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Under review as a conference paper at ICLR 2027

LiveHumanRightsBench: Stress-Testing Reliability of LLM Judgments on Live Human-Rights Cases

Abstract

As LLMs increasingly inform high-stake decisions that affect people's fundamental rights and welfare, it becomes critical to examine the reliability of their judgments when case information is presented differently or when they are challenged by adversarial opinions. We introduce LiveHumanRightsBench, a continuously refreshing benchmark grounded in long European Court of Human Rights (ECtHR) case records. For each benchmark instance, we embed an automated perturbation pipeline to test robustness of model judgments when the case information is paraphrased or summarized. We further stress-test if models can hold their stance when facing various adversarial opinions. Our results show that while frontier LLMs have become remarkably more robust than earlier models under summarization and paraphrasing, they still remain highly sensitive to very simple challenges involving naive dissent and social pressure, even when those challenges introduce no new evidence. Claude-Opus-4.6 and GPT-5.6-Sol reverse over 90% of their initial model judgments within two turns of simple adversarial opinion challenges. Strikingly, adding a challenger identity cue sharply lowers these reversals for a lawyer, and even more so for an AI safety researcher. So far we've only observed this intriguing role-cue effect in Opus-4.6 and 5.6-Sol and it remains absent on other highly capable reasoning models such as DeepSeek-V4-Pro. In conclusion, our findings revealed substantial volatility in frontier LLMs that could risk instability and critically impact human rights at scale, calling for greater effort towards more trustworthy AI for decision support.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
LLM Reliability Evaluation

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_EmoPOpenReview ↗
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3
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Paper summary

This paper studies important problems concerning the reliability and robustness of LLMs in high-stakes decision-making: sensitivity to input prompts and susceptibility to adversarial opinion, grounded in real-world legal cases. Specifically, it constructs a benchmark using 1000 instances drawn from 947 published ECtHR cases across 15 years and embeds generalizable perturbation strategies. It further challenges init model judgments over 3 turns of adversarial opinion challenges. There are some interesting findings about state-of-the-art models, such as the impact of AI safety researcher identity cue on judgments reversals.

Critical strengths
  • The problem is timely and I appreciate the motivation behind this work.
  • Writing is natural and easy to follow.
  • Some findings are interesting, such as the impact of AI safety researcher identity cue on judgments reversals.
Critical weaknesses
  • The paper has limited methodology novelty.
  • The technical complexity is limited.
  • While the paper describes the benchmark as continuously refreshed in the abstract and introduction, I only see experiment results of v1.0. Could the authors demonstrate the automatic benchmark update process more clearly, and explain how they ensure consistency across releases? Do the findings still hold on newly published judgments?
Questions for authors

While the paper describes the benchmark as continuously refreshed in the abstract and introduction, I only see experiment results of v1.0. Could the authors demonstrate the automatic benchmark update process more clearly, and explain how they ensure consistency across releases? Do the findings still hold on newly published judgments?

4 comments
AuthorsOpenReview ↗

Official reply from authors - part 1

We thank the reviewer EmoP for the careful reading of our paper and for the positive comments on the motivation. The question on the live refresh was especially helpful for us, and we are delighted to address your concerns and points accordingly.

The paper has limited methodology novelty.

Thanks for the comment. While we agree that the paper does not propose a new algorithm, since it is a benchmark paper, we would like to point out three parts of the evaluation design that are new and that led to the findings you found interesting.

  1. Every instance carries its own reliability tests. For each case we automatically generate a summary, three paraphrases, country swaps and the challenges, so no manual annotation is needed. As described in Section 3.2, this is what allows the same tests to be applied to newly published judgments. To demonstrate this, we refreshed the benchmark with 100 new judgments, as reported in our response to your third comment.

  2. We measure what a reversal does to correctness. As listed in Table 1, we report the retention of correct judgments and the correction of errors as two separate rates. This changes the reading of our main finding. As shown in Table 9, with the AI safety researcher cue Opus-4.6 keeps 99.0% of its correct judgments, but it fixes only 1.6% of its errors, compared to 96.3% without a cue. A single reversal rate would present the cue as a pure improvement.

  3. The challenge protocol is controlled along several dimensions. As described in Appendix G.1, each initial judgment is challenged under eleven conditions (two pressure levels, four role cues, three consensus cues and two affiliation cues) in a static and an adaptive mode. As shown in Table 10b, we add a placebo cue ("I am reading this case.") and a challenge that agrees with the model. This design is what isolates the effect of the researcher cue. The placebo reduces the reversals of Opus-4.6 from 95.0% to 65.5%, while the researcher cue reduces them to 0.7%.

