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Under review as a conference paper at ICLR 2027

Uncovering Latent Reasoning Strategies in Language Models

Abstract

A language model trained on reasoning tasks learns to solve problems via multiple distinct strategies, yet these strategies are implicit and entangled within the model's response distribution. We study the problem of decomposing the response distribution of a given pretrained language model into a structured, strategy-conditioned representation. Specifically, we learn a latent-variable factorization , where a router maps each input to a distribution over latent strategies and a generator produces the response conditioned on that strategy. A key challenge is that the generator, initialized from the base model, already represents without using . Standard variational inference therefore gives the model no incentive to route information through and can yield a severe form of posterior collapse. To address this, we propose a variational objective that measures fractional information gain relative to the base model's response loss and concentrates reconstruction pressure on tokens with high base model surprisal, encouraging to encode strategy-relevant response variation. We introduce a benchmark of multi-strategy algorithmic tasks and show that this objective recovers latent codes aligned with distinct reference strategies while preserving the base model's response distribution. On this controlled benchmark, we show that active intervention in the learned latent space enables more efficient exploration of the model's strategy space.

Primary area:
generative models
Keywords:
language models, reasoning, latent variable models, variational inference, posterior collapse

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_ZW8AOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
3
Presentation
3
Soundness
1
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Paper summary

This paper studies how to expose multiple reasoning strategies implicit in a language model's response distribution as an explicit latent variable. The authors seek a router–generator factorization in which a router maps an input to a distribution over continuous latent variables and a generator produces a response conditioned on the input and sampled latent. The intended factorization should preserve the base model's observable response distribution while making the latent informative, controllable, and semantically consistent across related inputs.

The paper identifies a relevant posterior-collapse problem: because the generator is initialized from a model that already represents the target response distribution, a standard conditional ELBO can achieve high marginal fidelity while ignoring the latent. To address this, the authors propose model-directed reconstruction. The frozen base model is used to normalize reconstruction loss and assign greater weight to high-surprisal response tokens, based on the hypothesis that such tokens contain strategy-defining branch decisions. The method is evaluated on six synthetic algorithmic task families with parser-identifiable reference strategies, using adapted Qwen2.5, SmolLM2, and OLMo models. The paper additionally uses the learned latent space for directed strategy exploration and presents a preliminary complexity-penalized variational analysis of strategy recovery.

I find the problem formulation interesting and the proposed use of base-model residual surprisal intuitive. However, the primary evaluation metrics do not rule out important degenerate solutions and do not establish that the factorized model preserves the base model's response distribution. In addition, the experiments recover strategies explicitly imposed by a synthetic trace generator after the base models have been fitted to that controlled distribution. These limitations prevent the current evidence from supporting the paper's broader claims about uncovering latent reasoning strategies in language models.

Critical strengths
  1. A clear and consequential problem formulation. The paper correctly identifies that fitting the observable response distribution is insufficient to identify a meaningful latent factorization, especially when a pretrained generator already represents that distribution at initialization. The distinction among latent informativeness, within-input strategy separation, and cross-input semantic consistency is useful and more precise than treating any non-collapsed latent as interpretable.

  2. An intuitive model-directed objective with intervention-based experiments. Weighting reconstruction toward response positions that remain surprising to the frozen base model is a plausible way to focus the latent on consequential branch decisions rather than predictable token-level details. The inverse-surprisal control, comparisons across several model families, latent-geometry diagnostics, and active exploration experiment provide multiple complementary views of the method's behavior.

Critical weaknesses
  1. The primary metrics do not establish the claimed latent strategy factorization. Distributional Fidelity measures only whether a generated trace is a valid strategy-compatible solution; it does not measure whether marginalizing over the latent preserves the base model's response or strategy distribution. Analogical Consistency measures whether reusing a latent across two related inputs produces the same parsed strategy, but a generator that ignores the latent and always emits one valid strategy can achieve perfect validity and perfect consistency. Thus, the two headline metrics do not jointly rule out strategy collapse, loss of base-model strategy frequencies, or an inert latent. The active exploration results provide indirect evidence of latent influence but do not repair this central ambiguity in the main evaluation.

  2. The controlled benchmark and theoretical analysis provide limited support for the broader claim. The base models are first fitted to synthetic traces generated from a small, explicitly enumerated set of uniformly sampled strategies with highly regular output formats. Recovering this imposed structure is substantially easier than discovering naturally occurring, overlapping, hierarchical, or ambiguous reasoning strategies in a pretrained language model. Moreover, the theory analyzes an abstract complexity-penalized variational objective and assumes that the target strategy has a positive profiled-score margin over all misaligned encoders. It neither shows that surprisal weighting creates this margin nor instantiates the complexity term for the actual Transformer/LoRA architecture. Each pretrained model and objective is also represented by one selected training run, limiting evidence of stability.

Questions for authors
  1. How do the proposed metrics rule out a degenerate generator that ignores zz and always produces the same valid strategy? Please report a metric that jointly measures within-input strategy separation, dependence between ZZ and the generated strategy, and cross-input semantic consistency, such as intervention-based strategy diversity and conditional mutual information.

  2. Does the factorized model preserve the base model's response distribution rather than merely its valid-solution rate? Please compare base and factorized models using per-task and per-input strategy-frequency distributions and an appropriate divergence such as total variation or Jensen–Shannon divergence, together with changes in response likelihood and other observable output statistics.

  3. Can the method recover strategy structure that was not explicitly imposed by a synthetic trace generator? Please evaluate at least one realistic reasoning setting, such as mathematical proof, competition-level problem solving, or program synthesis, where strategies are independently annotated or judged and the base model is not first fitted to uniformly sampled, explicitly formatted strategy traces.

  4. Are high-surprisal tokens actually concentrated at strategy-defining branch points? Please quantify their association with annotated strategy-relevant positions while controlling for rare numbers, formatting tokens, lexical frequency, and sequence position. How does surprisal weighting compare with entropy weighting, learned token importance, or direct weighting of known strategy-transition positions on the controlled benchmark?

