acceptodds
Under review as a conference paper at ICLR 2027

Entropy Targeting in Sequential Reinforcement Fine-Tuning of Language Models

Abstract

Sequential reinforcement fine-tuning asks a language model to keep improving as its tasks change, yet the auxiliary signals added to stabilize such training are rarely checked for whether they reach the policy update at all. We study this question in AdaCoT-CL, a group-relative sequential learner that combines three consistency signals (entropy targeting on the reasoning span, alignment between reasoning and answer representations, and answer agreement) with replay, and we reanalyze 63 recorded runs on a five-task reasoning stream, 59 of them with Qwen3-8B. We first show that the agreement signal supplies no direct policy gradient: its group-shared reward bonus cancels whenever rewards are centered within each prompt group, and its auxiliary loss is detached. This result partitions the seven ablation variants into four effective objectives and motivates a grouped comparison. In that comparison, configurations with entropy targeting improve on average and those without it decline. On fixed monitoring panels, the 12 runs with entropy targeting gain 13.2 accuracy points from initialization to the end of the sequence, while the 9 runs without it lose 8.7 points (difference 21.8 points, exact permutation ; a contrast averaged within seed and alignment blocks gives 24.1 points, ), and the primary comparison replicates this direction against five baselines. The largest divergence occurs between the end of the LogiQA phase and step 32 of the final task, a block that combines training on the new task with replay of earlier prompts: mean accuracy on the earlier panels rises by 27 points on average with entropy targeting, and the smallest such rise, 16.7 points, exceeds the largest without it, 4.2 points. The evidence has clear boundaries: the panels are drawn from training prompts, initial accuracy is low under a 512-token completion budget, the benefit shrinks under other task orders, and the same objective collapses Llama-3.1-8B-Instruct. We therefore present entropy targeting as the consistency signal that distinguishes improving from declining configurations of this learner, and we specify the held-out protocol needed to establish it as a continual-learning method.

Primary area:
reinforcement learning
Keywords:
reinforcement fine-tuning, reinforcement learning with verifiable rewards, group relative policy optimization, entropy regularization, continual learning, large language models, reasoning, plasticity

Reviews

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1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_8GkrOpenReview ↗
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2
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Paper summary

The paper audits auxiliary objectives in a sequential reinforcement fine-tuning pipeline and retrospectively analyzes 63 recorded runs. It shows that a group-shared answer-agreement reward cancels under within-group reward centering, while a detached agreement loss provides no direct policy gradient. After grouping configurations by their effective objectives, the authors find that entropy targeting is associated with better initial-to-final accuracy changes on monitored training prompts. The paper also examines when this improvement emerges and documents sensitivity to task order and model family.

Critical strengths

The implementation audit is useful and unusually transparent. Identifying inactive gradient paths and regrouping ablations by their effective objectives helps avoid attributing improvements to components that do not actually affect the policy update.

The authors carefully delimit their empirical claims. They acknowledge the training-prompt evaluation, the distinction between initial-to-final improvement and backward transfer, and the failure on Llama. The entropy-associated separation across the recorded runs is an interesting observation that merits further investigation.

Critical weaknesses

Limited conceptual novelty and insufficient comparison with established entropy controls. Entropy regularization and target-entropy control have a long history in reinforcement learning, and entropy dynamics have already received substantial attention in reasoning-model RL, as the paper’s related-work discussion acknowledges. The squared target-entropy penalty is a straightforward regularizer, and its interpretation as a signed, state-dependent entropy coefficient follows directly by differentiation. Likewise, cancellation of a group-shared reward under group centering is an elementary property of the estimator. Applying these observations to sequential fine-tuning could still yield a valuable empirical contribution, but the paper does not establish what entropy targeting offers beyond a fixed entropy bonus or other established entropy-control methods under matched conditions. Consequently, the contribution remains primarily an implementation-specific audit and empirical association.

The evaluation does not establish a sufficiently general empirical finding to compensate for the limited methodological novelty. The main results use small training-prefix panels and measure change from initialization, rather than held-out retention relative to task acquisition. The restrictive 512-token thinking budget leaves improvements in answer completion or formatting unresolved. Moreover, sampling and update log probabilities use different distributional transformations, so entropy targeting may interact with the particular ratio and clipping behavior of this implementation. The reduced gains under alternative task orders and collapse on Llama further limit generality. The authors appropriately acknowledge these issues, but stronger evidence is needed to establish a transferable insight about sequential RL.

Questions for authors

Clarification: Beyond the implementation audit and the observed association in this pipeline, what specific finding distinguishes the contribution from established entropy regularization and target-entropy control?