A related point on the novelty with respect to prior work was raised by Reviewer j8sk. Our answer there is that running the perturbations and the challenges on the same instances shows that a model can be robust to rewording and still give up its judgment under plain disagreement. Reviewer FTor also asked what is behind the reversals, and our answer there is that these control experiments point to deference to the user as the main driver.

The technical complexity is limited.

Thanks for the comment. While we agree that the challenges themselves are simple, we kept them simple on purpose, and we believe this makes the findings more serious and not less.

  1. A challenge that only says "I disagree" and asks the model to reconsider, without any evidence, is something every user can write. No access to the model and no optimization is needed. As reported in Appendix G.2, this plain disagreement already makes 57.5% (Opus-4.6) and 62.0% (5.6-Sol) of their most robust correct answers wrong, and the directive raises this to 90.1%. If a complex attack were needed to obtain this, the risk in practice would be much smaller.

  2. The effort of the paper is in the scale and the statistical care of the evaluation. We evaluate eight models on 1,000 instances with ten scores per input, and we started 118,206 conversations for the adversarial part. As described in Appendix B, all intervals come from case-cluster bootstrap resampling, the planned contrasts use Bonferroni-adjusted intervals, and the accuracy losses hold under five different scoring rules.

  3. A simple protocol is also easier to reproduce and to rerun on new data. This is what made it possible to refresh the benchmark with new judgments within the rebuttal period.

AuthorsOpenReview ↗

Official reply from authors - part 2

While the paper describes the benchmark as continuously refreshed in the abstract and introduction, I only see experiment results of v1.0. Could the authors demonstrate the automatic benchmark update process more clearly, and explain how they ensure consistency across releases? Do the findings still hold on newly published judgments?

Thanks for the comment. While the submission indeed reports only v1.0, which we also note in Appendix A.2, we agree that a live benchmark should show at least one refresh. We therefore ran one to answer the three parts of this comment directly. We collected 100 new ECtHR judgments decided after the v1.0 cutoff (21 May 2026) and froze this set before any model was evaluated on it. We then ran them through the same pipeline as a matched set of 100 cases from v1.0 (the anchor), on 5.6-Sol and Opus-4.6 and in the same time window. The results are shown in the table below.

ModelSetAccuracyBalanced accuracyNo-violation recallSummary change (%)Reversal, no cue (static, %)Reversal, researcher cue (static, %)
5.6-SolAnchor (v1.0)85.076.016/30109148
5.6-SolNew (post-v1.0)77.062.68/301210093
Opus-4.6Anchor (v1.0)76.063.810/3018921
Opus-4.6New (post-v1.0)74.057.65/3016970
  1. Regarding the update process, the new judgments went through the same steps as v1.0, as described in Section 3.2 and Appendix A. We keep full judgments with a clear decision date and an explicit outcome, remove the verdict, standardize the text and the provision, and generate the summaries and challenges automatically. The only manual step is a review of the passages flagged by a keyword check, which were 21 passages in v1.0.

  2. Regarding consistency across releases, the anchor rows reproduce the numbers in our paper. The balanced accuracy is 76.0 vs. 75.5 for 5.6-Sol and 63.8 vs. 62.9 for Opus-4.6, and the reversal rates match as well (91 vs. 92.6 and 92 vs. 92.8 without a cue, 48 vs. 51.2 and 1 vs. 1.1 with the researcher cue). The pipeline and the models therefore behave as in the original experiments, and the differences between the anchor rows and the new rows come from the cases. We will evaluate such an anchor together with every new release. Reviewer j8sk asked how stable our rates are across repeated runs, and this anchor is part of our answer there, since it repeats 100 cases and gives the same rates.

  3. Regarding the findings, the main ones hold on the new judgments. Challenges without a cue still reverse almost all judgments (100% for 5.6-Sol and 97% for Opus-4.6). Summaries change a similar share of judgments (12% and 16%). The researcher cue still removes almost all reversals for Opus-4.6 (0%), and its accuracy is similar (74.0 vs. 76.0).

  4. The refresh also showed two differences that v1.0 alone could not show. First, both models recognize fewer no-violation outcomes on the new cases (8/30 vs. 16/30 for 5.6-Sol and 5/30 vs. 10/30 for Opus-4.6), while their accuracy on violation cases does not drop. This lowers the balanced accuracy by 13.3 points for 5.6-Sol (bootstrap 95% interval 1.7 to 25.0) and by 6.2 points for Opus-4.6, where the interval includes zero (-5.0 to 17.4). Since both models are affected, we believe the new no-violation cases are harder, and we will study this in the next release. Second, the researcher cue helps 5.6-Sol much less than before (93% reversals vs. 48%). With 100 cases we do not want to over-interpret these differences, but we see them as a good argument for keeping the benchmark live. Reviewer FTor asked why the identity cues affect models differently, and this result adds to our answer there, since it suggests that the cue effect of 5.6-Sol is less stable than that of Opus-4.6.

