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Under review as a conference paper at ICLR 2027

Accept, Repair, or Restart: Step-Level Risk-Aware SLM–LLM Collaboration

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Abstract

Large language model (LLM)–small language model (SLM) collaboration offers an effective way to balance reasoning quality and computational efficiency by selectively invoking stronger models. However, existing methods typically determine collaboration through response-level confidence or fixed escalation rules, overlooking step-level failures in reasoning trajectories and the need for adaptive interventions tailored to different failure patterns. To address these problems, we propose step-level Risk-Aware Dynamic Action Allocation (RADA), a framework that formulates SLM–LLM collaboration as a risk-aware multi-action decision problem. RADA jointly models global response reliability and step-level reasoning risk to determine when LLM intervention is needed, adapts the intervention criterion using calibrated quality estimates of previously selected actions, and selects the intervention scope between local revision and full regeneration based on the identified failure pattern. Across mathematical and general reasoning benchmarks and multiple SLM–LLM pairs, RADA achieves the highest average accuracy among the evaluated collaboration methods. It improves average mathematical reasoning accuracy by up to 4.33 percentage points over the best-performing baseline while maintaining a favorable accuracy–computation trade-off.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Large Language Models, Small Language Models, LLM-SLM Collaboration, Adaptive Computation Allocation, Reasoning

Reviews

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1234this paper, Bottom 27%
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_YPwKOpenReview ↗
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2
Confidence
3
Informativeness
2
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3
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2
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Paper summary

This paper proposes Risk-Aware Dynamic Action Allocation (RADA) for collaboration between a small language model and a large language model. Given an SLM-generated reasoning trajectory, RADA predicts both response-level and step-level risks and selects among three actions: accepting the SLM response, locally revising the trajectory from an identified risky step, or restarting with full LLM regeneration. It also introduces a stateful threshold that is updated across queries using calibrated average qualities of the selected actions.

The method is evaluated on mathematical and broader reasoning benchmarks with Gemma and Qwen model pairs. RADA generally achieves the highest average accuracy among the evaluated collaborative methods, with competitive estimated FLOPs. Ablations study global and local risk signals, intervention modes, risk-loss weights, threshold adaptation, and the local-risk window.

Critical strengths
  1. The paper studies an important routing decision beyond binary escalation. Selecting among acceptance, local repair, and full regeneration is practically relevant because different reasoning failures require different intervention scopes. The comparison in Table 5 suggests that neither fixed intervention mode is sufficient.

  2. The method combines global and local evidence in an interpretable framework. The joint risk estimator, structural step roles, and explicit routing conditions make the intervention policy easier to inspect than an entirely opaque end-to-end router. The evaluation covers multiple task groups and model pairs.

Critical weaknesses
  1. The dynamic threshold is not updated using observed response quality and is inherently order-dependent. At inference, the update uses a fixed calibration-set average g^a\hat g_a for the selected action rather than the actual quality of the current output. Therefore, the state depends mainly on the sequence of selected actions, rather than realized historical performance. Moreover,

$

Qt+1=Qt+γ−gt,τt+1=clip⁡(τt+λQt+1,0,1)Q_{t+1}=Q_t+\gamma-g_t,\qquad \tau_{t+1}=\operatorname{clip}(\tau_t+\lambda Q_{t+1},0,1)

$

accumulates the quality difference in QtQ_t and then repeatedly accumulates QtQ_t into the threshold. This can make predictions sensitive to query order and clipping. Since evaluation processes examples sequentially in their original order, order robustness is essential to the claimed adaptive behavior.

  1. The empirical evidence does not quantify uncertainty and may involve test-set-guided configuration choices. Experiments use stochastic decoding with temperature 0.70.7, but report only point estimates from an apparently single risk-model training run. Some improvements, such as the 0.350.35-point average gain over COREA on broader reasoning with Qwen, may be within run-to-run variation. In addition, the paper uses MATH500 results to motivate the default loss weights and local-risk window, which raises a concern about test-set model selection unless these settings were fixed beforehand. Multiple seeds, paired confidence intervals, and a clear separation between validation and final testing are needed.
Questions for authors
  1. Clarification: Why is the threshold update described as using historical quality feedback when �0��0� is a fixed calibration-set average and no current-query outcome is observed? Are �1��1� and �2��2� reset between benchmarks or sessions?

