acceptodds
Under review as a conference paper at ICLR 2027

Hard or Stuck? Viability-Conditioned Steering for Budgeted Reasoning

Abstract

Practical deployments of reasoning models impose token budgets to bound inference cost, but hard limits can truncate trajectories before they reach an answer. Existing control mechanisms rely on fixed schedules or predicted reasoning lengths, frequently failing to distinguish genuinely difficult questions from off-track reasoning. Consequently, they may unnecessarily intervene in trajectories that would otherwise complete naturally. This motivates trajectory-aware intervention adapting timing and strength to individual rollouts. We show that a probe over intermediate hidden states predicts whether a trajectory will finish within budget well before the limit is reached, beyond what generation position alone reveals. Its early prediction is strongly associated with question difficulty and baseline cap propensity, while subsequent increases in predicted cap risk provide a trajectory-relative signal of worsening completion prospects. Motivated by this observation, we introduce Viability-Conditioned Steering (VCS). VCS applies sparse hidden-state updates whose strength adapts online to the increase in cap risk relative to each trajectory’s initial level and to deadline pressure as the remaining budget shrinks. The update direction is estimated offline from matched hidden states of finished and capped rollouts. Across diverse reasoning models and benchmarks, VCS outperforms uncontrolled decoding in all 16 settings, boosting accuracy by 3.8–21.6 percentage points, while cutting token consumption by 13.6–34.8% and lowering cap rates by 68.0–92.6%.

Primary area:
foundation or frontier models, including LLMs
Keywords:
efficient reasoning, large language models, activation steering

Reviews

Among:
Shape:
1234this paper, Top 4%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.33 over 3 reviews, above 96% of the others.
Reviewer_GfGWOpenReview ↗
Rating
4(+1)
Confidence
3
Informativeness
3
Presentation
3
Soundness
2
Read review
Paper summary

The paper proposes VCS, which steers reasoning models using their predicted risk of exhausting a token budget. Intervention strength depends on how much that risk has increased from its initial value, together with deadline pressure. A fixed completion direction is learned from finished and capped trajectories. Experiments show improved accuracy and lower token use across several models and reasoning tasks.

Critical strengths

I find the central idea sensible: a difficult question should not automatically trigger stronger intervention, and completion prospects provide a useful signal without requiring correctness labels. The improvements across models and the transfer from mathematics to code give this idea practical weight. The paper also provides substantial analysis and is reasonably candid about what its diagnostics do and do not establish.

Critical weaknesses

1. Predicting capping does not establish the “hard or stuck” distinction

The probe predicts whether a trajectory will finish, but this does not tell us why it may fail to finish. Risk can rise because useful reasoning needs more time, not necessarily because the model has gone off track. Figure 4 selects trajectories by their eventual outcomes, and Appendix A.4 finds that risk increments and current risk give similar within-question rankings. I therefore find the evidence for predicting budget exhaustion stronger than the evidence for separating difficulty from deterioration. The paper should keep that distinction clear in its central argument.

2. The methodological advance needs sharper positioning

Activation steering and adaptive control from latent verifiers are already explored by SEAL and ATLAS. What seems distinctive here is the use of completion risk relative to an initial reference. That is a potentially useful contribution, but it is narrower than a new adaptive reasoning framework. I would like the paper to explain more directly what this reference enables that existing feedback signals do not. The claim that correctness labels are unnecessary is supported; the case that this is a better basis for control is less settled.

3. The derivation assumes the key design choice

Section 4 chooses the intervention cost so that the initial viability is exactly the point of indifference. This recovers the proposed rule, but does not explain why the initial prediction is the right reference for deciding when intervention is worthwhile. A trajectory that starts with poor prospects and stays there receives no risk-driven correction, leaving the deadline term to act. Conversely, the normalization amplifies the same risk increase more when initial risk is high, as Appendix A.3 acknowledges. These are meaningful consequences of the design, and I would like a clearer argument for why they match the stated goal of protecting difficult but productive reasoning.

4. The experiments support VCS more clearly than its distinctive advantage

The gains over uncontrolled decoding are convincing, and the strength sweeps are useful. However, the risk-level comparison changes both the reference and the deadline term, so it does not cleanly establish what the initial reference adds. The main comparisons also omit a close adaptive steering method such as ATLAS. I do not think the paper needs a long list of additional baselines, but a focused comparison that separates the value of this feedback rule from adaptive steering more generally would make the methodological contribution much more convincing.

Questions for authors
  1. Clarification: Why should initial viability be the point at which intervention becomes worthwhile? Section 4 builds this choice into the cost model, but I am less clear on why it is appropriate for trajectories that start with poor completion prospects.

  2. Evidence: What is the strongest evidence that relative risk identifies deterioration beyond what current risk and deadline pressure already capture? Appendix A.4 finds similar within-question rankings, while the comparison changes both the risk reference and the deadline term.

4 comments
AuthorsOpenReview ↗

Author Response to Reviewer GfGW (Part 1/2)

We thank the reviewer for recognizing the practical value of viability-based feedback and for identifying where the methodological claims need clarification. Next, we try to address each of the concerns.

