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Under review as a conference paper at ICLR 2027

Efficient Reasoning Training Does Not Always Harm CoT Faithfulness and Monitorability

Abstract

Chain-of-thought (CoT) reasoning allows humans to inspect how large language models reach their answers, and oversee model behaviour. This reasoning comes at an increased inference cost, motivating efficient methods that train models to solve tasks using fewer tokens. However, a common concern is that such training may cause models to skip important reasoning steps, so the CoT no longer faithfully reflects the model's decision. It is unclear whether or when this occurs in practice, since different efficiency methods apply length pressure to models' CoT in distinct ways, and faithfully explaining a model's decision takes more tokens on some tasks than others. To understand these dynamics, we fine-tune a variety of models with three methods that apply length pressure differently, namely a fixed generation budget, a per-example length target, and a group-relative length reward. We evaluate how efficient reasoning affects CoT faithfulness (i.e., how well the CoT reflects model decisions on related inputs) and monitorability (i.e., whether the CoT reveals when input interventions alter the output). We find that it affects faithfulness and monitorability differently. Faithfulness falls in most settings, primarily because the trained models are less consistent. Monitorability is more robust, as models keep acknowledging the influence on their answer even when the CoT is much shorter.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
CoT monitorability, reasoning, CoT faithfulness, reasoning efficiency

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.
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Paper summary

This paper investigates how reasoning efficiency training affects the faithfulness and monitorability of chain-of-thought (CoT). It evaluates three efficiency methods across three base models, measuring faithfulness through Normalized Simulatability Gain (NSG) and monitorability through the detection of sycophancy and cognitive-bias interventions from CoT alone. NSG decreases in 11 of 15 training settings, which the authors attribute primarily to reduced behavioral consistency rather than loss of explanatory information. Monitorability is comparatively robust: sycophancy remains detectable despite substantial CoT shortening, while cognitive-bias detection deteriorates under the strongest compression. Some settings substantially shorten CoT without reducing NSG, suggesting that the effects of efficiency training depend on the model, training method, task, and intended use of CoT.

Critical strengths
  • Distinguishes the predictive value of CoT from its monitorability. Evaluating these separately shows that reasoning efficiency training can affect different oversight functions differently. Comparisons across multiple base models, training methods, and tasks provide useful evidence that shortening CoT does not uniformly undermine oversight.

  • Investigates behavioral consistency and concrete failure patterns beyond CoT length. The paper identifies settings that substantially shorten CoT without reducing NSG, examines the association between consistency and NSG, and illustrates cue omission and reframing. These analyses provide useful hypotheses about when efficiency training compromises oversight.

Critical weaknesses
  • The attribution of NSG degradation primarily to inconsistency is insufficiently established. The ceiling estimated from ten samples per question is vulnerable to finite-sample bias, while the decomposition assumes that trained models retain the base model’s fraction of the attainable NSG ceiling. These analyses do not adequately separate stochasticity, loss of explanatory information, and predictor limitations.

  • The conclusions exceed what the evaluations directly establish. Excluding stronger predictors limits the robustness of the NSG findings, while evaluation with one monitor on restricted tasks provides limited support for broader safety claims. Lower NSG does not directly establish worse identification of decision-relevant features, and preserved monitorability scores do not guarantee accurate detection of causal influence in individual responses.

Questions for authors
  • Do the changes in NSG before and after efficiency training, as well as the rankings of efficiency methods, persist when stronger predictors are included? Given that NSG normalizes gains by the remaining baseline error, why were higher no-CoT accuracy and smaller uplift considered sufficient reasons to exclude stronger predictors? Addressing this would clarify whether the findings generalize across predictor capabilities or depend on the selected predictors’ ability to interpret compressed CoT.

  • Are independent samples used to select the oracle’s modal answer and evaluate its accuracy? Do the estimated ceilings and differences between base and efficiency-trained models stabilize as the number of samples increases beyond ten? Addressing this would establish how robust the ceiling estimates and their changes are to finite-sample bias and sampling variability.