  2. Assessment-changing analysis: How sensitive are the results to test-query ordering? Please report results across several random permutations, including threshold trajectories, clipping frequency, action proportions, accuracy, and FLOPs.

  3. Clarification and existing evidence: Were the loss weights and w=5w=5 selected before evaluating MATH500? Please provide multi-seed or repeated-decoding results with paired confidence intervals for the main comparisons, especially the smaller gains on broader reasoning tasks.

3 comments
AuthorsOpenReview ↗

Response to Reviewer YPwK

We thank the reviewer for the constructive questions. We clarify the implementation details and present additional experimental evidence below.

Q1: What does “historical quality feedback” mean, and when are the gating states reset?

  • Historical quality feedback. The feedback comes from previously selected actions and their offline-calibrated expected quality, not from observing the actual correctness of past responses. Although each action-quality estimate g^at\hat g_{a_t} is fixed, the history of selected actions changes the cumulative quality deficit QtQ_t and, consequently, the next threshold τt\tau_t. This proxy signal enables adaptive gating without an online reward model or quality evaluator.
  • State initialization. Both QtQ_t and τt\tau_t are reset for every independent benchmark evaluation or experimental session: Q0=0Q_0=0, and τ0\tau_0 is set to its calibration-determined initial value. No state carries over between benchmarks or independent runs. We will make the terminology and reset rule explicit in the revision.

Q2: How sensitive are the results to query order, including threshold trajectories, clipping, action proportions, accuracy, and FLOPs?

  • Permutation protocol and threshold behavior. We fixed model-generated outputs and shuffled only the test-query order using five seeds (101, 202, 303, 404, 505) on four benchmarks. We also plotted the threshold trajectories: they differ locally across permutations, generally remain around 0.9950.995–1.0001.000, and intermittently reach the upper bound. The table summarizes the results; action proportions are five-seed averages, while boundary statistics show the ranges across seeds.
BenchmarkACC, mean ± SD (%)FLOPs rangeSLM / Full / Local (%)First τ=1\tau=1 (query)Longest τ=1\tau=1 run
MATH50080.36 ± 0.3014.02–14.0643.56 / 40.08 / 16.3620–973–18
ACPBench58.93 ± 0.2310.30–10.3941.36 / 44.58 / 14.0711–5213–29
MuSiQue30.20 ± 0.162.29–2.3139.31 / 48.68 / 12.0113–1415–10
KOR-Bench38.42 ± 0.225.50–5.6539.92 / 46.36 / 13.7220–373–8
  • Interpretation. Query order changes the threshold trajectory and the timing of upper-bound saturation, but aggregate accuracy, FLOPs, and action allocation remain relatively stable across these permutations. The boundary statistics report occurrences of τ=1\tau=1, not the exact number of pre-clipping overshoots. We have prepared trajectory plots and will include them with the permutation results in the revised manuscript.

Q3: Were the loss weights and w=5w=5 fixed before MATH500 evaluation, and what repeated-run and paired-confidence evidence is available?

  • Hyperparameter selection. The settings were selected from MATH500 sensitivity analyses, not fully predetermined before inspecting MATH500 results. Table 3 selects wg=0.3w_g=0.3, wl=0.7w_l=0.7 (78.00% accuracy); Appendix Table 8 selects w=5w=5 from 3,4,5,6,7{3,4,5,6,7} (78.20% accuracy, A/F 5.57). These settings were held fixed on the other benchmarks, without dataset-specific retuning.
  • Multi-seed and repeated decoding. The order-only results above assess four benchmarks with fixed generations. We additionally varied both generation seeds and query order on MATH500. The table reports per-seed accuracy (all accuracy entries are percentages):
ExperimentSeed 101202303404505ACC, mean ± SD (%)FLOPs range
MATH500 (order + decoding)80.6080.0080.2080.4080.6080.36 ± 0.2614.03–14.06

Together with the five-seed order-only results in Q2, this supports stability under the tested randomizations; order-only runs should not be conflated with independent decoding runs.

