reasons unrelated to the action's quality).
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Verifiable binary outcome rewards: All three benchmarks provide clean, verifiable success/failure signals (task completion in ALFWorld, purchase success in WebShop, patch correctness in SWE-bench). AEM's mechanism relies on the sign of the advantage
A(a, s)to determine whether to apply entropy-increasing or entropy-decreasing pressure. In domains with continuous or noisy rewards—where the magnitude of reward matters as much as the sign—modulating advantage magnitude based on entropy could distort the reward signal in ways not captured by the current analysis. -
Relatively short trajectories: ALFWorld caps at 50 steps, WebShop at 15 steps. These are long enough to create a credit assignment challenge (sparse outcome rewards over dozens of steps) but short enough that the compounding effect of many small misassignments may not accumulate to policy-destroying levels. In settings with hundreds or thousands of steps (e.g., long-horizon scientific discovery, extended software development cycles), the quality of the entropy proxy and the stability of within-group normalization would face a much harder test.
The consequence. AEM's effectiveness may not generalize to:
- Stochastic environments where the entropy-advantage interaction no longer cleanly separates exploration from noise.
- Continuous or graded reward settings where multiplying advantages by entropy-derived coefficients could distort the relative weighting of small improvements vs. large improvements.
- Very long-horizon tasks where the within-group normalization may become unreliable (if groups span diverse states with very different entropy characteristics) and the proxy quality may degrade due to compounding approximation error over many steps.
- Model families with different entropy characteristics—e.g., models trained with different tokenizers, different architectural choices (mixture-of-experts vs. dense), or different pretraining objectives may have different token-level entropy distributions, potentially requiring retuning of the method's hyperparameters (
λ, min-max threshold).
Additionally, all experiments use instruct-tuned models (Qwen2.5-Instruct, Qwen3) as the starting point for RL training. These models have already been aligned to follow instructions and may have more structured response distributions (clearer separation between "confident" and "uncertain" responses) than base pretrained models. AEM's entropy signal may be less informative when starting from a base model with flatter, less differentiated response distributions.
What evidence exists in the paper. All experiments are on these three benchmarks with Qwen models. The paper provides no evidence that AEM transfers to other types of environments (stochastic, continuous-reward, dialogue-based, multi-agent), other model families (Llama, Mistral, Gemma), or other starting points (base models vs. instruct-tuned models). The authors present the consistency across benchmarks and model scales as evidence of generality, but the benchmarks and models share structural properties that limit the strength of this claim.
Mitigation status. Not addressed. The paper's concluding statement that AEM "consistently improves strong baselines" is true for the tested settings but overstates the demonstrated level of generality. The paper does not discuss domain-specific assumptions that might limit transfer, does not test on a stochastic environment, and uses a single model family (Qwen) for all experiments. For practitioners using different model families or deploying agents in substantially different environments, the paper provides no guidance on whether AEM's mechanism is likely to transfer or what failure modes to watch for.
7. Implications and Future Directions
How This Work Changes the Landscape
This paper shifts how the field should think about credit assignment in multi-turn agentic RL: from imputing missing step-level rewards to modulating the entropy consequences of existing outcome-level advantages using the policy's own intrinsic uncertainty. This is not a paradigm shift—it does not replace group-based RL, nor does it introduce a new optimization framework—but it is a substantive reframing of the credit assignment problem that opens a new axis of investigation orthogonal to prior approaches. The paper's theoretical core (Theorem 3.2.2)—showing that entropy drift under natural-gradient updates is governed by the interaction advantage × relative surprisal—provides a principled bridge between credit modulation and entropy dynamics that did not previously exist in the LLM RL literature.
The practical consequence of this reframing is that the policy's own uncertainty becomes a first-class credit assignment signal, not merely a regularization target or a diagnostic metric. Before this work, entropy in LLM RL was treated primarily as something to be controlled—added as a bonus to encourage exploration (Mnih et al., 2016b; Xu et al., 2025b), monitored to detect premature convergence (Shen, 2026), or used for token-level gradient recalibration (Wang et al., 2025b; Dong et al., 2026a). AEM demonstrates that response-level entropy can play a more active role: by rescaling advantages according to whether a response was unusually certain or uncertain given the policy's current state, one can shape entropy dynamics toward an exploration-exploitation transition without any external scheduling, auxiliary models, or structural trajectory assumptions. This is significant because it converts entropy from a training artifact to be managed into a control signal that can be deliberately manipulated through advantage rescaling.
