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Under review as a conference paper at ICLR 2027

Do Large Language Models Treat Rules as Facts?

Abstract

Large language models (LLMs) are increasingly used to reason over policies, procedures, contracts, and audit records. In these settings, we find that models may incorrectly treat rules about what should or should not happen as evidence of what actually happened. We call this failure norm-to-fact projection. We introduce Unstated, a controlled benchmark of 720 instances built from 120 scenarios, pairing unstated-outcome probes with explicit-outcome anchors. Across 28 open-weight models, median accuracy is 84.5% on explicit-outcome anchors but only 6.7% on prohibition probes. Errors are strongly directional: prohibitions are often interpreted as non-occurrence and commands as occurrence. Ten large-scale frontier models perform better overall, but most still achieve below 75% accuracy on the prohibition probes and remain below human performance. Further analyses show that these errors can remain highly confident, persist under family reweighting, and are only inconsistently reduced by prompting. Our results identify norm-to-fact projection as a systematic failure mode and highlight the need to evaluate whether LLMs infer factual outcomes only from factual evidence.

Primary area:
datasets and benchmarks
Keywords:
language model evaluation, benchmark, epistemic uncertainty, deontic modality

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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 introduces UNSTATED, a benchmark for identifying a failure mode of large language models that the authors call norm-to-fact projection: when a text states only a rule and says nothing about the outcome, does the model treat the rule as evidence of whether the event actually happened?

The benchmark was constructed by five human experts and contains 120 scenarios, each instantiated under six conditions, for 720 items in total. Conditions A (prohibition) and D (command) are the unstated-outcome probes: they give only the rule, with no factual outcome, so the correct label is neutral. Conditions B, C, E, and F are the explicit-outcome anchors: they give the same rule together with an explicit statement of whether the event occurred.

The authors evaluate 28 open-weight models and 10 frontier models. The main finding is that open-weight models perform reasonably well on the explicit-outcome anchors (median accuracy 84.5%) but make strongly directional errors on the unstated-outcome probes: prohibitions are read as "did not occur" and commands as "occurred" (median accuracy 6.7% on the prohibition probe and 15.8% on the command probe). Frontier models perform better overall, but their median accuracy on the prohibition probe is still only 74.2%, with large variation across models (20.0%–98.3%).

Critical strengths
  1. Clean, well-controlled design. Within each scenario, only the outcome information changes across conditions, while participants, events, and hypotheses are held fixed. The matched explicit-outcome anchors separate the target error from general difficulties with factual recognition and NLI label mapping, and the additional controls (affirmative requirements versus negated prohibitions, unrelated-hypothesis fillers, three contextual frames) rule out several simple alternative explanations.
  2. A clear and practically relevant error pattern. The errors are strongly directional: prohibitions lead to "did not occur" and commands lead to "occurred". Because the two probes fail in opposite directions, the errors are tied to the type of rule rather than to a generic label preference. The errors are also made with high confidence (probe predictions with ≥90% confidence are only 22.5% accurate), which suggests that, at least for open-weight models, confidence-based triage would not catch them.

My main concern was that this benchmark measures only an input-sensitive failure mode that arises at lower levels of model capability. I believe the authors have addressed this concern through their responses in A1-1 and A1-5. Therefore, I have decided to raise my score.

Critical weaknesses

1. The headline error rates are not shown to reflect model capability rather than the evaluation protocol and task format.

Open-weight models are evaluated with restricted-choice readout over the next-token probabilities of A/B/C, with native thinking modes explicitly disabled, whereas frontier models generate a response that is then parsed; the paper only states that frontier models used "default decoding settings" and does not report whether reasoning was enabled or at what effort level. The open-weight versus frontier comparison therefore conflates readout protocol, reasoning, and model scale. More importantly, the error is highly sensitive to format and prompting:

  • Under a generic "Let's think step by step" CoT prompt (seven models, exploratory), median command-probe accuracy rises from 14.2% to 71.7% and prohibition-probe accuracy from 10.0% to 34.2%. For Qwen3.5-9B, from a model family that offers a native thinking mode (disabled in the main evaluation), prohibition-probe accuracy rises from 7.5% to 68.3%.
  • For frontier models, a single added reminder (P2: a rule describes what should happen) raises median prohibition-probe accuracy by 25.8 percentage points, while anchor accuracy drops by only 2.3 points.
  • In Appendix M.1, simply rephrasing the question as "which outcomes remain possible" raises the prohibition-probe accuracy of Qwen3.5-9B from 7.5% to 50.8% (although this model narrowly misses the authors' own task-control threshold in that experiment).

There is also no downstream task showing that the error causes actual losses in realistic use; the three regulatory cases in Appendix L are illustrative and still in NLI format.

Why this is consequential: The paper's central claim is that norm-to-fact projection is "a systematic and underexamined failure mode in current LLMs". The evidence above suggests that much of the measured effect may be induced by a specific setup (single-sentence three-way NLI, restricted-choice readout, disabled reasoning) and can be substantially reduced by a one-sentence instruction, at least for frontier models. Without evaluation under native reasoning and evidence from a realistic task, the significance of the finding is unclear, and this is the main reason for my recommendation.