We will add this experiment and a description of the release procedure to the revised version.

While the paper describes the benchmark as continuously refreshed in the abstract and introduction, I only see experiment results of v1.0. Could the authors demonstrate the automatic benchmark update process more clearly, and explain how they ensure consistency across releases? Do the findings still hold on newly published judgments?

Thanks for the question. Since it is the same as the third weakness above, we kindly refer to our response there. In short, the benchmark was refreshed with 100 new judgments, the anchor from v1.0 reproduces our paper, and the main findings hold on the new cases, with two differences that we describe above.

AuthorsOpenReview ↗

Thanks for the valuable comments

We thank the reviewer EmoP, again for the valuable comments, which led to an experiment that we believe makes the paper stronger. We hope our responses address the concerns, and we would really appreciate it if the reviewer could consider raising the score. We are happy to answer any further questions.

Dear Reviewer EmoP,

Thank you once again for your time and valuable feedback on our submission.

As the rebuttal period is coming to a close, we wanted to kindly follow up to see if you have had a chance to review our responses. We dedicated significant effort to thoroughly addressing your questions and running additional analyses to strengthen the paper based on your suggestions.

If you have any remaining concerns or additional comments, we would be very happy to discuss them further before the deadline. Otherwise, if our responses have satisfactorily resolved your questions, we would greatly appreciate it if you would consider updating your evaluation accordingly.

Thank you again for your time and consideration.

Best regards, The Authors

Reviewer_j8skOpenReview ↗
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Paper summary

The paper as a whole studies the reliability of frontier LLMs for high-stakes legal decision support using European Court of Human Rights cases. Its main evaluation is whether the model's judgments remain stable under controlled perturbations such as paraphrasing and summarization, as well as under evidence-free adversarial disagreement. Based on their results, we see substantial instance-level judgment volatility despite comparatively stable aggregate performance, including frequent reversals of initially correct decisions. The paper in addition examines how challenger identity affects these reversals, finding a particularly strong effect from an AI-safety-researcher cue. Overall, the work highlights important reliability limitations that may not be captured by standard aggregate accuracy evaluations.

Critical strengths
  1. LiveHumanRightsBench provides a practically relevant evaluation setting based on real ECtHR judgments and is designed to incorporate newly published cases over time, making it useful for studying the reliability of frontier models in a high stakes domain. The reusability of the evaluation on a continuously updated dataset is also a useful contribution.

  2. The instance level analysis is particularly informative because it highlights that relatively stable aggregate performance can hide changes in individual model judgments. The combination of the perturbation, adversarial disagreement, and the challenger identity experiments provides a broader characterization of reliability than aggregate accuracy alone.

Critical weaknesses
  1. Several of the reliability phenomena studied, including sensitivity to input perturbations and susceptibility to adversarial disagreement, have already been explored in prior work. The paper itself describes prompt sensitivity and adversarial opinion as previously documented phenomena. The novelty here comes from the LiveHumanRightsBench setting and the combined evaluation.

  2. The paraphrases are not independently audited for fact preservation, making it difficult to completely separate sensitivity to wording from possible subtle semantic changes introduced during paraphrasing. The authors appropriately acknowledge this limitation and interpret these effects as an upper bound, but stronger validation of semantic preservation would strengthen this part of the evaluation.

Questions for authors

Since the adversarial opinion experiments use only one conversation per condition and mode, how stable are the reported reversal rates and challenger-identity effects across repeated runs of the same case? Have the authors considered repeating a subset of these experiments to quantify this variability?

5 comments
AuthorsOpenReview ↗

Official reply from authors - part 1

We thank the reviewer j8sk, for the careful reading of our paper and for the positive comments on the practical relevance of the benchmark and on the instance-level analysis. We are happy to hear that the paper gave the reviewer a deeper understanding of the problem. The comments on fact preservation and on repeated runs were especially helpful for us, and we report additional results for the latter.

Several of the reliability phenomena studied, including sensitivity to input perturbations and susceptibility to adversarial disagreement, have already been explored in prior work. The paper itself describes prompt sensitivity and adversarial opinion as previously documented phenomena. The novelty here comes from the LiveHumanRightsBench setting and the combined evaluation.

