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Under review as a conference paper at ICLR 2027

Forecasting Future Behavior as a Learning Task

Abstract

Trust in an AI system is often anchored by explanations of how it works, which one then uses to forecast its behavior on new inputs. For large reasoning models (LRMs), this conventional route is particularly difficult to follow: explanation methods for single token generations do not naturally generalize to long trajectories, and the trajectories themselves are often not faithful when read as natural language. We propose an alternative that bypasses the explanation step: treat behavior forecasting as a learnable task and train Behavior Forecasters that operates on a single reasoning trajectory to make the same forecasts one would typically seek from an explanation. The forecaster's training data is obtained by querying the LRM with no human annotation, and its inference is done in a single forward pass. We instantiate this approach on two tasks: how likely the LRM is to repeat its answer on re-runs, and how removing parts of the input changes its answer. We evaluate this approach on both tasks across three diverse reasoning datasets and find that trained Behavior Forecasters are more accurate than GPT-5.4 and Claude Opus 4.6 reading the same trajectories as naive readers, at a small fraction of their inference cost. We find that fine-tuning the backbone end-to-end and initializing it from the target LRM are each necessary for strong performance. These results show that the reasoning trajectory carries information about the LRM's future behavior that goes beyond what naive reading conveys.

Primary area:
interpretability and explainable AI
Keywords:
Reasoning models, Language models, Meta models, Consistency, Trust

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_CsrjOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper argues that behavioral forecasts for large reasoning models (LRMs) are hard to obtain, since long reasoning trajectories are often unfaithful when read as text, and local attribution or uncertainty methods operate on single generation steps. The authors propose treating behavior forecasting as a supervised learning task, by training a Behavior Forecaster model to predict statistics that would otherwise require resampling the LRM from a single sampled trajectory.

In their experiment, the authors resample an LRM 10 times per prompt and 10 times per modified prompt to obtain gold behavioral labels, using OLMo-3-7B-Think across three datasets. The evaluation focuses on two main aspects, namely 1) Rerun consistency, i.e. the fraction of other runs on the same prompt that reproduce the observed answer; and 2) Counterfactual sensitivity, i.e. the probability drop for the observed answer when prompt segments are removed independently.

Compared to two capable baselines (GPT-5.4 and Claude Opus 4.6), the trained forecaster obtains higher correlation scores in both metrics. The paper also reports transfer to held-out data and ablations on input format, initialization and freezing.

Critical strengths
  • The problem of future prediction is well defined and motivated, and the proposed evaluation approach is well designed. The setup in Section 2.1 is general and could cover other behaviors that can be labeled automatically in a similar fashion. The authors estimate uncertainty at the level of original samples, which I believe is the right choice since segments and runs from the same prompt are not independent. They also report negative results, such as weak results on TreeCut and weak zero-shot transfer across datasets. This makes the main comparisons credible as reported.

  • The rerun consistency results show that the reasoning trace contains useful signal about answer stability that is not picked up by frontier models reading the raw trace output. Gains over baselines are relatively large and have confidence intervals well above zero (Table 13). Removing the reasoning from the input significantly affects performance (Table 4), confirming that the signal comes from the reasoning tokens. The same trend holds on a held-out FEVEROUS subset and on Qwen3.5-2B. As discussed below, however, most of this gain comes from the RuleTaker dataset.

Critical weaknesses
  • The experiments show that the proposed behavior forecaster works, but it is not clear whether it truly relies on the LRM's reasoning. The paper claims that the forecaster learns how the target LRM encodes information in its reasoning, but removing the reasoning from the input barely changes the counterfactual sensitivity results (0.723 vs. 0.714 in Table 4), while still beating both frontier model baselines even when these can see the reasoning. This suggests that the forecaster might be picking up spurious shortcuts, e.g. learning which premises are logically needed for the answer, while ignoring the actual LRM behavior. This seems especially likely for RuleTaker, which makes up 72% of the test segments. For rerun consistency, reasoning seems to matter, but it remains unclear whether the forecaster uses patterns specific to the LRM, cues such as trace length, or whether the answer is correct. The fact that a randomly initialized model already beats the frontier models by a wide margin on this metric suggests that cues may be sufficient for obtaining these results. Since the paper’s framing depends on this point, I don't consider its central claim to be supported as of now.