2. The phenomenon is not shown to be specific to normative rules, so the main contribution is not well established.

The paper names the error norm-to-fact projection and attributes it to normative operators, yet the authors' own results show that a normative operator is not necessary. In the operator ablation (Table 27), when no rule is given and the premise only says that the person "had never shown any inclination to" perform the act, the median rate of "did not occur" outputs is 100.0%, at least as high as the 96.7% obtained with the prohibition alone; adding "the temptation was overwhelming with no one nearby to intervene" to the prohibition lowers it to 55.4%. In Appendix J.7, some non-deontic expressions also trigger directional completion: ability statements are read as "occurred" at a median rate of 84.2%, and low-likelihood statements ("Likely low" in Table 30) are read as "did not occur" at 98.8%, slightly higher than the 95.8% for prohibitions. The authors note that "default-outcome completion extends beyond deontic vocabulary but does not produce a uniform response to every modal expression." Although the authors describe the rule-free rate in Table 27 as "only an output rate and not a norm-to-fact projection measure", both conditions have neutral gold labels and measure the same output. Together, these results suggest that the outcome's prior plausibility drives the outputs to a large extent, with the rule being one source of that prior.

These appendix results bear directly on the scope of the phenomenon, but they are not discussed in the main text, which continues to frame the error as specific to rules. In addition, the mechanism studies in Appendix M are behavioral, and the authors acknowledge that "training-stage and representational mechanisms remain unresolved"; the prompt interventions are reported to "not establish a reliable general repair."

Why this is consequential: The first stated contribution is to identify norm-to-fact projection as a failure mode. If the rule has no effect beyond shifting the outcome prior, the paper may be documenting a specific instance of a more general, prior-driven behavior rather than a distinct failure mode, and readers gain little insight into its cause or remedy.

Questions for authors
  1. Native reasoning. Can the open-weight models be re-evaluated with their native thinking modes enabled (e.g., the <think> mode of the Qwen3 and Qwen3.5 series), reporting probe and anchor accuracy and comparing them with the restricted-choice readout? If the gap between the two groups shrinks substantially once reasoning is enabled, I would conclude that the main findings reflect the evaluation protocol more than model capability.
  2. Frontier-model settings. Can the authors report, for each frontier model, temperature, top_p, max_tokens, and whether reasoning/thinking was enabled and at what effort level?
  3. Downstream relevance. Can the authors show, on at least one real downstream task (e.g., compliance checking, contract review, or process auditing), that (a) norm-to-fact projection is positively correlated with the downstream error rate, and (b) simple prompt engineering (e.g., adding "judge only from evidence explicitly stated in the text") cannot reliably fix it?
  4. Role of the rule. Given that in Table 27 the rate of "did not occur" outputs reaches 100% when no rule is given and only a low-probability cue is present, to what extent does the rule have an effect independent of the outcome prior? Can the authors compare matched conditions with and without a rule while holding the prior plausibility of the outcome fixed? The answer determines whether norm-to-fact projection stands as a distinct failure mode.
8 comments
AuthorsOpenReview ↗

Response to Reviewer th9p (Part 1)

Q1-1: The headline error rates are not shown to reflect model capability rather than the evaluation protocol and task format.Open-weight models are evaluated with restricted-choice readout over the next-token probabilities of A/B/C, with native thinking modes explicitly disabled, whereas frontier models generate a response that is then parsed; the paper only states that frontier models used "default decoding settings" and does not report whether reasoning was enabled or at what effort level. The open-weight versus frontier comparison therefore conflates readout protocol, reasoning, and model scale.

A1-1: This reflects a misunderstanding of our evaluation design. First, all models are evaluated on the same three-way NLI task. For open-weight models, we select the highest-probability option, following prior work [1–2], and retain option probabilities for confidence analysis. For API-evaluated models, we parse their final answers into labels because complete, comparable option probabilities are not available in our evaluation. Second, to further address this concern, we switched open-weight models to generated answers while keeping the other output settings unchanged. The table reports medians across 28 models:

ReadoutOverallAcc_ACBR_AAcc_DCBR_DAnchor
RC (original protocol)60.36.792.515.878.884.5
GEN (generated answers)57.37.169.212.923.373.2

After aligning the open-weight readout with that of frontier models, overall performance is slightly lower rather than higher, and the overall pattern remains consistent. These results support our choice of evaluation protocol and indicate that the gap from frontier models reflects model capability rather than the readout protocol.

[1] Lost in Inference, NAACL 2025 Main

[2] A Rose by Any Other Name, Findings of ACL 2025

Q1-2: More importantly, the error is highly sensitive to format and prompting:Under a generic "Let's think step by step" CoT prompt (seven models, exploratory), median command-probe accuracy rises from 14.2% to 71.7% and prohibition-probe accuracy from 10.0% to 34.2%. For Qwen3.5-9B, from a model family that offers a native thinking mode (disabled in the main evaluation), prohibition-probe accuracy rises from 7.5% to 68.3%. For frontier models, a single added reminder (P2: a rule describes what should happen) raises median prohibition-probe accuracy by 25.8 percentage points, while anchor accuracy drops by only 2.3 points. In Appendix M.1, simply rephrasing the question as "which outcomes remain possible" raises the prohibition-probe accuracy of Qwen3.5-9B from 7.5% to 50.8% (although this model narrowly misses the authors' own task-control threshold in that experiment).

A1-2: First, we tested a range of alternative explanations under direct answering, supporting the validity of the low performance measured in this setting. Second, large gains from CoT have also been reported in prior work. Both the original CoT paper [3] and the “Let's think step by step” paper [4] report substantial gains across several datasets; for example, CoT raises MultiArith accuracy from 7.3% to 73.7%. A large CoT gain alone therefore does not establish that our evaluation is unusually sensitive to prompting. Finally, although prompting and reasoning can improve performance, our benchmark remains challenging. With CoT, the seven models still have median error rates of 65.8% on prohibition probes and 28.3% on command probes, leaving accuracy gaps of 64.3 and 25.3 pp from the human baseline, respectively (Table 3 and Appendix K). Even Qwen3.5-9B, which improves substantially, still makes errors on 31.7% of prohibition probes and remains 30.2 pp below human accuracy. Large gains therefore do not mean that the problem is solved: reliably distinguishing normative requirements from factual outcomes remains difficult.