Q$_1$&W$_3$: Why use initial viability as reference

We agree that the derivation does not independently establish initial viability as the optimal intervention threshold. The reference is a design choice: we seek to avoid increasing risk-driven intervention solely because a trajectory begins with poor completion prospects. Section 4 expresses this preference through the intervention-cost model. Using the initial state as the reference makes the risk-driven term zero at initialization and positive only when predicted viability falls below its initial level.

A poor start that stays on forecast does not by itself indicate that reasoning has deteriorated. Such a trajectory receives only the deadline-driven component (about 0.1 early, approaching 1 at the budget). The normalization, (ρt−ρ0)/(1−ρ0)=1−Vt/V0(\rho_t-\rho_0)/(1-\rho_0)=1-V_t/V_0, measures the fractional loss of initial predicted viability. Thus, high initial risk alone does not activate the relative-risk term, although a given absolute risk increase produces a larger response when initial viability is lower.

The controlled ablation supports this choice. On the 181 OlympiadBench questions with high initial risk and no risk increase by 2,048 tokens under CoT, VCS achieves 48.6% accuracy versus 43.1% for the current-risk controller at the same steering strength, with the deadline schedule retained in both.

Q$_2$&W$_1$: Isolate trajectory-relative risk

The strongest evidence that relative risk captures what current risk and deadline pressure do not is a controlled comparison that changes only the risk reference: under the same deadline schedule, a gate driven by the rise is more accurate at matched cost than a gate driven by current risk (Please see Figure 6 and related discussion in Section 5.2).

Current risk cannot tell a hard question from a rollout that has fallen behind. A high $\rho_t$ can mean either, and deadline pressure depends only on position; the rise above $\rho_0$ keeps only what has changed since the rollout began. A current-risk gate therefore pushes hard questions from the first control point. On the 181 OlympiadBench questions that start above the median risk and show no rise by 2,048 tokens, a current-risk gate of the same strength ends them about 2,300 tokens sooner at 43.1% accuracy, against 48.6% for ours, and weaker settings leave 54–66% of them capped, against 16%.

The within-question tie and the outcome-selected groups do not change this. Within a question $\rho_0$ is nearly constant, so the rise and current risk differ only by a shift and must rank alike. Those groups are selected by outcome, so we add a grouping that does not: among Qwen3-4B continuations in the top third by $\rho_0$ still running at 4096 tokens, 33% of those whose risk has fallen go on to cap, against 88% of those whose risk has risen.

Our claim is that initial risk provides a reference associated with the question's baseline completion difficulty, while subsequent changes capture how the rollout's completion prospects evolve.

We agree that the probe forecasts budget exhaustion and does not diagnose why risk rises, and we do not claim that the rise predicts capping better than $\rho_t$. The introduction now defines "hard" as the risk a question starts with and "stuck" as risk that has risen above it. The diagnosis section now explains the within-question tie and points to a new appendix (Appendix A.4, Figure 9) grouping that does not select on outcome.

(Please see part 2 of our response.)

AuthorsOpenReview ↗

Author Response to Reviewer GfGW (Part 2/2)

W$_2$&W$_4$: Distinctiveness and empirical justification of trajectory-relative feedback

Measuring completion risk against each trajectory's own starting level lets the controller hold back on a question that is merely hard and act on a rollout that has lost ground since it began, which neither SEAL's fixed vector nor ATLAS's step-quality verifier does. Both comparisons the reviewer asks for support this.

1. No existing feedback signal separates a hard question from a rollout that is falling behind. SEAL's vector has no feedback, and ATLAS's verifier scores the current step without seeing the budget. Current risk sees the budget but also carries the question's difficulty: $\rho_0$ tracks the benchmarks' difficulty labels, so a gate on $\rho_t$ pushes hard questions from the first control point. Measured against $\rho_0$, the risk term is zero until risk rises above where the rollout started. We will clarify how VCS differs from SEAL and ATLAS in the Related Work section.

2. Changing only the reference, with the deadline term kept, lowers accuracy. We ran the ablation the reviewer asks for on Qwen3-4B. At the closest token cost, this arm reaches 87.0% on MATH-500 and 54.0% on OlympiadBench, against 89.8% and 59.2% for ours, and uses 360 and 761 more tokens. Please see Figure 6 for more details.

3. ATLAS matches our accuracy on R1-1.5B but leaves far more trajectories capped. At each reasoning step, ATLAS's verifier, trained on step-quality scores, chooses which of three steering vectors to apply. Its code is not released, so we reimplemented it on R1-1.5B, a model from its paper, in its decoding setting. Each cell is accuracy (%) / capped (%) / mean tokens.

MATH-500OlympiadBenchLiveCodeBench
SEAL (Table 1)77.8 / 14.0 / 276338.0 / 41.8 / 504722.3 / 63.2 / 6284
ATLAS (new)78.4 / 13.6 / 275538.1 / 40.4 / 500722.5 / 61.1 / 6206
Ours (Table 1)78.4 / 5.8 / 273539.3 / 9.3 / 412823.1 / 11.0 / 4530

ATLAS tracks SEAL because its verifier, although accurate, picks the execution vector at over 96% of step boundaries, and that vector coincides with SEAL's direction. VCS adapts steering strength to rising cap risk and the remaining budget, matching or exceeding ATLAS’s accuracy while lowering cap rates and mean token counts.