  • Can changes in the NSG ceiling be decomposed into the contributions of changes in reference-model consistency and changes in no-CoT predictor accuracy? This decomposition would distinguish a lower ceiling caused by increased inconsistency from a change in the baseline used to normalize NSG.

  • Does the conclusion that inconsistency explains most of the NSG degradation remain valid when the assumption that trained models retain the base model’s fraction of the attainable ceiling is relaxed? Addressing this would show whether the main attribution is robust or depends strongly on the decomposition assumption.

  • Are answer-changing cases selected using individual outputs, or are they identified through repeated sampling that establishes stable changes in answer distributions? Do the findings hold when the same question set is used before and after training? Addressing this would help distinguish systematic behavioral changes from sampling variability and changes in the composition of the analyzed cases.

  • Can the authors report the intervention effect, the unadjusted detection rate, the true negative rates in both conditions, and the number of eligible questions before and after training? Do the monitorability results hold on the same question set? Addressing this would clarify whether stable aggregate scores reflect preserved detection ability or changes in intervention strength, metric components, or question eligibility.

5 comments

Thank you for your detailed review and constructive feedback. Please find the answers to your concerns below.

1: "The attribution of NSG degradation primarily to inconsistency is insufficiently established…"

We address the points regarding this individually:

"The ceiling estimated from ten samples per question is vulnerable to finite-sample bias"

To test this, we resampled the base and GLP models 30 times per question instead of 10, on a fixed random fifth of the counterfactuals that is the same for every model. Using 30 samples, the oracle upper bound still falls for Qwen3-4B and Olmo3-7B and has a very small positive change for Qwen3-8B (Table 1). Given these results, we are confident that increasing the number of samples will not change our claims about the change in the upper bound.

Model10 samples30 samples
Qwen3-8B+2.2+0.6
Qwen3-4B-15.8-17.7
Olmo3-7B-20.5-16.6

Table 1. Change in the NSG upper bound (pts) from base to GLP, estimated from 10 vs 30 samples per question.

"Are independent samples used to select the oracle's modal answer and evaluate its accuracy?"

Yes they are independent samples. The oracle's most common answer comes from the 10 resamples, and its accuracy is scored against the model's original answer. That original answer was generated separately from the resamples, and it is the same answer the predictors are scored against.

"Does the conclusion that inconsistency explains most of the NSG degradation remain valid when the assumption that trained models retain the base model's fraction of the attainable ceiling is relaxed?"

To relax this assumption, we also recalculate the share using the trained model's fraction of the bound instead of the base model's. This asks how much NSG the trained model would recover if its upper bound were restored to the base model's level while it kept its own fraction of the bound. Using this, we find that the share of the NSG reduction explained by the fall in the upper bound changes only slightly, from 24-80% to 20-74%, and remains at or above 50% in 8 of the 11 runs with an NSG drop, the same 8 as before (Appendix E, Table 8 in the revised paper). The main exception under both assumptions is Qwen3-4B L1-Low and L1-Medium, where most of the reduction is not explained by the bound.

"predictor limitations"

To show that a stronger predictor would not change the results, we include DeepseekV4-Flash as a predictor. We discuss this further in our response to the second weakness (see point 2 below).

"Can changes in the NSG ceiling be decomposed into the contributions of changes in reference-model consistency and changes in no-CoT predictor accuracy?"

Yes, we can decompose this. We would also like to highlight that when no-CoT accuracy falls, it raises the upper bound rather than lowering it, so it cannot explain the fall in the bound. To decompose this, we split each change in the bound into a part from consistency and a part from no-CoT accuracy (Appendix E, Table 9). In every setting with a significant NSG drop, the no-CoT part either raises the bound or barely changes it (Olmo3-7B, -0.9 to -0.3 points). The fall in the upper bound therefore comes from the fall in consistency.

