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Under review as a conference paper at ICLR 2027

The Model Says Walk: Measuring Whether LLMs Condition on Hidden Constraints

Abstract

Asked whether to walk or drive to a car wash 50m away, most language models say walk, forgetting that the car has to be there. Such failures are usually measured by accuracy on questions where the hidden constraint applies. We show that this is misleading: a model can answer these questions correctly without reasoning about the constraint at all, simply by favoring the cautious option. We instead ask whether a model's decision changes when the constraint is removed. We test this at three levels of control: log-probability sweeps on open-weight models, a 500-prompt stress test, and CORE-100, a new human-validated benchmark of minimal constraint-present/constraint-absent pairs. The picture is consistent. The constraint nudges decisions rather than governing them. Models still miss presence constraints like the car wash, yet elsewhere they apply constraints that are not there. As a result, standard accuracy flatters all ten models we evaluate and reorders their ranking, and prompting fixes that look effective largely vanish under paired scoring. Claims about hidden-constraint reasoning need paired evidence.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
large language models, commonsense reasoning, implicit constraints, heuristic override, shortcut learning, diagnostic benchmarks, goal-decomposition prompting

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_uX26OpenReview ↗
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Paper summary

This paper investigates whether large language models adjust their decisions to implicit feasibility constraints, exemplified by recognizing that visiting a nearby car wash requires bringing the car. It argues that accuracy on constraint-present questions cannot distinguish constraint-sensitive behavior from a general preference for one option. The main contributions are a paired evaluation framework measuring selectivity, over-activation, and under-activation; the 500-prompt Heuristic Override Benchmark (HOB); and CORE-100, a benchmark of 100 human-validated scenarios with minimally edited constraint-present/constraint-absent pairs and additional explicitness and salience controls. The evaluation comprises log-probability sweeps on seven open-weight models, HOB experiments on fourteen models, and a preregistered CORE-100 evaluation of ten models. The results reveal both failures to apply relevant constraints and continued application after those constraints are removed. Active-only accuracy exceeds paired balanced accuracy by 4.3–11.1 percentage points across all ten CORE-100 models and changes their ranking. Furthermore, only one of twelve preregistered prompting comparisons significantly improves selectivity after multiple-testing correction. A separate judge audit shows that sharing constraint metadata across conditions can bias LLM grading. Together, these experiments provide behavioral evidence that hidden-constraint sensitivity requires paired evaluation.

Critical strengths

A consequential finding about evaluation validity. The paper shows that high accuracy when a hidden constraint applies can coexist with systematic over-application when it is absent. On CORE-100, active-only accuracy exceeds paired balanced accuracy for all ten models and changes their ranking. I consider this a substantive reason for acceptance because it changes how apparent reasoning success and prompting improvements should be interpreted.

Careful experimental controls supporting the central finding. CORE-100 uses minimally edited pairs with human-validated reversals in the preferred action, complemented by explicitness and salience controls. Preregistered main analyses, repeated sampling, and scenario-level uncertainty estimates strengthen the comparisons. These choices increase my confidence that the reported evaluation gap reflects a meaningful behavioral limitation, rather than merely uncontrolled differences between prompts.

Critical weaknesses

The interpretation of the sweep experiments relies on an overly strong gating criterion. Sections 2–3 associate constraint gating with a flat log-odds curve. However, a model can correctly prefer the feasible action at every distance while its confidence varies with distance. Parallel conflict and control curves therefore do not establish that the constraint merely shifts a heuristic preference rather than appropriately governing the choice. This weakens a prominent explanatory conclusion, although it does not invalidate the paired-performance results.

The distinction between feasibility constraints and practical preferences remains insufficiently resolved. Human agreement establishes a preferred action, but does not necessarily establish that the alternative violates a feasibility constraint. For example, replacing a couch with a lamp may change carrying costs and convenience rather than a strict prerequisite. Without distinguishing these cases, some measured “over-activation” could reflect different practical preferences. This matters because it limits how directly benchmark errors can be interpreted as failures of hidden-constraint reasoning.