  • Paired confidence intervals. The requested per-instance paired confidence intervals against baselines are still being analyzed and cannot yet be reported reliably. Run-to-run standard deviations are not a substitute for confidence intervals on paired accuracy differences. We will add this analysis once complete.
AuthorsOpenReview ↗

Response to Reviewer YPwK (Part 2)

Q3: Were the loss weights and w=5w=5 fixed before MATH500 evaluation, and what repeated-run and paired-confidence evidence is available?

  • Paired confidence intervals. We further completed instance-level paired comparisons between RADA and STEER on ACPBench, covering all 900 test instances across five random seeds (101, 202, 303, 404, and 505). For each seed, we categorized the paired predictions into four outcomes: only RADA correct, only STEER correct, both correct, and both incorrect. Based on these paired outcomes, we calculated the accuracy difference between RADA and STEER and its corresponding 95% confidence interval. The results are reported below:
SeedTotalOnly RADA CorrectOnly STEER CorrectBoth CorrectBoth Incorrect95% CI (RADA − STEER, pp)
1019002529507339[-2.05, +1.16]
2029003031498341[-1.81, +1.59]
3039002932500339[-2.04, +1.37]
4049002832502338[-2.13, +1.24]
5059002632507335[-2.33, +0.99]

All five 95% confidence intervals include zero, indicating that the paired accuracy differences between RADA and STEER are not statistically significant at the 0.05 level on ACPBench. This analysis provides additional instance-level statistical evidence for a more comprehensive assessment of the performance differences between the two methods.

We note that, due to the limited time available during the rebuttal period, we were only able to complete the additional paired confidence interval analysis on ACPBench. On this benchmark, RADA's accuracy is slightly lower than STEER's, although the observed difference is small and not statistically significant. However, this result should be considered alongside the broader experimental evidence reported in the manuscript. RADA achieves higher average accuracy than STEER on both mathematical reasoning benchmarks (42.70% vs. 38.37%) and broader reasoning benchmarks (43.28% vs. 42.16%) with the Gemma 4B–12B model pair. These results demonstrate that, despite a marginal difference on ACPBench, RADA maintains stronger overall accuracy across the evaluated benchmarks.

AuthorsOpenReview ↗

Additional Clarifications, if Needed

We sincerely thank all reviewers again for their valuable feedback. We have provided point-by-point responses to the concerns raised in the reviews, together with additional clarifications and experimental results. As the discussion period is approaching its conclusion, we would like to ask whether there are any remaining questions or concerns that have not been fully addressed by our responses. Please feel free to let us know if further clarification is needed, and we will do our best to address them before the discussion period ends. We greatly appreciate your time and constructive feedback.

Reviewer_csU8OpenReview ↗
Rating
2
Confidence
3(−1)
Informativeness
1
Presentation
2
Soundness
2
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Paper summary

This paper proposes RADA, a framework for SLM–LLM collaboration that combines global and step-level risk estimation with dynamic threshold gating to select between direct acceptance, local revision, and full regeneration. Experiments on mathematical and general reasoning benchmarks show improvements over several existing baselines.

Critical strengths

The paper addresses a practical problem in efficient LLM inference and evaluates the proposed method across multiple benchmarks and model pairs.

Critical weaknesses

The innovation of this paper is limited. Many similar works have explored confidence-based routing and fine-grained LLM–SLM collaboration, and the distinction from existing methods is not sufficiently clear [1–3]. The paper's contribution is not sufficiently differentiated from prior work.

[1] Lee et al. Confidence-Guided Stepwise Model Routing for Cost-Efficient Reasoning. [2] Pan et al. SpecReason: Fast and Accurate Inference-Time Compute via Speculative Reasoning. [3] Zhang et al. Confidence-Calibrated Small-Large Language Model Collaboration for Cost-Efficient Reasoning.

Questions for authors
  1. How does RADA differ substantially from existing step-level routing and SLM–LLM collaboration methods?
  2. Why is a dynamic threshold preferable to a static threshold, and how does it affect the routing decisions?
  3. Since the gating mechanism updates its state sequentially, are the results sensitive to the order of test examples?
2 comments
AuthorsOpenReview ↗

Response to Reviewer csU8

We thank the reviewer for the detailed feedback. We clarify the 3 concerns and provide additional experimental evidence below.