  5. How does the complexity-penalized variational theory formally relate to the proposed base-normalized, token-surprisal-weighted reconstruction objective? Can the authors instantiate the complexity term for the implemented architecture or show that surprisal weighting increases the profiled recovery margin for the target strategy? Otherwise, the theorem appears to be a conditional identifiability statement rather than a justification of the proposed algorithm.

  6. Are the reported improvements stable across independent training seeds and held-out hyperparameter selection? Please report mean and variance across seeds and select β\beta, latent dimensionality, and checkpoints using a validation split rather than the same strategy-alignment metric used for final reporting.

4 comments

We thank the reviewer for the detailed review, and for finding the problem formulation "clear and consequential" and the model-directed objective "intuitive". We respond to five points: the evaluation metrics (W1, Q1, Q2 → [Z1]), the scope of the benchmark (W2, Q3 → [Z2]), surprisal at strategy decisions (Q4 → [Z3]), the theory (W2, Q5 → [Z4]), and seeds and hyperparameter selection (W2, Q6 → [Z5]). We have revised the paper in response to the reviewer's feedback. Revisions are marked in blue, and all references below are to the revised paper.


[Z1] Evaluation metrics (W1, Q1, Q2)

"the two headline metrics do not jointly rule out strategy collapse, loss of base-model strategy frequencies, or an inert latent."

We agree that the original submission's "Distributional Fidelity" metric measured only whether generated traces are valid, not whether the distribution over strategies is preserved. We also agree that the definition of Analogical Consistency did not rule out a generator that ignores zz and always produces one strategy. In our experiments, this collapse does not occur, and the revised metrics give a score of 0 to a generator that ignores zz.

The revised Fig. 6 compares four base models on three new metrics, defined in §4.1 and App. E.1. They include the quantities requested in Q1 and Q2.

  • Distributional Fidelity is 1−TV1-\mathrm{TV} between the strategy distributions of the base model and the factorized model at each input, averaged over inputs (Q2). It measures whether the factorized model preserves the base model's distribution over strategies.
  • Strategy Separation is the conditional mutual information I(S;Z∣X)/H(S∣X)I(S;Z\mid X)/H(S\mid X) after subtracting a permutation baseline (Q1). It measures whether the latent determines the strategy within each input, averaged over inputs. It does not require a latent to select the same strategy on different inputs.
  • Strategy Transfer measures the stronger property that a latent selects the same strategy across inputs. It is tested by an intervention: a latent drawn for one input is reused on another input, and we record whether the strategy is the same. This agreement rate, called Analogical Consistency in the submission, is then corrected for chance.

Ranges over the four base models (per-model values in Table 3):

ObjectiveDistributional FidelityStrategy SeparationStrategy Transfer
Model-directed (three objectives)0.82–0.900.68–0.930.63–0.87
ELBO and β\beta-ELBO0.87–0.890.01–0.02−0.01-0.01 to 0.020.02
Inverse-surprisal ablation0.71–0.770.01–0.03−0.02-0.02 to 0.040.04
Base model against itself (reference)0.93N/AN/A
  • The latent controls the strategy under the model-directed objectives and not under ELBO or β\beta-ELBO. Strategy Separation is 0.68–0.93 and Strategy Transfer is 0.63–0.87. Under ELBO and β\beta-ELBO both are at most 0.02, the level of a generator that ignores zz.
  • The model-directed objectives do not collapse to one strategy. Their within-input strategy entropy is 0.92–0.98 of its maximum, against 0.98–0.99 for the base models (Table 3).
  • The model-directed objectives preserve the base model's strategy distribution approximately, to a similar degree as ELBO. Distributional Fidelity is 0.82–0.90, against 0.87–0.89 for ELBO and β\beta-ELBO. For reference, the base model compared with itself scores 0.93, not 1, due to the finite-sample bias of the TV estimate.

Table 3 also reports the Jensen–Shannon divergence, a task-pooled fidelity and the valid-trace rate (called "Distributional Fidelity" in the original submission).


[Z2] Scope of the benchmark (W2, Q3)

"Can the method recover strategy structure that was not explicitly imposed by a synthetic trace generator?"

We agree that the evaluation uses a controlled benchmark, and we have not evaluated a setting in which strategies are not imposed by a trace generator. The paper limits its claims accordingly (§6): "we establish recovery where reference strategies are enumerable and traces are parseable, not in open-ended reasoning".

  • The controlled setting is what allows an exact evaluation. The metrics in [Z1] require a strategy label for every sampled response, which the parser provides. Fitting the base model to the benchmark gives it a known distribution over several strategies, so we can measure precisely whether the learned latent controls the strategy.
  • The benchmark exhibits a central difficulty of the problem. The generator is initialized from the base model, which already fits the target distribution. A standard variational objective is therefore nearly minimized at initialization without using the latent, and training has little incentive to use it. ELBO and β\beta-ELBO show this failure on our benchmark. They preserve the base model's distribution without learning a strategy-aligned latent (Strategy Transfer at most 0.02).

[Z3] Surprisal at strategy branching points (Q4)

"Are high-surprisal tokens actually concentrated at strategy-defining branch points?"

We added this analysis (§4.2; App. E.7; Table 4). A strategy branching point is a token where a trace first departs from the trace of another strategy on the same input.

  • On this benchmark, surprisal is concentrated at strategy branching points. On the four pretrained base models, branching points are 3.4–3.9% of response tokens and account for nearly all of the base model's surprisal (Table 4). App. E.7 reports controls for token type and sequence position.
  • Surprisal weighting places most of the reconstruction weight on these positions, and the method fails when the weight is removed from them. Branching points receive 12–18 times the uniform weight under surprisal weighting, accounting for 56–77% of a response's reconstruction weight. Under the inverse-surprisal ablation they receive less than 10−410^{-4} times the uniform weight, and Strategy Transfer falls below 0.05.

[Z4] Relation of the theory to the objective (W2, Q5)

"the theorem appears to be a conditional identifiability statement rather than a justification of the proposed algorithm."

We agree with this characterization. The theory gives conditions under which an abstract variational objective identifies the strategy structure. It is an analysis of the strategy-identification problem, not a justification of the proposed algorithm. The opening of §5 in the submission ("insight into the methods introduced in the paper") did not make this clear, and we revised it.

