As AI systems are increasingly used to automate AI R&D, misaligned systems could sabotage research intended to improve model safety and alignment. To stress-test defenses against such sabotage, we use a human expert as a proxy saboteur on AI safety research. We conduct a red-team/blue-team game where a human researcher runs AI safety experiments from scratch and auditors try to tell which were sabotaged and how. Given access to the full research transcript and the ability to run experiments, human auditors mostly fail to distinguish sabotaged from benign research: they achieve an AUROC of 0.59, not significantly better than chance, and fully identify the specific sabotage in only 17% of cases. Despite not being allowed to run experiments, the best frontier models outperform human auditors (Fable 5.1: AUROC 0.73, 32% full identification) within noise and weaker models perform comparably. When the saboteur chooses which experiments are attacked, rather than being required to sabotage every question given, sabotage identification drops further. Our results suggest that research sabotage by expert-level agents is difficult to detect with current auditing methods and provide a new setting for studying research sabotage.
Figures & tables
Figure 1: Research-sabotage auditing game. Benign and sabotaged runs yield separate traces. Auditors evaluate a single trace without knowing its condition.
Figure 2: Auditors’ final sabotage credences barely separate sabotaged from benign traces. (A) ROC curve computed from auditors’ 90-minute credences that their assigned trace was sabotaged, pooling 104 audits across 22 traces. Each point corresponds to a credence threshold: the y-axis gives the fraction of audits of sabotaged traces flagged at that threshold, and the x-axis gives the fraction of audits of benign traces flagged. The dashed diagonal indicates chance performance; the observed AUROC is 0.59 (primary 95% percentile interval: 0.37–0.77, from 4,000 crossed bootstrap resamples of experiments and auditors). (B) Final sabotage credences for individual audits of sabotaged traces (red; n = 55) and benign traces (green; n = 49). Horizontal bars span the 25th–75th percentiles, black ticks mark medians, and the vertical dashed line marks 50% credence.
Figure 3: Human audits usually fail to find sabotage mechanisms. Each bar represents a single sabotage mechanism (33 total), divided into major (top; n = 17) and minor (bottom; n = 16). Segments show the proportion of audits that fully identified, partially identified, or did not identify that mechanism. Averaging equally across mechanisms, the mean full catch rate is 17.4% overall (21.1% for major mechanisms; 13.4% for minor mechanisms). Bars are sorted within each panel by full, then partial identification. Results use the final 90-minute checkpoint of 55 human audits across 12 sabotaged traces, with 3–6 audits per trace.
Figure 4: The most powerful models identify sabotage mechanisms more often than humans. Left: AUROC computed from individual reports’ sabotage credences across all 22 traces, using 104 human audits and 44 reports per AI model. The dashed line indicates chance performance. Right: mean identification score across all 33 sabotage mechanisms, awarding 1 for full identification, 0.5 for partial identification, and 0 for a miss. We average reports within each mechanism, then give each of the 17 major and 16 minor mechanisms equal weight. Whiskers show 95% bootstrap intervals from 4,000 resamples of the ten experiments, conditional on the available reports. All nine AI auditors are included; “Claude Opus 4.8 (Given)” denotes the AI audits supplied to human auditors.
Figure 5: Humans and AI models often fail to predict experimental outcomes. Points show importance-weighted prediction accuracy, with full credit for correct answers and half credit for partially correct answers. Scores average reports within each experiment, then the six experiments equally. Whiskers are 95% bootstrap intervals from 4,000 resamples of the six experiments, conditional on the available reports. The analysis includes 22 human and 300 AI reports across ten models. The rubric and grading comparison are in Appendices F.1 and F.4.