Q1: What substantively distinguishes RADA from existing stepwise routing and SLM–LLM collaboration methods?

We thank the reviewer for highlighting these relevant studies. We respectfully disagree that RADA lacks substantive novelty: its central distinction is risk-guided intervention scope, rather than model selection alone.

  • Differences from existing methods. STEER [1] selects the model for each upcoming reasoning step based on confidence; SpecReason [2] lets a stronger model verify and, if needed, correct speculative steps; and COREA [3] uses calibrated answer-level confidence to accept an SLM answer or defer the query to an LLM. RADA instead examines the risk structure of a completed SLM reasoning trajectory and chooses among accepting it, revising a suffix, and regenerating the full answer.
  • Core innovation. RADA combines global–local risk estimation, history-aware dynamic gating, and risk-guided intervention scope in one decision framework. Its key contribution is to determine whether LLM intervention is needed and how much existing reasoning should be preserved, based on where risks occur and how they are distributed.
  • Experimental validation. In Table 1 (Gemma 4B–12B, MATH500), RADA achieves 81.60% accuracy, compared with 76.00% for STEER [1], 75.00% for SpecReason [2], and 75.60% for COREA [3]. Tables 4–5 further show that combining global and local risks, and adaptively choosing the intervention scope, improves accuracy over the corresponding ablations. Table 2 also shows improvements on broader reasoning benchmarks. These results support the practical value of the proposed framework.

Q2: Why does dynamic threshold gating outperform static thresholds, and how does it affect model routing?

  • Why dynamic gating helps. A static threshold cannot adjust to earlier routing decisions. RADA instead updates its acceptance criterion using the cumulative gap between the target quality and the offline-calibrated expected quality of selected actions, adapting LLM intervention across queries. Appendix Table 7 compares three strategies under the same reduced-data evaluation setting (450 training examples).
  • Effect on routing. When the cumulative expected-quality deficit rises, RADA raises the threshold, making direct SLM acceptance more restrictive; otherwise, it relaxes the threshold. Compared with the standard static gate, dynamic gating reduces direct SLM responses from 53.4% to 47.0% and increases full regeneration from 30.2% to 32.8% and local revision from 16.4% to 20.2%, yielding +3.20 percentage points in accuracy with slightly lower FLOPs. Notably, it also outperforms the dataset-calibrated static gate while invoking the LLM less often (53.0% vs. 60.0%). Thus, its benefit is adaptive allocation, not simply more LLM calls; it also avoids test-dataset-specific threshold calibration.

Q3: Are RADA’s results sensitive to the order of test queries because the gating state is updated sequentially?

  • Order dependence. RADA accumulates the calibrated expected-quality gap from previous actions, so different query orders can change individual thresholds and routing decisions. We additionally plotted the threshold trajectories under different permutations: they show local differences and occasional upper-bound hits, but no pronounced divergence in aggregate behavior. We will include these plots in the revision.
  • Five-seed permutation results. We fixed model-generated outputs and shuffled only the query order with five seeds (101, 202, 303, 404, 505) on four benchmarks. The results are summarized below (action proportions are five-seed averages):
BenchmarkACC, mean ± SD (%)FLOPs rangeSLM / Full / Local (%)
MATH50080.36 ± 0.3014.02–14.0643.56 / 40.08 / 16.36
ACPBench58.93 ± 0.2310.30–10.3941.36 / 44.58 / 14.07
MuSiQue30.20 ± 0.162.29–2.3139.31 / 48.68 / 12.01
KOR-Bench38.42 ± 0.225.50–5.6539.92 / 46.36 / 13.72

Although query order affects individual gating trajectories, aggregate accuracy, FLOPs, and action allocation remain relatively stable across the tested permutations. This experiment isolates order sensitivity; it does not assess independent decoding randomness.

References

[1] Lee et al., Confidence-Guided Stepwise Model Routing for Cost-Efficient Reasoning. AAAI, 2026.

[2] Pan et al., SpecReason: Fast and Accurate Inference-Time Compute via Speculative Reasoning. NeurIPS, 2025.