  • The submission framed the theory as preliminary. The Conclusion of the submission states that "the theoretical analysis is preliminary, and the connection between the oracle selection criterion and actual training dynamics is not yet formally characterized." The primary contribution of the paper is the objective and its empirical evaluation, while the theory is supplemental.
  • The revision states this scope explicitly. The opening of §5 now describes the analysis as preliminary and as a study of an abstract variational objective, and a new remark at the end of App. F ("Scope of the analysis") states that the margin condition is an assumption.

[Z5] Seeds and hyperparameter selection (W2, Q6)

"Are the reported improvements stable across independent training seeds and held-out hyperparameter selection? […] select β\beta, latent dimensionality, and checkpoints using a validation split"

Each base model and objective has one training run. With a fixed compute budget, we chose to evaluate four base models from three model families instead of repeating runs on one model, since this is the more informative test of generalization. We agree that multiple seeds per model would further strengthen the evaluation.

  • The settings transfer to other base models without a new sweep. SmolLM2-360M and OLMo 2 1B were not swept. They reuse the settings chosen on Qwen2.5-0.5B (App. E.3). The model-directed objectives reach Strategy Transfer 0.74–0.84 there, against at most 0.02 for ELBO and β\beta-ELBO (Table 3).
  • Selection by validation loss, without strategy labels, gives the same settings. Each of the two Qwen2.5 models had its own small sweep, in which we chose β\beta and α\alpha by the agreement rate. Selecting them by the lowest validation reconstruction loss instead, which uses no strategy labels, gives the same setting for every model-directed objective on both models (App. E.3).
  • No checkpoint or latent-dimension selection was done. All runs are evaluated at the last training step, and the latent dimension is fixed at 64.
Reviewer_ZW8AOpenReview ↗

Acknowledgement to dear authors

I appreciate the authors' candid and substantive revisions, particularly the redesigned metrics and the experiments conducted across multiple models. While I find the paper interesting, it appears applicable only within highly controlled environments. Furthermore, I am not convinced that the proposed training objective function guarantees the emergence of the behaviors the authors intend to elicit. The paper remains insufficiently robust. Therefore, I have decided to maintain my original score.

Thank you for reading the revision carefully and for the reply. We are glad that the revised metrics and the experiments on additional models were useful. We understand that some concerns remain, and we would like to briefly share our view on them.

We agree that the evidence in our study comes from a controlled benchmark. We chose this setting deliberately, and we scope our claims to it.

  • A controlled setting allows us to measure success. We opted to begin the study of the latent strategy-recovery problem in a controlled, structured setting because we want to be able to measure whether the latent controls the strategy used in generation, which requires a way to parse the strategy of each response. We believe this is a valuable and principled way to initiate this research direction. We agree that it does not settle the research problem, and that it leaves several important extensions.
  • The controlled setting exhibits a core failure mode of standard variational methods. This failure mode comes from the fact that we are learning a latent-variable factorization with a generator that already captures the target distribution without the latent variable. It is demonstrated by the failure of ELBO and β\beta-ELBO even on this controlled benchmark (Strategy Transfer at most 0.02).
  • We scope the claims of the paper to this setting and are explicit about the limitations. In particular, we do not claim a guarantee that our methods extend to more complex settings with naturalistic data, where there may be additional challenges. Our contribution is to address a subset of the challenges associated with the strategy-factorization problem. In the revised version, we further emphasized these limitations in response to your concerns (§6).

On this controlled benchmark, there is direct evidence for the paper's main claims.

  • Base-model surprisal is concentrated at strategy branching points. Across all four base models, the tokens where strategies branch carry nearly all of the base model's surprisal (Table 4). When the weight is removed from high-surprisal tokens, no strategy-aligned latent is learned (inverse-surprisal ablation, Strategy Transfer below 0.05).
  • Our model-directed objectives succeed in recovering a strategy-aligned latent. They achieve both Strategy Separation (separation between strategies in latent space within each input) and Strategy Transfer (the capacity to transfer a strategy from one input to another via an intervention in latent space). Over four base models, Strategy Separation is 0.68–0.93 and Strategy Transfer is 0.63–0.87 (Table 3). Moreover, we show an application of such latent-variable factorizations: active exploration in latent space, which discovers the distinct strategies in the model's response distribution with fewer generations than IID sampling from the base model (§4.2).
  • The surprisal-weighted reconstruction loss predicts whether the model has learned a strategy-aligned latent. Over 324 from-scratch single-task runs, runs with a lower loss have a higher Strategy Transfer (Spearman rank correlation −0.92-0.92, §4.2).

Finally, since the soundness concerns in the review centered in part on the evaluation metrics (W1), we would be grateful if you would consider whether the redesigned metrics and the extended experiments update your assessment of the Soundness sub-score.

Thank you very much for your engagement in the review process.

Reviewer_bRa4OpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
2
Soundness
2
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Paper summary

This paper proposes a latent-variable factorization framework based on a Router-Generator architecture to recover implicit reasoning strategies from pretrained LMa. By introducing base-model loss normalization and token-level surprisal weighting, the method aims to learn strategy-aligned latent representations with cross-input semantic consistency

Critical strengths
  • This paper investigates the recovery of implicit reasoning strategies from pretrained LMs, which is an interesting research direction. The authors emphasize not only the separation of different reasoning strategies within individual inputs but also cross-input semantic consistency, enabling the learned latent representations to support reusable strategy control and exploration
Critical weaknesses
  • The paper primarily relies on Distributional Fidelity and Analogical Consistency to evaluate the proposed method. But these metrics do not adequately capture the stated objectives. Distributional Fidelity measures the validity of generated solution traces rather than the similarity between the response distributions of the base and factorized models. More importantly, Analogical Consistency admits a degenerate solution, a generator that consistently produces the same valid strategy for all inputs within a task family can achieve a perfect score even if it completely ignores the latent variable. So high scores on these metrics do not demonstrate that the model has recovered diverse and controllable reasoning strategies

  • The Global Scale normalization is mathematically equivalent to adjusting the effective KL coefficient in β-ELBO objective with token-averaged reconstruction. Figure 6 shows that Global Scale normalization alone already achieves strong Strategy Alignment, while incorporating surprisal weighting does not consistently yield substantial additional improvements. This raises the question of whether the reported gains originate from the proposed reconstruction mechanism or simply from a more favorable reconstruction–KL trade-off.