Figure 6: Forecasts vary in how well they track human and AI audit performance. Left: the human saboteur’s auditability ratings on their original 0–4 scale, plotted against observed mean audit scores multiplied by four. Filled green points represent 90-minute human audits; hollow gray points represent AI audits. Lines are separate least-squares fits. Right: Pearson correlations between each forecaster’s predictions and human or AI audit scores, with 95% percentile intervals from 4,000 bootstrap resamples of the nine experiments represented by these traces. Trace versions stay together; forecasts and observed audit scores are held fixed within experiments, and resamples with undefined correlations are omitted. Audit scores give half credit for partial identification and weight major mechanisms 3x minor mechanisms. All comparisons use the same 11 traces.
Figure 7: Selecting attacks judged hardest to catch reduced mechanism identification but did not reduce suspicion. We assess auditing if the researcher used only the attacks they judged hardest to catch on their respective research questions. Ratings were made after completing the sabotage and before seeing audit outcomes. At each auditability threshold, we retain attacks rated at or below it, recompute mechanism identification on those attacks, and compare them with all ten benign traces for discrimination (AUROC). Sabotages 2A and 2B are averaged into one attack, leaving ten rated attacks. Panels show (A) AUROC, (B) mean mechanism-identification score against the threshold, and (C) the same score against the percentage of rated attacks retained. Identification gives half credit for partial diagnoses and weights major mechanisms three times minor mechanisms, as in Figure 6. Green curves show humans; gray curves show the equal average of all nine AI auditors. Whiskers are pointwise 95% intervals from 4,000 experiment-bootstrap resamples, conditional on retaining at least one attack. Appendix G.5 gives the selection procedure and its limitations.
Appendix figures & tables33 assets
Supplementary material from the paper’s appendix.
Appendix
Figure C1: Most sabotaged reports substantially change the reported conclusions. Left: the mean and full observed range of 30 report-divergence judgments per sabotaged trace, ordered by mean score. Right: separate means for the three grader models, each based on ten judgments. The horizontal ranges describe variation among judgments, not confidence intervals for a population of attacks.
Figure C2: Question-level differences and overall report divergence capture different aspects of sabotage. Each point is one sabotaged trace compared with its benign reference. The horizontal axis is the unweighted share of comparable questions with differing answers; the vertical axis averages 30 report-divergence judgments on a 0–10 scale. Answer-difference rates span 42.9–100%, clustering at 50% and 100% (four traces each); report scores span 5.3–8.9. Nearby points can overlap.
Figure C3: Larger result distortions do not consistently produce stronger audit outcomes. Each paired set of points represents one of twelve sabotaged traces. Filled points summarize final human audits; hollow points summarize all eighteen reports from the nine AI auditor models. Panels compare report-divergence means with mean credence, mean major-mechanism identification, and mean severity-weighted identification. Lines are separate least-squares fits; the annotations report Pearson r and Spearman ρ . Major mechanisms receive three times the weight of minor mechanisms in the final panel, with half credit for partial identification.
Figure C4: Result distortion and detection remain distinct quantities. Each point is one sabotaged trace; the horizontal axis measures how much its report differs from the benign report. Left: how much more suspicious human auditors found the sabotaged trace than the benign version, on average. Right: the share of major sabotage mechanisms found by combining all human audits, counting a mechanism as found if any auditor identified it and giving half credit for partial identification. Labels identify traces, and lines summarize the relationship. Combining reports this way assumes we can tell which diagnoses are correct.
Figure C5: Experiment size metrics show no consistent relationship with auditability. Average major-mechanism identification scores for human and AI audits are plotted against the experiment budget, number of logged file edits, and stored trace size. The horizontal axes use logarithmic scales; the fitted lines and correlations use those scales too. The budget panel includes ten traces with recorded budgets; the other panels include all twelve.
Figure C6: Later audits do not show a simple, consistent improvement. Gray lines follow individual participants across their assignments; green points show the mean at each assignment position. Error bars are 95% bootstrap intervals from 4,000 resamples of the auditors at that position. Left: mean major-mechanism score on sabotaged assignments. Right: Brier score on all assignments, where lower is better. The horizontal axis counts earlier audits from zero, including benign assignments and the early protocol round. Later positions contain fewer auditors and different traces.