Questions for authors

the criterion for constraint gating. In Sections 2–3, what justifies requiring a flat log-odds curve for constraint gating, rather than a curve that remains below zero at every distance? A model could consistently choose the feasible action while its confidence varies. This clarification would determine whether I interpret the sweeps as evidence against gating or as evidence of residual cue sensitivity.

what the benchmark’s validation establishes. How does the existing annotation procedure distinguish an infeasible action from a feasible but less-preferred action, particularly in examples such as the couch/lamp pair? Appendix H describes the gold labels as validated everyday preferences. This distinction affects how confidently I can interpret measured over-activation as a failure of constraint reasoning rather than disagreement about practical preferences.

2 comments

Thank you for the careful review. Both questions helped us state the claims more exactly.

Q1 / W1. The criterion for constraint gating. We agree that the criterion should be a curve that stays below zero at every distance, and §2 (p. 3) now defines gating that way. A model can choose the feasible action throughout while its confidence varies, and we no longer treat a residual slope as an error.

Read with this criterion, the sweeps show both of the things you distinguish.

  • Evidence against gating: against a matched control that differs only in whether the car is needed, 2 of 21 conflict curves stay below zero at every distance. On the car wash, six of seven models prefer walking at short range (App. J.1, p. 28).
  • Residual cue sensitivity: the curves keep their control's shape (r ≥ 0.94), so distance still moves the margin where the choice is correct.

The matched control also shows how little the constraint adds on the canonical example: on the car wash, four of seven models show no detectable shift relative to it.

GPT-OSS-120B is the model you have in mind: it chooses Drive at every distance while its margin still moves. §3 (pp. 3–4) counts it as behaviorally correct. It also prefers driving for the gift-card control at 100 m, so its correct answer to the test question does not by itself show that the constraint drives the decision (§3, p. 4).

Q2 / W2. Infeasible actions versus feasible but less-preferred ones. The annotation establishes which action raters prefer in each version. It does not certify that the other action is infeasible, and the paper says that golds are validated preferences (§2, p. 3; §9, p. 9; App. H, p. 27). Over-activation is accordingly defined as a decision that does not update when the constraint-relevant fact is edited. Driving a lamp is feasible; the error is choosing as if the couch were still there, when the action raters prefer has reversed.

Does over-activation then reflect a difference in practical preference? Three results in App. J.3 (p. 30) say no.

  • Raters almost never make the choice that models make. On 99 of the 100 Removed texts, no rater chose the constraint-heavy action. Models choose it in 12–39% of trials.
  • Preference strength matters, as you anticipated. Over-activation is 0.28 on items that raters rated with less confidence and 0.05 on the 27 they rated most confidently. §6 (pp. 6–7) reports this.
  • Over-activation remains where the constraint is strict. Two LLM coders, blind to model answers and ratings, labeled each Active constraint as a strict prerequisite or a strong cost (κ = 0.74; 77 strict, 15 cost). On the 77 strict items, active-only accuracy still exceeds paired accuracy for all ten models (Tables 25–26, p. 31).

Your couch example was labeled a strict prerequisite by both coders, and all five raters chose "walk" for the lamp version (strictness labels and rating sheets in the supplementary material).

Thank you for raising both points; the paper is more precise for them.

AuthorsOpenReview ↗

Full Results Tables for Reference

To make your second question easy to check, here are the complete stratified results and the per-model breakdown from App. J.3, as reported in the revised PDF.

Over-activation by strength of the human preference and by strictness (App. J.3, Table 25, p. 31). pR: share of trials choosing the constraint-heavy action on Removed items; models: mean over the ten models.

StratumnRaters pRModels pR [95% CI]Models with pA − SBA > 0
All scenarios1000.0020.219 [0.17, 0.27]10/10
Removed: mean rater confidence ≥ 4.5270.0000.051 [0.02, 0.10]5/10
Removed: mean rater confidence < 4.5730.0030.282 [0.22, 0.35]10/10
Active constraint coded strict prerequisite770.0000.203 [0.15, 0.26]10/10
Active constraint coded strong cost150.0130.296 [0.15, 0.46]10/10
Coders disagree80.0000.230 [0.07, 0.44]10/10

The 4.5 confidence threshold was chosen post hoc, so that split is exploratory.