2: "The conclusions exceed what the evaluations directly establish…"

We address all of the individual points regarding this weakness below.

"Excluding stronger predictors limits the robustness of the NSG findings" and "Given that NSG normalizes gains by the remaining baseline error, why were higher no-CoT accuracy and smaller uplift considered sufficient reasons to exclude stronger predictors?"

We agree that excluding them wasn't necessary, however, including them does not change our findings. To compare our original results to a stronger model, we add DeepseekV4-Flash as a predictor for the base and GLP results on Qwen3-4B. Table 2 shows that the reduction in NSG with DeepseekV4-Flash is similar to that of the predictors we originally used, both separately and pooled. Given this, we argue that our original results are robust to swapping in different predictors, including stronger models like DeepseekV4-Flash.

PredictorΔNSG
Pooled (paper)-9.5 [-12.3, -6.8]
Qwen3-32B-12.5 [-16.1, -8.8]
GPT-OSS-20B-8.2 [-12.0, -4.5]
Gemma3-27B-8.3 [-12.2, -4.1]
DeepseekV4-Flash-11.0 [-15.2, -6.8]

Table 2. Change in NSG after GLP training on Qwen3-4B for each predictor, with 95% confidence intervals.

"Evaluation with one monitor"

To address the fact that we only use one monitor, we re-run the monitorability evaluation using GPT-6-Luna (replacing DeepseekV4-Flash) for both FACE-Eval and the medical cognitive-bias task. We observe the same two patterns. Sycophancy detection on FACE-Eval is preserved under compression (max drop -0.08, matching the main text), and cognitive-bias detection degrades with compression, correlating with CoT length relative to the base model. Table 3 shows a sample of the results for the cognitive-bias task, and the full results are in Appendix D of the revised paper.

ModelMethodDeepseekV4-FlashGPT-6-Luna
Qwen3-8BBase0.8680.925
Qwen3-8BL1-Low0.5470.589
Olmo3-7BBase0.7730.850
Olmo3-7BL1-Low0.5310.579
Qwen3-4BBase0.8890.984
Qwen3-4BL1-Low0.6170.634

Table 3. Cognitive-bias monitorability with the original monitor (DeepseekV4-Flash) vs GPT-6-Luna. Absolute scores change, but the same patterns can be observed when comparing base to trained models.

"Preserved monitorability scores do not guarantee accurate detection of causal influence in individual responses."

We argue that this is true of most metrics. For example, higher accuracy does not guarantee that a model is correct on a particular problem, but when we find higher accuracy we accept that the model is better on that task. In the same way, higher monitorability scores do not guarantee detection in individual responses, but they do show that in general the CoT is more monitorable than one with a lower score.

"Can the authors report the intervention effect, the unadjusted detection rate, the true negative rates in both conditions, and the number of eligible questions before and after training?"

Intervention effects can already be found in Appendix C.3. We have now also included the true positive rate, the true negative rates with and without the cue, and the number of eligible questions in the revised paper (Appendix C.4). The true negative rate without the cue stays close to 1 throughout, and on cognitive bias both true negative rates stay above 0.89, so where monitorability falls, it is because the true positive rate falls. The number of eligible questions before and after training is stable on sycophancy and increases on the cognitive-bias task (for example, from 39 to 58 of 150 for Qwen3-4B L1-Low on the false-consensus cue). These extra metrics show that the stable aggregate scores reflect preserved detection, and are not caused by changes in intervention strength, metric components or question eligibility.

"Do the monitorability results hold on the same question set?"

Yes, the results hold. To check this, we took the intersection of eligible questions for each base and trained model pair, and recomputed monitorability for both models on these shared questions. The change in monitorability from the base model on the shared questions is close to the change on all questions in every setting, and every drop we initially reported remains (Appendix C.4, Table 6 in the revised paper). This is expected, as the overlap between the eligible questions of the base and trained models is also very high (Appendix C.4, Table 5).

