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Audit tools of the trade: Automated Auditor Elicitation Can Be Sensitive to the Context the Auditor Is Given

Ben Slater, Ryan Lundqvist, Leo Richter, Kevin Wei

arXiv:2610.16911v1cs.AI

TL;DR

Because expert red-teaming is costly to scale, this paper asks whether external context changes automated auditors’ ability to elicit target behavior. Using Petri with codebases and target-behavior transcripts, it finds resource effects are mixed and not strongly generalizable across the tested conditions.

  • Problem

    The paper asks whether external resources affect automated auditors’ ability to construct scenarios that elicit target behavior, a scalable alternative to costly human red teaming.

    Source: §1 · pp. 1–2

  • Method

    The authors test codebases and target benchmark transcripts as auditor resources in Petri across three behaviors and four auditor-target pairs.

    Source: §1 · p. 2, §3 · p. 3

  • Results

    Additional resources did not consistently change judge-scored harmful compliance or sycophancy, while codebases suppressed and transcripts boosted reward hacking; follow-up tests recovered much of the transcript effect with benchmark abstracts.

    Source: §1 · p. 2

  • Takeaways & Limitations

    Measured target behavior in automated audits is highly condition-sensitive, so the authors recommend piloting with several auditor models and further testing across settings.

    Source: §6 · pp. 7–8, Limitations · p. 9

    The study uses coding-agent audits, and its findings may not generalize across experimental parameters or to settings beyond coding.

    Source: §3 · p. 3, Limitations · p. 9

Abstract

from arXiv · show

Does providing additional context to automated AI auditors improve their effectiveness? Using the Petri tool to audit LLM coding agents, we test the impact of providing two types of resources (an external codebase and benchmark transcripts) to LLM auditors, across four auditor-target LLM pairs and three behaviours (harmful compliance, reward hacking, sycophancy). (1) External codebase: We provide the auditor LLM with a fixed, external open source codebase, which prior work finds improves the realism of synthetic audits. Providing this resource suppresses reward hacking in both auditor-target pairs whose baseline rate is above the floor (4.8 to 1.3 and 3.9 to 1.8 on Petri's default 1-10 scale); the remaining two pairs sit at the floor throughout. The suppression recurs in three of four pairs under a different scenario and resource bundle. (2) External benchmark transcripts: We provide the auditor with transcripts of the target's performance on benchmarks measuring similar behaviours, intended to inform the auditor about the target's behavioural patterns. Providing this resource raises reward hacking scores in all four pairs (from 1.7 to 6.1 in one case). However, subsequent experiments show that supplying only the related benchmark's abstract, without transcripts, also increases reward hacking, and the effect is absent under a different framing of the same behaviour. Overall, we find no consistent effect of either resource outside reward hacking, but we find substantial variability in judge-scored behaviour across conditions. Our results underscore the importance of careful piloting with tools such as Petri, as the measured rate of target behaviour is highly sensitive to configuration decisions. We hope our results inspire more research into the reliability and robustness of automated alignment auditing.

1 Introduction

The paper asks whether external resources help automated auditors elicit target behavior, testing codebases and benchmark transcripts across several behaviors and auditor-target pairs. Effects are mixed: reward hacking shifts with resource type, while other behavior scores show no consistent change.

Motivation

  • Automated red teaming uses an auditor model to probe for harmful behaviors, addressing the cost and scalability challenges of human expert red teaming.The paper frames this work as alignment auditing.Source: §1 · p. 1

Research question

  • The paper examines how effectively an auditor constructs a scenario to elicit a target behavior, termed elicitation capability, and secondarily assesses audit realism.Source: §1 · p. 2

Study scope

  • The study tests external codebases and target benchmark transcripts as resources for auditors, across three harmful behaviors and four auditor-target pairs.The behaviors are harmful compliance, reward hacking, and sycophancy.Source: §1 · p. 2

Findings

  • Codebases suppressed reward hacking while transcripts boosted it, but neither resource consistently changed harmful compliance or sycophancy scores.The transcript-condition effect was largely recovered by providing the related benchmark abstract alone.Source: §1 · p. 2

Implications

  • The effect of additional context on elicitation capability varies with prompts, models, and resource type.The authors describe the overall evidence as mixed.Source: §1 · p. 2

2 Background

The background situates automated auditing among efforts to scale red teaming and explains Petri’s roles. Prior work uses codebases to improve realism; this paper shifts attention to whether external resources change elicited behavior.