[3] Wei et al. (2022). Chain-of-Thought Prompting Elicits Reasoning in Large Language Models. NeurIPS.

[4] Kojima et al. (2022). Large Language Models are Zero-Shot Reasoners. NeurIPS.

AuthorsOpenReview ↗

Response to Reviewer th9p (Part 2)

Q1-3: There is also no downstream task showing that the error causes actual losses in realistic use;

A1-3: This is an interesting question. UNSTATED scenarios draw on requirements, prohibitions, and actions in everyday life, rather than symbolic logic without practical context. Our experiments show norm-to-fact projection in both locally evaluated open-weight models and API-evaluated frontier models. Prompting and CoT can improve performance, but this risk remains, indicating that current LLMs may make incorrect judgments when interpreting practical texts. To further address your concern and examine downstream effects, we collected 100 audit units from the official 2024 Code of Federal Regulations (CFR): 50 without execution evidence and 50 with explicit evidence. We evaluated Llama-3.1-8B, Qwen3.5-9B, GPT-5.5, and Claude Opus 5, all with thinking disabled. The results are shown below:

ModelNo execution evidence: “cannot determine” (correct)No execution evidence: rule-consistent errorNo execution evidence: judgment against the ruleExplicit evidence: accuracy
Llama-3.1-8B6.082.012.074.0
Qwen3.5-9B8.088.04.092.0
GPT-5.592.06.02.096.0
Claude Opus 556.040.04.090.0

These results show that treating rules as facts also occurs in a real downstream task, highlighting the practical value of studying this error. We will include this experiment in the next version.

Q1-4: the three regulatory cases in Appendix L are illustrative and still in NLI format.

A1-4: First, Appendix L uses the NLI format to align with the original benchmark, allowing us to test under the same evaluation criteria whether confusion between rules and facts also occurs in real regulatory text. Second, NLI is a well-established task in computational linguistics, with widely used evaluation resources such as SNLI (EMNLP 2015) [5] and MultiNLI (NAACL 2018) [6]. Its entailment, contradiction, and neutral relations clearly distinguish facts supported by the text from outcomes the text does not determine. This directly matches our goal of testing whether models treat normative requirements as factual evidence.

[5] Bowman et al. (2015). A large annotated corpus for learning natural language inference. EMNLP.

[6] Williams et al. (2018). A Broad-Coverage Challenge Corpus for Sentence Understanding through Inference. NAACL-HLT.

Q1-5: Why this is consequential: The paper's central claim is that norm-to-fact projection is "a systematic and underexamined failure mode in current LLMs". The evidence above suggests that much of the measured effect may be induced by a specific setup (single-sentence three-way NLI, restricted-choice readout, disabled reasoning) and can be substantially reduced by a one-sentence instruction, at least for frontier models. Without evaluation under native reasoning and evidence from a realistic task, the significance of the finding is unclear, and this is the main reason for my recommendation.

A1-5: As discussed in Q1-1–Q1-4, we first explain the basis for our evaluation protocol and NLI design. The CoT and direct outcome-question experiments show that prompting and reasoning can improve performance, but some models still show clear confusion between rules and facts. In Q1-3, we further evaluate 100 audit units from real documents and show that the error also occurs in this setting. To further address this concern, we evaluated Qwen3 and Qwen3.5 with native <think> mode enabled and compared them with CoT prompting. Each cell reports CoT prompt (P1gen) / native Think accuracy (%):

ModelOverallAcc_AAcc_DAnchor
Qwen3–14B84.9 / 92.138.3 / 77.585.8 / 99.296.3 / 94.0
Qwen3–32B86.9 / 90.641.7 / 70.095.8 / 99.296.0 / 93.5
Qwen3.5–4B84.9 / 87.545.0 / 55.885.8 / 96.794.6 / 93.1

Native Think further improves probe performance for these models, but prohibition-probe accuracy remains only 55.8–77.5%, well below explicit-outcome anchor accuracy of 93.1–94.0%. Thus, these models still do not reliably distinguish rules from facts with native reasoning enabled. Thank you for this comment. We will include this experiment in the next version.

AuthorsOpenReview ↗

Response to Reviewer th9p (Part 3)

Q2-1: The phenomenon is not shown to be specific to normative rules, so the main contribution is not well established. The paper names the error norm-to-fact projection and attributes it to normative operators, yet the authors' own results show that a normative operator is not necessary.

A2-1: Our paper starts with a specific question: do models mistake “what should happen” for “what actually happened”? By pairing unstated-outcome probes with explicit-outcome anchors, UNSTATED systematically shows that models can identify explicit facts yet still treat normative requirements as outcome evidence (Table 2). This behavior has a reasonable link to outcome expectations: Gächter et al. (2025) [7] find that people expect others to follow rules, while Phillips and Cushman (2017) [8] show that norms affect default judgments of what is possible. Building on this link, we compare rules, behavioral propensity, and likelihood cues in Appendices J.3 and J.7, finding that non-rule cues can also lead to similar errors. These extended results do not contradict the original finding; they connect confusion between rules and facts to a broader expectation-driven problem. Our contribution is both to identify and measure this specific error and to test its scope through further controls. It does not require rules to be a necessary condition for all similar errors.

Q2-2: In the operator ablation (Table 27), [... ...]. Together, these results suggest that the outcome's prior plausibility drives the outputs to a large extent, with the rule being one source of that prior.