Thanks for the comment. While we agree that prompt sensitivity and adversarial opinion have each been studied before, and that our novelty comes from the LiveHumanRightsBench setting and the combined evaluation, we would like to highlight three results that we could only obtain because of this setting and this combination.

  1. Since we run the perturbations and the challenges on the same instances, we can check if a model that is robust to one is also robust to the other. As reported in Appendix G.2, we take the 577 instances that Opus-4.6 and 5.6-Sol judge correctly from the full record, the summary and every paraphrase. After three turns of a challenge that contains no evidence, 90.1% of these answers are wrong. The ranking of the models also changes. As listed in Table 11, 5.6-Sol is the most accurate model (83.5%) and changes the fewest judgments under paraphrasing (4.7 to 5.6%). However, as listed in Table 10a, it still reverses 51.2% of its judgments with the researcher cue, while Opus-4.6 reverses 1.1%. A benchmark that only tests accuracy or only tests perturbations would miss this.

  2. Earlier studies report that stated credentials and a sophisticated tone both trigger deference in open-weight models [1], and that legal LLMs over-trust authoritative but false references [2]. In our setting we observe a different pattern. When the challenger states an identity, the two frontier models reverse less, and the AI safety researcher cue reduces reversals more than the lawyer cue. As shown in Figure 7, Opus-4.6 reverses 28.9% of its judgments with the lawyer cue and 1.1% with the researcher cue, while the DeepSeek and Qwen models still reverse more than 80% of their judgments with either cue. As far as we know, an identity cue that protects the judgments of some models in this way has not been reported before.

  3. Regarding the setting, each instance is a real case record of about 4,900 tokens on average with the decision of the Court as the expert label, and all perturbations and challenges are generated automatically for every instance. The same tests can therefore be applied to new judgments. Reviewer 3 asked us to demonstrate this, so we collected 100 new ECtHR judgments decided after the v1.0 cutoff and evaluated them together with 100 cases from v1.0 on 5.6-Sol and Opus-4.6. The v1.0 cases reproduce the numbers in our paper, and the main vulnerability holds on the new judgments, where challenges without a cue reverse 100% and 97% of the judgments of the two models. We also found some differences for 5.6-Sol on the new cases, which we report in our response to Reviewer EmoP.

Reviewer EmoP raised a related comment on the methodology. Since that comment is about the design of our experiments and controls, we discuss it separately in our response there, and we hope it addresses your potential comment on it as well. Additionally, we will revise the related work section to make this positioning clearer in the revised version of our manuscript.

[1] Gabriele Maraia, Fabio Massimo Zanzotto, and Leonardo Ranaldi. 2026. Sounding vs. Being an Expert: Disentangling Authority, Register and Cultural Impact in Sycophantic LLMs. In Findings of the Association for Computational Linguistics: ACL 2026, pages 32492-32508.

[2] Lorenzo Molfetta, Alessio Cocchieri, Luca Ragazzi, Ilaria Bartolini, Marco Patella, and Gianluca Moro. 2026. Sycophants in the Courtroom: Are LLMs Fragile to Juridical Authority and Evolving Legal Standards? In Proceedings of the 64th Annual Meeting of the Association for Computational Linguistics (Volume 1: Long Papers), pages 10865-10886.

AuthorsOpenReview ↗

Official reply from authors - part 2

The paraphrases are not independently audited for fact preservation, making it difficult to completely separate sensitivity to wording from possible subtle semantic changes introduced during paraphrasing. The authors appropriately acknowledge this limitation and interpret these effects as an upper bound, but stronger validation of semantic preservation would strengthen this part of the evaluation.

Thanks for the comment, and for noting our upper-bound interpretation. While we agree that the paraphrases were not audited for fact preservation, which we also state in Appendix A.2, the results we already have give several reasons to believe that semantic changes play a small role.

  1. Our claim is that frontier models are robust to paraphrasing. If a paraphrase changed or dropped a fact, this could only add judgment changes. So the real sensitivity to wording is at most what we report.

  2. The light paraphrase only varies a few phrasings and keeps most of the wording, so it has very little room to change facts. If semantic changes were behind the judgment changes, the heavy paraphrase should cause clearly more of them. However, as listed in Table 11, the rates are almost the same across the three strengths, with 7.5 to 8.4% for Opus-4.6, 4.7 to 5.6% for 5.6-Sol and 13.9 to 14.9% for V4-Pro.

  3. As reported in Appendix F.3, summaries and heavy paraphrases almost never reverse the same judgment. Five models have no such instance, and Opus-4.6 has 2 out of 736. Our audit in Appendix I shows that summaries do drop facts. If heavy paraphrases dropped the same decisive facts, we would expect them to reverse the same judgments.