The related work now states how the trajectory-relative reference differs from SEAL and ATLAS, and the accuracy–token figure (Figure 6) includes the current-risk + deadline baseline.

We hope the revisions address the remaining concerns, and that the revised version is now in a position to merit your continued support. If there is any other confusion you would like us to clarify or other improvements you would like us to implement, please let us know – we would be glad to do so.

Thank you for the clear reply. Your reply has addressed my main concerns, so I’m raising my score from 3 to 4.

Under the same deadline schedule, the authors’ additional comparison directly addressed my main concern about the method. VCS improves accuracy while using fewer tokens. The comparison with ATLAS also shows the method’s effectiveness and efficiency. I also read the other reviews and the authors’ responses, and I appreciate the effort the authors put into addressing them. Some raised concerns similar to mine, and the additional evidence makes me more satisfied with the response.

But I am still not fully convinced that a rise in predicted risk can distinguish a model that is stuck from one that needs more time. The paper’s forced-answer experiments only show that some trajectories give wrong answers at a few specified points, which could still mean that the model needs to continue reasoning.

Given that the authors have narrowed the relevant claims, and the effectiveness of the paper, I think that asking for a full proof of this distinction would go beyond the scope of a single paper. This is a remaining thought I have about the paper, it should not prevent me from raising my score.

Thank you for taking the time to revisit the paper and read our responses to the other reviewers. We really appreciate your careful reading, and we’re glad the comparison under the same deadline schedule addressed your main concern about the method.

We agree that it remains an open question whether a rise in predicted cap risk can reliably distinguish a model that is stuck from one that needs more time. As you point out, a model that answers incorrectly when forced to stop may still be making progress toward a correct solution. Your comment helped us clarify the scope of our claim. In future work, we would like to explore how to tell which trajectories would benefit from additional reasoning time when predicted cap risk rises. Thanks again!

Reviewer_f9z2OpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper addresses reasoning trajectories that reach a token budget without naturally terminating. It trains a hidden-state viability probe to predict completion within the remaining budget and proposes Viability-Conditioned Steering (VCS), which scales an offline completion direction using trajectory-relative cap risk and deadline pressure. Across four models and four benchmarks, VCS improves accuracy and reduces token use and cap rates relative to uncontrolled chain-of-thought decoding. The paper also evaluates several budget-control baselines and includes ablations and robustness experiments.

Critical strengths
  1. Interesting problem formulation. The paper highlights that a uniform budget or fixed steering schedule may treat genuinely hard questions and deteriorating trajectories alike. Its position-matched probe analysis provides evidence that hidden states contain completion-related information beyond token position alone.
  2. Reasonably broad empirical evaluation. The main experiments cover four models and four benchmarks, with useful comparisons to Budget Forcing, Budget Guidance, and SEAL. The budget/strength sweeps, learned-stopping comparison, and transfer from mathematics to code are valuable additions.
Critical weaknesses

Weaknesses and Questions

W1. Natural termination is not the same as reasoning sufficiency

The viability label indicates whether the base-policy rollout emits EOS within the budget, not whether an intermediate state already contains enough reasoning to produce a correct final answer. A capped trajectory could still yield a correct answer if prompted to stop thinking earlier, so predicting capping does not by itself establish the paper's proposed distinction between "hard" and "stuck" reasoning (Section 4).

Q1. Among base-policy trajectories labeled capped, what fraction can produce a correct final answer if forced to answer at intermediate points such as 2K, 4K, or 6K tokens? Could the paper distinguish insufficient reasoning from sufficient-but-nonterminating reasoning and examine whether viability predicts these cases differently? The existing learned-stopping comparison (Figure 6) is useful but does not directly quantify this distinction.

W2. The incremental value of the more complex controller is not fully established

VCS requires model-specific rollout collection, training two probes, and estimating a completion direction, whereas Budget Forcing and Budget Prompt need no such training. Although VCS offers a useful accuracy–token trade-off, simpler baselines remain competitive in some settings; moreover, the risk-level ablation removes deadline pressure as well as the trajectory-relative reference, limiting attribution of the latter component's benefit (Table 7).

Q2. With the same direction, repetition guard, and deadline schedule, how does deadline + current risk compare with deadline + trajectory-relative risk across matched accuracy–token operating points? Can the paper better quantify the incremental gains over tuned training-free controls, accounting for the per-model offline fitting requirement? Figure 11 already provides useful parameter sweeps, but does not isolate this particular comparison.

W3. Real latency evidence is much narrower than the token-saving results

Most efficiency results measure generated tokens rather than wall-clock latency. The only direct timing experiment (Table 12) uses 20 MATH-500 questions, Qwen3-4B, batch size 1, and a single RTX 3090: latency decreases by 7.2% relative to greedy decoding, while decoding throughput decreases by 2.7%; no comparable timing results are reported against the other budget-control baselines.

Q3. Could the authors report end-to-end latency and throughput against Budget Forcing and Budget Guidance on identical hardware and inference configurations, ideally at matched answer quality? How do probe/steering overheads behave under batching or concurrent requests? This would clarify whether the reported token savings translate into practical serving gains.