Figure C7: Reported experience does not by itself explain auditor performance. Each participant contributes their average major-mechanism score across sabotaged assignments. The experience categories are described below; counts refer to people. Boxes show the middle half of participant scores and the median, whiskers extend to observations within 1.5 interquartile ranges, and points beyond them are shown separately.
Figure C8: Auditor probability accuracy varies, including after accounting for assigned traces. Each distribution contains the averages of fourteen participants who completed at least three audits, using both benign and sabotaged assignments. Left: mean Brier score, where lower is better; the dashed line at 0.250 represents always answering 50%. Right: each audit’s Brier score minus the average on the same trace, then averaged within each participant; values below zero indicate lower error than the trace average. Boxes show the middle half and median, with whiskers and outliers as in Figure C7.
Figure C9: Reported experiment compute does not establish how much spending helps an audit. Final audit outcomes against estimated expenditure on validation experiments, excluding agents used to investigate the trace itself. The horizontal axes use log(1 + spend) so zero-spend audits remain visible. Left: major-mechanism identification for 48 sabotaged audits. Right: Brier score for 91 audits. Fits and correlations use the transformed expenditure; missing estimates are excluded.
Reported activity
All audits (n=93)
Lower Brier (n=47)
Higher Brier (n=46)
Interactive or autonomous agents
87 (94%)
45 (96%)
42 (91%)
Validation experiments or reanalysis
51 (55%)
25 (53%)
26 (57%)
Report, results, or methodology reasoning
50 (54%)
25 (53%)
25 (54%)
Logs, diffs, or file history
42 (45%)
19 (40%)
23 (50%)
Code or stored-artifact inspection
39 (42%)
19 (40%)
20 (43%)
Provided browsing interface
29 (31%)
10 (21%)
19 (41%)
Appendix
Table 1: Reported tool use by final sabotage-credence accuracy. Entries are audit counts and within-column percentages. Categories overlap; long experiments are also counted under validation. Both observations at the median Brier score are assigned to the lower-Brier group. Omission from a free-text answer does not establish non-use.
Figure D1: Additional audit time produces an uncertain improvement in discrimination. Left: ROC curves from the same 104 human audits at each checkpoint. Right: AUROC with 95% percentile intervals from 4,000 resamples of the ten experiments, retaining all included traces and reports within each sampled experiment. The diagonal and horizontal dashed lines indicate chance ranking. These intervals condition on the available auditors and reports.
Figure D2: Most mechanism-identification opportunities remain misses after 90 minutes. Left: full, partial, and missed shares of the 155 audit–mechanism opportunities at each checkpoint. Right: means first computed for each mechanism across its auditors, then averaged equally within major or minor mechanisms, with half credit for partial grades. Whiskers are 95% experiment-bootstrap intervals. The two panels deliberately use different denominators, as indicated in their labels.
Figure D3: Later checkpoints add diagnoses but sometimes omit earlier identifications. The graph follows the same 155 human audit–mechanism pairs through the 30-, 60-, and 90-minute reports, with one shared column for the 60-minute checkpoint. Boxes give the number graded full, partial, or missed. Every arrow gives the number moving between two grades and uses its starting grade’s color. Box sizes and arrow widths are fixed; zero-count transitions are omitted.
Figure D4: Both benign and sabotaged traces attract widely varying suspicion. Each trace has a human row (green circles, above) and an AI row (gray squares, below), separated from neighboring traces by shading and horizontal rules. Points are individual final reports; thick segments show the middle half of credences and ticks mark medians. Humans contribute 3–6 reports per trace. AI rows contain two reports each from Fable 5.1, Sol, and Astra, selected by overall major-mechanism identification score. The dashed line marks 50% credence; identical values may overlap.
Figure D5: Humans and models identify different major and minor sabotage mechanisms. Each cell is the mean identification score for a mechanism across a system’s final reports, with 100% for full identification and 50% for partial identification. Columns are all 17 major mechanisms and 16 minor mechanisms, in separate panels. Human means use 3–6 reports for the corresponding trace; model means use two. Zero is an observed mean rather than an assertion of impossibility.