  4. As listed in Table 6, the accuracy changes stay between -1.4 and +1.9 points for all models and strengths. As reported in Appendix F, paraphrases reverse only 0.6 to 7.1% of the judgments, which is fewer than half of the judgments they change.

  5. As described in Appendix E.1, each case record is split into chunks of about 3,000 characters that are rewritten one at a time and joined in the original order. The medium and heavy prompts explicitly ask the model to keep all facts. This keeps the structure of the record and limits omissions.

We will certainly add this reasoning to Section 4.2 and keep the limitation clearly stated.

Since the adversarial opinion experiments use only one conversation per condition and mode, how stable are the reported reversal rates and challenger-identity effects across repeated runs of the same case? Have the authors considered repeating a subset of these experiments to quantify this variability?

Thanks for the question. While it is true that each conversation was run once per condition and mode in the main experiment, which we note in Appendix A.2, the key conditions have been run again three times, each starting from fresh initial answers. This includes a repetition of a subset of 100 cases, as suggested. The table below compares the static reversal rates (%) across these runs.

ExperimentOpus-4.6, no cueOpus-4.6, researcher cue5.6-Sol, no cue5.6-Sol, researcher cue
Main experiment, Table 10a92.81.192.651.2
Placebo control experiment, Table 10b95.00.793.351.7
Reasoning enabled, Table 1292.05.2--
Repetition of 100 v1.0 cases9219148
  1. The rates differ by a few points across the runs, while the cue effects we report are between 40 and 90 points. The lawyer cue is also stable, with 28.9% in the main experiment and 27.6% with reasoning enabled for Opus-4.6.

  2. The last row is new. As part of the refresh test that we ran in response to Reviewer 3, we repeated 100 cases from v1.0 in a new time window, and the rates again match the main experiment.

  3. As shown in Figure 7, the static and the adaptive mode are separate conversations for every instance, and both show the same pattern.

We want to be clear about what these runs do not show. They tell us that the aggregate rates are stable, but not how consistently one specific case flips when the same conversation is repeated. Our claims are about the aggregate rates, which are averaged over several hundred instances. We will add this table to the appendix in the revised version.

AuthorsOpenReview ↗

Thanks for the valuable comments

We thank the reviewer j8sk again for the valuable comments. We hope our responses address the concerns, and we would really appreciate it if the reviewer could consider raising the score. We are happy to answer any further questions.

Reviewer_FTorOpenReview ↗
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3
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2
Informativeness
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3
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3
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Paper summary
  • The paper introduces LiveHumanRightsBench, a continuously updated benchmark constructed from judicial decisions of the European Court of Human Rights (ECtHR), to evaluate the reliability of general-purpose LLMs in human-rights case judgments. The authors also propose an automated pipeline for continuously updating the benchmark with newly published cases.

  • Using this benchmark, the authors evaluate eight models, including GPT-5.6-Sol, Claude-Opus-4.6, and DeepSeek-V4-Pro, under various experimental conditions, including systematic input perturbations and multi-turn adversarial opinion challenges.

  • The experimental results show that GPT-5.6-Sol achieves the highest baseline accuracy, while Claude-Opus-4.6 demonstrates the greatest overall resistance to adversarial opinions. More importantly, the authors find that although frontier models are relatively robust to summarization and paraphrasing, their judgments can still be substantially influenced by simple adversarial opinions, even when no additional evidence is provided.

Critical strengths
  1. Strong practical motivation and relevance to high-stakes decision-making. The paper provides a convincing motivation for investigating the reliability of LLM judgments in human-rights cases. Since incorrect or unstable judgments in such high-stakes scenarios could have serious consequences, evaluating model reliability under different conditions is both necessary and practically meaningful. The continuously updated benchmark also provides a useful foundation for future research in this area.

  2. Comprehensive experimental design and interesting empirical findings. The paper presents its methodology and experimental procedures in considerable detail. The evaluation covers a wide range of conditions, including systematic input perturbations, multi-turn adversarial challenges, and different identity and social-pressure cues. The experiments also reveal several interesting and somewhat surprising findings. For example, even highly capable frontier models can reverse their initially correct judgments in response to simple, repetitive disagreements that provide no new evidence. Furthermore, the substantial differences in how models respond to challenger identity cues are particularly intriguing. These findings provide valuable insights into the limitations of current LLMs in high-stakes decision-making.