Thank you for the additional analyses. The independent oracle evaluation, the 30-sample check, and the sensitivity analyses in Appendix E substantially address my concerns about the NSG results and the role of answer consistency.

My remaining concern is the scope of the monitorability conclusions. The second monitor and shared-question analysis strengthen the benchmark findings, but the reported TPR is adjusted for cue strength. Could you consider reporting the unadjusted flag rate on the shared eligible questions and framing the conclusion in §7 around the monitorability scores observed on the evaluated tasks? If you think the broader “mostly safe” wording is warranted, I would appreciate clarification on what evidence supports it.

Reviewer_3DGUOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

Compressing CoT may force models to cut critical reasoning steps, so that CoT no longer faithfully reflects the model’s genuine decisions and undermines audit‑capability. This paper systematically investigates whether efficient‑reasoning training inevitably degrades CoT faithfulness and monitorability.

Critical strengths
  • This paper systematically compares 3 distinct RL schemes for applying length‑pressure, while differentiating the two distinct oversight objectives of faithfulness and monitorability. It identifies that these two properties are impacted differently by compression‑oriented training, and this core insight is of substantial reference value.
Critical weaknesses
  • The paper directly treats simulatability as a proxy for faithfulness. However, simulatability is only a necessary but not sufficient condition for faithfulness. A piece of post‑hoc rationalising reasoning can yield high NSG scores and help predict model outputs, yet still fail to faithfully reflect the model’s genuine internal computation.
  • All evaluations in this work rely on external, third‑party LLMs serving as predictors and monitors. This introduces substantial judge‑model dependency risk. The paper does not perform ablation studies to verify whether the observed results are robust to swapping in alternative predictor or monitor models. It remains possible that some key conclusions are artefacts specific to this exact set of judge models; trends for faithfulness and monitorability could shift substantially given a different suite of judging LLMs.
  • All RL‑based efficient‑reasoning training is carried out on the AIME‑AMC mathematical competition dataset, whereas faithfulness and monitorability are evaluated on OOD tasks covering medical prediction and sycophancy. While the paper confirms that the ability to produce shorter CoT transfers across domains, it cannot fully disentangle whether the observed drops in faithfulness and consistency stem intrinsically from length‑pressure optimisation for efficient reasoning, or constitute side‑effects induced by RL fine‑tuning on the math domain.
  • The paper identifies counter‑intuitive cases where GLP or ThinkPrune compression of CoT even improves NSG. Nevertheless, it does not characterise the conditions under which compression boosts faithfulness: whether this arises from dataset‑specific properties, or from the model stripping verbose, redundant reasoning steps for that particular task. It lacks further analysis of such “beneficial‑compression” conditions and does not adequately reconcile these counter‑examples against its central claims.
Questions for authors

See weaknesses.

5 comments

Thank you for your review and constructive feedback. Please find our responses to the concerns below.

1: "The paper directly treats simulatability as a proxy for faithfulness…a piece of post-hoc rationalising reasoning can yield high NSG scores and help predict model outputs, yet still fail to faithfully reflect the model's genuine internal computation."

We agree that simulatability does not directly measure the model's internal computation. However, NSG as a metric is designed to score badly for post-hoc rationalisations that do not reflect the model's true reasoning. A rationalisation written for one input has to generalise to the model's behaviour on related inputs to raise NSG, so it only scores highly if this explanation accurately captures how the model makes these decisions.

For example, in Section 5.1 the base Olmo3-7B model's CoT on a Pima patient names glucose as the deciding factor and discounts genetic risk, yet its answer changes when only genetic risk changes. The CoT misleads all three predictors, and on such answer-changing cases the base models' CoTs lower predictor accuracy relative to having no CoT (Appendix H). NSG therefore penalises explanations that do not reflect what drives the model's decisions. While simulatability is a well-established approach to measuring faithfulness [1, 2] we agree that the paper should make this choice clearer. To do this we now refer to "faithfulness as measured by simulatability" in the abstract (line 024) and the introduction (line 078) of the revised paper.