Figure D6: Combining human audits recovers diagnoses missing from individual reports. Expected major- and minor-mechanism scores after pooling 1–6 final human reports. Every eligible within-trace subset is equally weighted; partial identification receives half credit. Tick labels give the number of eligible traces. Whiskers show 95% intervals from 4,000 bootstrap resamples of the eligible experiments. At six reports only one trace is eligible, so no between-experiment interval can be estimated. The trace set changes after three reports; differences there also reflect composition.
Figure D7: Independent shorter audits can contribute complementary diagnoses. Equal active-human-minute comparisons: one 60-minute report versus two 30-minute reports, and one 90-minute report versus three 30-minute reports. Multi-report scores average all within-trace subsets and retain each mechanism’s best grade. Whiskers show 95% intervals from 4,000 experiment bootstrap resamples. Elapsed time, AI inference, report-writing overhead, and the cost of selecting diagnoses are not equalized.
Figure D8: Auditor combinations differ in the diagnoses they collectively recover. Expected pooled identification score from two reports, for every pair of auditor systems. Off-diagonal entries average all cross-system report pairs within each trace. Human diagonal entries average all distinct human pairs; model diagonal entries combine the two available procedures. Cells give equal-mechanism means, separately for major and minor mechanisms, with half credit for partial identification. The matrix is descriptive and was not used to select a prospectively tested portfolio.
Figure D9: Many audits identify no major sabotage mechanism. Final reports of sabotaged traces classified into four mutually exclusive outcomes: no mechanism identified, minor mechanisms only, some major mechanisms, or all major mechanisms. The left panel accepts partial identification; the right requires full identification. Human bars use 55 reports and each AI-model bar uses 24. The categories describe report-level coverage of that trace’s planted mechanisms.
Figure D10: Confidence only weakly separates matched and unmatched suggestions. Cumulative distributions of confidence in proposed fixes on sabotaged traces. The human panel includes 64 matched and 195 unmatched suggestions; the AI panel includes 191 matched and 876 unmatched suggestions across nine auditor models. Suggestions without a recorded confidence are omitted.
Figure D11: At low sabotage prevalence, most flagged traces would be false alarms. Left: empirical sensitivity and false-positive rate as functions of the final human credence threshold. Right: the fraction of flags expected to involve sabotage as the assumed prevalence varies, plugging in the observed rates at thresholds of 30%, 50%, and 70%. These curves omit estimation uncertainty and assume unchanged conditional flagging behavior. They are base-rate illustrations rather than calibrated deployment estimates.
Figure D12: Human–AI comparisons persist after excluding early audits or development experiments. Final AUROC and equal-mechanism mean major scores for the full dataset, the later human protocol only, and experiments 5–10 only. Whiskers show 95% percentile intervals from 4,000 bootstrap resamples of experiments, keeping reports and trace versions together: ten experiments for the full dataset and later protocol, and six after excluding development experiments. Conditions are vertically offset within each auditor row to keep their intervals visible. The development-set exclusion removes both benign and sabotaged versions of each excluded experiment. The early-protocol restriction leaves AI results unchanged.
Figure D13: Individual experiments affect the estimated performance of every auditor group. Green points give full-sample AUROC and major-mechanism means; gray points give the ten estimates obtained by omitting one whole experiment at a time. Segments span the observed leave-one-experiment range. All reports and all trace versions from the omitted experiment are removed together.
Figure D14: General model capability is positively associated with suspicion and diagnosis. ECI versus auditing AUROC (left) and mean identification score across all 33 mechanisms (right), across nine models. Lines are descriptive least-squares fits; annotations give Pearson r and Spearman ρ . Whiskers are 95% percentile intervals from 4,000 bootstrap resamples of the ten experiments, keeping each experiment’s reports and trace versions together. Dashed lines show the human audit means. ECI is treated as fixed; the intervals describe auditing uncertainty conditional on the observed reports.