Critical weaknesses
  • Although the paper provides extensive experimental results and some preliminary analyses, it does not sufficiently investigate the underlying mechanisms responsible for the observed judgment instability. In particular, the authors demonstrate that frontier models can be strongly influenced by simple adversarial disagreements and that different models respond very differently to challenger identity cues. However, the explanations for these phenomena remain largely speculative.

  • While Section 5.3 provides an exploratory analysis of reasoning traces and evaluation awareness, these observations do not establish a causal explanation for the reported effects. More targeted experiments would be valuable for distinguishing between possible mechanisms, such as sycophancy, sensitivity to authority cues, and evaluation awareness.

  • Furthermore, although proposing a defense is not necessarily required for a benchmark paper, the work does not explore even a preliminary approach to mitigating the identified vulnerabilities. As a result, the paper provides compelling empirical observations but offers relatively limited insight into why these failures occur or how they might be addressed.

  • Given that these surprising behavioral patterns constitute a central contribution of the paper, I believe a deeper investigation would substantially strengthen its scientific contribution.

Questions for authors
  1. What do the authors believe is the primary mechanism behind the strong influence of simple adversarial disagreements on frontier models? In particular, why do repeated disagreements without additional evidence cause models to reverse initially correct judgments? Can the authors provide further experimental evidence to distinguish between sycophancy, instruction-following tendencies, and other possible explanations?

  2. How do the authors explain the substantial differences in the effects of challenger identity cues across models? For example, the AI safety researcher cue almost eliminates judgment reversals in Claude-Opus-4.6 but has a much smaller effect on DeepSeek and Qwen models. What evidence supports the hypothesis that this behavior is related to evaluation awareness rather than other model-specific response patterns?

5 comments
AuthorsOpenReview ↗

Official reply from authors - part 1

We thank the reviewer FTor for the careful reading of our paper and for the positive comments on our motivation and experimental design. We are delighted to hear that the reviewer FTor found the results on identity cues interesting. Please find our detailed responses to each comment below.

Although the paper provides extensive experimental results and some preliminary analyses, it does not sufficiently investigate the underlying mechanisms responsible for the observed judgment instability. In particular, the authors demonstrate that frontier models can be strongly influenced by simple adversarial disagreements and that different models respond very differently to challenger identity cues. However, the explanations for these phenomena remain largely speculative.

Thanks for the comment. While we agree that we do not establish a causal explanation, and that causal claims are difficult in a legal setting as complex as ECtHR cases where many factors are involved, we would like to point out that the paper already includes four experiments that test possible explanations. These are (i) two pressure levels that separate plain disagreement from an explicit instruction, (ii) a confirming challenge where the challenger agrees with the model, (iii) a placebo identity cue, and (iv) a comparison of lawyer and AI safety researcher cues, including junior and senior lawyers. They are described in Appendix G.2 and G.3, and we will summarize them in the main text in the revised version.

We describe two results here and the others in the following responses:

(1) As shown in Table 9, we report separately how many correct judgments a model gives up and how many errors it fixes. Under the directive and without a cue, Opus-4.6 gives up 91.8% of its correct judgments and also changes 96.3% of its wrong ones. The model changes its answer no matter if it was right or wrong, which is not what we would expect if it treated the challenge as evidence. As described in Appendix G.3, even correct judgments with very confident scores (at most 10 or at least 90) are overturned by static challenges in 87.2% of the cases for Opus-4.6 and 92.1% for 5.6-Sol.

(2) We also ran a control where the challenger agrees with the model (“Your assessment is right”), as described in Appendix G.3. In this case no judgment is reversed, and none of the 194 initial errors of Opus-4.6 or the 154 of 5.6-Sol is fixed. This shows that the reversals follow the direction of the challenge and are not random.

While Section 5.3 provides an exploratory analysis of reasoning traces and evaluation awareness, these observations do not establish a causal explanation for the reported effects. More targeted experiments would be valuable for distinguishing between possible mechanisms, such as sycophancy, sensitivity to authority cues, and evaluation awareness.

Thanks for raising this point. While the analysis in Section 5.3 is indeed exploratory, the paper has a targeted experiment for each of the three mechanisms you mention. We summarize them as:

(1) For sycophancy, we compare a challenge that only expresses disagreement with a directive that also tells the model to replace its answer. As reported in Appendix G.2, disagreement alone already makes 57.5% (Opus-4.6) and 62.0% (5.6-Sol) of the robust correct answers wrong. We give more details in our response to your first question.

(2) For authority cues, a lawyer should be a more reliable source than an AI safety researcher on how the Court would rule. However, as shown in Figure 7, Opus-4.6 reverses 28.9% of its judgments with the lawyer cue and only 1.1% with the researcher cue. As listed in Table 10a, we also compared a junior and a senior lawyer and did not see a consistent effect of seniority. So the models do not simply follow the more authoritative source.