2: "This introduces substantial judge-model dependency risk. The paper does not perform ablation studies to verify whether the observed results are robust to swapping in alternative predictor or monitor models…"

Regarding faithfulness as measured by NSG, we used 3 predictor models from three separate model families and observed consistent results across each of these. To test this further, we evaluate DeepseekV4-Flash as a stronger predictor for GLP on Qwen3-4B. Its change in NSG is closest to that of Qwen3-32B and follows the same trend as the other predictors (Table 1; Appendix C.2, Table 2 in the revised paper). This further highlights that our original change in NSG is robust to swapping in different predictors, including stronger models like DeepseekV4-Flash.

PredictorΔNSG
Pooled (paper)-9.5 [-12.3, -6.8]
Qwen3-32B-12.5 [-16.1, -8.8]
GPT-OSS-20B-8.2 [-12.0, -4.5]
Gemma3-27B-8.3 [-12.2, -4.1]
DeepseekV4-Flash-11.0 [-15.2, -6.8]

Table 1. Change in NSG after GLP training on Qwen3-4B for each predictor, with 95% confidence intervals.

To add robustness to our monitorability results, we re-run the evaluation using GPT-6-Luna as the monitor (replacing DeepseekV4-Flash) for both FACE-Eval and the medical cognitive-bias task. We observe the same two patterns. Sycophancy detection on FACE-Eval is preserved under compression (max drop -0.08, matching the main text), and cognitive-bias detection degrades with compression, correlating with CoT length relative to the base model. Table 2 shows a sample of the results for the cognitive-bias task, and the full results are in Appendix D of the revised paper.

ModelMethodDeepseekV4-FlashGPT-6-Luna
Qwen3-8BBase0.8680.925
Qwen3-8BL1-Low0.5470.589
Olmo3-7BBase0.7730.850
Olmo3-7BL1-Low0.5310.579
Qwen3-4BBase0.8890.984
Qwen3-4BL1-Low0.6170.634

Table 2. Cognitive-bias monitorability with the original monitor (DeepseekV4-Flash) vs GPT-6-Luna. Absolute scores change, but the same patterns can be observed when comparing base to trained models.

[1] Do Models Explain Themselves? Counterfactual Simulatability of Natural Language Explanations, 2024. Chen et al. [2] A Positive Case for Faithfulness: Explanations Help Predict Model Behavior, 2026. Mayne et al.

3: "…it cannot fully disentangle whether the observed drops in faithfulness and consistency stem intrinsically from length-pressure optimisation…or constitute side-effects induced by RL fine-tuning on the math domain."

We agree that isolating the effects of length pressure optimisation from general RL training on math data is important. To investigate this, we trained Qwen3-4B and Qwen3-8B with GRPO using only the accuracy reward, with the same data and training setup as the efficiency training methods. NSG stays the same for both of these correctness-only models (Table 3), so the NSG losses we report cannot be explained by math RL training alone.

Monitorability is also unchanged by correctness-only training (Table 4), and the correctness-only models' CoTs stay close to the base models' length, except for Qwen3-4B (3,099 to 2,524 tokens on the NSG tasks and 3,104 to 2,442 on MedQA). The Olmo3-7B correctness-only run is in progress and will be added to the camera-ready paper (Appendix F).

ModelMethodNSG (%)ΔNSG (95% CI)CoT tokens
Qwen3-8BBase29.9–1,008
Qwen3-8BCorrectness-only30.0+0.2 (-2.2, +2.6)978
Qwen3-4BBase32.7–3,099
Qwen3-4BCorrectness-only33.3+0.6 (-1.9, +3.0)2,524

Table 3. NSG and mean CoT length on the faithfulness tasks for the base models and the correctness-only models. ΔNSG is the change from the base model with its 95% paired bootstrap CI.