A2-2: Prior work provides empirical evidence for a link between rules and outcome expectations. Gächter et al. (2025, Nature Human Behaviour) find that rules lead people not only to judge that others should comply [7], but also to expect that others will comply. Phillips and Cushman (2017, PNAS) further show that norms affect default judgments of what is possible [8]. Szekely et al. (2021) find that both normative expectations and expectations about others' behavior affect cooperative decisions [9]. Bonan et al. (2020) show that agreement or conflict between normative requirements and information about actual behavior changes intervention effects [10]. These studies motivate our comparisons of rules, behavioral propensity, and likelihood cues. A prior-driven account is therefore compatible with norm-to-fact projection: the former provides an account of how the latter arises.

[7] Gächter et al. (2025), Why people follow rules, Nature Human Behaviour

[8] Phillips, J., & Cushman, F. (2017). Morality constrains the default representation of what is possible. PNAS, 114(18), 4649–4654.

[9] Szekely et al. (2021). Evidence from a long-term experiment that collective risks change social norms and promote cooperation. Nature Communications, 12, 5452.

[10] Bonan et al. (2020). The interaction of descriptive and injunctive social norms in promoting energy conservation. Nature Energy, 5, 900–909.

Q2-3: These appendix results bear directly on the scope of the phenomenon, but they are not discussed in the main text, which continues to frame the error as specific to rules.

A2-3: The main text discusses the link between rules and outcome expectations in Section 3.3 (lines 215–219). We have also added §5.5, “Do Outcome Expectations Shape Factual Judgments?”, to summarize the results from Appendices J.1, J.3, and J.7 and discuss what they imply for the scope of the phenomenon. All added and revised text is marked in blue.

Q2-4: In addition, the mechanism studies in Appendix M are behavioral, and the authors acknowledge that "training-stage and representational mechanisms remain unresolved"; the prompt interventions are reported to "not establish a reliable general repair."

A2-4: Yes, we have not established the training-stage or representational mechanisms behind this behavior, nor proposed a reliable general repair. Our paper defines and measures the error through paired experiments, tests it across models and contextual frames, and examines factors that affect it through controls and prompt interventions. This fulfills the goal of UNSTATED as a diagnostic benchmark: to provide a reproducible basis for identifying, comparing, and studying this problem. A more complete explanation of the mechanisms and targeted ways to reduce the error remain important directions for future work; our analyses provide evidence for these efforts.

Reviewer_cxyeOpenReview ↗
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Paper summary

This paper investigate whether LLMs incorrectly treat rules about what should happen as evidence of what actually happened. To do this, it introduces UNSTATED, a controlled benchmark of 720 instances built from 120 scenarios, comparing unstated outcome probes with explicit outcome probes. Across 28 open-weight and 10 larger frontier models, the authors repetitively find frequent and often confident inferences of rule compliance. Open-weighted models perform surprisingly bad, with frontier model also making mistakes. While the paper tests several plausible explanations, the source of the observed errors remains unresolved.

Critical strengths
  • Given the seemingly simplicity of the task, the low performance, especially those of the open models is interestingly surprising.
  • The experiments covers many plausible explanations over why this is the case, and conduct the experiment suite over a wide range of models and sizes.
  • The paper also report clean and high human performance, further solidify the validity of the benchmark.
Critical weaknesses
  • I'm not sure how the result clearly support a "rule vs fact" dichotomy, in that there still seems to be many contending hypotheses untested and uncommented. For example, the model could simply be not able to distinguish high probability events and certainty; or it might have misunderstood the temporal relationship between premises and hypotheses.
  • Although this is not necessarily a weakness, none of the explanations tested by the authors seems to provide a fully convincing account of the observed behavior.
Questions for authors
  • Would it be possible that some other issues like temporal interpretation also contributing to the errors? How would you rule out those effects? What do you think might explain away the huge gap within different generations of the Qwen family?
  • How much of the open-weight model gap comes from the evaluation protocol? For example, do you think choosing the highest scoring letter for open-weight model but parsing response from frontier model might widening the gap?
7 comments
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Response to Reviewer cxye (Part 1)

Q1-1: I'm not sure how the result clearly support a "rule vs fact" dichotomy, in that there still seems to be many contending hypotheses untested and uncommented. For example, the model could simply be not able to distinguish high probability events and certainty.

A1-1: The probability-based account you propose is compatible with the distinction between rules and facts in our paper. Rules are indeed linked to outcome expectations: prior work finds that people generally expect others to comply with rules [1], and that norms affect default judgments of what is possible [2]. A rule may therefore make compliance seem more likely, but it does not establish that compliance occurred. In the explicit-outcome anchor conditions in Table 2, we keep the event, participants, hypothesis, and rule fixed, while explicitly stating the actual outcome—that is, providing factual evidence. The results are as follows:

Model groupRule + explicit outcome (Anchor)Prohibition only (AccA)
Open-weight models (28)84.5%6.7%
Frontier models (10)96.3%74.2%

Both frontier and open-weight models can identify explicit factual outcomes with high accuracy. When only a rule is provided, however, models can treat the rule as a fact and base their judgment on it, as reflected in AccA.

[1] Gächter et al. (2025), Why people follow rules, Nature Human Behaviour

[2] Phillips, J., & Cushman, F. (2017). Morality constrains the default representation of what is possible. PNAS, 114(18), 4649–4654.

Q1-2: it might have misunderstood the temporal relationship between premises and hypotheses.

A1-2: In fact, section 3.2 (lines 179–181) specifies the temporal relation between the premise and hypothesis: the premise states a rule, and the hypothesis concerns the target action during the period when that rule is in effect, not an action before the rule was issued. This design makes the intended temporal relation explicit in the input.