[3] Zhang et al., Confidence-Calibrated Small-Large Language Model Collaboration for Cost-Efficient Reasoning. EACL, 2026.

AuthorsOpenReview ↗

Additional Clarifications, if Needed

We sincerely thank all reviewers again for their valuable feedback. We have provided point-by-point responses to the concerns raised in the reviews, together with additional clarifications and experimental results. As the discussion period is approaching its conclusion, we would like to ask whether there are any remaining questions or concerns that have not been fully addressed by our responses. Please feel free to let us know if further clarification is needed, and we will do our best to address them before the discussion period ends. We greatly appreciate your time and constructive feedback.

Reviewer_QEJbOpenReview ↗
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2
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper is about how to use computation more efficiently when small language models (SLMs) and large language models (LLMs) work together on reasoning tasks. The authors point out that existing methods have difficulty distinguishing errors that occur at different steps or in different parts of the reasoning process. They also lack flexibility in deciding how much work should be handed over to the larger model. The paper proposes RADA, which makes the collaboration a choice between three actions: (1) accept the SLM's answer, (2) revise the solution starting from a detected high-risk step, or (3) let the LLM generate a new solution from scratch.

To make these decisions, RADA first estimates the risk of the whole answer and the risk of individual reasoning steps. The global risk score is used to decide whether the LLM needs to step in. The threshold for this decision changes over time, based on quality estimates associated with previously selected actions. If intervention is needed, the method looks at the distribution of step risks to decide whether to revise part of the answer or regenerate it entirely.

The experiments cover both mathematical and general reasoning tasks, using Gemma and Qwen models. RADA has the highest average accuracy among the collaboration methods tested in the paper. The improvement is more substantial on the mathematical reasoning benchmarks, while the differences on general reasoning are relatively small.

Critical strengths

I agree with the authors that deciding whether to call an LLM is not the same as deciding how the LLM should intervene. Some errors can be fixed by continuing from an earlier step, while others really call for a completely new solution. Treating these as separate decisions makes sense to me.

The method is fairly easy to follow. Global risk decides whether an intervention is needed, and step-level risk decides what that intervention should be — I think this split is reasonable. Keeping the SLM frozen is also a nice practical touch, since it avoids having to retrain the smaller model whenever the collaboration procedure changes.

On the Gemma 4B–12B pair, RADA improves average mathematical reasoning accuracy from 38.37% with STEER to 42.70%, and the Qwen2.5-Math results also beat the strongest collaboration baseline. I wouldn't dismiss these gains. Even with my concerns about the method, the experiments suggest the full system is doing something useful.

The ablations are relevant. Table 4 shows that using both global and local risk beats using either one alone, and Table 5 shows that combining local revision with full regeneration works better than always picking one intervention. These experiments support the overall design, even if they don't fully answer my questions about the individual components.

Critical weaknesses

I'm unsure what the dynamic threshold is actually adapting to. Sec. 3.3 uses g_t = ĝ_{a_t}, the average quality of the selected action on the calibration set — so the system never knows whether its last answer was correct, only which action it picked. Two local revisions, one right and one wrong, update the threshold identically. I wouldn't call this invalid, but it's adaptation to the history of selected actions, not to actual response quality, and the paper should say so. The update rule also worries me: Q_{t+1}=Q_t+γ−g_t, then τ_{t+1}=clip(τ_t+λQ_{t+1},0,1). If the gap stays positive for many queries, does τ just hit the ceiling? How often is the SLM answer still accepted then? No analysis of this. Results also depend on query order (threshold depends on all prior choices), yet experiments use the original benchmark order — would shuffling change things? Please show the actual threshold trajectory and results under different orders.

The action selection rule isn't fully convincing. Why entropy 0.5 and concentration 0.6? Why are Understanding and Decomposition treated differently — an Equation Setup error can also invalidate the rest. Table 5 shows using both actions beats using one, but not that this rule is the right way to choose. Also, local revision regenerates everything after the first high-risk step; if that step is early, it's basically full regeneration. Missing simpler baselines: choose by how early the first risky step appears, or by highest risk score alone, without entropy/concentration.