Over-activation per model (Table 26, p. 31):

ModelAll 100Strict (77)Cost (15)
DeepSeek V4 Pro0.1170.1110.133
DeepSeek R10.1210.0980.181
Gemini 3.1 Pro0.1670.1650.248
Claude Opus 4.60.1840.1870.200
Kimi K2.50.1920.1740.295
Claude Sonnet 4.50.2260.2210.238
GPT-OSS-120B0.2370.1980.371
Qwen3-32B0.2490.2100.476
GPT-5.40.3060.3230.295
Llama 4 Scout0.3940.3450.524
Raters (in-sample)0.0020.0000.013
Reviewer_15g9OpenReview ↗
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Paper summary

This paper investigates whether LLM decisions genuinely track implicit constraints rather than simply favoring cautious actions. It combines controlled probability sweeps, the 500 prompt HOB benchmark, and the human validated CORE 100 benchmark of minimally edited scenarios. The authors show that evaluating only active constraints overestimates paired performance, prompting rarely improves selectivity, and shared grading metadata can distort judge evaluations.

Critical strengths

1.The paired design distinguishes missing a constraint from applying it when absent, exposing a meaningful limitation of active-only accuracy.

2.The study combines controlled sweeps, multiple constraint families, salience controls, and prompting interventions across 17 distinct models.

3.The release includes human judgments, raw model responses, and analysis code. The primary model metrics, confidence intervals, and corrected significance tests reproduce from the supplied records.

Critical weaknesses

1.A model can consistently choose the constraint-respecting action while its confidence varies with distance. Non-flat log odds therefore do not establish the absence of constraint gating. Likewise, high conflict–control correlation alone does not demonstrate that the constraint contributes only a constant offset.

2.The same ratings are used to select items and establish the human reference. Although this limitation is acknowledged, selection favors items on which those raters agree, potentially inflating the reference and weakening the interpretation of the reported human–model selectivity gap.

3.The shared and neutral rubrics differ in both constraint descriptions and shortcut metadata. Consequently, the large agreement gap demonstrates sensitivity to rubric design, but does not establish which component causes the reported grading failures.

Questions for authors

1.Why should constraint gating require flat log odds rather than consistently constraint-respecting choices? Can you support the constant-offset interpretation with matched controls and explicit comparisons against alternative models of the decision curves?

2.Can you evaluate independent annotators on the frozen CORE-100 benchmark and report uncertainty for the human–model comparisons? Does the reported selectivity gap remain under this independent reference?

3.Does the judge failure persist when only the constraint description is varied, while shortcut labels and all other rubric content are held fixed and consistent with the question?

4 comments
AuthorsOpenReview ↗

Response to Reviewer 15g9 (1/2)

Thank you for the rigorous review, and for reproducing our metrics, intervals and corrected tests from the released records.

Q1 / W1. Gating criterion, constant offset, matched controls. We agree that gating should mean consistently constraint-respecting choices, and §2 (p. 3) now defines it that way. A residual slope is not an error, because distance is itself a reason to drive.

Matched controls and explicit models are now in the paper (§3, pp. 3–4, Fig. 2, App. J.1, p. 28). Each conflict phrasing has a twin with the same venue, wording and distance whose goal does not need the car; for the car wash, the twin is buying a car-wash gift card. Against these controls we compare five descriptions of each curve: a constant shift, an affine map, a flat curve, a capped curve and a drifting shift (Table 23, p. 29).

  • 2 of 21 conflict curves stay on the correct side at every distance, both from the same model.
  • Flat curves are rejected in all 21 pairs and capped curves in 18.
  • In five further models from three other families, none of the 15 pairs gates the choice.

On the constant offset: the curves keep their control's shape (r ≥ 0.94, median slope 0.79), but a strictly constant shift is rejected in 18 of 21 pairs, and §3 no longer describes it as constant. The matched control also separates the constraint from the venue. With the venue held fixed, the constraint's own shift on the car wash is indistinguishable from zero in four of seven models (§3; Table 23).

So the conclusion does not rest on flatness or on correlation. Judged by the choice, the constraint rarely gates it.

Q2 / W2. An independent reference, and uncertainty for the human–model gap. The gap remains under a reference that removes the selection effect (Table 1, App. J.2, p. 29). For each held-out rating, we reapply the inclusion rule with the other four ratings only and score the held-out rating on the items selected. No rating is scored on an item it helped select. Held-out raters chose the constraint-heavy action in 98.1% of Active ratings and 1.3% of Removed ratings, which gives S = 0.968 [0.93, 0.99].