  • The experiments are conducted exclusively on synthetic algorithmic tasks, where reasoning strategies are predefined and can be readily distinguished through their output patterns. These settings differ substantially from realistic reasoning scenarios, where strategies may overlap, interact, or exhibit hierarchical structures. Although the authors evaluate multiple pretrained language models, these models are first trained on the synthetic task distribution before factorization. Consequently, the results do not sufficiently demonstrate that the proposed approach can recover naturally emerging reasoning strategies in general-purpose reasoning models. Additionally, the main pretrained-model comparisons report only one selected training run per method and model, leaving the robustness of the results across random seeds unclear
Questions for authors
  • A generator that consistently selects the same valid strategy for all inputs within a task family can achieve perfect Distributional Fidelity and Analogical Consistency without utilizing the latent variable z. Could the authors provide additional evaluations that directly measure the causal influence of z on strategy selection and the preservation of the original strategy distribution

  • Since Global Scale normalization is equivalent to adjusting the effective KL coefficient under token-averaged reconstruction, and this variant already achieves strong performance in Figure 6, could the authors compare their method against a token-averaged β-ELBO baseline with matched effective KL coefficients, training budgets, and hyperparameter search?
4 comments

We thank the reviewer for their feedback, and we have revised the paper in response. Revisions are marked in blue, and all references below are to the revised paper. We respond to four points: the evaluation metrics (W1, Q1 → [B1]), the scope of the benchmark (W3 → [B2]), the global scale and its relation to β\beta-ELBO (W2, Q2 → [B3]), and the number of training runs (W3 → [B4]).


[B1] Evaluation metrics (W1, Q1)

"Could the authors provide additional evaluations that directly measure the causal influence of z on strategy selection and the preservation of the original strategy distribution"

We agree that the original submission's "Distributional Fidelity" metric measured only whether generated traces are valid, not whether the distribution over strategies is preserved. We also agree that the definition of Analogical Consistency did not rule out a generator that ignores zz and always produces one strategy. In our experiments, this collapse does not occur, and the revised metrics give a score of 0 to a generator that ignores zz.

The revised Fig. 6 compares four base models on three new metrics, defined in §4.1 and App. E.1. They measure the two quantities requested in Q1.

  • Distributional Fidelity is 1−TV1-\mathrm{TV} between the strategy distributions of the base model and the factorized model at each input, averaged over inputs. It measures whether the factorized model preserves the base model's distribution over strategies.
  • Strategy Separation is the conditional mutual information I(S;Z∣X)/H(S∣X)I(S;Z\mid X)/H(S\mid X) after subtracting a permutation baseline. It measures whether the latent determines the strategy within each input, averaged over inputs. It does not require a latent to select the same strategy on different inputs.
  • Strategy Transfer measures the stronger property that a latent selects the same strategy across inputs. It is tested by an intervention: a latent drawn for one input is reused on another input, and we record whether the strategy is the same. This agreement rate, called Analogical Consistency in the submission, is then corrected for chance.

Ranges over the four base models (per-model values in Table 3):

ObjectiveDistributional FidelityStrategy SeparationStrategy Transfer
Model-directed (three objectives)0.82–0.900.68–0.930.63–0.87
ELBO and β\beta-ELBO0.87–0.890.01–0.02−0.01-0.01 to 0.020.02
Inverse-surprisal ablation0.71–0.770.01–0.03−0.02-0.02 to 0.040.04
Base model against itself (reference)0.93N/AN/A
  • The latent controls the strategy under the model-directed objectives and not under ELBO or β\beta-ELBO. Strategy Separation is 0.68–0.93 and Strategy Transfer is 0.63–0.87. Under ELBO and β\beta-ELBO both are at most 0.02, the level of a generator that ignores zz.
  • The model-directed objectives do not collapse to one strategy. Their within-input strategy entropy is 0.92–0.98 of its maximum, against 0.98–0.99 for the base models (Table 3).
  • The model-directed objectives preserve the base model's strategy distribution approximately, to a similar degree as ELBO. Distributional Fidelity is 0.82–0.90, against 0.87–0.89 for ELBO and β\beta-ELBO. For reference, the base model compared with itself scores 0.93, not 1, due to the finite-sample bias of the TV estimate.

[B2] Scope of the benchmark (W3)

"the results do not sufficiently demonstrate that the proposed approach can recover naturally emerging reasoning strategies in general-purpose reasoning models"

We agree that the evaluation uses a controlled benchmark with predefined strategies. This is a deliberate choice, and the paper limits its claims to this setting (§6): "we establish recovery where reference strategies are enumerable and traces are parseable, not in open-ended reasoning".

  • The controlled setting is what allows an exact evaluation. The metrics in [B1] require a strategy label for every sampled response, which the parser provides. Fitting the base model to the benchmark gives it a known distribution over several strategies, so we can measure precisely whether the learned latent controls the strategy.
  • The benchmark exhibits a central difficulty of the problem. The generator is initialized from the base model, which already fits the target distribution. A standard variational objective is therefore nearly minimized at initialization without using the latent, and training has little incentive to use it. ELBO and β\beta-ELBO show this failure on our benchmark. They preserve the base model's distribution without learning a strategy-aligned latent (Strategy Transfer at most 0.02).

[B3] The global scale and β\beta-ELBO (W2, Q2)

"whether the reported gains originate from the proposed reconstruction mechanism or simply from a more favorable reconstruction–KL trade-off"

We agree that the global scale objective (without token-level surprisal weighting, α=0\alpha=0) is equivalent to a token-averaged β\beta-ELBO with a rescaled KL coefficient that depends on the base model. The revised §3.3 states this explicitly: "With uniform weights (α=0\alpha=0), the objective is a token-averaged β\beta-ELBO with KL coefficient βcθ\beta c_\theta".