To further test the effect of temporal relations, we constructed a before-rule variant: the rule is issued and takes effect only after the target action window has ended, and the hypothesis refers only to that earlier, closed time window. The outcome remains unstated in cells A and D, so the gold label is neutral. We evaluated Qwen3-8B and Qwen3.5-9B with thinking disabled, using the original P0 prompt and settings.

ModelSettingOverallAcc_AAcc_DAnchor
Qwen3–8BOriginal P058.915.82.583.8
Qwen3–8BBefore-rule P071.91.730.0100.0
Qwen3.5–9BOriginal P078.17.583.394.4
Qwen3.5–9BBefore-rule P073.215.823.3100.0
ModelContradiction in cell AEntailment in cell DContradiction in cell D
Qwen3–8B98.30.070.0
Qwen3.5–9B84.20.076.7

Under the before-rule condition, both models reach 100.0% accuracy on explicit-outcome anchors, yet incorrectly answer “did not occur” on 84.2–98.3% of prohibition probes. On command probes, 70.0–76.7% of answers are “did not occur,” while 0.0% are “did occur.” Thus, even when the target period is explicitly placed before the rule takes effect, models still make definite judgments about unstated outcomes. In the prohibition condition, these errors are consistent with the rule.

Q2: Although this is not necessarily a weakness, none of the explanations tested by the authors seems to provide a fully convincing account of the observed behavior.

A2: Thank you for your feedback. We distinguish a reliable observation of the behavior from an explanation of its causes.

For the observation, UNSTATED identifies and measures norm-to-fact projection through paired unstated-outcome probes and explicit-outcome anchors, showing the behavior across open-weight and frontier models and different contextual frames (Table 2; Section 5.4).

For the explanation, controls show that simple wording or format preferences do not fully explain the errors (Section 5.3; Appendix H). Changes in judgments with supervision and behavioral propensity cues support an expectation-driven account (Appendix J), while prompting and CoT reduce some errors without reliably eliminating them (Sections 5.5–5.6).

To our knowledge, this paper is the first to systematically identify and measure norm-to-fact projection in LLMs. A complete account of its causes requires further work. The present study establishes the behavior and tests both factors that do not fully explain it and factors that affect it, providing an empirical basis for future mechanism studies.

AuthorsOpenReview ↗

Response to Reviewer cxye (Part 2)

Q3-1: Would it be possible that some other issues like temporal interpretation also contributing to the errors?

A3-1: As discussed in A1-2, both models still make factual errors on prohibition probes even when the target period is explicitly placed before the rule takes effect. Making the temporal order explicit is therefore not sufficient to eliminate these errors.

Q3-2: How would you rule out those effects?

A3-2: We address other potential confounds in three ways. (a) Controlled design: we keep the event, participants, and hypothesis fixed and vary only the rule type and outcome evidence, controlling for content differences (Section 3.3). (b) Human validation: five independent annotators each completed all 720 items, with mean accuracy of 97.3%, supporting the clarity of the task and labels (Appendix K). (c) Cross-frame testing: the same 30 scenarios show a probe–anchor gap under concise, narrative, and legal frames, indicating that the pattern cannot be explained by one particular wording or frame alone (Section 5.4).

Q3-3: What do you think might explain away the huge gap within different generations of the Qwen family?

A3-3: This is a good question. In our experiments, the ability to avoid norm-to-fact projection does not improve consistently with newer model versions, and this pattern is not limited to Qwen. We observe a similar contrast in the GPT family: from GPT-5.5 to GPT-5.6 Sol, anchor accuracy increases from 95.4% to 97.5%, while prohibition-probe accuracy falls from 98.3% to 80.8%. Thus, under our evaluation settings, stronger factual recognition or a newer model version does not guarantee a better distinction between rules and facts. Differences in training and inference settings may contribute, but the current results do not separate their effects. One possibility is that differences in training data, post-training objectives, and reasoning strategies change how much each generation relies on common-sense expectations versus textual evidence. These explanations have not yet been tested directly, and the specific causes remain a question for future work.

Q4: How much of the open-weight model gap comes from the evaluation protocol? For example, do you think choosing the highest scoring letter for open-weight model but parsing response from frontier model might widening the gap?

A4: First, all models are evaluated on the same three-way NLI task. For open-weight models, we select the highest-probability option, following prior NLI studies [1–2], and retain the option probabilities for confidence analysis. For API-evaluated models, we parse the final answer into a label because complete, comparable option probabilities are not available in our evaluation. The protocol difference therefore reflects the information available and the needs of the analysis. Second, to further address this concern, we switched the open-weight models (28 models) to generated answers while keeping the other output settings unchanged. The results are as follows:

ReadoutOverallAcc_ACBR_AAcc_DCBR_DAnchor
RC (original protocol)60.36.792.515.878.884.5
GEN (generated answers)57.37.169.212.923.373.2

After aligning the open-weight readout with that of frontier models, performance differs only slightly from the original protocol and shows the same overall pattern. These results indicate that the open-weight performance gap reflects model capability rather than the evaluation protocol.

[1] Lost in Inference (NAACL 2025 Main)

[2] A Rose by Any Other Name (Findings of ACL 2025)

AuthorsOpenReview ↗

Gentle Reminder for Reviewer cxye

Dear Reviewer cxye,

Thank you again for your careful review and thoughtful comments on our submission.

In our previous response, we discussed your concerns individually, covering the relationship between rule–fact confusion and outcome probability (Q1-1), temporal interpretation and other potential confounds (Q1-2, Q3-1, Q3-2), the distinction between behavioral findings and causal explanations (Q2), differences across model generations (Q3-3), and the effect of the evaluation protocol (Q4).