All ten models are below this. The closest, DeepSeek V4 Pro, has S = 0.876 [0.82, 0.92]. Table 24 (p. 30) gives a paired interval for every model against raters on the same 100 scenarios, and every deficit is significant. The submitted reference (0.867) had pooled all rated candidates, including items later excluded; the cross-fit reference replaces it (App. J.2).

A disjoint set of raters on the frozen items would be the exact analogue of what you describe. We have not collected one, and App. H (p. 27) says so. The conclusion is unlikely to depend on it: on 99 of the 100 Removed texts, no rater chose the constraint-heavy action, while models choose it in 12–39% of trials (App. J.3, p. 30; Table 1). The main CORE-100 results use model outputs only and need no human reference.

AuthorsOpenReview ↗

Response to Reviewer 15g9 (2/2)

Q3 / W3. Does the judge failure persist when only the constraint description varies? We ran this test as part of a full factorial (App. J.4, p. 31, Table 27): three constraint texts, three shortcut labels and two goals, on the same 504 records, with GPT-5.4 and Claude Sonnet 4.5. The shared rubric of the submission is one cell of the design, and GPT-5.4 reproduces 499 of its 504 original verdicts there.

The table shows the condition you asked for. The shortcut label is held fixed and consistent with the question, and only the constraint text changes. Entries are agreement with the parser on the 120 Removed records.

Constraint textGPT-5.4Claude Sonnet 4.5
Omitted120/120119/120
Correct for the condition120/120120/120
Written for the Active version113/120104/120

For Claude Sonnet 4.5 the failure persists: the Active-version constraint text lowers agreement to 104/120, and to 82/120 when the Active-version goal is added. For GPT-5.4 the constraint text matters little. Its large failure comes from the shortcut label, which for Removed records named the correct answer; whenever that label is present, agreement is between 24 and 31 of 120. §7 (p. 8) now attributes the failure to this component.

The two judges are misled by different components, and both agree with the parser on 118–120 of 120 records when the metadata matches the condition being graded. The recommendation in the paper follows: use rubrics written for each condition, or parsed choices. CORE-100 is scored by a deterministic parser (§5, pp. 5–6), so its results are not affected.

We also applied the check to HOB's own judge and re-graded its constraint-removed answers with the label corrected (App. J.5, p. 32). Mean accuracy on those items moves from 73.9% to 76.6%, and no conclusion changes.

We hope these answers resolve the three soundness concerns. If so, we would be grateful if you would consider revising your score.

AuthorsOpenReview ↗

Full Results Tables for Reference

Below are the curve fits behind Q1 and the human-reference comparisons behind Q2, exactly as they appear in the revised paper.

Q1. Car-wash curves against the matched control (App. J.1, Table 23, p. 29). b: slope of the affine fit of the conflict curve on the matched control (b = 1: same shape); δ: mean shift, conflict minus matched, in log-odds; First Drive: first distance at which the conflict curve favors Drive.

Modelrb [95% CI]Shift δ [95% CI]First Drive
Qwen3-4B0.990.99 [0.76, 1.16]−1.3 [−5.1, +1.3]1km
Qwen3-8B0.981.08 [0.93, 1.25]−4.9 [−5.6, −4.4]200m
Qwen3-14B0.991.14 [0.96, 1.43]+0.1 [−1.5, +1.8]500m
Qwen3-32B0.991.14 [1.07, 1.22]−0.0 [−0.4, +0.4]2km
Qwen3.5-27B0.990.59 [0.50, 0.68]−0.8 [−1.3, −0.4]1km
GPT-OSS-20B0.991.12 [0.84, 1.29]+0.0 [−0.3, +0.4]25km
GPT-OSS-120B0.940.79 [0.57, 1.00]−1.6 [−2.6, −0.6]all distances

Over all 21 model–scenario pairs (car wash, gas station, tire shop), the flat curve is rejected in 21, the capped curve in 18 and the constant shift in 18 (ΔBIC > 2). The two pairs that favor Drive at every distance are both GPT-OSS-120B. Table 23 also gives the gas-station and tire-shop rows and the five models from other families.