The paper also reconciles a tension in the self-supervised credit assignment literature. Prior self-supervised methods like GiGPO (Feng et al., 2025) and IGPO (Wang et al., 2026) attempt to infer step-level credit from trajectory structure—which step "caused" the outcome—and the paper identifies their vulnerabilities as context inconsistency, grouping bias, and dependence on structural assumptions (Section 2). By sidestepping causal attribution entirely and instead modulating credit based on how the policy generated each response (its uncertainty, captured by entropy), AEM avoids needing to model which actions caused which outcomes. This resolves the apparent contradiction that self-supervised methods can improve credit assignment (as shown by prior work) while being brittle to structural assumptions (as the paper argues): the brittleness comes from trying to infer causality from structure; AEM's approach of modulating based on generation-time uncertainty is structurally simpler and empirically more robust (though still imperfect, as the 14% sign-disagreement rate in Analysis A indicates).
The paper's methodological contribution—specifically, the shuffle and reverse ablations that establish necessary conditions for entropy-based credit modulation—provides a template for how the field should evaluate future credit assignment methods. If a new method claims to improve credit assignment through advantage rescaling, it should demonstrate both that (a) randomizing the assignment destroys the benefit (+AEM_shuffle) and (b) reversing the modulation direction causes harm (+AEM_reverse). This two-condition test distinguishes genuine mechanism-driven improvements from incidental benefits of increased advantage heterogeneity (which the shuffle ablation shows provides only marginal Score improvement and no Success Rate improvement). The fact that AEM passes both tests—shuffling degrades performance, reversing degrades it severely—while producing consistent gains provides some of the strongest mechanistic evidence in the current LLM RL literature. This ablation protocol should become standard for papers proposing entropy-aware or uncertainty-aware credit modulation methods.
The work also shifts attention from the token level to the response level as the correct granularity for uncertainty estimation in agentic RL. Theorem 3.2.1's formal nesting of token → response → policy entropy is technically straightforward but practically important: it justifies why per-token entropy fluctuates with vocabulary-level noise (synonyms, formatting variants) while response-level entropy captures the uncertainty that matters for environment interaction. This insight should influence how future method designers choose the granularity of their uncertainty signals—not just for credit modulation, but for any mechanism that uses policy uncertainty to guide training (adaptive curricula, difficulty estimation, exploration bonuses). The paper's response-level analysis does not invalidate token-level methods (which may be appropriate for single-turn settings where each token can affect the outcome), but it establishes a boundary condition: in multi-turn settings where the environment reacts only after complete responses, token-level uncertainty signals are misaligned with the causal structure of interaction.
One direction that becomes less attractive as a result of this paper: pursuing ever-more-complex causal attribution methods for step-level credit inference. If a simple, supervision-free entropy modulation can capture much of the benefit of step-level credit assignment (AEM's 8.8 pp gain on GRPO with 1.5B on ALFWorld is competitive with or exceeds the improvements reported for GiGPO and IGPO on similar benchmarks), the marginal benefit of adding complex trajectory-structure analysis may not justify the engineering complexity and brittleness. The paper does not directly compare against these methods (a limitation, as discussed in Section 5), but its strong absolute performance on GRPO—the simplest group-based backbone—suggests that there is substantial low-hanging fruit in modulating existing outcome-level advantages before attempting to reconstruct missing step-level signals.
Follow-Up Research This Work Enables
Direct comparison of AEM against GiGPO and IGPO on identical benchmarks, with per-difficulty breakdowns. The paper criticizes GiGPO and IGPO for context inconsistency, grouping bias, and dependence on structural assumptions, but never empirically compares against them. A strong follow-up would run GRPO+AEM, GRPO+GiGPO, and GRPO+IGPO on ALFWorld and WebShop under identical training budgets (same model, same group size, same step count), and report both aggregate performance and per-difficulty-quintile breakdowns. The specific hypothesis: GiGPO and IGPO should outperform AEM on problems where the trajectory structure clearly indicates which steps were causal (e.g., clean "before vs. after" state changes), while AEM should outperform them on problems with delayed, nonlinear, or ambiguous action-outcome mappings (where structural credit inference is unreliable). Per-difficulty analysis—binning prompts by the base model's success rate before RL, as done in the compute-optimal test-time scaling literature—would reveal whether AEM's entropy mechanism is most beneficial on easy-to-medium problems (where the model sometimes succeeds and entropy is informative) or on hard problems (where it never succeeds and entropy modulation may be counterproductive). Such an analysis would directly address the limitation identified in Section 6 regarding difficulty awareness.