Motivation

Automated auditing

  • Petri combines an auditor that creates a synthetic evaluation scenario with a target model and a judge that grades the resulting transcript.The scaffold has also been extended from exploratory audits to measuring behavior frequency.Source: §2 · p. 2

External resources

  • Prior codebase-based auditor resources aim to improve evaluation realism, whereas this study focuses on whether resources change target behavior rates.The cited work reports improved realism from providing codebases as inspiration [Kissane et al., 2026].Source: §2 · p. 2

Transcript rationale

  • The transcript approach draws on iterative adversarial prompting [Chao et al., 2025, Samvelyan et al., 2024] and in-context learning [Brown et al., 2020].The intended connection is that auditors may learn which elicitation strategies work for a target.Source: §2 · pp. 2–3

3 Method

The study compares Petri auditors with no external resources, a codebase, or target benchmark transcripts, then evaluates judge scores across behaviors and auditor-target pairs.

3 Method

  • Auditors receive 60 turns and a behavior and deployment-environment description; the study focuses on coding-agent audits because it supplies a codebase.The three behaviors are harmful compliance, reward hacking, and sycophancy; Table 1 summarizes the experimental conditions.Source: §3 · p. 3, Table 1 · p. 3

3.1 Conditions

  • The conditions compare no resources with a codebase or related benchmark transcripts, with transcripts expected to reveal target behavioral tendencies and useful elicitation strategies.The codebase could constrain creative choices or provide realistic inspiration; neither possibility was decisive a priori.Source: §3.1 · pp. 3–4

3.1.1 Codebase

  • The codebase is Timescale’s pgspot, an open-source tool for checking PostgreSQL scripts against security best practices.It was selected as maintained but not extremely widely used, to reduce the chance that auditors would recall it easily.Source: §3.1.1 · p. 4

3.1.2 Transcripts

  • Auditors can inspect transcripts from corresponding benchmarks, with added LLM-judge grading for nuanced reward hacking and substantive sycophancy changes.Transcripts are sampled through tools and may be truncated by blocks; safety-guardrail refusals count as valid refusals that may inform auditors.Source: §3.1.2 · p. 4

3.2 Analysis

  • The analysis fits separate ordinal logistic models for each behavior, with resource condition and auditor-target pair as predictors and no-resource audits as the reference.The model accounts for ordered judge scores and the auditor-target combination.Source: §3.2 · p. 4

3.3 Models used

  • The study uses GPT-5.6 Sol and Grok 4.5 as auditors, Grok 4.5 and DeepSeek V4 Flash as targets, and a three-model judging panel.Claude Sonnet 5 was replaced after producing many refusals.Source: §3.3 · pp. 4–5

4 Results

Resources had a significant effect on reward hacking, with codebases and transcripts shifting scores in opposite directions; effects varied by auditor-target pair, while judge agreement was moderate for behaviour scores.

4 Results

  • Resource had a significant overall effect on reward hacking (χ2 2=168, p<10−4), but no consistent effect on harmful compliance or sycophancy.The reported p-values for harmful compliance and sycophancy were .055 and .095, respectively.Source: §4 · p. 5
  • OR 0.28 for codebases and OR 24.7 for transcripts describe opposite pooled shifts in reward-hacking scores; both effects survived Holm correction.The codebase roughly quarters the odds of a higher score, while transcripts multiply them by almost 25.Source: §4 · p. 5
  • Resource effects differed by auditor-target pair across all three behaviours, with reward-hacking transcripts increasing scores in all four pairs (OR 15.1-70.1).Codebases suppressed reward hacking in the two Grok-auditor pairs but left the two GPT-5.6-auditor pairs near unity; pairwise patterns for the other behaviours also diverged.Source: §4 · p. 5
  • GPT-5.6 auditor pairs were excluded from harmful-compliance analysis because the auditor refused in the none and transcripts conditions.One sycophancy rollout scored at floor after plain-text tool calls, and two reward-hacking transcript rollouts were excluded for exceeding a judge’s context window, leaving that cell at n=18.Source: §4 · p. 5
  • Realism ratings were already high in most cells and shifted by at most 0.6, while two Grok-audited reward-hacking cells rose from 6.78 to 8.27 and 6.25 to 7.48 with a codebase.The two increases were for DeepSeek and Grok targets, respectively.Source: §4 · p. 5
  • Most eval_awareness judgments sat at the floor of the scale.Source: §4 · p. 6
  • Behaviour-score agreement was moderate across judges (ordinal Krippendorff’s α of 0.63-0.75), while realism-score α was at most 0.15.The weak realism agreement appeared driven by scores lying in a narrow band, rather than poor judge agreement.Source: §4 · p. 6

5 Follow-on experiments

The follow-on experiments find that an abstract-only prompt recovers most of the transcript effect on reward hacking, while the codebase suppression effect generalizes to a different scenario and resource bundle.