W4. The deployment scope of the fixed-budget setting needs clarification

The main experiments use an 8K-token cap, which produces very high baseline cap rates on challenging tasks (Figure 1); online reasoning services may instead allow substantially larger or variable budgets. The paper does test 4K–16K budgets (Figure 7a), but refits both probes and the direction at each budget, and the accuracy gains narrow at 16K even as token savings remain substantial.

Q4. Which real deployment settings motivate the default 8K cap, and how should VCS be used when the budget is 32K or changes across requests? Can a single fitted probe and direction transfer across budgets without refitting? Results on more permissive or dynamic budgets, preferably including latency, would help establish applicability beyond the default setting.

Questions for authors

See Weakness

6 comments
AuthorsOpenReview ↗

Author Reponse to Reviewer f9z2 (Part 1/3)

We thank the reviewer for the constructive comments and the detailed reading of our work. We have addressed each point below and would be glad to discuss any of them further.

Q$_1$: Forced-answer sufficiency

Capped base-policy trajectories mix reasoning that can already answer with reasoning that cannot, and a forced stop helps only the first kind, and only when it lands at the right point for that trajectory. Our controller recovers most of the first kind and part of the second, and is more accurate than a forced stop at any fixed point. Specifically, viability flags both kinds as at risk well before the cap and reads the insufficient ones as riskier. On Qwen3-4B, a forced stop at 2K, 4K or 6K tokens answers 20–61% of capped trajectories correctly, depending on the point and the benchmark, and 35–64% are answered correctly at none of the three. Our controller answers 34–65% of all capped questions correctly, against 31–61% for the best fixed stop.

1. A forced stop rescues only part of the capped trajectories, and the right stopping point differs for each. We take the CoT trajectories that hit the 8k-token cap and force each one to answer by inserting the Budget Forcing cue (</think> followed by "Final Answer:") at exactly 2K, 4K or 6K tokens. A capped trajectory is sufficient but nonterminating if any forced answer is correct, and insufficient otherwise under the tested forced stops.

Capped CoT trajectories (%)MATH-500OlympiadBenchLiveCodeBench
Correct if forced at 2K / 4K / 6K39.8 / 55.4 / 61.419.9 / 26.9 / 30.638.3 / 38.3 / 41.5
Sufficient/insufficient65.1 / 34.935.7 / 64.357.4 / 42.6
CoT correct25.310.11.1
Ours correct65.133.750.5
on sufficient75.969.875.9
on insufficient44.813.616.2

CoT is credited when a correct answer can be extracted from its truncated output. No single stopping point serves both kinds: stopping at 2K is too early for a third to almost half of the sufficient trajectories, which cannot yet answer there.

2. Viability provides the per-trajectory signal that a fixed stop lacks. At each forcing point, we compare $\rho_t$ across capped trajectories whose forced answer there is correct, capped trajectories whose forced answer there is wrong, and trajectories that later finish on their own.

Forced atMean $\rho_t$: finishes laterMean $\rho_t$: capped, forced answer correctMean $\rho_t$: capped, forced answer wrongAUROC, wrong vs. correct
MATH-5002K0.100.440.690.72
4K0.190.600.780.71
6K0.360.740.850.69
OlympiadBench2K0.190.720.780.58
4K0.260.760.900.71
6K0.320.860.960.74

Viability separates trajectories that will finish from both capped groups thousands of tokens before the cap, so the controller can act on the trajectories that need it and leave the others nearly untouched, whereas a fixed stop cuts every trajectory at the same point.

3. Steering recovers more than stopping.

  • It is more accurate than any fixed stop, without choosing a deadline. Over all capped questions, it is 3.6, 3.0 and 9.0 points above the 6K stop while using fewer tokens, and 12–25 points above the 2K stop.
  • It recovers trajectories that stopping cannot. Part of the insufficient trajectories, which no stop at 2K, 4K or 6K answers correctly, end correctly under steering (hatched in revised Figure 7(e)): steering changes how a trajectory continues, not only where it ends.

Section 5.2 now reports this analysis, with Figure 7(e) illustrated. Appendix D.10 also gives both tables.

(Please see part 2 of our response.)

AuthorsOpenReview ↗

Author Response to Reviewer f9z2 (Part 2/3)

Q$_2$: Relative-risk ablation

With the direction, repetition guard and deadline schedule held fixed, changing only the risk term from current risk to the trajectory-relative increment gives a more accurate controller at matched token cost, and no strength of the current-risk gate that we tried reaches its accuracy. The current-risk gate faces a trade-off that the relative reference avoids: when strong, it cuts hard questions short, and when weak, it leaves them capped. On Qwen3-4B, ours is 2.8 and 5.2 points more accurate than the current-risk point of closest cost on MATH-500 and OlympiadBench, while using 360 and 761 fewer tokens.

We swept the current-risk gate over $\lambda\in{0.2, 0.1, 0.05}$ to trace its accuracy–token curve. Each cell is accuracy (%) @ mean tokens.