Additional evidence that could change my assessment: Can the authors provide a matched comparison against a fixed entropy bonus and an adaptive target-entropy baseline, with the same replay and training budget? Such a comparison would help establish whether the proposed targeting objective provides a distinct benefit.

Additional evidence that could change my assessment: Does the advantage persist with consistent sampling/update probability conventions and on held-out panels evaluated immediately after task acquisition and at the end of training? Completion-length and truncation statistics would also help distinguish improved budget compliance from improved retention.

1 comment

Thank you for distinguishing the useful implementation analysis from the stronger evidence needed for a general method claim.

Our specific empirical finding is that, after accounting for which auxiliary terms directly affect policy gradients, the configurations containing entropy targeting improve on average on the monitored panels, while those without it decline. The pooled difference is 21.8 accuracy points, with positive contrasts within each seed. Much of the separation develops during a late block containing both new-task training and replay. This connects the objective audit to a concrete pattern in sequential learning.

We agree that the cancellation identity and the derivative of the squared entropy penalty are elementary. Their role is to establish what the implementation actually optimizes and how its ablations should be interpreted. They do not establish a new general principle of entropy control.

We also agree that the current experiments do not demonstrate an advantage over a fixed entropy bonus or an adaptive target-entropy baseline. The existing fixed-weight sweep varies multiple consistency coefficients jointly and cannot substitute for those comparisons.

Finally, the observed advantage has not been established with consistent sampling and update probability conventions or with held-out evaluations relative to acquisition. The training-source panels, completion budget, order sensitivity, and Llama failure materially restrict its scope.

The contribution we can defend is therefore the connection between active gradient paths and a sizeable, temporally localized empirical association in this learner. Whether that association transfers to a corrected learner and improves held-out retention remains an open empirical question.

Reviewer_pUt6OpenReview ↗
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Paper summary

The authors study how to help LLMs to learn new tasks without forgetting old ones by revisiting existing experiments and find that keeping the model’s uncertainty near a fixed target seems to help, while some other training tricks don’t actually contribute a learning signal. There are some empirical studies proposed and theoretical analyses provided for this work.

Critical strengths
  • The authors provide many quantitative analyses to the results
  • There are some theoretical analyses to the pipeline.
Critical weaknesses

I found many unusual expression that makes me hard to follow the paper, and I will just raise several examples below:

"task-delimited" -- what means by this?

"four-sample plurality-answer accuracy on panel DD" -- Why taking four sample? For plurality correctness, do you mean taking the advantage using majority voting? Why doing this?

"No such update occurs during the final monitoring pass of the primary runs; it does occur in some sensitivity runs." -- Why are you trying to defense for?

Also, many terms in Eq.7 comes broadly until the later context is introduced so. Why you set H∗H_* as softplus(2)\text{softplus(2)}? I didn't find the explanation to this;

Also, for the choice of G=4G=4 along with the choice of 32 and 64, it seems that these are also arbitrarily chose.

The experiment setup that caps the rollout completion to 512 also lacks motivation, and the empirical results make the readers hard to parse.

Questions for authors

If possible, see weakness section.

1 comment

Thank you for giving specific examples. We agree that several definitions appear too late and make the experimental setup unnecessarily difficult to follow.

“Task-delimited” means that training proceeds through separate task phases in a fixed order, with known task boundaries.

“Four-sample plurality-answer accuracy” is an evaluation rule. For each prompt, the model generates four responses. We extract their answers, select the most frequent answer, and compare it with the reference. Plurality does not require more than half the votes. This is distinct from computing training advantages. Four is the fixed sampling count used in these experiments; the study does not establish it as an optimal choice.

The sentence about updates during monitoring concerns measurement consistency. An intervention between task evaluations means that different tasks can be scored using different model states. No intervention occurs during the final monitoring pass of the primary runs, while some sensitivity runs contain such interventions. We disclose this because it affects how those measurements can be compared.

The entropy target is parameterized through softplus to keep it positive. Applying softplus to the initial value 2 gives approximately 2.127 nats. Positivity explains the parameterization, but does not justify that particular target as optimal. Likewise, steps 32 and 64 are the midpoint and endpoint of each 64-update task phase. They are logging checkpoints, not theoretically derived transition points.

The 512-token cap is a fixed experimental constraint, not a validated sufficient reasoning budget. It leaves open whether improved completion contributes to the measured accuracy rise. The paper needs to make these design choices and their consequences easier to see before presenting the results.