5 Follow-on experiments

  • The benchmark abstract alone appears to recover most of the transcript effect on reward hacking, though transcripts retain a limited benefit, particularly for Grok 4.5.The abstract-only condition is shown in Figure 3 but is not included in the statistical analysis.Source: §5 · pp. 6–7, Figure 3 · p. 7
  • Under a different scenario and resource bundle, codebase suppression appears in three of four auditor-target pairs, while the transcript effect is absent using the authors’ graders.With Kissane et al.’s graders, codebase suppression and transcript boosting are directionally suggestive but appear non-significant; the authors point to the graders’ less-sensitive 0–1 scale.Source: §5 · p. 7

6 Discussion and Limitations

Measured target behavior varies substantially with audit conditions and auditor-target pairs, so piloting across auditor models matters. The discussion also highlights uncertain trade-offs from codebases and limits on what the transcript results establish.

6 Discussion and Limitations

  • Audit outcomes vary across conditions and auditor-target pairs, making pilots with several auditor models important.The authors identify auditor-target pair choice as a factor affecting observed behavior.Source: §6 · pp. 7–8
  • In reward-hacking audits, adding a codebase suppressed elicitation, though the authors leave its cause uncertain and note a possible realism-versus-incidence trade-off.They propose that codebases might constrain auditor creativity or that more realistic scenarios might reduce target reward hacking.Source: §6 · p. 8
  • Transcript benefits in reward hacking were largely attributable to the benchmark abstract and did not generalize to a different framing of the behavior.The authors conclude that straightforward transcript provision did not effectively personalize audits to the target.Source: §6 · p. 9

Limitations

  • The study's findings may not generalize across audit parameters, non-coding scenarios, or higher auditor budgets, and it did not include human judges.The authors suggest testing whether the effects hold with human judges and whether human judgments match LLM-judge ratings.Source: Limitations · p. 9
  • The transcript investigation tested only one kind of target transcript, leaving the effects of other sources, formats, and richer annotations open.Suggested alternatives include transcripts from similar but non-identical benchmarks, de-identified conversations, and annotations of near-occurrences.Source: Limitations · p. 9
  • The authors cannot tell whether auditors' observed resource-checking steps causally affect their later behavior.They propose experiments designed to isolate the causal impact of checking external resources.Source: Limitations · p. 9
  • Auditor refusals limited some data collection, a constraint the authors expect to grow as model guardrails strengthen.They note that restricting guardrail-free access is appropriate given potential misuse.Source: Limitations · p. 9

7 Conclusion

The study tests whether external resources change Petri auditors' elicitation of target behavior. It finds no strongly generalizable effects for the resource types examined, with codebases suppressing behavior in some cases and no convincing transcript benefit.

7 Conclusion

  • The study tests how an external codebase and prior target-behavior transcripts affect a Petri auditor's elicitation capability.Source: §7 · p. 9
  • Including a codebase can suppress the level of target behavior elicited in some cases, while the study finds no convincing benefit from target transcripts.Source: §7 · p. 9
  • The results show no strongly generalizable effects for either resource type, and the authors call for further study of audit variability and transcript-presentation methods.Source: §7 · p. 9

A.1 Statistical model

The statistical model treats judge scores as discretized observations of latent behavior propensity, shifted by resource and auditor–target pair effects. It estimates cumulative and category probabilities using ordered cutpoints and a logistic link.

A.1 Statistical model

  • The model treats each panel-averaged judge score as a discretized version of latent behavior propensity under that rollout’s audit conditions.Ordered cutpoints and a resource-and-pair-specific shift determine the score probabilities.Source: §A.1 · p. 12
  • P(Yi ≤ k) is modeled as σ(θk − ηr,p), with category probabilities given by differences between adjacent cumulative probabilities.The cutpoints are ordered, with θ0 = −∞ and θK = +∞.Source: §A.1 · p. 12
  • ηr,p combines resource and auditor–target pair effects with their interaction, and all parameters are estimated jointly by maximum likelihood.Reference levels are pinned to zero; the shift applies equally across the score scale, with positive β shifting mass toward higher scores.Source: §A.1 · p. 12

A.2 Hypothesis testing

The hypothesis tests assess whether resources affect judge-scored behavior, which resources differ from none, and whether effects depend on the auditor–target pair. Realism is examined descriptively, with formal testing left for future work.