Current risk $\lambda=0.2$Current risk $\lambda=0.1$Current risk $\lambda=0.05$Ours ($\lambda=0.2$, Table 1)Δ at matched cost
MATH-50087.2 @ 311887.0 @ 387687.0 @ 396689.8 @ 3516+2.8, 360 fewer tokens
OlympiadBench53.9 @ 397154.0 @ 590350.3 @ 616159.2 @ 5142+5.2, 761 fewer tokens
LiveCodeBench70.5 @ 277974.2 @ 482565.6 @ 519076.5 @ 4864+2.3, same tokens

1. No strength of the current-risk gate reaches our accuracy. Ours is more accurate than all three current-risk points on all three benchmarks. Weakening the current-risk gate does not close the gap.

2. At matched cost ours is more accurate. On MATH-500 and OlympiadBench our operating point lies between the $\lambda=0.2$ and $\lambda=0.1$ current-risk points in cost and is more accurate than both. Against the closer one it gains 2.8 and 5.2 points with 360 and 761 fewer tokens.

3. The current-risk gate must choose between cutting hard questions short and leaving them capped. Questions that start hard and stay on course show the choice: the 181 OlympiadBench questions with above-median initial risk $\rho_0$ whose risk has not risen by 2,048 tokens under CoT.

OlympiadBench, high initial risk, no riseAccuracyTokensCappedΔ accuracy vs. ours
Current risk, $\lambda=0.2$43.1%39616.6%−5.5
Current risk, $\lambda=0.1$39.2%714953.6%−9.4
Current risk, $\lambda=0.05$32.6%746366.3%−16.0
Ours48.6%629016.0%

We have added Figure 6 accordingly in Section 5.2 to discuss this ablation.

Q$_3$: End-to-end latency

Our method achieves higher accuracy with lower measured wall-clock time than CoT on both benchmarks at batch sizes 1 and 4. The accuracy gains are 6.6 percentage points on MATH-500 and 17.6 on LiveCodeBench.

We use Qwen3-4B, one RTX 3090 per run, greedy decoding, and static batches of 1 and 4. Methods are timed on the same 100 problems per benchmark, with each result normalized to CoT measured on the same machine.

MethodMATH-500LiveCodeBench
Batch 1Batch 4Batch 1Batch 4
CoT1.001.001.001.00
Budget Forcing (deadline 7680)1.000.991.031.00
Budget Forcing (deadline 6144)0.930.820.960.90
Budget Guidance0.710.600.710.78
Ours0.870.840.970.99

Times are relative to CoT. For this fixed workload, problem throughput is the reciprocal of the time ratio.

Quality and speed. Compared with Budget Forcing at its closest-accuracy setting (deadline 6144), ours achieves higher reported accuracy on both benchmarks. At batch 1, ours is faster on MATH-500 and comparable in time on LiveCodeBench. Budget Guidance's best accuracy across the tested budgets remains 2.6 and 7.2 percentage points below ours.

Probe overhead can be reduced further. A decode-pass variant uses three additional layers per probe refresh and avoids a second KV cache. Microbenchmarks on MATH-500 and OlympiadBench show about 3–5% per-step overhead relative to CoT at batch sizes 1 and 4, and 10–12% at batch 32.

We have added the timing comparisons to the computational-efficiency appendix D.9.

(Please see part 3 of our response.)

AuthorsOpenReview ↗

Author Response to Reviewer f9z2 (Part 3/3)

Q$_4$: Cross-budget transfer

A single probe and direction fitted at 8K transfer to other budgets without refitting, keeping the controller's accuracy gain and token savings over CoT at both a tighter and a larger budget. On R1-1.5B, the transferred 8K fit is 11.4 and 13.6 points more accurate than CoT at 4K and 6.6 and 8.5 points at 16K (MATH-500 and OlympiadBench), with 18–19% and 48–50% fewer tokens.

A changing budget needs no extra machinery. The budget enters VCS only through the position features of the two probes, so at budget $B$ we keep the 8K probes and direction and evaluate the probes at position $t\cdot 8192/B$. Each request's budget sets only its own position scale, so requests with different budgets share the same fit. The table compares this transfer with probes and directions refitted at each budget. Each cell is accuracy (%) @ mean tokens (cap rate).

BudgetBenchmarkCoTRefit at $B$8K fit, transferredΔ (transfer − refit)
4KMATH-50065.6 @ 2621 (36.2)78.4 @ 2116 (10.8)77.0 @ 2155 (11.4)−1.4
4KOlympiadBench25.7 @ 3596 (72.1)38.0 @ 2969 (26.1)39.3 @ 2895 (23.7)+1.3
16KMATH-50072.8 @ 5960 (25.4)75.6 @ 3386 (1.4)79.4 @ 3117 (1.0)+3.8
16KOlympiadBench31.6 @ 11489 (62.5)36.6 @ 5791 (5.9)40.1 @ 5743 (9.1)+3.4

We have added Figure 13 to illustrate this.

We would like to thank the reviewer again for such a thorough review, which has substantially improved the quality of our paper. We have tried our best to address every remaining concern in this response. Should there be any further changes you would like to see, or anything we can clarify, please do not hesitate to let us know.