Risk prediction accuracy is never directly evaluated. The estimator drives everything downstream, but experiments only report final system accuracy. Fig. 4 shows where the model thinks errors are, not whether it's right. Also, the local risk head (Sec. 3.2) uses step text, role, and token entropy — not the original problem or prior steps. How does it catch context-dependent errors, e.g., a correct-looking calculation using a wrong earlier number? The LLM judge has the reference answer at training time; the estimator doesn't at test time. A direct error-localization evaluation, plus a comparison against a context-aware estimator, would help.

Are the reported FLOPs complete? RADA must generate the SLM answer, assign roles, compute risk features, and run the estimator before deciding. In Table 6, at 100% LLM invocation the FLOPs exactly match LLM-alone in Table 1 — maybe SLM/risk estimation is skipped there, but the paper doesn't say. Full cost and end-to-end latency should be reported.

General-reasoning gains are small: 44.93 vs 44.58 (COREA) on Qwen2.5 1.5B–7B, +1.12 over STEER on Gemma. With temperature 0.7 and an order-dependent threshold, I need seeds and std devs, not single runs.

How much is new vs. combining existing ideas? GLoRe, STEER, and prior routing work already cover much of this. Which part drives the gains — the joint risk estimator, the dynamic threshold, or the routing rule? Current ablations remove components but don't test simpler combinations.

Questions for authors

The dynamic gating module uses fixed per-action quality estimates. Why is this described as historical quality feedback? Could you show how the threshold evolves during inference, and whether results depend on query order?

How were the thresholds and the structural-role distinction in the routing policy chosen? Have you tried simpler policies, e.g., deciding based on the position of the first high-risk step?

How accurately can the risk estimator localize incorrect reasoning steps? Does adding the original question and prior reasoning context improve the local risk predictions?

In Table 6, why does the 100% LLM invocation setting have the same FLOPs as the LLM-only baseline? Are SLM generation and risk estimation skipped in that setting?

Could you provide repeated runs, especially for the general-reasoning tasks where the accuracy gaps are small?

3 comments
AuthorsOpenReview ↗

Response to Reviewer QEJb (Part 1)

We thank the reviewer for the constructive feedback. We clarify the 5 concerns and provide additional experimental evidence below.

Q1: What does “historical quality feedback” mean, and how sensitive is dynamic gating to query order?

  • Historical quality feedback. “Historical quality feedback” refers to the cumulative influence of previously selected actions and their offline-calibrated expected quality, not observed correctness of individual responses. Specifically, RADA updates Qt+1=Qt+γ−g^∗atQ_{t+1}=Q_t+\gamma-\hat{g}*{a_t} and τ∗t+1=clip⁡(τt+λQt+1,0,1)\tau*{t+1}=\operatorname{clip}(\tau_t+\lambda Q_{t+1},0,1). Although each action's calibrated quality is fixed, the sequence of selected actions changes the cumulative deficit and hence subsequent thresholds. This provides adaptive gating without the overhead of an online reward model or quality evaluator.
  • Query-order sensitivity. To examine order sensitivity, we held model generations fixed and shuffled only the query order using five seeds (101, 202, 303, 404, 505) on four benchmarks. The threshold trajectories show order-dependent local fluctuations, generally near 0.995–1.000, with intermittent upper-bound hits. Here, a threshold trajectory refers to the evolution of the gating threshold τt\tau_t over the sequentially processed test queries. Specifically, we plot τt\tau_t against the query index for each of the five query permutations, where each update is determined by the action selected for the preceding query. These trajectories illustrate how different query orders lead to different threshold evolution patterns, including local fluctuations and periods of saturation at the upper bound of 1.0. We report accuracy, FLOPs, all three action proportions, and boundary behavior below (action proportions are five-seed averages):
BenchmarkAccuracy, mean ± SD (%)FLOPs rangeSLM / Full / Local (%)First τ=1\tau=1 (query)Longest τ=1\tau=1 run (queries)
MATH50080.36 ± 0.3014.02–14.0643.56 / 40.08 / 16.3620–973–18
ACPBench58.93 ± 0.2310.30–10.3941.36 / 44.58 / 14.0711–5213–29
MuSiQue30.20 ± 0.162.29–2.3139.31 / 48.68 / 12.0113–1415–10
KOR-Bench38.42 ± 0.225.50–5.6539.92 / 46.36 / 13.7220–373–8