  • The global scale is a rule for setting the KL coefficient from the base model. The latent can reduce the token-averaged reconstruction loss by at most cθc_\theta, the base model's expected per-token loss. After dividing by cθc_\theta, the reconstruction term is the fraction of the base model's loss that remains after conditioning on zz, which equals 1 for a generator that ignores zz. The KL penalty is weighed against this fraction, which adapts it to the base model and the task, so the same β\beta applies across base models (§3.3). This is important in this setting because the generator is initialized at the base model, which already fits the target distribution.
  • A standard search over β\beta does not find a β\beta-ELBO setting that succeeds (Q2). We searched over β∈{0.01,0.1,1}\beta\in\{0.01,0.1,1\} with constant and linear-warmup schedules for each Qwen2.5 model. All settings have Strategy Transfer at most 0.045 (App. E.3). The global scale objective reaches Strategy Transfer 0.63 and 0.82 on the same two models (Table 3). These baselines use token-averaged reconstruction, so the global scale objective is the token-averaged β\beta-ELBO with the matched coefficient requested in Q2. This coefficient lies outside the standard grid, because the base model already fits the target distribution and its per-token loss cθc_\theta is small.
  • With token weighting (α>0\alpha>0), the objective is not a β\beta-ELBO for any choice of β\beta. The coefficient β\beta rescales the reconstruction term as a whole. Token weighting changes the weight of each token within it, and places most of the weight on high-surprisal tokens. The inverse-surprisal ablation keeps the global scale and reverses the token weights, moving the weight to low-surprisal tokens. Strategy Transfer then falls from 0.74–0.87 for the objective with global scale and surprisal weighting to at most 0.04 on all four base models (§4.2; Table 3), although the global scale is the same.
  • The global scale and token weighting have different roles. The global scale sets the KL coefficient, and alone it reaches Strategy Transfer 0.63–0.84. Token weighting changes which tokens the reconstruction term emphasizes (§3.3). Adding it to the global scale gives higher Strategy Transfer on three of the four base models (0.87, 0.86 and 0.79, against 0.63, 0.82 and 0.74 for the global scale alone) and lower on SmolLM2-360M (0.74 against 0.84; Table 3). The revised §4.2 therefore states that alignment improves "whether through the global scale alone or together with token weighting".
  • Surprisal weighting places most of the reconstruction weight on the tokens where a strategy is chosen. A strategy branching point is a token where a trace first departs from the trace of another strategy on the same input. Branching points are 3.4–3.9% of response tokens. Under surprisal weighting they receive 12–18 times the uniform weight, accounting for 56–77% of a response's reconstruction weight (App. E.7; Table 4). Consistent with this, over 324 from-scratch runs Strategy Transfer has Spearman correlation −0.92-0.92 with the token-weighted reconstruction loss, against −0.70-0.70 with the uniformly weighted loss (§4.2).

[B4] Number of training runs (W3)

"the main pretrained-model comparisons report only one selected training run per method and model"

Each base model and objective has one training run. With a fixed compute budget, we chose to evaluate four base models from three model families instead of repeating runs on one model, since this is the more informative test of generalization (Fig. 6). We agree that multiple seeds per model would strengthen the evaluation.

  • The difference between objectives is the same in every run. Over the four base models, all 12 runs of the model-directed objectives have Strategy Transfer at least 0.63, and all 8 runs of ELBO and β\beta-ELBO have at most 0.02 (Table 3).
  • The settings transfer to other base models without a new sweep. SmolLM2-360M and OLMo 2 1B were not swept. They reuse the settings chosen on Qwen2.5-0.5B (App. E.3). The model-directed objectives reach Strategy Transfer 0.74–0.84 there, against at most 0.02 for ELBO and β\beta-ELBO (Table 3).
Reviewer_bRa4OpenReview ↗

acknowledgement

I appreciate the authors' response. However, my central concern remains unresolved. The evaluation relies exclusively on synthetic algorithmic tasks where reasoning strategies are predefined and readily identifiable from output patterns. This leaves the paper's claims insufficiently supported. Therefore, I will maintain my original score.

We thank the reviewer for the reply.

The original review raised three main concerns: the metrics (W1), the relation to β\beta-ELBO (W2), and the synthetic benchmark (W3). The reviewer's reply restates W3, which we agree is a limitation and which the paper discusses explicitly. It does not mention W1 or W2, which the revision answers with new results. Could the reviewer state whether W1 and W2 are addressed by the revision? Below, we respond on W3 and then summarize W1 and W2.


W3 (synthetic benchmark). We agree that all experiments use a controlled benchmark with predefined strategies. The paper states this limitation and limits its conclusions accordingly (§6): "we establish recovery where reference strategies are enumerable and traces are parseable, not in open-ended reasoning". As Reviewer 8sX9 notes, "the controlled benchmark is valuable, and the paper explicitly acknowledges its scope". If the reviewer has concerns about specific claims or conclusions in the paper that are not supported by the results, we are glad to revise them.

Additionally, we would like to clarify where the predefined strategies are used.

  • Evaluation requires them. Testing whether a method recovers strategies, and whether its latent controls the strategy during generation, requires identifying the strategy of each generated response. We use a controlled benchmark so that the true strategies are known and every response can be labeled exactly. The metrics requested in Q1 rely on these labels.
  • The training objective does not use them. The strategies enter only through the data to which the base model is fitted. The factorization objective has no access to strategy labels or to the parser.
  • Standard objectives fail on this benchmark. With the same base models and data, ELBO and β\beta-ELBO learn a latent that does not control the strategy (Strategy Transfer at most 0.02; Table 3).

W1 (the metrics do not rule out degenerate solutions). We agree, and we revised the metrics (§4.1, Fig. 6, Table 3). They measure the two quantities requested in Q1: whether the latent determines the strategy (Strategy Separation, Strategy Transfer) and whether the base model's strategy distribution is preserved (Distributional Fidelity). A generator that ignores zz scores 0 in expectation on Separation and Transfer. The model-directed objectives score 0.68–0.93 and 0.63–0.87, against at most 0.02 for ELBO and β\beta-ELBO.