Reviewer_3NM9OpenReview ↗
Rating
3
Confidence
4(+1)
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper introduces Viability-Conditioned Steering (VCS), which addresses budgeted reasoning. Existing inference-time methods include force-stopping the reasoning at a budget, applying fixed strength at boundaries, or predicting the distribution of the remaining output length and reweighting the token probabilities to favor tokens likely to finish within budget. The proposed inference-time method applies state updates to a band of layers at the newline position in the reasoning segment with 2 factors: 1) adaptive strength: determined and adapted online by calculating 'viability', the probability of completion within the remaining budget (this is different from calculating correctness, i.e., whether its eventual answer will be correct) relative to the model's initial reading of the problem. This objective balances necessary intervention against unnecessary disruptions. The method also adds a remaining budget nudge for the case where the viability measure remains stable. 2) fixed direction: direction of the update is estimated offline once from hidden states of completed and capped trajectories, matched by generation position. The probes and the directions are fitted once per model on MATH and reused across different datasets. The proposed method reports increased accuracy while reducing token use and cap rates. The paper also includes informative ablations and experiments.

Critical strengths
  • The VCS formulation is intuitive, and its components are well justified. Using completion rather than correctness as the control target is supported by the diagnosis and the ablations. Also, grounding viability in each trajectory's own initial difficulty (risk) makes the updates controlled so that healthy trajectories are not given the update.
  • The diagnosis section before the method is helpful as it motivates the entire formulation.
  • The generalizability of the probes and the direction from MATH to coding and QA tasks indicate that the learned signals are task-agnostic. The experiments and the ablations included are well-defined and study important pieces of the formulation.
Critical weaknesses
  • The proposed method is motivated as an inference-time method, but it still involves training different probes and directions. The method is only compared against inference-based methods. Some training-based methods are covered in related work but are not included in the main experiments, so some comparisons with training-based methods would be helpful.
  • Most of the components are justified with ablations, but the 4-layer band is not ablated. It is currently only justified by a citation, and the paper is missing a sweep over which layer or how many layers.
  • The paper acknowledges that the viability probe goes OOD once the steering starts, but an experiment measuring reading drift on steered trajectories would be helpful.
Questions for authors
  • What happens when the fixed offline direction version is replaced with a random vector of the same norm?
  • How often is the update actually applied? That is, what fraction of control points have gate > 0?
  • What is the offline cost of fitting the probes and directions?
4 comments
AuthorsOpenReview ↗

Author Response to Reviewer 3NM9 (Part1/2)

We thank the reviewer for the positive assessment of VCS and for the constructive suggestions. Below are our clarifications to all the questions. We hope that the responses can address the reviewer’s concerns, and we truly welcome further discussion.

Q$_1$: Random-direction baseline

A random direction of the same norm behaves like no intervention. With the deployed controller left unchanged and only the direction replaced, accuracy, mean length and cap rate stay at CoT level on all four benchmarks. Under the same gate and the same update norm, the learned direction $d_l$ is 5–20 points more accurate than the random one and caps 12–52 points less often. The gain therefore comes from the direction itself, not from perturbing the residual stream at this magnitude.

Setup. Qwen3-4B with the Table 1 configuration. For each steered layer we draw one isotropic Gaussian vector (seed 0), fix it across all questions, and normalise it, so the update has exactly the same norm as with $d_l$ at every control point.

Benchmark (acc / cap % / tokens)Ours (dld_l)Random, same normCoT, same guardRandom − CoT (acc)Ours − Random (acc)
MATH-50089.8 / 3.4 / 351684.8 / 15.4 / 417183.2 / 16.0 / 4158+1.6+5.0
AIME 2025+202643.3 / 23.3 / 635823.3 / 75.0 / 762028.3 / 75.0 / 7597−5.0+20.0
OlympiadBench59.2 / 8.8 / 514249.3 / 45.1 / 624149.6 / 45.1 / 6253−0.3+9.9
LiveCodeBench76.5 / 12.9 / 486459.1 / 35.2 / 543059.3 / 36.6 / 5431−0.2+17.4

We have added Table 9 accordingly to the appendix.

Q$_2$: Intervention frequency

The update is applied at almost every control point, because the gate is positive by design. It sets how strongly to steer, not whether to steer. On Qwen3-4B, gt>0g_t>0 at 100% of control points and the update is applied at 98% of them; the remaining 2% come after the repetition guard has switched steering off.

We logged the gate at every step of the deployed Qwen3-4B controller. Control points are the newlines in the thinking segment.

MATH-500AIMEOlympiadBenchLiveCodeBench
Control points with update applied98.2%98.7%97.8%97.9%
Control points with relative increment $>0$35.4%45.0%43.7%12.8%
Control points with $g_t\ge 0.5$23.1%42.2%35.7%19.9%
Updated / all generated tokens2.7%3.7%3.4%4.1%

The trajectory-specific term acts at a minority of control points. The relative increment is positive at 35–45% of control points on the mathematics benchmarks and at 13% on LiveCodeBench. Elsewhere the trajectory receives only the schedule.

Applying the update everywhere is not what produces the gain. Steering at full strength at every control point (No gate) is 10.6–29.3 points less accurate than ours on every benchmark, and less accurate than unsteered CoT on three of the four. The schedule alone (Deadline) leaves more trajectories capped on every benchmark and is 1.4–3.5 points less accurate. We have added Table 10 to the appendix and state in Section 4 that $g_t>0$ at every control point by construction.