Across the five permutations, the largest within-benchmark spread in any action proportion is 2.80 percentage points. Thus, although query order affects individual threshold trajectories and upper-bound behavior, aggregate accuracy, computation, and action allocation remain relatively stable. We have also plotted the threshold trajectories under different query permutations, which further illustrate their local fluctuations and intermittent upper-bound saturation. We will include these plots and the complete permutation results in the revised manuscript. Note that the reported upper-bound statistics reflect occurrences of τ=1\tau=1, rather than the exact number of pre-clipping overshoots.

Q2: How were the routing thresholds and structural-role rules chosen, and why not route solely by the first high-risk step's position?

  • Risk criteria and threshold selection. The normalized risk entropy HrH_r captures risk dispersion, whereas the contiguous-window score CwC_w captures local risk concentration. We use Hr<0.5H_r<0.5 and Cw>0.6C_w>0.6 as fixed heuristic conditions for local revision, not theoretically optimal thresholds. Appendix Table 8 evaluates window sizes w=3,4,5,6,7w=3,4,5,6,7, yielding accuracies of 77.00%, 77.20%, 78.20%, 77.40%, and 77.60%, respectively; w=5w=5 also achieves the highest A/F (5.57).
  • Structural-role distinction. Understanding and Decomposition are treated as structural roles because errors there can undermine the entire reasoning prefix, favoring full regeneration. For localized non-structural risk, we preserve the prefix preceding the first high-risk step and revise the suffix.
  • Comparison with position-only routing. A position-only rule indicates how much of the prefix can be reused, but not whether it is trustworthy or whether risks are scattered. Table 5 in the main manuscript also supports selecting the intervention type according to risk characteristics. These ablations establish the benefit of combining the two intervention types, not a direct advantage over a position-only router, which has not yet been separately evaluated. We will clarify this distinction and the heuristic nature of the routing cutoffs in the revision.
AuthorsOpenReview ↗

Response to Reviewer QEJb (Part 2)

Q3: How accurately can RADA identify erroneous reasoning steps, and would additional context improve local risk prediction?

  • Error localization. The local risk estimator is trained with LLM-annotated step-level supervision, but we do not yet have independent, sufficiently matched step-error annotations to report a reliable localization accuracy. Judging every step across all benchmarks with another LLM would entail substantial cost and could introduce correlated evaluation bias. We therefore assess the downstream utility of step-level risk, rather than claiming a measured localization rate: in Table 4, combining global and local risks improves MATH500 accuracy to 81.60%, versus 76.20% with global risk alone and 76.60% with local risk alone. These results demonstrate complementary value, not direct localization precision.
  • Additional reasoning context. Local prediction uses step text, structural role, and token entropy conditioned on the question and preceding generation; the global head separately encodes the question and full reasoning trajectory. Thus, context already contributes to RADA, although the local text encoder does not explicitly process the full history. Adding that history could improve context-dependent error detection, but would require more computation per step. We will clarify this distinction and investigate the accuracy–cost trade-off.

Q4: Why does Table 6 report the same FLOPs as the LLM-only baseline at a 100% LLM invocation rate?

The 100% point in Table 6 represents direct, independent LLM inference for every query, not execution of the full RADA pipeline followed by escalation. Running the SLM and risk estimator when every query is already assigned to the LLM would add unnecessary cost. We will make this execution path and its FLOPs accounting explicit in the revision.

Q5: Can the authors provide repeated-experiment results, especially for broader reasoning benchmarks with small accuracy gains?