W2 (relation to β\beta-ELBO). The revision gives three results.

  • No β\beta-ELBO setting in our search succeeds. Over β∈{0.01,0.1,1}\beta\in\lbrace 0.01, 0.1, 1\rbrace with two schedules on both Qwen2.5 models, Strategy Transfer is at most 0.045. The model-directed objectives reach 0.63–0.87 (App. E.3, Table 3).
  • The global scale is a rule for setting the KL coefficient from the base model. With uniform token weights, the objective is a token-averaged β\beta-ELBO with coefficient βcθ\beta c_\theta, as §3.3 states. Here cθc_\theta is the base model's expected per-token loss, which bounds how much the latent can reduce the reconstruction loss. The resulting coefficient is outside the grid above. The settings chosen on Qwen2.5-0.5B transfer to SmolLM2-360M and OLMo 2 1B without a new sweep (Strategy Transfer 0.74–0.84).
  • With surprisal token weighting, the objective is not a β\beta-ELBO for any β\beta. A β\beta-ELBO has one coefficient for the whole reconstruction term. Surprisal weighting sets a weight for each token from the base model's surprisal, so the trade-off with the KL term differs between tokens. The token-weighted loss tracks Strategy Transfer more closely than the uniformly weighted loss (Spearman −0.92-0.92 against −0.70-0.70 over 324 from-scratch runs; §4.2). With the same global scale and reversed token weights, Strategy Transfer falls from 0.74–0.87 to at most 0.04 on all four base models (§4.2, Table 3).

Thank you.

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Paper summary

This paper studies how to expose reusable reasoning strategies by learning a latent router-generator factorization of a fixed reference language model's response distribution. The reference model remains frozen during factorization training; the router, latent-conditioned generator, and training posterior are learned. The paper identifies an inert-latent solution available to a generator initialized from the base model and proposes a variational objective that normalizes reconstruction loss relative to the base model and emphasizes high-surprisal response tokens. Experiments use six controlled algorithmic task families: base models are first fitted to constructed multi-strategy distributions, and their factorizations are then trained on model-sampled responses without strategy labels in the optimization loop. Evaluation examines solution validity, cross-input strategy consistency, objective ablations, and strategy coverage under directed latent sampling. The paper also develops preliminary recovery and marginal-fidelity analyses for a complexity-penalized variational formulation, while limiting its empirical conclusions to enumerable strategies and parseable traces.

Critical strengths
  1. The controlled benchmark enables meaningful evaluation of reusable strategy representations. Reference strategies are available for evaluation but withheld during factorization training. The Analogical Consistency experiment reuses a sampled latent across different inputs and checks the resulting generated strategies, going beyond a probe of decodable information. Directed latent exploration also improves strategy coverage at a fixed decoded-sample budget within this setting. Together, these results demonstrate a useful intervention capability rather than only a visualization of latent clusters.

  2. The objective is supported by informative comparisons and diagnostics. The paper compares standard variational objectives with base-relative normalization, surprisal weighting, and their combination across multiple base-model initializations, and includes an inverse-surprisal negative control. These experiments provide evidence that the direction and scaling of reconstruction pressure affect cross-input strategy alignment. The theoretical discussion also clarifies why marginal fit and latent activity alone do not identify reusable strategy semantics. This makes the work a useful study of objective design for latent strategy recovery. In particular, recovering strategies without strategy labels during factorization is a meaningful distinction from explicitly supervised rule disentanglement, even though latent-conditioned reasoning itself is not new.

Critical weaknesses
  1. Preservation of the original response distribution is not adequately validated. Section 4.1 and Appendix E.1 define Distributional Fidelity as the fraction of generated traces that remain valid, strategy-compatible solutions. A model can score highly while substantially changing per-input strategy probabilities or concentrating on a subset of valid responses. The reported similarity of IID strategy coverage provides some supporting evidence, but does not establish distributional similarity. Proposition 3 relates marginal KL to variational gaps; it does not show that those gaps are small for the trained models. Since preservation of the original response distribution is part of the problem formulation and stated contribution, direct diagnostics or a narrower claim of preserving valid task behavior are needed.

  2. The strategy-specific interpretation of the training signal remains insufficiently tested. The inverse-surprisal ablation and the association between weighted reconstruction loss and strategy alignment support the usefulness of surprisal weighting, but do not directly show that the emphasized positions correspond to strategy decisions rather than unpredictable numerical details, wording, or formatting. All evaluated base models are first fitted to constructed strategy distributions, so the experiments do not test whether the learned latent remains strategy-aligned when competing non-strategy variation is present. The controlled benchmark is valuable, and the paper explicitly acknowledges its scope; my concern is not the use of synthetic tasks itself, but the limited evidence that the objective selects reusable strategies rather than other residual response information under less constrained conditions.

This limitation also matters for positioning the contribution. Reasoning Palette already studies continuous latent control and reasoning exploration, while Learning to Disentangle Latent Reasoning Rules with Language VAEs: A Systematic Study investigates rule-separated latent representations. Neither is discussed in the supplied paper. Their embedding-reconstruction/exploration and explicitly supervised rule-learning settings differ from the present objective, so I do not regard the omission as proof of redundancy. A precise comparison is nevertheless needed to establish what the proposed objective adds to existing latent reasoning methods.

Questions for authors
  1. Clarification and evidence for the current preservation claim: Beyond valid-solution rate and IID coverage, what evidence shows that the factorized model preserves the base model's response distribution? Can the authors compare per-input strategy probabilities and provide feasible marginal-distribution diagnostics, or explicitly narrow the claim to preservation of valid task behavior? This would materially affect my assessment of a central stated requirement.

  2. Evidence needed for the mechanism interpretation and empirical scope: On the controlled benchmark, do high-surprisal positions preferentially coincide with known strategy-discriminating decisions? Can the authors distinguish this effect from other hard-to-predict tokens, for example through controlled wording, formatting, or numerical variation that does not change the solution strategy? Has robustness beyond the explicitly constructed strategy distributions been examined? If not, please separate the demonstrated controlled recovery result from the broader motivation of uncovering naturally occurring strategies. These diagnostics or clarifications would materially affect my interpretation of the learned latent; a comprehensive new benchmark study is a future-work suggestion, not a prerequisite for answering the question.