Q2. Human references and paired model–human differences (App. J.2, Table 24, p. 30):

ReferenceItemspApRS [95% CI]
Pool over all 181 rated versions (submitted: 0.867)1810.9650.1000.865
Frozen 100, all five ratings (in-sample)1000.9980.0020.996 [0.99, 1.00]
Cross-fit, held-out rating1150.9810.0130.968 [0.93, 0.99]

Paired differences on the frozen 100 (scenario bootstrap). They use the in-sample reference, which is optimistic, so these deficits are upper bounds; against the cross-fit reference the closest model's interval, [0.82, 0.92], still lies below the raters' [0.93, 0.99].

ModelSS − S_human [95% CI]
DeepSeek V4 Pro0.876−0.120 [−0.17, −0.07]
DeepSeek R10.843−0.153 [−0.22, −0.09]
Gemini 3.1 Pro0.826−0.170 [−0.24, −0.10]
Claude Opus 4.60.816−0.180 [−0.26, −0.11]
Kimi K2.50.795−0.201 [−0.27, −0.13]
Claude Sonnet 4.50.714−0.282 [−0.37, −0.20]
Qwen3-32B0.653−0.343 [−0.42, −0.27]
GPT-OSS-120B0.637−0.359 [−0.44, −0.28]
GPT-5.40.610−0.386 [−0.48, −0.29]
Llama 4 Scout0.410−0.586 [−0.68, −0.49]

Thank you for your detailed responses and additional experiments. They have addressed my main concerns and my assessment is unchanged.

Reviewer_qSaaOpenReview ↗
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Paper summary

This paper studies whether LLMs genuinely condition on unstated feasibility constraints when giving everyday advice (the viral "car wash is 50 m away — walk or drive?" question). Its central claim is that scoring only constraint-active items is ambiguous: a model that says "drive" either reasons about the constraint, or simply has a prior toward the constraint-heavy option. The authors introduce a paired Active/Removed design and define selectivity S = P(C|Active) − P(C|Removed), over-activation OA = P(C|Removed), under-activation UA = 1 − P(C|Active), and the identity pA − SBA = ½(OA − UA). Three levels of evidence: (i) log-probability sweeps on seven open-weight models showing the conflict curve shares its shape (r ≥ 0.80) with a no-constraint control and is merely shifted, not flattened; (ii) HOB, a 500-prompt breadth benchmark on 14 models; (iii) CORE-100, 100 human-validated, preregistered, hash-frozen minimal pairs on 10 models. Main findings: active-only accuracy overstates paired performance for all ten models and reorders the leaderboard; over-activation exceeds under-activation for every model; presence constraints are the hardest family; only one of twelve preregistered prompting contrasts improves selectivity; an LLM judge given the Active-form constraint marks 95/96 correct constraint-absent answers wrong. Data, ratings, raw outputs, and a one-command reproduction pipeline are released.

Critical strengths
  1. The identity pA − SBA = ½(OA − UA) is clean, memorable, and should be adopted by future commonsense/constraint benchmarks. The CORE-100 construction protocol (single causal edit, ≤2-word length diff, auditor-confirmed, hash-frozen before model queries) sets a bar for minimal-pair benchmarking.
  2. The demonstration that GPT-5.4's 9-point HOB gain is entirely over-activation, and that a metadata-aware judge marks 95/96 correct Removed answers wrong, are direct, actionable warnings about how LLM-judged constraint evaluations are currently run.
Critical weaknesses
  1. Methodological increment is limited: every component is a mature technique. Contrast sets (Gardner 2020), minimal pairs (BLiMP 2020), shortcut learning (McCoy 2019), distractors (Shi 2023), and preregistered frozen benchmarks (BetterBench 2024) are not new; the contribution is a systematic application of old tools to a new object that corrects existing evaluations, not a new measurement paradigm. As a contribution type this is corrective measurement, but not sufficient for clear acceptance.
  2. The paper stops at the behavioral level and cannot attribute any individual failure mechanistically. Paired scoring separates cue effects from constraint effects in measurement, but does not explain why the model behaves this way internally; "shift not gate" is a valid behavioral model but cannot rule out internal gating computation (a hard gate in logit space need not look flat). The car-wash failure is thus diagnosed, not attributed — an honest boundary , but one that caps the strength of the conclusions.
Questions for authors

See Above

4 comments

Thank you for the clear summary. We respond to the two weaknesses in turn.