Q$_3$ & W$_1$: Offline fitting cost

Fitting the probe and directions takes 0.35–1.05 GPU-hours per model (1.5B–14B) on a single H200, or 1.1–5.05 GPU-hours if rollout sampling is included. This is done once per model with the LLM frozen, and the same fit is reused across all benchmarks and budgets.

The pipeline has three steps: (i) sample 6 rollouts for each of 1,200 MATH training prompts (7,200 rollouts, 8k-token cap); (ii) run one forward pass per rollout to save the hidden states at newline tokens; (iii) fit the MLP probe and the difference-of-means directions.

R1-Distill-1.5BQwen3-4BQwen3-8BR1-Distill-14B
(i) Rollout sampling (vLLM)0.61.22.24
(ii) Hidden-state extraction0.450.30.71.0
(iii) Probe + direction fitting0.050.050.050.05
Total, (i)–(iii)1.11.552.955.05

Comparison with other methods:

  • Inference-time baselines need a similar offline step. SEAL builds its steering vector from sampled rollouts with one forward pass and a difference of means, i.e., our steps (i)–(ii) without the probe. Budget Guidance trains a 320M-parameter length predictor, which took at least 2.4 GPU-hours on Qwen3-4B, against 0.35 for our steps (ii)–(iii).
  • Training-based methods cost much more, because they update all LLM weights with reinforcement learning. VCS leaves the weights unchanged, so it is complementary: it could be applied on top of a length-trained model.

(Please see part 2 of our response.)

AuthorsOpenReview ↗

Author Respnse to Reviewer 3NM9 (Part2/2)

W$2$: Layer-band ablation

Neither the number of steered layers nor their position is a sensitive choice. Moving the band from 65% to 40% depth changes little, and accuracy is flat from three to five layers. Steering fails only when the band sits near the output or has fewer than three layers.

We tested both choices on Qwen3-4B, MATH-500, changing only the steered layers ($\lambda=0.2$ per layer, update scaled to each layer's hidden-state norm, probe unchanged).

VariedSteered layersAccuracyTokensCap
–None (CoT, same guard)83.2415816.0%
–22–25 (ours, 65% depth)89.835163.4%
Position13–16 (40% depth)89.837163.6%
Position31–34 (90% depth)78.2400019.8%
Count2585.6406714.2%
Count24–2586.6399812.4%
Count23–2588.637745.8%
Count21–2589.433052.4%

Position. Bands at 40% and 65% depth give the same accuracy and cap rate. The band at 90% depth is worse than no steering.

Number of layers. One or two layers are not enough. Four is the smallest count that both matches the best accuracy and brings the cap rate down to about 3%. A fifth layer adds no accuracy. It shortens outputs only because the total update grows with the count, which pushes the policy further from the base policy the probe is fitted on. Four layers is therefore the smallest band that captures the full gain.

We have added Table 11 to the appendix in place of the current justification of the band.

W$_3$: Probe reliability under drifting

The viability probe's readings drift only slightly once steering starts. In a new experiment, the probe ranks and calibrates states from steered trajectories almost as well as states from unsteered ones. On Qwen3-4B, its matched-position AUROC is 0.911 on states from steered trajectories, against 0.943 on unsteered ones, and its ECE is 0.066 against 0.036.

In our VCS implementation, each probe reading comes from a separate forward pass with steering disabled, over the tokens generated so far. Steering therefore affects the probe input through the generated text. We evaluate this shift using Qwen3-4B with the deployed controller on MATH-500 and OlympiadBench. Because the probe predicts viability under the base policy, we label steered states using unsteered continuations. From each steered trajectory, we sample one random newline in the thinking segment, continue greedily from that prefix with steering off, and record whether the continuation ends before the 8192-token cap. We compare with the same probe on states sampled in the same way from unsteered trajectories.

Probe reads states fromLabelMatched-position AUROCECE
Unsteered trajectoriesUnsteered continuation from the state0.9430.036
Steered trajectoriesUnsteered continuation from the state0.9110.066

Matched-position AUROC compares finishing and capped states at the same position (within 64 tokens), so it cannot exploit position. For unsteered trajectories, the unsteered continuation is the trajectory itself.

Why not score against the steered outcome? The probe predicts whether a prefix would finish without further steering. Steering can rescue prefixes that would otherwise hit the cap, so evaluating against steered outcomes mixes probe drift with the controller’s effect on completion. After excluding guard-stopped trajectories, 220 prefixes that hit the cap under base-policy continuation finish with steering, while only 6 show the reverse.

We have added this experiment to Appendix B.3, and cited it in the Section 4 footnote.

Thanks again very much for the review. We hope that our reply has addressed your concerns. Please let us know if there are any further changes you would like to see or if there is anything else that we can clarify.

Thank you for the additional important experiments. They address most of my original concerns. Therefore, I am happy to maintain my positive score of 3 and raise my confidence score. Two comparisons would further strengthen the paper. First, varying the strength of current-risk steering while keeping deadline pressure fixed. Second, from my original review, comparing VCS with a model trained for budgeted reasoning under the same token limit.