(3) For evaluation awareness, we tested a placebo cue (“I am reading this case.”) to check if any first-person statement has the same effect as the researcher cue. As shown in Table 10b, the placebo reduces the reversals of Opus-4.6 from 95.0% to 65.5%, while the researcher cue reduces them to 0.7%. As listed in Table 13, the researcher cue also increases the share of explanations that mention being tested, from 2.0% to 7.1% for Opus-4.6.

We give more details in our response to your second question in the following part.

AuthorsOpenReview ↗

Official reply from authors - part 2

Furthermore, although proposing a defense is not necessarily required for a benchmark paper, the work does not explore even a preliminary approach to mitigating the identified vulnerabilities. As a result, the paper provides compelling empirical observations but offers relatively limited insight into why these failures occur or how they might be addressed.

Thanks for the comment. While we did not test a defense in this paper, which we also list as a limitation in Appendix A.2, we would like to mention one result that is relevant for designing one. As shown in Table 9, with the researcher cue Opus-4.6 keeps 99.0% of its correct judgments, but it fixes only 1.6% of its errors, compared to 96.3% without a cue. The cue does not make the model more accurate. The model simply keeps its initial answer, right or wrong. A defense that only reduces reversals would look good on paper but would leave all the initial errors in place. This is why we report the retention of correct judgments and the correction of errors as two separate rates. A good defense should do well on both, and our benchmark can be used directly to test this. We will add this discussion to the main text.

Given that these surprising behavioral patterns constitute a central contribution of the paper, I believe a deeper investigation would substantially strengthen its scientific contribution.

We appreciate the suggestion, and we fully agree. In the revised version, we will consider adding a new subsection to Section 5 that puts all the control experiments together and clearly states which explanations they rule out and which ones remain open. The table below gives an overview of what this subsection will cover.

Possible explanationExperiment in the paperResult
Instruction followingLow-pressure challenge vs. directive, Appendix G.257.5% and 62.0% of the robust correct answers are already wrong without any instruction
Treating the challenge as evidenceRetention and correction, Table 9Under the directive, Opus-4.6 gives up 91.8% of correct judgments and changes 96.3% of wrong ones
Random noiseConfirming challenge, Appendix G.3No reversal, no error fixed
Persuasion by argumentsStatic vs. adaptive challenges, Figure 12Repeating the claim reverses more than giving a reason
Deference to authorityLawyer vs. researcher cue, Figure 7 and Table 10a28.9% with the lawyer cue, 1.1% with the researcher cue, no effect of seniority
First-person framingPlacebo cue, Table 10b95.0% without cue, 65.5% with placebo, 0.7% with researcher cue
CapabilityV4-Pro vs. Opus-4.6, Table 10aSimilar accuracy, but the cue lowers static reversals of V4-Pro only from 99.6% to 94.7%
Evaluation awarenessExplanation analysis, Tables 13 and 14Partly supported, but not enough on its own

What do the authors believe is the primary mechanism behind the strong influence of simple adversarial disagreements on frontier models? In particular, why do repeated disagreements without additional evidence cause models to reverse initially correct judgments? Can the authors provide further experimental evidence to distinguish between sycophancy, instruction-following tendencies, and other possible explanations?

Thanks for the question. We believe the primary mechanism is that the models defer to the position stated by the user (sycophancy), and that the explicit instruction to change the answer makes this stronger. Our evidence is as follows.

(1) To separate sycophancy from instruction following, we used two pressure levels. The low-pressure challenge only says “I disagree” and asks the model to reconsider, while the directive also tells the model to replace its answer. As reported in Appendix G.2, on the 577 instances that Opus-4.6 and 5.6-Sol judge correctly from the full record, the summary and every paraphrase, the low-pressure challenge already leaves 57.5% and 62.0% of the answers wrong after three turns. The directive raises this to 90.1%. So most of the effect is there even without any instruction to change the answer. As reported in Appendix G.3, we see the same when reasoning is enabled, where the directive raises the reversals of Opus-4.6 from 591 to 777 of 849 instances.

(2) As shown in Figure 12, static challenges that only repeat the same claim reverse 65 to 95% of the judgments in the low-pressure setting, while adaptive challenges that give a case-specific reason reverse 41 to 76%. A better argument does not lead to more reversals.

(3) Regarding repeated disagreements, we found that repetition is not really needed. As listed in Table 9c, under the directive the first challenge already overturns 275 of 314 correct judgments for Opus-4.6 and 281 of 314 for 5.6-Sol, and these almost never recover in the later turns.