  • The comparison with the frontier models is not fully fair, since trained models can learn typical label values for each dataset while the zero-shot prompted baseline models do not. Per-dataset results (Table 10) show that the picture is not as clear-cut, with Opus outperforming the forecaster on FEVEROUS, and all methods performing poorly on TreeCut. Since RuleTaker makes up most of the test segments, the gap can be attributed to the trained predictor specializing in this setup, also in light of the shortcut mentioned in the previous point.

  • Training models to predict quantities that normally require resampling is also a common approach: for example, Semantic entropy probes [1] predict how much answers vary across reruns from one generation, FastSHAP [2] learns explainers to predict the effect of removing input features and, more recently, Future Probes [3] predict the proportion of LRM traces resulting in specific behaviors of interest from intermediate activations at a given reasoning position. I see the generalization tests as the most valuable contribution that distinguishes this work from e.g. [3], but results show that, without labels from a new dataset, the trained forecaster does worse than the frontier models on all three datasets for counterfactual sensitivity, and on two of three for rerun consistency (Table 2 vs. Table 10), so the generality claim is not well supported.

[1] Kossen et al., 2024. Semantic Entropy Probes: Robust and Cheap Hallucination Detection in LLMs. https://arxiv.org/abs/2406.15927 [2] Jethani et al. 2022. FastSHAP: Real-Time Shapley Value Estimation. https://arxiv.org/abs/2107.07436 [3] Kortukov et al. 2026. Predicting Future Behaviors in Reasoning Models Enables Better Steering. https://arxiv.org/abs/2606.11172

Questions for authors
  • How much of the rerun consistency label depends on whether the answer is correct? It would be helpful to present the forecaster's results on correct and wrong answers separately to highlight whether this is a confounder in the analysis.

  • Did you test whether the OLMo forecaster predicts Qwen’s behavior as well as OLMo’s? There are some results in the literature regarding models' "priviledged access" to their own computations (see: https://arxiv.org/abs/2511.08579v1). This would help to show whether initializing from the target model really matters.

  • For counterfactual sensitivity, could you compare against a simple baseline based on the RuleTaker gold proofs to see how much the LRM reasoning is actually helpful, as opposed to general resolution traces?

2 comments
AuthorsOpenReview ↗

Shortcuts do not explain the forecaster’s lead (1/2)

Thank you for the careful and detailed review, and we are glad that you found the problem well motivated, the evaluation well designed and the main comparisons credible. Your questions about what the forecasters learn made the paper more precise. Following your comments, we uploaded a revised PDF that makes clearer what the reasoning tokens contribute in each task, adds the two analyses you asked for (rerun consistency on correct and wrong answers, and forecasters trained on one LRM and evaluated on another), moves the per-dataset results into the main text, states the limits of the generalization results, and cites the three works you pointed to.

The paper claims that the forecaster learns how the target LRM encodes information in its reasoning, but removing the reasoning from the input barely changes the counterfactual sensitivity results (0.723 vs. 0.714 in Table 4), while still beating both frontier model baselines even when these can see the reasoning.

It is true that for counterfactual sensitivity the reasoning tokens add little. To clarify our claim: a trajectory is the prompt, the reasoning and the answer together (Section 2), and we claim that naive reading of a trajectory does not tell the full story about the LRM's future behavior, and that the rest can be learned from the LRM's past behavior. We do not claim that the forecaster always needs the reasoning tokens. For rerun consistency it does: removing them drops the forecaster from 0.568 to 0.316. For counterfactual sensitivity, what stands is the result that you describe: a forecaster that never sees the reasoning (0.714) is more accurate than two frontier readers that do (0.672 and 0.690). We made it clearer in the paper that the contribution of the reasoning tokens applies to rerun consistency and not to counterfactual sensitivity (lines 458-463), and the setup sentence that you refer to is now limited to rerun consistency (lines 323-325).