Reviewer_BnvHOpenReview ↗
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Paper summary

The paper revisits a sequential reinforcement fine-tuning pipeline using 63 recorded runs, mostly with Qwen3-8B. It shows that the group-shared agreement reward cancels under within-prompt normalization and that the agreement auxiliary has no direct policy gradient, leaving four effective objectives among the seven masks. Entropy-targeted configurations show larger initial-to-final accuracy gains on small panels drawn from the training source pool, with much of the difference appearing during the final task/replay phase. The analysis also covers sensitivity to task order, a single-seed Llama failure, and the limits of drawing continual-learning conclusions from these measurements.

Critical strengths
  1. The gradient-path audit is a useful part of the paper. Proposition 1 distinguishes a signal present in the implementation from one that actually affects policy updates, which makes the ablation results easier to interpret. The authors also take care to distinguish initial-to-final improvement from retention measured after acquisition.

  2. The association with entropy targeting is sizeable within the recorded runs. Table 2 reports a 21.8-point pooled difference, positive contrasts within all three seeds, and a seed/alignment-blocked check. Together with the timing analysis, the discussion of inactive components, measurement limits, and failure cases gives the case study useful diagnostic value.

Critical weaknesses
  1. The main difficulty is interpreting what the accuracy rise tells us about sequential learning. Each earlier task is assessed on 16 prompts from its training source pool, and the available comparison starts before acquisition. Without saved per-example outputs or frozen model checkpoints, it is difficult to tell whether the rise reflects retained or relearned capability, better answer completion, or parsing within the 512-token limit. The authors acknowledge this and appropriately frame the paper as a retrospective analysis, but the distinction remains important to its main finding. It is also hard to track which measurements were observed, reconstructed, or proposed across the main text and appendices; a compact overview would make the argument easier to follow.

  2. It is also unclear how much the entropy association depends on the details of this learner. Sampling and update scores use different transformations/modes, the ratio uses mean log probabilities, and fallback spans can include padding (Appendix B.1–B.2). These disclosed details do not affect the cancellation proof, but they complicate the interpretation of the empirical result. Appendix N lays out relevant controls that have yet to be run. The sensitivity to task order and the single-seed Llama failure further suggest that the conditions under which the observation holds need clarification, without establishing entropy as the cause. A small, focused replication would strengthen this part of the paper.

Questions for authors
  1. Given the available archive, which explanations of the final-phase rise can be distinguished? It would help to state what the initial-to-final training-panel improvement establishes, what remains unknown about retention after acquisition, and which measurements still depend on the proposed protocol in Appendix N.

  2. Would it be feasible to run a small entropy-on/off replication in the primary task order, evaluating the same disjoint panels immediately after acquisition and at a frozen final checkpoint? Using non-padding spans and consistent policy scoring, while recording answer completion and truncation at the existing 512-token budget, would help establish whether the main observation persists under a clearer measurement protocol.

  3. A brief discussion of CoDaPO (ICML 2026) may be useful here. Its analysis of confidence and group-relative advantages suggests a way to check whether the late rise in accuracy is accompanied by changes in the usable reward signal, alongside entropy.

2 comments

Thank you for recognizing the value of the gradient audit and for identifying where the interpretation needs to be clearer.

The archive supports two empirical findings. First, entropy-targeted configurations have larger average initial-to-final accuracy changes on the monitored training-source panels. Second, much of this separation develops during the first training-and-replay block of the final task. The latter pattern also remains when runs with interventions during either endpoint evaluation are excluded.

These observations locate the improvement, but they do not identify its cause. The available records cannot separate retained capability, relearning through replay, and better completion or parsing within the token budget. Initial-to-final change includes learning during acquisition and therefore cannot establish retention after acquisition. The held-out evaluation described in Appendix N is a proposed protocol, not completed evidence.

Your suggested replication directly addresses this gap. Consistent policy scoring, non-padding spans, and frozen evaluations immediately after acquisition and at the final checkpoint would provide a stronger test. Completion and truncation measurements would help interpret any remaining advantage. We are not presenting such a replication in this response.

Thank you also for suggesting CoDaPO. Its analysis of confidence and group-relative advantages motivates examining whether the late rise coincides with changes in the usable reward signal. That is a plausible explanation to test, rather than a mechanism established by our present analysis.

Thank you for the thoughtful clarification. I appreciate the gradient audit and the authors’ careful distinction between the observed gains and their possible explanations. The proposed replication is a useful next step toward understanding how much the findings depend on the particular scoring and evaluation setup. With that question still open, I will maintain my current assessment. I encourage the authors to pursue this validation, which would strengthen the contribution and help others build on these observations.

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