Sensitivity analysis of the entropy proxy: how does the α ≈ -(S − H_resp) relationship change across training, model scales, and task types? The paper reports a Pearson r = 0.63 and 85.9% sign agreement between α−1 and Monte Carlo estimates of -(S − H_resp) for n = 64 states probed at an unspecified training point. A systematic follow-up would track this correlation across training checkpoints (e.g., every 25 steps on WebShop) and across states stratified by: (a) the absolute response-level entropy (are low-entropy states more or less reliable for the proxy?), (b) the number of previous environment interactions in the trajectory (does proxy quality degrade in later trajectory steps due to compounding context?), and (c) the task category (are the per-category regressions on ALFWorld's Heat and Look categories correlated with reduced proxy quality?). Such a study would identify when the entropy proxy is unreliable and could motivate adaptive proxy designs—e.g., falling back to the base advantage estimator when the proxy quality is expected to be low, similar to AEM's existing fallback when the min-max range is <0.1. It could also motivate training a lightweight "proxy quality predictor" that estimates the current sign-agreement probability from easily-computed statistics (group size, entropy variance, trajectory length) and adjusts the modulation temperature λ accordingly.
Combining AEM with difficulty-aware or compute-adaptive policy selection at the prompt level. AEM modulates credit uniformly across all prompts based on within-group relative entropy, discarding absolute entropy magnitude and prompt difficulty. A natural extension would combine AEM's per-response modulation with a per-prompt strategy selector that uses the absolute group-level entropy statistics to decide how to allocate training signal. For instance, prompts where the within-group entropy spread is very wide might benefit from stronger AEM modulation (higher λ), while prompts where all responses have similar low entropy might indicate near-saturation and benefit from reduced modulation or an alternative strategy (e.g., rejection sampling fine-tuning rather than RL). Alternatively, the base RL algorithm could be switched per-prompt: GRPO+AEM for medium-difficulty prompts (where credit modulation helps), standard GRPO for easy prompts (where credit assignment is already clear), and a more exploratory variant (e.g., GRPO with a higher temperature or explicit entropy bonus) for hard prompts (where the model never succeeds and needs more aggressive exploration before AEM's modulation can be useful). The paper's finding that AEM provides the largest gains when applied to the weakest backbone (GRPO, +8.8 pp) and smaller gains on stronger backbones (DAPO, +0.5–6.0 pp) suggests that the optimal combination of base RL algorithm and credit modulation strategy is prompt-dependent—a meta-optimization problem that a difficulty-conditioned selector could address.
Training a "revision model" whose proposal distribution benefits from AEM-guided entropy dynamics. The paper studies AEM purely as a credit modulation method for RL training, but the exploration-exploitation transition it induces (higher early entropy, lower late entropy) suggests a connection to iterative revision approaches in single-turn reasoning (as studied in the compute-optimal test-time scaling paper from the reference example). A strong follow-up would use AEM-trained policies as the proposal distribution within a test-time search or revision framework. The hypothesis: because AEM preserves higher response diversity early in training and then converges more completely, the resulting policy should produce a better proposal distribution for test-time strategies like best-of-N weighted selection or beam search against a process reward model. Specifically, one could compare the pass@k rate (fraction of k sampled responses that contain at least one correct answer) of AEM-trained policies vs. baseline-trained policies, and then evaluate whether downstream verifier-guided selection achieves higher accuracy from the AEM-trained proposal distribution. This connects AEM's training-time exploration-preserving mechanism to the test-time compute allocation literature, testing whether entropy-aware credit modulation during training produces policies that are better "explorers" at inference time.
Stress-testing AEM on stochastic environments where the entropy-advantage relationship may break. All three benchmarks in this paper are largely deterministic given the agent's actions. In stochastic environments—multi-agent dialogue with sampled interlocutor responses, game-playing against randomized opponents, or tool-use where API calls return non-deterministic outputs—the mapping from action quality to outcome is noisier. A high-entropy exploratory action that fails in a stochastic environment might have failed due to environment randomness rather than action quality, and amplifying its negative advantage (as AEM would for a low-uncertainty bad response) would incorrectly penalize the policy. A critical stress-test would deploy AEM on a deliberately stochastic benchmark—e.g., a multi-turn negotiation task where the counterparty's responses are sampled from a distribution, or a text-based game with random events—and measure whether AEM's performance gains persist, diminish, or reverse. If AEM degrades performance in stochastic settings, that would establish a boundary condition: entropy-aware credit modulation is effective only when outcome variance is predominantly driven by action quality, not environment noise. This would also motivate a variant that incorporates an estimate of environment stochasticity into the modulation—e.g., reducing λ (weakening modulation) when reward variance within a group is high, since high reward variance in a deterministic environment with fixed prompts indicates that action quality varies meaningfully, but high variance in a stochastic environment could indicate noise.