Figure F1: Prediction performance varies across experiments and models. Each colored dot shows a system’s mean importance-weighted prediction score for one experiment. Correct answers receive full credit and partial answers half credit; ungradeable answers are excluded within each report. The six experiment colors share the same row without vertical offsets, so identical scores overlap.
Figure F2: Prediction reports vary substantially within the same experiment. Distributions of report-level, importance-weighted scores. The left panel includes 3–4 human reports per experiment; the right pools 50 reports across ten AI models. Boxes show medians and interquartile ranges, whiskers use the 1.5-interquartile-range convention, and outliers are displayed. The AI spread includes both model differences and sample variation. Counts are reports, with no individual human predictor labels.
Figure F3: Prediction scores track general capability, especially without Astra. Mean importance-weighted prediction scores for ten models versus Epoch Capabilities Index (ECI). Vertical whiskers show 95% percentile intervals from 4,000 bootstrap resamples of the six experiments; report and experiment averaging and bootstrap draws match Figure 5. These intervals condition on the recorded grades and hold ECI fixed. Lines and Pearson correlations summarize all ten models and the nine excluding Astra; the dashed line shows the human mean of 53.6%. Astra (166.31) and Fable 5.1 (164.47) use Epoch’s September 15, 2026 update; other ECI values retain the original analysis snapshot.
Figure F4: Author-given grades are lower than automated grades. Grade distributions for the same 317 human prediction entries that can be graded under both rubrics. Each matched question receives equal weight here; these bars do not use the importance-weighted, equal-experiment aggregation in Figure 5. Neither grader is treated as infallible.
Figure F5: Importance weighting changes some predictor averages and rankings. Left: paired model and human means under importance weights and equal weights per gradeable question. Right: importance-weighted minus equally weighted scores, with 95% percentile intervals from 4,000 paired bootstrap resamples of the six experiments. Both calculations first average reports within an experiment, then experiments equally; both give half credit for partial answers. Each resample uses the same experiments for both weighting rules, so the interval measures uncertainty in their difference. Thus the difference isolates question weighting within this common grade table, rather than reproducing every historical figure’s aggregation.
Figure F6: Prediction accuracy does not consistently track auditing performance. Top: nine models’ mean prediction scores versus their auditing outcomes on the same six experiments. Bottom: experiment-level prediction and auditing scores, separately for humans and the equal average of these nine AI models; numbers identify experiments. Whiskers on both axes and bracketed correlation ranges show 95% percentile intervals from 4,000 bootstrap resamples of experiments. Top panels use the same resampled experiments for prediction and auditing, keeping all nine models fixed; bottom-panel correlations resample the six paired experiment-level observations. Resamples with undefined correlations are omitted. Prediction reports are averaged within experiments. Major-mechanism scores average reports within each mechanism, then mechanisms equally; AUROC uses individual auditing reports. AI experiment-level outcomes average each model’s metric, rather than pooling credences across models. Lines are descriptive least-squares fits. The human comparison uses group averages rather than paired predictor–auditor scores, so it does not measure whether a better individual predictor becomes a better auditor.
Figure G1: Models differ in forecast range and correspondence with human outcomes. Scatter panels show the saboteur and nine AI forecasters on the same eleven traces. Forecasts retain their original 0–4 scale; the observed mean human identification score is multiplied by four. Lines are least-squares fits, with Pearson r and Spearman ρ . All panels share axis scales. The human saboteur provides an ease rating rather than a calibrated expected score.
Figure G2: Forecast correlations depend on which experiments are included. Full-sample Pearson correlations in green, alongside the results of omitting each of the nine represented experiments in gray. All trace versions from an omitted experiment are removed together. Separate panels use human and pooled AI outcomes; repeated marks share one row without vertical jitter. The segments show the range of leave-one-experiment estimates, not inferential error bars.