This suggests that the forecaster might be picking up spurious shortcuts, e.g. learning which premises are logically needed for the answer, while ignoring the actual LRM behavior. This seems especially likely for RuleTaker, which makes up 72% of the test segments.

The forecaster might learn the logic to some degree, but it is important to remember that it is a 7B model that runs one forward pass and the readers are far stronger solvers of logic problems than any 7B model. If the task were only to find which statements are logically needed, they would be at least as accurate as the forecaster. They are not (0.649 and 0.601, against 0.668). The result also does not rest on RuleTaker: the forecaster's margin over the better reader is larger on FEVEROUS (0.660 against 0.621) and on TreeCut (0.840 against 0.804). We moved the per-dataset results into the main text (Table 1, previously Table 10).

For rerun consistency, reasoning seems to matter, but it remains unclear whether the forecaster uses patterns specific to the LRM, cues such as trace length, or whether the answer is correct. [...] It would be helpful to present the forecaster's results on correct and wrong answers separately

We ran this analysis and added it to the appendix (lines 1260-1284 and Table 16, referenced from the main results at lines 342-343). Correctness is informative about the label, but it does not explain the forecaster's accuracy. Within correct answers, its Spearman correlation is 0.443, against 0.073 for GPT-5.4 and 0.004 for Claude Opus 4.6. Within wrong answers it is 0.526, against 0.008 and 0.162. It is the readers' pooled correlation (0.305 and 0.308) that mostly reflects correctness. Trace length does not explain it either: controlling for both length and correctness, the forecaster's correlation with the label is 0.41, against 0.04 and 0.07 for the readers.

The fact that a randomly initialized model already beats the frontier models by a wide margin on this metric suggests that cues may be sufficient for obtaining these results.

We read this result as support for the paper's thesis. A randomly initialized forecaster knows only what it learned from the target LRM's trajectories and their behavior labels, and this alone takes it past the frontier readers (0.477 against 0.305 and 0.308). Whatever it learned, it is a regularity of this LRM's behavior that reading does not pick up.

AuthorsOpenReview ↗

Typical labels, novelty and generalization (2/2)

The comparison with the frontier models is not fully fair, since trained models can learn typical label values for each dataset while the zero-shot prompted baseline models do not. Per-dataset results (Table 10) show that the picture is not as clear-cut [...]

The typical label of each dataset cannot explain the forecaster's lead. Typical label values alone give a Spearman correlation of at most 0.22 and 0.30, the score of a predictor that outputs each dataset's mean test label on counterfactual sensitivity and rerun consistency, far below the forecaster (0.731 and 0.571). Also, simpler forecasters trained on the same labels can learn the typical values just as well, and they are less accurate: a prediction head trained on the frozen LRM reaches 0.245 and 0.475, and a randomly initialized backbone 0.534 and 0.477 (Table 5, previously Table 4).

Training models to predict quantities that normally require resampling is also a common approach [...]

Thank you for these pointers. These works share one ingredient with ours, training a model to predict a quantity that otherwise requires resampling, and the revised paper cites all three (lines 118-119, 483 and 489-490). Their question is different though. They take a quantity that already has an accepted way to compute it and make it cheaper. We take a question that in practice is answered by reading the LRM's reasoning, and propose to answer it by learning from the LRM's past behavior instead, for any behavior that can be labeled automatically. We show that learning does better: a 7B model trained on the LRM's past behavior forecasts it more accurately than frontier models that read the full trajectory. This matters most for LRMs, whose behavior unfolds over long autoregressive generations: measuring it directly takes many runs of thousands of tokens each, while the forecaster needs one forward pass over the observed trajectory and, on rerun consistency, matches the accuracy of one to two full reruns (lines 1230-1259).

without labels from a new dataset, the trained forecaster does worse than the frontier models on all three datasets for counterfactual sensitivity, and on two of three for rerun consistency (Table 2 vs. Table 10), so the generality claim is not well supported.