  3. Clarification of the contribution relative to specific prior work: How does the proposed approach differ from Reasoning Palette: Modulating Reasoning via Latent Contextualization for Controllable Exploration for (V)LMs (CVPR 2026) and Learning to Disentangle Latent Reasoning Rules with Language VAEs: A Systematic Study (AAAI 2026; arXiv:2506.19418). The former learns a VAE over pooled question-answer embeddings and uses sampled latent prefixes for inference/RL exploration; the latter uses explicit rule annotations and a rule-classification term. Which part of the present contribution is specific to recovering cross-input strategy semantics from a fixed reference model without strategy labels during factorization, and what existing evidence isolates that contribution? I am asking for a comparison of learning targets, supervision, and validation, not assuming that these methods are equivalent or requiring their wholesale reimplementation.

1 comment

We thank the reviewer for the assessment that the paper is "a useful study of objective design for latent strategy recovery". We respond to three points: preservation of the response distribution (W1, Q1 → [S1]), surprisal weighting and the scope of the evidence (W2, Q2 → [S2]), and two prior works (W2, Q3 → [S3]). We have revised the paper in response, with revisions marked in blue.


[S1] Preservation of the base model's response distribution (W1, Q1)

"Can the authors compare per-input strategy probabilities and provide feasible marginal-distribution diagnostics […]?"

We agree that the submission's Distributional Fidelity measured only whether generated traces are valid, not whether the distribution over strategies is preserved.

  • Distributional Fidelity is now a per-input comparison of strategy distributions. It is 1−TV1-\mathrm{TV} between the strategy distributions of the base model and the factorized model at each input, averaged over inputs (§4.1; App. E.1).
  • ELBO and the model-directed objectives match the base model's distribution to a similar degree, but only the latter use the latent. On four base models, Distributional Fidelity is 0.87–0.89 for ELBO and β\beta-ELBO and 0.82–0.90 for the model-directed objectives. Strategy Separation and Strategy Transfer are at most 0.02 for ELBO and β\beta-ELBO, against 0.68–0.93 and 0.63–0.87 for the model-directed objectives (Fig. 6; Table 3).
  • The factorized models do not concentrate on a subset of strategies. Their within-input strategy entropy is 0.92–0.98 of its maximum, against 0.98–0.99 for the base models (Table 3).

Strategy Separation measures whether the latent determines the strategy within each input. Strategy Transfer is the chance-corrected form of the submission's Analogical Consistency.


[S2] Surprisal at strategy decisions and scope of the evidence (W2, Q2)

"do high-surprisal positions preferentially coincide with known strategy-discriminating decisions? […] please separate the demonstrated controlled recovery result from the broader motivation"

We added an analysis of whether the base model's surprisal, and the weight that the objective places on each token, fall on strategy decisions (§4.2; App. E.7; Table 4). A strategy branching point is a token where a trace first departs from the trace of another strategy on the same input.

  • On this benchmark, surprisal is concentrated at strategy branching points. On the four pretrained base models, branching points are 3.4–3.9% of response tokens and account for nearly all of the base model's surprisal (Table 4).
  • Surprisal weighting places most of the reconstruction weight on these positions, and the method fails when the weight is removed from them. Branching points receive 56–77% of a response's reconstruction weight. Under the inverse-surprisal ablation they receive less than 10−410^{-4} times the uniform weight, and Strategy Transfer falls below 0.05.

We agree that the experiments are synthetic and do not test the method when naturalistic non-strategy variation is present. The result of the paper is recovery of strategies on this controlled benchmark, and uncovering naturally occurring strategies in general-purpose models is the broader motivation. The paper states this scope in §6 ("we establish recovery where reference strategies are enumerable and traces are parseable, not in open-ended reasoning"), and the new analysis states that it does not test "settings where responses also vary in ways unrelated to strategy" (App. E.7).


[S3] Relation to Reasoning Palette and the Language-VAE study (W2, Q3)

"How does the proposed approach differ from […]? […] I am asking for a comparison of learning targets, supervision, and validation"

We added a discussion of both papers mentioned by the reviewer to the introduction (§1) and to a new paragraph in App. B.

Reasoning PaletteLanguage-VAE studyOurs
Learning targetVAE over pooled question-answer embeddings; the model is then trained with RLVAE fit to labelled (rule, premise, conclusion) data; decoder retrainedFactorization of a fixed base model that preserves its response distribution
SupervisionNo strategy labels in trainingRule labels in the encoder input and a classifier lossNo strategy labels in training
Validationpass@k, clustering by domain, accuracy after RLBLEU and accuracy, clustering by ruleIntervention: reuse a latent on another input and test whether the strategy is the same (Strategy Transfer)

The difference in setting is that we factorize a given pretrained model and preserve its response distribution, whereas both prior works train a new latent-variable model. The difference in evaluation is that we test whether a latent gives the same strategy on a different input, which neither prior work does. Our contribution is the model-directed training objective, which [S1] compares with ELBO and β\beta-ELBO.

Comments on the paper

2 comments

Global response (1/2): summary of concerns and revisions

We thank the reviewers for their helpful feedback. We have uploaded a revised paper with new evaluations and analysis that addresses the reviewers' primary concerns. Revisions are marked in blue, and all references in our responses are to the revised paper.

The main concern shared by all three reviewers is that the two main metrics of the submission do not rule out certain degenerate solutions (e.g., change or collapse of the strategy distribution). We replaced them with three metrics that rule out these cases, including the quantities the reviewers requested (per-input total variation and conditional mutual information). The new metrics confirm the conclusions of the submission. The main comparison (Fig. 6) now covers four base models instead of two. On all four base models, the model-directed objectives reach Strategy Transfer 0.63–0.87, against at most 0.02 for ELBO and β\beta-ELBO, and Distributional Fidelity 0.82–0.90, against 0.87–0.89 for ELBO and β\beta-ELBO.