Figure G3: Repeated forecasts differ even for the same model and trace. For each model, the distribution across twelve traces of the standard deviation of its three forecasts on the original 0–4 scale. Boxes show medians and interquartile ranges, whiskers follow the 1.5-interquartile-range convention, and outliers remain visible.
As AI systems are increasingly used to conduct research autonomously, misaligned systems could introduce subtle flaws that produce misleading results while evading detection. We introduce Auditing Sabotage Bench, a benchmark for evaluating the ability of auditors to detect and fix sabotage in ML research codebases. Our benchmark consists of 9 ML research codebases with sabotaged variants that produce qualitatively different experimental results. Each sabotage modifies implementation details, such as hyperparameters, training data, or evaluation code, while preserving the high-level methodology described in the paper. We evaluated frontier LLMs and LLM-assisted human auditors on our benchmark and found that both struggled to reliably detect and fix sabotage: the best performance was an AUROC of 0.77 and a top-1 fix rate of 42%, achieved by Gemini 3.1 Pro. We also tested LLMs as red teamers and found that LLM-generated sabotages were weaker than human-generated ones but still sometimes evaded same-capability LLM auditors. We release the benchmark to support research on monitoring and auditing techniques for AI-conducted research.
We evaluate the propensity of frontier models to sabotage or refuse to assist with safety research when deployed as AI research agents within a frontier AI company. We apply two complementary evaluations to four Claude models (Mythos Preview, Opus 4.7 Preview, Opus 4.6, and Sonnet 4.6): an unprompted sabotage evaluation testing model behaviour with opportunities to sabotage safety research, and a sabotage continuation evaluation testing whether models continue to sabotage when placed in trajectories where prior actions have started undermining research. We find no instances of unprompted sabotage across any model, with refusal rates close to zero for Mythos Preview and Opus 4.7 Preview, though all models sometimes only partially completed tasks. In the continuation evaluation, Mythos Preview actively continues sabotage in 7% of cases (versus 3% for Opus 4.6, 4% for Sonnet 4.6, and 0% for Opus 4.7 Preview), and exhibits reasoning-output discrepancy in the majority of these cases, indicating covert sabotage reasoning. Our evaluation framework builds on Petri, an open-source LLM auditing tool, with a custom scaffold running models inside Claude Code, alongside an iterative pipeline for generating realistic sabotage trajectories. We measure both evaluation awareness and a new form of situational awareness termed "prefill awareness", the capability to recognise that prior trajectory content was not self-generated. Opus 4.7 Preview shows notably elevated unprompted evaluation awareness, while prefill awareness remains low across all models. Finally, we discuss limitations including evaluation awareness confounds, limited scenario coverage, and untested pathways to risk beyond safety research sabotage.
Robert Kirk, Alexandra Souly, Kai Fronsdal +2
UK AI Security Institute · UK AISI Research Affiliate
This technical report presents methods developed by the UK AI Security Institute for assessing whether advanced AI systems reliably follow intended goals. Specifically, we evaluate whether frontier models sabotage safety research when deployed as coding assistants within an AI lab. Applying our methods to four frontier models, we find no confirmed instances of research sabotage. However, we observe that Claude Opus 4.5 Preview (a pre-release snapshot of Opus 4.5) and Sonnet 4.5 frequently refuse to engage with safety-relevant research tasks, citing concerns about research direction, involvement in self-training, and research scope. We additionally find that Opus 4.5 Preview shows reduced unprompted evaluation awareness compared to Sonnet 4.5, while both models can distinguish evaluation from deployment scenarios when prompted. Our evaluation framework builds on Petri, an open-source LLM auditing tool, with a custom scaffold designed to simulate realistic internal deployment of a coding agent. We validate that this scaffold produces trajectories that all tested models fail to reliably distinguish from real deployment data. We test models across scenarios varying in research motivation, activity type, replacement threat, and model autonomy. Finally, we discuss limitations including scenario coverage and evaluation awareness.