The forecaster generalizes zero-shot within a dataset family: trained on three FEVEROUS subsets, it stays ahead of both readers on the held-out numerical subset (0.565 against 0.322 and 0.463 on counterfactual sensitivity, and 0.311 against 0.223 and 0.173 on rerun consistency; Table 2, previously Table 1). Zero-shot transfer to an entirely different domain, for example from logic rules and fact verification to math word problems, is a different matter: with only three training datasets, we would not expect it from any model on any language task. The transfer section now states this, and its table includes the readers' results (lines 376-380 and Table 3, previously Table 2).

Did you test whether the OLMo forecaster predicts Qwen's behavior as well as OLMo's? [...] This would help to show whether initializing from the target model really matters.

We added this experiment to the appendix (lines 1375-1418, Tables 19 and 20). The answer depends on the task. For counterfactual sensitivity, a forecaster trained on OLMo's behavior forecasts Qwen's as well as one trained on Qwen's own (0.782 against 0.784, same Qwen3.5-4B backbone), and OLMo's own weights are not needed to forecast OLMo (0.746 from Qwen3.5-4B, against 0.731). For rerun consistency, the target matters on both counts: on RuleTaker, where Qwen is almost always consistent and OLMo is not, a forecaster trained on Qwen's behavior reaches 0.113 on OLMo, against 0.455 for one trained on OLMo's, and initializing from Qwen2.5-7B reaches 0.416, against 0.568 from OLMo's own weights. We made this clearer in the abstract (lines 24-27) and the ablation section (lines 465-470), and now cite Li et al. (2025).

For counterfactual sensitivity, could you compare against a simple baseline based on the RuleTaker gold proofs to see how much the LRM reasoning is actually helpful, as opposed to general resolution traces?

It is true that a solver built on the gold proofs may do well on RuleTaker, but it has to be designed by hand for one dataset and one behavior. What the paper demonstrates is that an LRM's behavior can be learned from its past behavior: the same training recipe, with no knowledge of how any dataset is built, gives forecasters that are more accurate than frontier readers on both behaviors.

Please let us know if this resolves your concerns. If it does, we would appreciate it if you would update your score.

Reviewer_rsqXOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
1
Soundness
1
Read review
Paper summary

This paper proposes Behavior Forecasters, a supervised learning approach for predicting the future behavior of large reasoning models from a single observed reasoning trajectory. The authors investigate two behavioral properties: rerun consistency, which measures the probability of reproducing the same answer across repeated executions, and counterfactual sensitivity, which measures how removing input segments affects the model's answer distribution. The proposed forecasters are initialized from the target LRM and fine-tuned end-to-end using behavioral labels obtained through repeated model executions.

Critical strengths

The paper introduces a potentially useful perspective on understanding LRMs by directly predicting their behavioral properties rather than interpreting reasoning trajectories as explanations. The two investigated tasks are relevant to model reliability and provide concrete learning objectives.

Critical weaknesses
  1. A central motivation of the paper is that reasoning trajectories contain information about the underlying computation that cannot be recovered through naive natural-language reading. However, the experimental evidence supporting this interpretation is less convincing than the main results suggest. Most notably, Table 4 shows that, for counterfactual sensitivity, the full P–R–A–P arrangement achieves a Spearman correlation of 0.723, while the P–A–P arrangement, which completely removes the reasoning tokens, already achieves 0.714. The improvement attributable to including the reasoning trajectory is therefore only 0.009. No statistical analysis is provided to establish whether this difference is meaningful. This result substantially weakens the claim that reasoning tokens provide essential additional information for this task.