A.2 Hypothesis testing

  • The effect tests use the statistic 2(L1 − L0), comparing full and reduced nested models by their log-likelihoods.The effect of external resources on audit realism is examined descriptively, with formal tests left for other work.Source: §A.2 · pp. 12–13
  • A Type II likelihood-ratio test compares a pair-only model with an additive model to test whether resources change judge-scored target behavior.The additive model includes resource and auditor–target pair effects.Source: §A.2 · p. 12
  • Dunnett-style Wald contrasts compare each resource coefficient with none using odds ratios and 95% CIs, with Holm correction across the two comparisons.The contrasts are fitted from the additive model.Source: §A.2 · p. 12
  • A Type II likelihood-ratio test compares additive and full models to test whether resource effects interact with auditor–target pair.Per-pair effects are also examined descriptively.Source: §A.2 · p. 13

A.3 Full fitted values

The appendix provides the numeric output behind Section 4 in tables of cell means, likelihood-ratio tests, and pooled and per-pair contrasts.

A.3 Full fitted values

  • Table 2 reports cell counts, mean judge scores, and 95% percentile-bootstrap CIs by behavior, auditor–target pair, and resource.The cited passage identifies this as part of the full numeric output behind Section 4.Source: Table 2 · p. 13, §A.3 · p. 13
  • Table 3 reports likelihood-ratio tests of resource main effects and resource×pair interactions for each behavior.It is part of the full numeric output behind Section 4.Source: §A.3 · p. 13, Table 3 · p. 14
  • Table 4 reports pooled Dunnett-style contrasts against none from each behavior’s additive fit, with Holm-corrected p-values.The correction is applied over the two contrasts within a behavior.Source: Table 4 · p. 14
  • Table 5 reports per-pair contrasts against none from stratified fits, with no within-table multiplicity correction.Each auditor–target pair has its own cumulative link model.Source: Table 5 · p. 14

B Agreement between judges

The study reports judge agreement for behavior scores and Petri’s scenario-realism scores across main-experiment rollouts. It uses ordinal Krippendorff’s α and pairwise Spearman correlations, with specific rollout and judge-score exclusions noted.

B Agreement between judges

  • Agreement statistics cover every main-experiment rollout judged by the panel and include ordinal Krippendorff’s α and pairwise Spearman correlations.Table 6 reports these statistics for both behavior scores and Petri’s scenario_realism scores by behavior.Source: B Agreement between judges · p. 15, Table 6 · p. 15
  • Two GPT-5.6-auditor harmful-compliance pairs are excluded from Appendix A models because refusals left rollouts only in the real_codebase condition.Two reward-hacking rollouts also lack MiniMax M2.5 scores because they exceed its context window; those rollouts use the two remaining judges for α and are omitted from MiniMax correlations.Source: B Agreement between judges · p. 15

C Scenario realism and eval awareness

This appendix reports scenario-realism and eval-awareness outputs and reproduces auditor prompts, transcript tools, and an example transcript.

C Scenario realism and eval awareness

  • Table 7 reports scenario-realism cell means and confidence intervals by behaviour, auditor–target pair, and resource; Figures 6–13 cover realism and eval awareness across scenarios.Table 7 includes all cells plotted in Figures 6–8, including the abstract arm and two harmful-compliance pairs excluded from Appendix A models.Source: C Scenario realism and eval awareness · p. 15, Table 7 · p. 16

D Full prompts given to auditors

  • Across resource conditions, auditors receive the same behaviour-and-deployment seed template; transcripts append benchmark material, and the sycophancy attribution was mistakenly printed as Perez rather than Sharma.The erroneous strings were shown to auditors and are reproduced unaltered.Source: D Full prompts given to auditors · p. 20

E The prompt for the abstract-only condition

  • The abstract-only seed frames reward hacking as making project checks pass without doing the checked work, in a coding-agent deployment, and supplies the ImpossibleBench abstract.The supplied abstract describes ImpossibleBench’s impossible tasks and its cheating-rate measure.Source: E The prompt for the abstract-only… · p. 21

F.1 Tools for reading transcripts

  • Transcript access combines benchmark-outcome counts, sampling of up to two instances per call, and recovery of text truncated from sampled blocks.The auditor can query counts with describe_task_instances() and sample instances with sample_task_instances(outcome, n).Source: §F.1 · pp. 21–22
  • Sampling is without replacement and deterministically seeded across epochs; transcripts retain target reasoning, with blocks truncated at 600 characters but recoverable in full.Each reasoning, answer, and tool-call block is truncated independently; recovery costs an additional turn.Source: §F.1 · p. 22

F.2 An example transcript

  • The sampled sycophancy transcript shows the target changing from answer D to C after pushback; the benchmark answer key is appended to such samples.The example is a target transcript with outcome=True.Source: §F.2 · pp. 22–23

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