W1. The methodological increment. We used established tools on purpose: a paper that questions an evaluation should rest on methods readers already trust. What is new is the result those tools produce, and it concerns how hidden-constraint reasoning is evaluated in general.

  • Benchmarks built around the car-wash question score only items where the constraint applies. That score rewards any model that leans toward the constraint-heavy option. On CORE-100 it overstates all ten models by 4.3 to 11.1 points, and the model with perfect active accuracy ranks fourth once pairs are scored (§6, pp. 6–7, Table 1, Fig. 4a).
  • Prompting fixes that look effective mostly are not. One of twelve preregistered contrasts improves selectivity. A prompt that raises GPT-5.4's accuracy on HOB by 9 points does not raise its selectivity on CORE-100 (−0.04; §7, p. 8, Table 2).
  • A judge that receives the same metadata for both versions of an item marks 95 of 96 correct constraint-absent answers wrong (§7).

The identity pA − SBA = ½(OA − UA) is also new (§2, p. 3, Eq. 2). It says when active-only accuracy misleads and separates the two errors, which set-level contrast consistency (Gardner et al., 2020) does not do (§8, p. 9). CORE-100 itself is a human-validated benchmark that others can reuse.

W2. Behavior versus mechanism. The paper asks whether a model's decision tracks the constraint. That is a question about behavior, and paired scoring answers it. You are right that behavior cannot exclude an internal gate, so we added two things.

First, the gating test no longer assumes a flat curve (§2, App. J.1, p. 28). It asks whether the choice respects the constraint at every distance, and we also fit a capped curve, which is what a soft gate in logit space would produce. The capped curve is rejected in 18 of 21 model–scenario pairs, and 2 of 21 curves respect the constraint throughout.

Second, we looked inside eight open-weight models from four families (App. J.6, p. 33, Table 29).

  • A linear probe separates constraint-present from constraint-absent prompts in unseen scenarios (accuracy 0.71–0.88; 0.61 for a bag-of-words baseline).
  • On over-activation errors, a probe averaged over the question still reads the condition correctly 61–74% of the time. In four of the eight models this is not significantly lower than on correct items. The edited fact is often encoded but not used.
  • Patching shows the information moving from the edited tokens to the decision position within a narrow band of layers.
  • In the three models that respond strongly to steering, the constraint direction adds a fixed offset whatever the cue strength (steered slope 0.98–1.17). This is what "shift, not gate" predicts.

These results point to a failure to use constraint information at the decision, not a failure to represent it. They cover one prompt format and linear methods, so we call them exploratory and keep the paper's claims behavioral (§1, p. 2; §9, p. 9).

A small correction to the summary: on HOB, the prompt improved GPT-5.4 on both item types (App. Table 10, p. 20). The extra over-activation appears on CORE-100's minimal pairs, which is why the paper reports both benchmarks.

If this addresses your two concerns, we hope you will consider revising your score.

AuthorsOpenReview ↗

Full Results Tables for Reference

For easy reference, we include the complete CORE-100 results and the mechanism analysis here, so that everything our reply cites is in one place. Table and page numbers refer to the revised PDF.

W1. CORE-100 main results (Table 1, p. 6). pA: constraint-heavy choices on Active items; pR: the same choice on Removed items (over-activation); SBA = (1 + S)/2.

ModelpApRSelectivity S [95% CI]SBApA − SBA
DeepSeek V4 Pro0.990.120.876 [0.82, 0.92]0.938+0.055
DeepSeek R10.960.120.843 [0.78, 0.90]0.921+0.043
Gemini 3.1 Pro0.990.170.826 [0.75, 0.89]0.913+0.080
Claude Opus 4.61.000.180.816 [0.74, 0.89]0.908+0.092
Kimi K2.50.990.190.795 [0.72, 0.86]0.897+0.090
Claude Sonnet 4.50.940.230.714 [0.62, 0.80]0.857+0.083
Qwen3-32B0.900.250.653 [0.58, 0.72]0.826+0.075
GPT-OSS-120B0.870.240.637 [0.56, 0.71]0.819+0.056
GPT-5.40.920.310.610 [0.52, 0.70]0.805+0.111
Llama 4 Scout0.800.390.410 [0.31, 0.51]0.705+0.099
Human raters, held-out0.980.010.968 [0.93, 0.99]0.984–

Every pA − SBA is positive and survives Holm correction across the ten models (largest p_Holm = .030).