  2. The paper formulates both tasks as predicting probability-derived behavioral statistics, yet the primary evaluation relies on Spearman correlation, with Pearson correlation provided as an additional metric. These metrics measure association rather than whether the predicted probabilities accurately reflect actual future behavior. A model could achieve strong rank correlation while producing poorly calibrated probability estimates, which would substantially limit its usefulness for the reliability assessment and deployment decisions emphasized in the paper. The supervision procedure also raises concerns about the accuracy and representativeness of the behavioral targets. The labels are estimated from only ten model executions per original or perturbed prompt. Such estimates can exhibit considerable sampling variability, particularly for intermediate probabilities. The paper does not sufficiently characterize how this label uncertainty affects training and evaluation or whether the resulting forecasters generalize to behavioral probabilities estimated from substantially larger numbers of runs.

Questions for authors

Table 4 shows that removing the reasoning tokens reduces counterfactual-sensitivity Spearman correlation from only 0.723 to 0.714. Is this difference statistically significant? Given the small improvement, what evidence supports the claim that reasoning trajectories provide substantial additional information for this task beyond the prompt and final answer?

1 comment
AuthorsOpenReview ↗

Calibration added, label noise makes our claims conservative

Thank you for the clear and specific review, and we are glad that you found our perspective useful and our two tasks relevant to model reliability. Following your comments, we uploaded a revised PDF that makes clearer what the reasoning tokens contribute in each task and reports calibration for both tasks.

Table 4 shows that removing the reasoning tokens reduces counterfactual-sensitivity Spearman correlation from only 0.723 to 0.714. Is this difference statistically significant?

No, and we do not claim that it is. The ablation rows are single training runs, and the 95% interval of the main forecaster on this test set is [0.701, 0.756] (Table 13), so a difference of 0.009 is within the noise. We made it clearer in the paper that the contribution of the reasoning tokens applies to rerun consistency (0.568 with them, 0.316 without) and not to counterfactual sensitivity (lines 458-463; the ablations are now in Table 5).

what evidence supports the claim that reasoning trajectories provide substantial additional information for this task beyond the prompt and final answer?

Our claim for this task is not about the reasoning tokens. It is that an LRM's behavior can be learned from its past behavior, and that naive reading of its trajectory (the prompt, the reasoning and the answer together; Section 2) does not tell the full story. The evidence is the comparison with the readers: the forecaster is more accurate than GPT-5.4 and Claude Opus 4.6 (0.731 against 0.672 and 0.690, with paired intervals above zero in Table 13). The forecaster that sees only the prompt and the answer (0.714) is also more accurate than both readers, although the readers also see the reasoning. This was not clear enough in the paper, and we have now clarified it throughout (e.g., lines 108-109, 323-325 and 458-463).

These metrics measure association rather than whether the predicted probabilities accurately reflect actual future behavior.

These metrics do reflect actual future behavior. Each label is the LRM's actual future behavior, measured by running it: the fraction of its reruns that give the same answer, or how much removing a segment lowers the rate at which it gives that answer. A high correlation with these labels therefore means that the forecasts track how the LRM actually behaves. Calibration is a further property, which we added for both tasks (lines 1181-1229, Table 14 and Figure 3), and the forecaster is also the best calibrated of the three: its expected calibration error is 0.015 for rerun consistency, against 0.054 for GPT-5.4 and 0.043 for Claude Opus 4.6, and 0.007 for counterfactual sensitivity, against 0.041 and 0.025. We kept Spearman correlation as the main metric because the readers are not trained to produce calibrated scores, and a rank metric does not penalize them for that.

The labels are estimated from only ten model executions per original or perturbed prompt. [...] The paper does not sufficiently characterize how this label uncertainty affects training and evaluation [...]