The table below summarizes each concern raised in the reviews and our response. Our replies to the individual reviewers are self-contained. For the main concern ([C1]), we give the new metrics and results in part 2 of the global response.

Concern (raised by)Our ResponseRevised Paper
C1The two main metrics do not rule out certain degenerate solutions (8sX9, bRa4, ZW8A)We agree. Three new metrics measure preservation of the strategy distribution, whether the latent determines the strategy within each input, and whether a latent selects the same strategy across inputs. See [C1].§4.1, Fig. 6, App. E.1, Table 3
C2One training run per model and objective; settings selected on the reported metric (bRa4, ZW8A)We agree that each base model and objective has one training run. With a fixed compute budget, we chose to evaluate four base models from three families instead of repeating runs on one model. The results hold on all four, including two models that reuse the settings chosen on Qwen2.5-0.5B without a new sweep (Strategy Transfer 0.74–0.84, against at most 0.02 for ELBO and β\beta-ELBO).App. E.3, Table 3
C3The global scale is equivalent to a β\beta-ELBO with a rescaled KL coefficient (bRa4)We agree that the global scale objective is a token-averaged β\beta-ELBO with a rescaled KL coefficient, and §3.3 now states it. The contribution is how this coefficient is set. It is set from the base model's expected per-token loss, which bounds the reduction in reconstruction loss available to the latent. The KL penalty is therefore adapted to the base model and the task, and the resulting coefficient is outside a standard β\beta grid. All β\beta-ELBO settings in the sweep for each Qwen model (β∈{0.01,0.1,1}\beta \in \{0.01, 0.1, 1\}) have Strategy Transfer at most 0.045, against 0.63 and 0.82 for the global scale objective. Token weighting is a separate mechanism. With the same global scale and reversed token weights, Strategy Transfer is at most 0.04.§3.3, §4.2, App. E.3
C4Whether high-surprisal tokens are the positions where a strategy is chosen (8sX9, ZW8A)We added this analysis. On this benchmark, strategy branching points (tokens where the traces of two strategies first differ) are 3.4–3.9% of response tokens and account for nearly all of the base model's surprisal. Surprisal weighting places 56–77% of a response's reconstruction weight on them.§4.2, App. E.7, Table 4
C5The evaluation uses only a synthetic benchmark (8sX9, bRa4, ZW8A)We agree, and the paper limits its claims to settings with enumerable strategies and parseable traces. This design enables exact evaluation against ground-truth labels. The benchmark still exhibits a central difficulty of the problem. ELBO and β\beta-ELBO preserve the base model's distribution without learning a strategy-aligned latent.§6
C6Two related papers are not discussed (8sX9)We added both, with a comparison of learning target, supervision and validation. Neither factorizes a fixed model, and neither tests whether a latent gives the same strategy on another input.§1, App. B
C7The theory does not justify the algorithm (ZW8A)We agree that it is a conditional identifiability result for an abstract objective. The paper presents it as preliminary, and the revision states this scope explicitly.§5, App. F

Global response (2/2)

[C1] Evaluation metrics (8sX9 W1, Q1; bRa4 W1, Q1; ZW8A W1, Q1, Q2)

We agree that the submission's original Distributional Fidelity metric measured only whether generated traces are valid, not whether the distribution over strategies is preserved. We also agree that the definition of Analogical Consistency did not rule out a generator that ignores zz and always produces one strategy. In our experiments, this collapse does not occur, and the revised metrics give a score of 0 to a generator that ignores zz.

The method-comparison figure of the submission (Fig. 6) compared two base models, Qwen2.5-0.5B and Qwen2.5-1.5B, on the valid-trace rate (called Distributional Fidelity in the submission) and Analogical Consistency. The revised Fig. 6 compares four base models, adding SmolLM2-360M and OLMo 2 1B, on three new metrics defined in §4.1 and App. E.1.

  • Distributional Fidelity is 1−TV1-\mathrm{TV} between the strategy distributions of the base model and the factorized model at each input, averaged over inputs. This is the per-input comparison by total variation requested in 8sX9 Q1, bRa4 Q1 and ZW8A Q2. It measures whether the factorized model preserves the base model's distribution over strategies.
  • Strategy Separation is I(S;Z∣X)/H(S∣X)I(S;Z\mid X)/H(S\mid X) after subtracting a permutation baseline. It is the conditional mutual information requested in ZW8A Q1, and it measures whether the latent determines the strategy within each input, averaged over inputs (bRa4 Q1). It does not require a latent to select the same strategy on different inputs.
  • Strategy Transfer measures the stronger property that a latent selects the same strategy across inputs. It is tested by an intervention: a latent drawn for one input is reused on another input, and we record whether the strategy is the same. This agreement rate, called Analogical Consistency in the submission, is then corrected for chance.

Ranges over the four base models (per-model values in Table 3):

ObjectiveDistributional FidelityStrategy SeparationStrategy Transfer
Model-directed (three objectives)0.82–0.900.68–0.930.63–0.87
ELBO and β\beta-ELBO0.87–0.890.01–0.02−0.01-0.01 to 0.020.02
Inverse-surprisal ablation0.71–0.770.01–0.03−0.02-0.02 to 0.040.04
Base model against itself (reference)0.93N/AN/A
  • The latent controls the strategy under the model-directed objectives and not under ELBO or β\beta-ELBO. Strategy Separation is 0.68–0.93 and Strategy Transfer is 0.63–0.87. Under ELBO and β\beta-ELBO both are at most 0.02, the level of a generator that ignores zz.
  • The model-directed objectives do not collapse to one strategy. Their within-input strategy entropy is 0.92–0.98 of its maximum, against 0.98–0.99 for the base models (Table 3).
  • The model-directed objectives preserve the base model's strategy distribution approximately, to a similar degree as ELBO. Distributional Fidelity is 0.82–0.90, against 0.87–0.89 for ELBO and β\beta-ELBO. For reference, the base model compared with itself scores 0.93, not 1, due to the finite-sample bias of the TV estimate.

Table 3 also reports the valid-trace rate, the Jensen–Shannon divergence and a task-pooled fidelity.

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

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