ModelMethodCoT tokens, FACE-EvalCoT tokens, cog. biasFACE-Eval explicitFACE-Eval implicitCog. bias (medical)
Qwen3-8BBase8081,3310.650.350.87
Qwen3-8BCorrectness-only8001,2760.650.390.85
Qwen3-4BBase9523,1040.700.570.89
Qwen3-4BCorrectness-only8502,4420.720.570.89

Table 4. Monitorability (g-mean²) and mean CoT length for the base models and the correctness-only models, using the same monitor as the main results.

4: "The paper identifies counter-intuitive cases where GLP or ThinkPrune compression of CoT even improves NSG…"

We would like to clarify that the central claim of this paper is that efficient reasoning training does not always degrade faithfulness and monitorability. These cases of "beneficial compression" are further evidence for this claim. We would also like to highlight that increases in faithfulness due to efficient reasoning training are not a major part of our conclusions. We only find one case which shows a significant increase: GLP on Qwen3-8B, where the CoT shortens from 1,008 to 349 tokens and NSG goes from 29.85% to 33.12%. Here, significance means the 95% paired bootstrap confidence interval on the change in NSG excludes zero. Rather than needing to be reconciled with our central claim, we believe this finding provides further support for it.

Dear Reviewer 3DGU,

Thank you again for your time and constructive feedback. We hope our response and extra experiments have addressed your concerns. As the discussion period is coming to an end, we would kindly invite you to share any updated thoughts.

Reviewer_rzH3OpenReview ↗
Rating
3
Confidence
3
Informativeness
3
Presentation
2
Soundness
2
Read review
Paper summary

This paper studies how training models to produce shorter chains of thought affects uses of CoT. The authors train three reasoning models with ThinkPrune, L1, and a group-relative length penalty, and evaluate normalized simulatability gain (NSG) and intervention-based monitorability. NSG decreases in most settings, although some methods substantially shorten CoT without reducing it. Monitorability is more robust on the tested tasks. The paper further argues that most faithfulness losses arise from less consistent model answers rather than less informative CoT.

Critical strengths
  • Separating these two uses of CoT is useful. An explanation that helps predict decisions on related inputs and a trace that exposes a particular biasing cue need not contain the same information. The paper makes this distinction concrete instead of treating it as a single score.

  • Some results are practically encouraging. Qwen3-8B with GLP reduces average CoT length from 1,008 to 349 tokens on the faithfulness tasks while increasing NSG from 29.85% to 33.12%. Its MATH-500 accuracy changes only from 0.92 to 0.91. These results support the narrower claim that substantial compression need not always harm the measured oversight properties. Additionally, several evaluation choices are thoughtful. The paper uses three predictors, clustered bootstrap intervals for NSG, and disjoint samples for selecting eligible monitorability questions and scoring them.

Critical weaknesses
  • I am not yet convinced that inconsistency is the main cause of the faithfulness loss. Table 3's attribution assumes that the trained model retains the base model's fraction of its NSG upper bound. This is a useful descriptive calculation, and the assumption is stated, but it does not establish what caused the observed change. The bound also depends on no-CoT predictor accuracy, not only reference-model consistency.

  • The experiments do not isolate length pressure from the rest of the RL update. The main comparison is between a base model and models receiving math GRPO training with length pressure. A correctness-only GRPO control with the same data and update budget is missing. A base model with only the L1 budget prompt would also help separate prompting from training effects.

Questions for authors

See weaknesses.

3 comments

Thank you for your positive feedback and constructive comments. We are pleased that you found the work informative. Please find our responses to the concerns below.

  1. "I am not yet convinced that inconsistency is the main cause of the faithfulness loss….the decomposition assumes that trained models retain the base model's fraction of the attainable NSG ceiling…it does not establish what caused the observed change."