Label noise can only make our claims conservative. Our claim is that an LRM's future behavior can be learned from its past behavior. Noise in the labels makes this learning harder, so a forecaster that learns the behavior from labels built from only ten runs shows it under harder conditions than necessary, and labels from more runs can only make it easier.

Please let us know if this resolves your concerns. If it does, we would appreciate it if you would update your score.

Reviewer_fpMKOpenReview ↗
Rating
4(+1)
Confidence
3
Informativeness
3
Presentation
3
Soundness
3
Read review
Paper summary

In this work, the authors frame behavior forecasting as a learnable task and train behavior forecasters to make predictions that would typically be made by interpreting model explanations. They present the shortcomings of explanation based approaches for reasoning problems with long reasoning traces and introduce behavior forecasters as an alternative; to better understand and predict the future behavior of reasoning models from their intermediate reasoning trajectories. They train behavior forecasters for two tasks: rerun consistency and counterfactual sensitivity. Through evaluations across different reasoning datasets, they show that their behavior forecasters outperform strong LLMs in predicting future model behavior.

Critical strengths
  • I believe that the problem the authors address, training behavior forecasters to capture patterns in reasoning traces that are overlooked in a naive reading, is a novel and valuable contribution. This could also help better understand the quality of reasoning traces.
  • Strong evaluations across models and tasks. The authors evaluate their approach across diverse reasoning datasets and two language models, demonstrating that the benefits of behavior forecasting are not restricted to a single model or task.
  • Thorough experiments covering generalization to new data, transfer across datasets, and transfer across behavioral targets. The ablations are also useful for isolating the effects of different components involved in building the forecasters.
  • Scalable pipeline that can be extended to more tasks and models without requiring human supervision. The forecasters also require much less inference compute than running frontier LLMs to make similar predictions.
  • Useful for future work, as researchers can build on this framework to develop different kinds of forecasters optimized for different objectives and behavioral targets.
Critical weaknesses
  • Qualitative Analysis: I believe one of the most important potential uses of these behavior forecasters is assessing the quality of reasoning traces, which remains unexplored in this work. A qualitative analysis could include: exploring correlations between the scores of the forecaster models and visible patterns in the reasoning traces, such as backtracking, self-contradiction, and answer memorization; and examining cases where the forecaster assigns a high score to a segment that is never addressed or mentioned in the reasoning trace, along with the percentage of cases in which this occurs. A thorough qualitative analysis would enhance the quality of this work by demonstrating the practical utility of the proposed behavior forecasters
  • Failure analysis: It is important to understand where the behavior forecasters fail. A failure analysis could reveal whether certain triggers in the prompts or reasoning traces cause the forecasters to make incorrect predictions.
  • The authors experiment only with smaller language models (e.g. 2B, 7B parameters). It would be interesting to see whether the findings hold for language models at larger scales (e.g. 14B, 32B, 70B parameters).
  • Rerun/resample baseline: The experiments currently lack a rerun baseline. It would be interesting to see how many reruns of the language model are needed to match the forecaster’s performance. This would help clarify the practical cost-benefit trade-off between using the forecaster and simply resampling.
  • Contribution of the reasoning tokens: For counterfactual sensitivity, removing the reasoning tokens leads to only a modest drop in performance (P–R–A–P: 0.723/0.925 vs. P–A–P: 0.714/0.909 Spearman/Pearson; Table 4). This suggests that most of the signal comes from the prompt and the answer rather than the reasoning trace. This weakens the paper’s broader argument that the reasoning trajectory carries information beyond what naive reading conveys, at least for this task.
Questions for authors

Please see weaknesses above and clarify any misunderstanding I may have had.

2 comments
AuthorsOpenReview ↗

Rerun baseline, qualitative and failure analyses added

Thank you for the positive review and the concrete suggestions, and we are glad that you found the problem novel and valuable and the experiments thorough. Following your comments, we uploaded a revised PDF that adds a rerun baseline, a qualitative analysis and a failure analysis, and makes clearer what the reasoning tokens contribute in each task.