Extending the theoretical analysis to characterize when the entropy proxy's sign agreement degrades, and developing a corrected proxy. Theorem 3.2.2 provides the exact relationship D = A × (S − H_resp), but AEM approximates S − H_resp with the length-normalized token entropy sum ΣH_ℓ / |a| (minus its group-normalized counterpart). The Doob decomposition (Appendix F.4) shows that the approximation error is a zero-mean martingale M_L, but does not bound its variance or characterize when it is likely to be large. A theoretical follow-up would derive conditions under which the martingale term dominates—e.g., when the per-token entropy distribution is heavy-tailed, when the response length is short (few tokens over which to average the martingale noise), or when the policy's next-token distributions are multimodal (producing large per-token entropy variance and hence large martingale steps). These conditions could motivate a corrected proxy that adjusts the raw token-entropy sum by an estimate of the martingale variance—e.g., subtracting a term proportional to the variance of per-token entropies within the response, or re-weighting token entropies by the model's confidence in its top token choice (since high-confidence tokens with high entropy suggest multimodal distributions where the martingale noise is likely large). The corrected proxy could be evaluated using the same Monte Carlo probing protocol from Analysis A, with the goal of improving the sign agreement rate from 85.9% to >95%.
Practical Applications and Downstream Use Cases
Lightweight credit assignment upgrade for group-based RL training pipelines with zero additional model overhead. The most immediate practical application is as a drop-in module for any existing GRPO, DAPO, or GSPO training pipeline targeting multi-turn agent tasks. AEM requires no new models (no critic, no PRM, no auxiliary reward model), no additional forward passes (entropy values reuse logits already computed for importance sampling in GRPO), and only one hyperparameter (λ = 1, shown to work across benchmarks and model scales without tuning). The computational overhead is 1.1% of per-step training time (Section 5.4, Figure 6)—on ALFWorld with Qwen2.5-1.5B, this translates to approximately 5.6 seconds per training step out of a total of ~500 seconds, dominated by rollout generation and model updates. For a team already running GRPO-based agent training, adopting AEM means adding roughly 30 lines of code (response-boundary parsing, entropy aggregation, min-max normalization, softmax, self-calibration, advantage multiplication—matching Algorithm 1 in Appendix A) and accepting a ~1% increase in per-iteration wall-clock time. The expected return on this minimal investment is substantial: on WebShop with Qwen2.5-7B, AEM improves GRPO's Success Rate from 75.9% to 80.5% (+4.6 pp) and DAPO's from 86.7% to 88.9% (+2.2 pp). Even on the strongest baselines where gains are smaller, the cost is so low that AEM should be a default inclusion in the training stack—there is no scenario in this paper where AEM consistently hurts mean performance (though higher variance is a concern, as discussed in Section 6).
Improving sample efficiency of agent data generation for self-improvement loops. The compute-optimal test-time scaling literature showed that allocating inference compute adaptively based on problem difficulty can produce a 4× effective data efficiency gain—matching best-of-256 with only 64 generations. AEM offers an orthogonal efficiency gain on the training side: by providing more effective credit signals during RL, it enables the policy to learn more from each collected trajectory. The paper's training curves (Appendix D, Figures 7–11) show that AEM-augmented methods achieve higher success rates at equivalent step counts (and equivalent number of environment interactions, since both use the same rollout group size N = 8). For a self-improvement loop where an agent generates trajectories, evaluates outcomes, and retrains on successes—the paradigm underlying STaR, ReST^EM, and related methods—AEM could be deployed in the RL phase to extract more learning signal from each batch of collected trajectories, reducing the number of environment interactions needed to reach a target performance level. The specific benefit depends on the cost ratio of environment interaction (expensive—real-world actions, API calls, code execution) to training compute (cheap—GPU hours for gradient updates), which is typically high for agentic tasks. Even a 2–3% improvement in sample efficiency could translate to substantial cost savings when environment interactions are the bottleneck.