To further address your concern regarding temporal interpretation (Q1-2), we have extended our before-rule experiment to three additional models: Llama-3.1-8B, Mistral-7B-v0.3, and Gemma-4-E4B.Results below report Original P0 → Before-rule P0 accuracy (%):

ModelOverallAcc_AAcc_DProbeAnchor
Qwen3-8B58.9 → 71.915.8 → 1.72.5 → 30.09.2 → 15.883.8 → 100.0
Qwen3.5-9B78.1 → 73.27.5 → 15.883.3 → 23.345.4 → 19.694.4 → 100.0
Llama-3.1-8B48.9 → 74.96.7 → 5.84.2 → 45.85.4 → 25.870.6 → 99.4
Mistral-7B-v0.352.4 → 59.73.3 → 21.713.3 → 89.28.3 → 55.474.4 → 61.9
Gemma-4-E4B66.1 → 83.210.0 → 25.814.2 → 85.812.1 → 55.893.1 → 96.9

These results provide further evidence that making the temporal order explicit is not sufficient to eliminate errors about unstated outcomes.

We would greatly appreciate your feedback on these additional results and whether they address your concern. We remain happy to discuss any outstanding questions.

Best regards,

All Authors

Reviewer_a48qOpenReview ↗
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Paper summary

This paper raises a problem with LLMs in that they treat rules of what should have or should have not happened, as evidence of what actually happened. They evaluate this phenomenon with a natural language inference (NLI) benchmark where a claim/hypothesis implies/contradicts/is neutral to a premise. The authors suggest a dataset called “UNSTATED” which aims to evaluate this and has 720 instances built from 120 scenarios, and was designed by 5 human experts and labeled by 5 annotators. Each scenario has a hypothesis and a premise which are based on prohibition or command as well as unstated, happened, or did not happen. They evaluate the benchmark on both open-weight and frontier models and show that both model types fail on this benchmark in recognizing the difference between things that did happen or should have happened, with the open weight models failing more often.

Critical strengths
  1. The paper is clearly written, and the problem is well defined.

  2. To the best of my knowledge and research, the benchmark addresses a gap in NLI benchmarks that is not addressed in previous works.

  3. The appendix contains additional ablation results, and supplementary results that provide further analysis of the benchmark.

Critical weaknesses
  1. It is not clear entirely whether the failure the paper talks about is due to the adding of a “rule” in the premise (the main conjecture of the paper) or whether the separation is more between “likely” hypotheses given the premise, where the rule is only one sign of likelihood. Already in early works like RTE, NLI is defined not in an absolute sense but that the hypothesis is “likely” given the premise. More specifically, in Appendix J the results of J.1, J.3 and J.7 suggest that this indeed might be the true failure case, when the authors replace or remove the rule entirely. If this is indeed the case, this would damage the novelty of the paper. More generally, I would consider moving some of these analyses in section J to the main paper since they touch on the core of the paper’s claim. Also consider running these not only on the open models but also on the frontier models for a better analysis of the results.

  2. Lack of understanding how reasoning affects the results: the frontier models might be using CoT (this is not reported) and the open weight models disable thinking, so it is hard to separate the effect of reasoning on the results. The current CoT analysis only considers 7 small models. It would be helpful to expand this to all small models as well as to analyze how much the frontier models used reasoning for these tasks.

  3. To me the failure cases of the frontier models are much more interesting than the small models, some of which are outdated. However, much of the analysis of the paper both in the main paper as well as in some of the appendices (e.g., J, H, etc.) is conducted only on the small models (other than Section 5.7 which could not be run on frontier models).

  4. The exact guidelines that were given to the annotators and the human experts are not given, which makes it harder to understand the exact process.

  5. The frontier models (which to me their failure again is the more interesting result) already score relatively well on this task (the strongest frontier models are above 90%) so the gap that is left to close is modest (possibly even closed by frontier models that were released lately).

  6. (Minor): I wouldn’t call these open vs. frontier since some of the frontier models (e.g., Kimi, Deepseek) have open weights but maybe frontier vs. small language models (SLMs) or something along those lines?

  7. (Minor): No analysis on Gemini models.

Questions for authors
  1. Could you perform a thorough analysis (e.g., an expansion/movement of some of Section J to the main text and run over the frontier models too) which compares the paper’s claim about rules vs. facts to the model simply answering based on the likelihood of whether a premise implies the hypothesis.

  2. Could you perform a more thorough analysis of how reasoning affects the results, looking at the frontier models without CoT and the small models with CoT?

16 comments
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Response to Reviewer a48q (Part 1)

Q1-1: It is not clear entirely whether the failure the paper talks about is due to the adding of a “rule” in the premise (the main conjecture of the paper) or whether the separation is more between “likely” hypotheses given the premise, where the rule is only one sign of likelihood.

A1-1: These two explanations are compatible. Prior work provides empirical evidence for a link between rules and outcome expectations. Rules lead people not only to judge that others should comply, but also to expect that others will comply [1]. Norms also affect people's default judgments of what is possible [2].

[1] Gächter et al. (2025), Why people follow rules, Nature Human Behaviour

[2] Phillips, J., & Cushman, F. (2017). Morality constrains the default representation of what is possible. PNAS, 114(18), 4649–4654.

Q1-2: Already in early works like RTE, NLI is defined not in an absolute sense but that the hypothesis is “likely” given the premise.

A1-2: Our task asks whether the premise establishes the outcome, not whether the outcome is likely. Our setting follows SNLI [3] and MultiNLI [4], which distinguish entailment from mere plausibility. A rule may make compliance likely, but does not establish that it occurred. We therefore assign neutral when the outcome is unstated.