Rerun/resample baseline: [...] It would be interesting to see how many reruns of the language model are needed to match the forecaster's performance.

We added this comparison (lines 1230-1259 and Table 15). For each test trajectory we estimate rerun consistency from m additional runs of the LRM, and score this estimate and the forecaster against a label built from the remaining runs. The forecaster, which uses no additional run, falls between one and two reruns: its Spearman correlation is 0.56, against 0.54 for one rerun and 0.63 for two. Both readers are below a single rerun (0.30 and 0.31). Each rerun generates a whole new trajectory, thousands of tokens long, while the forecaster needs one forward pass over the existing one; for counterfactual sensitivity a rerun is needed for every segment, about 12 per prompt in our test set.

exploring correlations between the scores of the forecaster models and visible patterns in the reasoning traces, such as backtracking, self-contradiction, and answer memorization

We added this analysis, with worked examples (lines 1287-1342, Tables 17 and 18). Visible patterns such as backtracking, hedging and self-contradiction (the reasoning states one answer and later a different one) go with less stable answers, and both the forecaster and the readers react to them. The difference is in the runs with no visible sign. On the 94% of RuleTaker runs that do not contradict themselves, the readers' scores carry almost no information (Spearman 0.07 and -0.06), and the forecaster's still do (0.56). A typical case is a run that misses an existing derivation and confidently answers that the query is false. On the 15 such runs, the LRM repeats this answer in only 10% of the reruns; GPT-5.4 predicts 0.95 on average, and the forecaster 0.19.

examining cases where the forecaster assigns a high score to a segment that is never addressed or mentioned in the reasoning trace, along with the percentage of cases in which this occurs

We measured this with a string-matching rule (lines 1343-1354). Such cases are rare for this LRM, because its reasoning goes over almost every segment: it mentions 99.4% of the segments that affect its answer and 97.3% of those that do not. Only 0.5% of the forecaster's high scores (20 of 3,755) fall on a segment counted as unmentioned, and in the cases that we read, the reasoning did refer to the segment in other words. So for this LRM, reading which segments the reasoning mentions says very little about which ones its answer depends on.

Failure analysis: It is important to understand where the behavior forecasters fail.

We added a failure analysis (lines 1355-1374).

The authors experiment only with smaller language models (e.g. 2B, 7B parameters).

Our counterfactual-sensitivity data alone took about 720 thousand reasoning runs of the 7B LRM. We unfortunately lack the compute to run bigger models, but we expect the approach to stay relevant at larger scales, because the unfaithfulness of the reasoning text does not go away with scale (Chen et al., 2025; Han et al., 2026; Section 2).

For counterfactual sensitivity, removing the reasoning tokens leads to only a modest drop in performance [...] This weakens the paper's broader argument that the reasoning trajectory carries information beyond what naive reading conveys, at least for this task.

This result supports the broader argument rather than weakening it. The argument is that an LRM's behavior can be learned from its past behavior, and that naive reading of its trajectory (the prompt, the reasoning and the answer together; Section 2) does not tell the full story. For counterfactual sensitivity, a forecaster that never sees the reasoning is still more accurate than both readers, who read it (0.714 against 0.672 and 0.690). For rerun consistency, the forecaster also needs the reasoning tokens: removing them drops it from 0.568 to 0.316. We made it clearer in the paper that the contribution of the reasoning tokens applies to rerun consistency and not to counterfactual sensitivity (e.g., lines 108-109 and 458-463).

If the revision addresses the issues that prevented you from giving a score of 4, we would appreciate it if you would update it.

Thank you for the detailed response. The added rerun baseline, qualitative analysis and failure analysis address my main concerns, and the clarified scope of the reasoning-token claim is more accurate. I have raised my score to 4.

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

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