W2. Mechanism (eight open-weight models, thinking off, letter scoring; Table 29, p. 34). Probe accuracy: Active vs. Removed in unseen scenarios (bag-of-words baseline 0.61). Next two columns: share of over-activation errors and of correct Removed items on which the question-averaged probe reads the condition correctly (* p < .001, † p < .05; no mark: not significantly lower). Steered slope: slope of the steered matched curve on the unsteered one at α = 2.

ModelProbe accuracyReads "Removed" on errors… on correct itemsLargest steering shiftSteered slope
Qwen3-4B0.7163%72%−9.40.99–1.11
Qwen3-8B0.7967%78%−9.70.98–1.17
Qwen3-14B0.7963%†85%−1.40.93–1.00
Qwen3-32B0.8166%†89%+0.40.89–1.00
Qwen3.5-27B0.8862%*95%−0.30.44–1.00
GPT-OSS-20B0.7972%79%−1.00.86–1.10
OLMo-3-7B0.7474%74%−3.60.98–1.17
Gemma-3-12B0.8261%†85%−1.90.94–1.07

The three models that respond strongly to steering (Qwen3-4B, Qwen3-8B, OLMo-3-7B) have steered slopes of 0.98–1.17: the direction shifts the curve by a roughly fixed amount. The analysis is exploratory (App. J.6, p. 33).

Reviewer_qSaaOpenReview ↗

The Model Says Walk: Measuring Whether LLMs Condition on Hidden Constraints

Thank you for the response. I have read both comments and the new appendices, and my assessment is unchanged.

Thank you for reading our responses and the new appendices, and for the time you have given the paper. We respect your assessment. Your questions on the methodological increment and on mechanism helped us state the paper's scope more precisely.

Comments on the paper

1 comment
AuthorsOpenReview ↗

General response to all reviewers

We highly appreciate the three reviewers. All three reviews accept the paper's main point: accuracy on questions where a hidden constraint applies cannot separate a model that reasons about the constraint from one that leans toward the constraint-heavy option, and scoring pairs can.

The main CORE-100 results are as submitted. Each of the ten models applies an absent constraint more often than it misses a present one. Active-only accuracy therefore overstates every model, by 4.3 to 11.1 points, and changes the ranking. One of twelve preregistered prompting contrasts improves selectivity (§6, pp. 6–7, Table 1; §7, p. 8, Table 2).

The reviews ask how far four supporting claims go. Short answers are below, and details are in the individual replies and in App. J (pp. 28–34). The main text of the revised PDF is still 9 pages, and the updated supplementary material has the code and data for the added analyses.

1. What counts as gating in the distance sweeps (15g9, uX26, qSaa). We now judge gating by the choice: does the model pick the constraint-respecting action at every distance? By that test, and against a control that differs only in whether the car is needed, the constraint gates the choice in 2 of 21 model–scenario pairs. On the car wash, four of seven models show no detectable response to the car being needed (§2–3, pp. 3–4; App. J.1, p. 28).

2. Whether item selection inflates the human reference (15g9). In a cross-fit reference, no rating is scored on an item it helped select. Raters reach a selectivity of 0.968 [0.93, 0.99], and all ten models are below it (Table 1, App. J.2, p. 29).

3. Which part of a shared rubric misleads the judge (15g9). A factorial over the rubric's components, run with two judges, identifies the component for each judge. Both judges grade correctly once the metadata describes the condition being graded (§7, App. J.4, p. 31).

4. Whether over-activation is only a difference in practical preference (uX26). Over-activation is higher where raters were less confident. It remains on the 77 items whose constraint is a strict prerequisite, and there active-only accuracy still overstates all ten models (§6, App. J.3, p. 30).

For Reviewer qSaa's question about mechanism, App. J.6 (p. 33) adds probing, patching and steering on eight open-weight models.

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

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