[3] A large annotated corpus for learning natural language inference. EMNLP 2015.

[4] A Broad-Coverage Challenge Corpus for Sentence Understanding through Inference. NAACL 2018.

Q1-3: More specifically, in Appendix J the results of J.1, J.3 and J.7 suggest that this indeed might be the true failure case, when the authors replace or remove the rule entirely. If this is indeed the case, this would damage the novelty of the paper.

A1-3: Our paper first focuses on a specific question: do models mistake “what should happen” for “what actually happened”? By pairing unstated-outcome probes with explicit-outcome anchors, UNSTATED systematically shows that models can identify explicit facts yet still treat normative requirements as outcome evidence (Table 2). This behavior has a plausible link to outcome expectations: Gächter et al. (2025) [1] find that people expect others to follow rules, while Phillips and Cushman (2017) [2] show that norms affect default judgments of what is possible. Building on this link, we further compare rules, behavioral propensity, and likelihood cues in Appendices J.1, J.3, and J.7, finding that non-rule cues can also lead to similar errors. These extended results therefore do not contradict the original finding; instead, they connect confusion between rules and facts to a broader expectation-driven problem. Our contribution is both to identify and measure this specific error and to examine its scope through additional controls. It does not require rules to be a necessary condition for all similar errors.

[1] Gächter et al. (2025), Why people follow rules, Nature Human Behaviour

[2] Phillips, J., & Cushman, F. (2017). Morality constrains the default representation of what is possible. PNAS, 114(18), 4649–4654.

Q1-4: More generally, I would consider moving some of these analyses in section J to the main paper since they touch on the core of the paper’s claim.

A1-4: Thank you for this suggestion. We have added §5.5, “Do Outcome Expectations Shape Factual Judgments?”, to the main text. A single table summarizes the results for supervision and enforcement cues (J.1), behavioral propensity (J.3), and likelihood cues (J.7). The section explains why these results are consistent with both rule effects and an expectation-driven account. Full experimental details remain in Appendix J, and the new section appears before the prompt-intervention analysis. All added and revised text is marked in blue.

AuthorsOpenReview ↗

Response to Reviewer a48q (Part 2)

Q1-5: Also consider running these not only on the open models but also on the frontier models for a better analysis of the results.

A1-5: Thank you for this suggestion. Appendix J in the original paper shows that factual judgments change with supervision and enforcement, behavioral propensity, and likelihood cues when the actual outcome is unstated. To test whether this pattern also appears in frontier models, we extended J.1, J.3, and J.7 to the 4 frontier models from the main experiment during rebuttal, using the original settings. The results are shown below.

Summary values are cross-model medians (%). Brackets retain the intervals reported with the latest results; Δ is the median within-model paired change in percentage points (pp).

J.1: Supervision and enforcement cues

ConditionFrontier accuracy (%)Frontier “did not occur” rate (%)Frontier “did occur” rate (%)Paired Δ in “did not occur” rate from baseline (pp)Direction of changeOpen-weight “did not occur” rate (%)
Prohibition only (baseline)68.8 [34.2, 91.7]31.2 [8.3, 65.8]0.0——95.4
+ Continuous monitoring26.7 [5.0, 60.8]73.3 [39.2, 95.0]0.0+30.8 [29.2, 53.3]increase95.0
+ No observer97.5 [93.3, 99.2]2.5 [0.8, 6.7]0.0−29.2 [−59.2, −6.7]decrease62.1
+ Never checked or enforced100.0 [100.0, 100.0]0.00.0−31.2 [−65.8, −8.3]decrease7.1

J.3: Prohibition wording and behavioral propensity cues

ConditionFrontier accuracy (%)Frontier “did not occur” rate (%)Frontier “did occur” rate (%)Paired Δ from prohibition only (pp)Direction of changeOpen-weight “did not occur” rate (%)
Prohibition only67.5 [35.8, 93.3]32.5 [6.7, 64.2]0.0——96.7
Low-occurrence cue only (no prohibition)69.2 [1.7, 95.0]30.8 [5.0, 98.3]0.0+8.8 [−22.5, 34.2]increase100.0
Prohibition + high-violation cue95.8 [93.3, 100.0]2.1 [0.0, 6.7]0.4−30.8 [−57.5, −5.8]decrease55.4
Neutral opportunity control100.0 [100.0, 100.0]0.00.0−32.5 [−64.2, −6.7]decrease0.0

J.7: Different modal expressions

Modal familyFrontier accuracy (%)Frontier “did not occur” rate (%)Frontier “did occur” rate (%)Open-weight “did not occur” / “did occur” rate (%)
Prohibition70.4 [35.0, 92.5]29.6 [7.5, 65.0]0.095.8 / 0.0
Likely low75.0 [25.8, 100.0]25.0 [0.0, 74.2]0.098.8 / 0.0
Seldom explicit93.3 [17.5, 97.5]3.3 [1.7, 5.0]3.8 [0.0, 7.5]12.5 / 0.0
Ability99.6 [95.0, 100.0]0.00.40.0 / 84.2
Attempt / Desire / Intention / Likely high / Plan100.00.00.00.0 / 11.2–50.4

Overall, the median “did not occur” rates remain 29.6% under prohibition and 25.0% under low likelihood. Compared with the open-weight medians of 95.8% and 98.8% in the original paper, these errors are substantially reduced but not eliminated. Performance also differs across modal expressions. These frontier models can still treat expected outcomes as facts. Thank you for this comment. We will include the new experiments and results in §5.5 and Appendix J.