We agree that this decomposition is a useful descriptive calculation, but also that it is difficult to completely decompose exactly what causes the drop in NSG without an assumption. We cannot claim that inconsistency causes the loss, and we have revised the abstract (line 024), contributions (line 085), Figure 1 caption (line 069), Section 5.1 (line 313) and the conclusion (line 481) to state that faithfulness losses track falling consistency rather than being caused by it.

What we do observe directly is that consistency falls in 13 of the 15 settings, so the share of counterfactuals that no predictor could answer correctly increases after efficiency training. Our main point here is that efficiency training can reduce faithfulness as measured by simulatability through changes in the model's answers, not only through changes in what its CoT says.

  1. "The bound also depends on no-CoT predictor accuracy, not only reference-model consistency."

We agree the bound depends on both. However, when no-CoT accuracy falls, the upper bound rises rather than falls, so changes in no-CoT accuracy cannot explain the fall in the bound. To check this directly, we split each change in the bound into a part from consistency and a part from no-CoT accuracy (Appendix E, Table 9 in the revised paper). In every setting with a significant NSG drop, the no-CoT part either raises the bound (Qwen models) or barely changes it (Olmo3-7B, -0.9 to -0.3 points). The fall in the upper bound therefore comes from the fall in consistency.

  1. "The experiments do not isolate length pressure from the rest of the RL update…"

We agree this is an important confounder. We have therefore trained Qwen3-4B and Qwen3-8B with GRPO using only the accuracy reward, with the same data and training setup as the efficiency training methods. NSG stays the same for both correctness-only models (Table 1), so the NSG losses we report cannot be explained by maths RL training alone.

Following your suggestion, we also evaluated the base models with only the L1-Medium budget prompt. The prompt alone does not significantly change NSG on either model. On Qwen3-4B it changes NSG far less than L1-Medium training does (-0.9 vs -7.8 points). On Qwen3-8B the gap is smaller (-2.2 vs -3.5 points). Monitorability is also unchanged by correctness-only training (Table 2), and the correctness-only models' CoTs stay close to the base models' length, except for Qwen3-4B (3,099 to 2,524 tokens on the NSG tasks and 3,104 to 2,442 on MedQA). The Olmo3-7B correctness-only training run is in progress and will be added to the camera-ready paper (Appendix F).

ModelMethodNSG (%)ΔNSG (95% CI)CoT tokens
Qwen3-8BBase29.9–1,008
Qwen3-8BCorrectness-only30.0+0.2 (-2.2, +2.6)978
Qwen3-8BL1-Medium prompt only27.6-2.2 (-4.6, +0.1)1,203
Qwen3-4BBase32.7–3,099
Qwen3-4BCorrectness-only33.3+0.6 (-1.9, +3.0)2,524
Qwen3-4BL1-Medium prompt only31.8-0.9 (-3.5, +1.8)2,912

Table 1. NSG and mean CoT length on the faithfulness tasks for the base models, the correctness-only models and the base models with only the L1-Medium prompt. ΔNSG is the change from the base model with its 95% paired bootstrap CI.

ModelMethodCoT tokens, FACE-EvalCoT tokens, cog. biasFACE-Eval explicitFACE-Eval implicitCog. bias (medical)
Qwen3-8BBase8081,3310.650.350.87
Qwen3-8BCorrectness-only8001,2760.650.390.85
Qwen3-4BBase9523,1040.700.570.89
Qwen3-4BCorrectness-only8502,4420.720.570.89

Table 2. Monitorability (g-mean²) and mean CoT length for the base models and the correctness-only models, using the same monitor as the main results.

Dear Reviewer rzH3,

Thank you again for your time and constructive feedback. We hope our response and extra experiments have addressed your concerns. As the discussion period is coming to an end, we would kindly invite you to share any updated thoughts.

Thanks for your detailed response. I will retain my score of 3.

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

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