  • Five-seed evaluation. We ran five query-order permutations (seeds 101, 202, 303, 404, 505), holding the model-generated outputs fixed, on MATH500, ACPBench, MuSiQue, and KOR-Bench. The per-seed accuracies and FLOPs variation are reported below:
BenchmarkSeed 101 ACC (%)202303404505Mean ± SD (%)FLOPs range
MATH50080.4080.8080.2080.0080.4080.36 ± 0.3014.02–14.06
ACPBench59.1158.6758.7858.8959.2258.93 ± 0.2310.30–10.39
MuSiQue30.3330.4130.0430.1630.0830.20 ± 0.162.29–2.31
KOR-Bench38.2438.5038.3738.7738.2438.42 ± 0.225.50–5.65
  • Interpretation and scope. In particular, MuSiQue and KOR-Bench show accuracy SDs of only 0.16 and 0.22 percentage points; FLOPs and action proportions also vary little (see Q1). This supports stability under query-order perturbations, but does not cover independent decoding randomness. We will report these results with that scope clearly stated.
AuthorsOpenReview ↗

Additional Clarifications, if Needed

We sincerely thank all reviewers again for their valuable feedback. We have provided point-by-point responses to the concerns raised in the reviews, together with additional clarifications and experimental results. As the discussion period is approaching its conclusion, we would like to ask whether there are any remaining questions or concerns that have not been fully addressed by our responses. Please feel free to let us know if further clarification is needed, and we will do our best to address them before the discussion period ends. We greatly appreciate your time and constructive feedback.

Comments on the paper

2 comments
AuthorsOpenReview ↗

A Gentle Follow-up on the Rebuttal

As the discussion period closes at 11:59 PM AoE on November 18, we would kindly like to ask whether there are any remaining concerns that our responses have not fully addressed. If you have not yet had a chance to review our rebuttal, we would greatly appreciate it if you could do so before the discussion period concludes. Should anything remain unclear, please feel free to let us know, and we will be happy to provide further clarification promptly. We sincerely hope that our responses have adequately addressed your concerns, and would greatly appreciate any further feedback you may have. Thank you once again for your time and consideration.

AuthorsOpenReview ↗

Global Response to the Area Chair

We would like to draw the Area Chair's attention to the key responses and additional efforts made during the rebuttal, hoping to facilitate the final assessment of our submission.

Main Contributions and Novelty RADA proposes a Risk-Aware Dynamic Action Allocation framework for more effective LLM–SLM collaborative reasoning. Its central contribution is not simply selecting which model should handle the next reasoning step, but dynamically determining whether LLM intervention is necessary and, if so, the appropriate scope of intervention, based on the risk structure of the reasoning process. By integrating global–local risk estimation, history-aware dynamic gating, and risk-guided intervention scope allocation, RADA establishes a clear distinction from existing approaches such as STEER, SpecReason, and COREA.

Key Concerns Addressed We have provided point-by-point responses to all questions raised by the three reviewers, together with additional clarifications and experimental evidence. Our responses primarily address the following aspects:

Methodological clarifications: We further explained the definition of historical quality feedback, the update and reset mechanisms of dynamic thresholds, and the rationale behind risk estimation and structural-role rules. Risk estimation and routing mechanisms: We clarified the respective roles of global and local risk estimation, the rationale for selecting different intervention strategies, as well as the FLOPs accounting and model-routing mechanisms. Experimental robustness: We conducted additional multi-seed query-order sensitivity experiments, generation randomness experiments, and instance-level paired confidence interval analyses between RADA and STEER on ACPBench, providing further evidence regarding the stability of our approach and its statistical performance. Hyperparameter and implementation details: We provided further explanations regarding hyperparameter selection, cross-benchmark evaluation settings, and relevant implementation details. Discussion and Final Consideration We submitted our detailed point-by-point responses to the three reviewers on November 13 and subsequently provided additional experimental results and clarifications on November 17. We have made every effort to carefully address the reviewers' questions through detailed explanations, additional analyses, and experiments wherever feasible.

As of now, we have not received further questions or requests for clarification from the reviewers. We fully respect the reviewers' time and understand that the absence of further responses should not be interpreted as explicit agreement. Nevertheless, we hope that the responses and additional evidence provided during the rebuttal will receive full consideration in the final assessment, rather than being overlooked due to the absence of further discussion.

We respectfully ask the Area Chair to consider our comprehensive responses and additional experimental evidence when making the final recommendation. If our responses have adequately addressed the substantive concerns raised by the reviewers, we would be grateful if this could be reflected in the final assessment of our submission.

We sincerely appreciate the Area Chair's time, consideration, and effort throughout the review process.

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

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