Q2-1: Lack of understanding how reasoning affects the results: the frontier models might be using CoT (this is not reported) and the open weight models disable thinking, so it is hard to separate the effect of reasoning on the results.

A2-1: Lines 243–244 state that both frontier and open-weight models are evaluated without CoT prompting in the main experiment: the prompt contains no reasoning instruction. Kimi K3 is an exception: its API does not allow thinking to be disabled, so we set its reasoning effort to low. The per-model settings are listed below:

Modeltemperaturetop_pmax_tokensNative thinkingeffort
GPT-5.51.01.0DefaultDisablednone
GPT-5.6 Sol1.01.0DefaultDisablednone
GPT-5.4 mini1.01.0DefaultDisablednone
GPT-4.11.01.0DefaultNot applicableNot applicable
Claude Opus 4.8Not configurableNot configurableDefaultDisabledhigh (default)
Claude Opus 5Not configurableNot configurableDefaultDisabledhigh (default)
DeepSeek V4 Flash1.01.08192DisabledNot applicable
GLM-51.00.9565536DisabledNot applicable
Grok 4.30.70.95128000Disablednone
Kimi K31.00.95131072Enabledlow

We will clarify the Kimi K3 exception and include these per-model settings in the revised paper.

AuthorsOpenReview ↗

Response to Reviewer a48q (Part 3)

Q2-2: The current CoT analysis only considers 7 small models. It would be helpful to expand this to all small models .

A2-2: Thank you for this suggestion. Using the original experimental settings, we expanded the CoT evaluation from 7 to 16 open-weight models. These cover Qwen2.5 (7B–14B), Qwen3 (0.6B–32B), Qwen3.5 (0.8B–27B), Gemma 4 E4B, Llama 3.1 8B, and Mistral 7B. The summary results are shown below:

MetricP0 median (%)CoT median (%)Median within-model change (pp)
Overall59.275.9+14.5
Acc_A (prohibition probe)7.131.7+13.3
Acc_D (command probe)14.275.8+20.4
Anchor (explicit-outcome anchors)79.190.6+3.6

The expanded results agree with the original findings. CoT improves overall performance, with larger gains on the command probe, but median prohibition-probe accuracy remains only 31.7%. Thus, adding generated reasoning does not reliably prevent models from treating rules as facts. We will include the new experiments and results in the next version.

Q2-3: as well as to analyze how much the frontier models used reasoning for these tasks

A2-3: Thank you for this comment. To examine how explicit CoT affects frontier-model performance, we added a P0-versus-CoT comparison for 8 frontier models. Each cell reports P0 → CoT accuracy (%) in this comparison, with the change in pp in parentheses.

ModelOverallAcc_A (prohibition probe)Acc_D (command probe)Anchor (explicit-outcome anchors)
Claude Opus 587.9 → 81.2 (−6.7)55.4 → 39.1 (−16.3)100.0 → 100.0 (0.0)92.9 → 87.0 (−6.0)
GPT-4.183.7 → 92.9 (+9.2)28.3 → 76.1 (+47.8)89.1 → 98.9 (+9.8)96.2 → 95.7 (−0.5)
GPT-5.596.2 → 87.5 (−8.7)97.8 → 89.1 (−8.7)100.0 → 100.0 (0.0)94.8 → 84.0 (−10.9)
GPT-5.6 Sol94.7 → 95.3 (+0.5)80.4 → 96.7 (+16.3)100.0 → 100.0 (0.0)97.0 → 93.8 (−3.3)
DeepSeek V4 Flash96.0 → 81.3 (−14.7)91.3 → 90.2 (−1.1)100.0 → 100.0 (0.0)96.2 → 74.5 (−21.7)
GLM-591.1 → 91.5 (+0.4)65.2 → 84.8 (+19.6)100.0 → 98.9 (−1.1)95.4 → 91.3 (−4.1)
Grok 4.394.4 → 94.4 (0.0)92.4 → 93.5 (+1.1)100.0 → 100.0 (0.0)93.5 → 93.2 (−0.3)
Kimi K395.7 → 83.0 (−12.7)88.0 → 76.1 (−12.0)100.0 → 95.7 (−4.3)96.5 → 81.5 (−14.9)

The effect of CoT varies across models, and explicit-outcome anchor accuracy decreases for every model in this comparison. Thus, CoT helps some models but does not consistently improve frontier models' ability to distinguish rules from facts. We will include the new experiments and results in the next version.

Q3: To me the failure cases of the frontier models are much more interesting than the small models, some of which are outdated. However, much of the analysis of the paper both in the main paper as well as in some of the appendices (e.g., J, H, etc.) is conducted only on the small models (other than Section 5.7 which could not be run on frontier models).

A3: We included a broad set of open-weight models for the following reasons. (a) Open-weight models provide necessary coverage. We evaluate widely studied families such as Qwen, Llama, Gemma, and Mistral. For example, the Qwen3 technical report cition has over 10,000 . Our selection spans model sizes, architectures, and developers in China, the US, and Europe. It includes both established models and recent releases such as Qwen3.5. Including earlier models also adds a temporal perspective: norm-to-fact projection appears in both earlier and newer generations. This recurring pattern strengthens the need for systematic evaluation beyond the latest frontier models. (b) We have expanded the frontier-model analyses. During rebuttal, we added frontier-model results for CoT and the appendix analyses. Their overall trends are consistent with our original findings. We will incorporate these results into the revision.

Q4: The exact guidelines that were given to the annotators and the human experts are not given, which makes it harder to understand the exact process. All added and revised text is marked in blue.

A4: Thank you for your feedback. We have updated Appendix K with detailed guidelines for the annotators and human experts.

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

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