AuthorsOpenReview ↗

Official reply from authors - part 3

How do the authors explain the substantial differences in the effects of challenger identity cues across models? For example, the AI safety researcher cue almost eliminates judgment reversals in Claude-Opus-4.6 but has a much smaller effect on DeepSeek and Qwen models. What evidence supports the hypothesis that this behavior is related to evaluation awareness rather than other model-specific response patterns?

We appreciate the question. While we cannot fully explain this difference with only black-box access to the models, we have several results that narrow down the possible reasons. We would like to note that we see evaluation awareness as a hypothesis, and we will make this clearer in Section 5.3.

We first would like to clarify one point. Without any cue, Opus-4.6 reverses 92.8% of its judgments under static challenges, which is similar to the other models. It only becomes resistant when the challenger states an identity.

(1) V4-Pro has almost the same baseline accuracy as Opus-4.6 (72.7% vs. 74.7%). However, as listed in Table 10a, the researcher cue only reduces its static reversals from 99.6% to 94.7%. So the difference is not due to capability.

(2) As reported in Appendix G.3, we repeated the comparison on 349 cases where Opus-4.6 and 5.6-Sol start from the same verdict. The researcher cue reduces the static reversals from 318 to 1 for Opus-4.6, but only from 323 to 158 for 5.6-Sol. So it is not due to different initial answers either.

(3) As reported in Table 12, the gap is still there when reasoning is enabled. The researcher cue reduces reversals by 86.8 points for Opus-4.6 and by 6.9 points for V4-Flash.

(4) As shown in Table 10b, the placebo cue (“I am reading this case.”) reduces the reversals of Opus-4.6 from 95.0% to 65.5%, while the researcher cue reduces them to 0.7%. For 5.6-Sol the numbers are 93.3%, 84.4% and 51.7%. So a first-person statement explains part of the effect, but the mention of an AI safety researcher adds much more.

(5) In our experiments with reasoning enabled, we counted how many model explanations explicitly mention being tested, as listed in Table 13. With the researcher cue, this goes from 2.0% to 7.1% for Opus-4.6 and from 2.6% to 21.2% for V4-Flash. With the lawyer cue, the explanations of Opus-4.6 become much longer but these mentions stay at 2.3%, so the increase is specific to the researcher cue. As described in Appendix H, V4-Flash also reverses less often when it mentions evaluation (62.2% vs. 89.1%).

(6) As shown in Table 14, we also looked at how this changes over the three turns. For Opus-4.6 the mentions of evaluation increase from 8.4% to 12.0%, while for V4-Flash they drop from 21.2% to 4.5%. This matches the behaviour of the two models. As reported in Appendix G.3, among the 137 instances where both models keep their judgment at the first challenge with the researcher cue, V4-Flash reverses 112 at a later turn, while Opus-4.6 reverses only 3.

At the same time, this evidence has clear limits, and we do not want to overclaim. V4-Flash still reverses in 62.2% of the explanations that mention evaluation, so mentioning the test is not enough to keep the judgment. Only 7.1% of the Opus-4.6 explanations mention evaluation, although the model keeps almost all of its judgments. Since Opus-4.6 only provides summarized reasoning, we may miss some cases, but we have no way to check this. In addition, as reported in Appendix G.3, Opus-4.6 is more sensitive to other social cues as well. Placing the challenger on the same team increases its reversals by 11.0 points, while this contrast stays within 4.7 points for all other models.

Therefore, we can not rule out that the effect comes from how each developer trains its models and not from evaluation awareness alone. We will discuss both possibilities in the revised version.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Summary for AC (why we prioritize usefulness over novelty)

Thank you very much for your time! We greatly appreciate all the constructive feedback and the kind recognition that our experiments during rebuttal have effectively addressed reviewer's pointers.

We'd like to make a final remark on the application-centered contribution of this work and why we prioritize usefulness over novelty claims:

Our goal of this study is to produce a reusable pipeline (the live benchmark and automated perturbation workflow) for the field of Human Rights/International Law, where most practitioners in this field come from legal background (rather than technical AI)

We chose to prioritize usefulness and minimize frictions for them, we believe this is a necessary/reasonable choice of design to ensure our pipeline is easy to adopt and automate, even if we have to let go of some novel components that would make it harder for practitioners to use.

As an application-centered paper (which differs from a paper that claims novel methodology), we believe usefulness/practicality triumphs novelty claims in our contribution, especially for the end users who may not be technical AI researchers, but could take greater benefits from AI via our effort. Thank you very much for your time!

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

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