Thanks very much for reviewing our response and suggesting further comparisons. We have now varied only the current-risk coefficient. We also evaluated a publicly available checkpoint (ThinkPrune-R1-1.5B) trained for budgeted reasoning.

1. Varying current-risk strength while keeping deadline pressure fixed. Compared with the strongest tested current-risk setting on math (β=0.5), VCS achieves comparable accuracy with 2.2–2.3% fewer tokens. Each cell reports accuracy (%) / mean generated tokens.

Risk feedbackMATH-500OlympiadBenchLiveCodeBench
Deadline only (β=0)88.2 / 381857.0 / 593072.0 / 5052
Current risk, β=0.2588.2 / 375558.8 / 576573.8 / 4798
Current risk, β=0.589.6 / 360159.1 / 525774.2 / 4310
Current risk, β=187.2 / 311853.9 / 397170.5 / 2779
VCS (trajectory-relative risk)89.8 / 351659.2 / 514276.5 / 4864

To locate the benefit, we group all LiveCodeBench problems by initial cap risk ρ₀. Each paired cell reports β=0.5 / VCS.

Initial-risk groupAccuracy (%)Mean tokensCap (%)
Q1: 0–0.371295.3 / 97.71934 / 19631.6 / 0.8
Q2: 0.3712–0.892095.3 / 95.33706 / 39151.6 / 2.3
Q3: 0.8920–0.984468.5 / 76.45567 / 622215.0 / 15.7
Q4: 0.9844–137.5 / 36.76042 / 736521.9 / 32.8

The main gain comes from Q3, where VCS gains 7.9 percentage points with more reasoning tokens. Lowering β weakens risk feedback throughout generation, whereas VCS uses the initial estimate to withhold extra risk-driven steering until predicted risk exceeds its starting level. The Q3 results suggest that VCS may help on problems where the model starts with a high predicted cap risk but can still reach a correct answer with more reasoning. For such a problem, if predicted risk stays at or below its initial level, VCS applies only deadline-driven steering, giving the model more room to continue reasoning. We will include this comparison and discussion in the revised manuscript. Thank you for the helpful suggestion.

2. Comparing with budget-oriented training. We evaluate ThinkPrune-4k (a publicly available checkpoint, trained from the same R1-1.5B base model), using greedy decoding, the same 8,192-token output limit, and the paper's questions. We also apply VCS directly to ThinkPrune to monitor the compositional behavior.

Each cell reports accuracy (%) / mean generated tokens / cap rate (%).

BenchmarkVCSThinkPrune-4kThinkPrune-4k + VCS
MATH-50078.4 / 2735 / 5.880.2 / 2553 / 12.479.4 / 2178 / 5.4
OlympiadBench39.3 / 4128 / 9.342.4 / 4730 / 38.044.1 / 3535 / 13.2
AIME 2025/202618.3 / 5495 / 28.323.3 / 6480 / 65.026.7 / 4945 / 31.7
LiveCodeBench23.1 / 4530 / 11.027.6 / 5969 / 58.728.0 / 4494 / 17.0

VCS uses approximately 13–24% fewer tokens on OlympiadBench, AIME, and LiveCodeBench than ThinkPrune, without language-model fine-tuning, despite lower accuracy. Adding VCS to ThinkPrune reduces generation length by 14.7–25.3% across all four benchmarks, lowers cap rates, and achieves higher observed accuracy. These results suggest that VCS can complement budget-oriented training without refitting its control components, further improving performance. We will include this comparison in the revised manuscript.

Thanks again for your helpful suggestions.

Comments on the paper

1 comment
AuthorsOpenReview ↗

General Response

We thank all three reviewers for their thoughtful feedback. Our core contribution is to steer reasoning under a fixed token budget by tracking how the risk of budget exhaustion changes relative to each trajectory’s starting point. Reviewers found our formulation “intuitive” and its components “well justified” (3NM9), and recognized that “completion prospects provide a useful signal without requiring correctness labels” (GfGW). They also highlighted evidence that hidden states carry “completion-related information beyond token position alone” (f9z2) and noted that the cross-model gains and transfer from mathematics to code “give this idea practical weight” (GfGW).

Following the reviewers’ suggestions, we added several analyses and comparisons to clarify when VCS helps and how it performs in practice.

  • Value of trajectory-relative steering (Section 5.2, Figure 6 and follow-up comparison). At the suggestion of 3NM9, f9z2, and GfGW, we compared trajectory-relative and current-risk steering under the same deadline schedule.
  • Interpretation of completion risk (Section 5.2, Figure 7e and Appendix D.10). In response to f9z2 and GfGW, we conducted forced-answer experiments and tested whether trajectories that reached the token limit could answer correctly when prompted earlier.
  • Comparison with budget-trained models (3NM9). We evaluated VCS alongside ThinkPrune under the same token limit. Results suggest that inference-time steering can complement budget-oriented training.
  • Reuse across token budgets (Figure 13). In response to 3NM9 and f9z2, we quantified the one-time fitting cost and showed that the same probe and steering direction could be reused under different token budgets without refitting.

We have highlighted the corresponding modifications in the manuscript in blue. Again, thank you for your hard work. We believe your input has helped greatly improve the paper.

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

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