Enabling effective RL fine-tuning of small models (1–3B parameters) for multi-turn agent tasks, where credit assignment ambiguity is most severe. The paper's largest absolute gains occur at the smallest model scale: +8.8 pp on GRPO with Qwen2.5-1.5B on ALFWorld, +5.6 pp Success Rate on WebShop with 1.5B. This pattern—larger gains on weaker backbones—suggests that AEM is particularly valuable when credit assignment is most ambiguous, which is precisely the regime of small models where the policy's initial performance is low and most trajectories fail, producing batches dominated by uniformly negative outcome rewards with little differentiation between better and worse failures. Small models are increasingly important for on-device deployment (privacy, latency, cost), and the compute-optimal inference literature has shown that small models with smart test-time strategies can match much larger models on medium-difficulty tasks. AEM provides a training-side complement: it makes RL fine-tuning of small models for agentic tasks more effective than current group-based methods, potentially enabling small on-device agents that are trained with RL to perform multi-turn tasks (web navigation on mobile devices, simple software debugging in local IDEs) at previously unattainable quality levels. The specific deployment scenario: a 1.5B–3B model fine-tuned with GRPO+AEM on a corpus of web navigation or coding tasks, deployed on-device where a larger model would be infeasible due to memory constraints, achieving success rates that would previously have required a 7B+ model trained with standard GRPO.
A default diagnostic for new credit assignment methods: the shuffle-and-reverse ablation protocol. The paper's ablation methodology—shuffling coefficients to break alignment while preserving marginal statistics (+AEM_shuffle), and reversing the entropy-to-advantage mapping to test directional correctness (+AEM_reverse)—provides a template for evaluating any method that claims to improve credit assignment through per-sample advantage rescaling. This protocol is lightweight (it requires no new training infrastructure, just permuting or inverting the modulation coefficients before applying them), and it cleanly separates mechanism-driven improvement from incidental effects of increased advantage heterogeneity. The paper's specific finding—that shuffled coefficients marginally improve Score (85.6 vs. 83.6) but do not improve Success Rate (64.8% vs. 65.0%), while reversed coefficients actively harm both metrics—establishes a baseline that future methods can be judged against. A new credit modulation method that passes the shuffle test (shuffling destroys the benefit) but fails the reverse test (reversing does not cause harm) would indicate that the method's mechanism is partially but not completely aligned with the theoretical entropy-advantage interaction—useful diagnostic information for method developers. A method that passes neither test (shuffling doesn't hurt, reversing doesn't hurt) would indicate that the claimed credit assignment mechanism is not actually what drives performance, and the method's benefits likely come from some other property (regularization, variance reduction, implicit learning rate effects). The paper provides a concrete, replicable protocol for establishing this evidence, and the field would benefit from adopting it as a standard evaluation requirement for credit modulation methods.
When to Prefer This Method
The paper positions AEM as a general-purpose plug-in for group-based RL methods, not as an alternative to them. It does not frame a tradeoff against named competing credit assignment methods (GiGPO, IGPO, Tree-GRPO, ATPO), so a forced "prefer A over B" matrix would be speculative. However, the paper's results and limitations implicitly define conditions where AEM's mechanism is likely to be effective versus where alternatives should be considered:
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Prefer AEM when: (1) the training pipeline already uses a group-based RL method (GRPO, DAPO, GSPO) and the team wants a zero-model-overhead credit assignment improvement; (2) the environment is largely deterministic—outcome variance is driven by action quality, not stochasticity; (3) the policy generates responses with meaningful variation in per-response uncertainty (entropy spread within groups is non-trivial, so AEM's min-max normalization is informative); (4) the task involves moderate-length trajectories (10–50 steps) where sparse outcome rewards create genuine credit assignment ambiguity but the compounding of proxy errors remains manageable; (5) the prompt distribution contains a substantial fraction of solvable problems (the model sometimes succeeds, so AEM's exploration-preserving mechanism on failures has a path toward eventual success).
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Consider alternatives when: (1) the training budget is severely limited and a single bad seed is unacceptable—AEM's increased variance (systematically larger standard deviations in Table 1) means a risk-averse practitioner running only one or two seeds might prefer the more reliable baseline; (2) the environment is highly stochastic—outcome noise may corrupt the entropy-advantage relationship in ways this paper does not characterize; (3) the policy's token-level entropy distribution is pathological (e.g., all responses have nearly identical per-token entropy, making the min-max normalization uninformative and triggering frequent fallback to α = 1); (4) the task involves primarily unsolvable prompts (hard problems outside the model's capability range) where AEM's entropy-increasing pressure on failures cannot lead to eventual success and may inject destabilizing noise—difficulty-aware or capability-gated methods would be more appropriate; (5) the deployment setting requires a specific causal attribution of credit to individual steps (e.g., for interpretability or safety auditing), which AEM explicitly avoids—structural credit propagation methods like Tree-GRPO or SPA-RL would provide step-level credit estimates that AEM does not.
