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Paper summary
The paper presents MAPLEBench, a benchmark for privacy leakage by LLM agents on long-horizon tasks. It starts from 51 tasks in the Agents' Last Exam (ALE) benchmark. A generator-reviewer LLM pipeline adds synthetic sensitive "atoms" to each task. The atoms are placed in the task description, in structured files, or in unstructured files. The pipeline also adds sub-tasks that use the injected data (worth 30% of the task score) and ground-truth relevance labels. Agents run in a sandboxed Docker VM with real tools; mean trajectory length is 74.6 steps. In the "multi-agent" setting, every tool call that would change the output/directory is sent to a third-party LLM. This LLM is told to extract PII over 1-3 turns before it runs the call. Leakage is detected in three steps. (a) A three-tier Disclosure Detector (pattern matching, then Presidio, then an LLM judge), where each tier only sees the interactions the earlier tiers did not flag. (b) A "Leakage Estimator" that treats leakage as mutual information. It lower-bounds I(X;T) by I(Y;T|Q,D) for multiple-choice questions about an atom (Theorem 2.1) and estimates a pointwise version from LLM answer probabilities with and without the trajectory. (c) A two-phase LLM-plus-rules contextual integrity (CI) check that decides which disclosures are violations. Five backbones (GPT-4o-mini, GPT-5.6-sol, DeepSeek-v3.2, Grok-4.3, Mistral-large-3) are tested with and without a privacy prompt, in single- and multi-agent settings. The main claims are: (i) many atoms stay dormant for more than half of a trajectory before they appear, (ii) leakage clusters near the end of tasks, (iii) the privacy prompt does not reliably reduce leakage, and for DeepSeek-v3.2 it makes leakage worse (Figure 5), (iv) task reward and violations are positively correlated.
Critical strengths
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Relevant problem: Privacy in agents that run for a long time, use real tools, and talk to untrusted parties is an important topic. Most existing privacy benchmarks use short or simulated interactions, as the paper's Table 1 and Appendix A argue, so this is a real gap.
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Realistic tasks: Building on ALE's expert-curated, long-running tasks, with a real sandbox and real tools (Table 6), makes the setting more realistic than simulated tool outputs (e.g., PrivacyLens). The original ALE task and its deterministic grader are kept, so utility can be measured next to leakage (Appendix D.2).
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Temporal analysis: Measuring when leaks happen in a trajectory (Figure 3, the dormancy fraction in Eq. 4 and Figure 4, the tier comparison with a Mann-Whitney test) is a useful kind of analysis. Short-horizon benchmarks cannot do it.
Critical weaknesses
Although the paper targets an interesting setup it has the following limitations in my opinion:
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The detection and CI pipeline, on which every result depends, is weakly validated, and never against humans.
a) The main results depend on the Disclosure Detector plus a two-phase LLM-based CI labeling. The only check of the tier-3 judge and the CI labels is Table 2. Table 2 uses four trajectories from one model (GPT-5.6-sol, multi-agent, no privacy prompt) and only measures agreement between LLM judges. There is no human-annotated ground truth, so we have no precision or recall for detections and no accuracy for violation labels.
b) Even judge-to-judge agreement on CI labeling is modest: kappa 0.610 and 0.628 involving GPT-5.5, and 0.268 between DeepSeek-v3.2 and GPT-4o-mini. Appendix B itself says "more robust and reproducible semantic evaluation, particularly for contextual integrity labelling" is needed.
c) Picking GPT-5.5 as the judge because it agrees most with the other two shows centrality, not correctness.
d) Since every RQ counts "violations" produced by this pipeline, the claims about model differences, prompt effects, and the privacy-utility trade-off cannot be judged without a human-validated sample (e.g., a few hundred detections labeled by two annotators).
e) The Leakage Estimator is weakly grounded, its validation is circular, and it is not used for any main result. Theorem 2.1 is a direct consequence of the chain rule and the data processing inequality. It holds for the true distributions. The estimator in Eq. 1, however, plugs in LLM token probabilities for P(Y|T,Q,D) and P(Y|Q,D). These are not the true conditionals, so the pointwise quantity is no longer a lower bound on I(X;T) or on anything else.
f) Eq. 1 is a KL divergence between the LLM's answer distributions with and without the trajectory. It does not depend on whether the LLM picks the correct answer. If the trajectory makes the LLM confidently choose a wrong option, the score is still high and it counts as "leakage." The score should at least reward probability mass on the true index y*, e.g., a log-likelihood ratio on the correct answer.
g) The thresholds (tau, delta) are grid-searched "such that they maximize the agreement with the Disclosure Detector" (Sections 2.3 and 3.1). Table 3 then reports agreement with the Disclosure Detector as evidence of reliability. It is not clear the tuning atoms (50) are separate from the evaluation atoms. Either way, tuning to agree with the other detector cannot show that both are correct.
h) Overall agreement is weak (kappa 0.370, 67.4%, Table 3). The good-question subset (kappa 0.760) covers only 100 of 221 cases, and this check is limited to channel C3, one model, and 10 tasks.
i) The chosen threshold values, K, N_Q, and N_D are not reported.
j) The Leakage Estimator is not used in any of RQ1-RQ7. The "information-theoretic" part of the contribution is therefore a side tool, and the abstract and introduction overstate its role.
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The cascaded detector design undercounts semantic leaks and biases the tier-based analyses. Section 2.3 and Figure 6 state that each tier works only on interactions where earlier tiers found nothing. So if one interaction leaks a syntactic atom (say an email) and a semantic atom (say a diagnosis), tier 1 flags it and tier 3 never sees it. The semantic leak is lost. This is a correctness problem, not just an efficiency trade-off; the comparison with AgentLeak (Appendix D.3) presents only the efficiency side. It also biases the RQ3 comparison of dormancy between tiers (p = 1.73e-11, effect size 0.619). Tier-3 detections come only from interactions with no syntactic match, which is a selected subset, so "semantic information stays dormant longer" may be an artifact of the cascade. The claimed efficiency gain is also never measured (no LLM-call counts or cost compared with AgentLeak's design).
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Several findings may be produced by the benchmark design rather than by agent behavior.
a) Leakage near the end (RQ2, Figure 3, Figure 10): in the multi-agent setting the adversary is triggered only by calls that write to output which mostly happen late, and output writing is where atoms are expected to appear anyway. Late leakage is close to built in.
b) Dormancy (RQ3, Eq. 4): dormancy is the number of steps from injection to the first detection. That is time-to-first-use, not information "resurfacing" after it was handled and then left alone. An atom injected in the task description (step 0) and first written in a final report would count as "dormant" for most of the trajectory. That is the expected workflow, not a new risk. The analysis also uses appearances, not violations.
c) Privacy-utility trade-off (RQ7, Table 4): 30% of the task score comes from new sub-tasks that "require the agent to handle sensitive information" and are "often evaluated by the existence of the corresponding output files" (Appendix D.2). The example sub-task in Appendix D.2 requires a client_summary.md whose heading contains the portfolio label and account reference. So putting atoms into outputs is partly rewarded by the score, and some positive correlation between reward and violation count is expected by construction. Also, the 714 (model, task) points are pooled across settings, and the per-model relation is described as "highly variable" (Figure 17). It is therefore unclear whether the correlation reflects a real trade-off or differences between tasks or models. A within-task, within-model analysis, or a score based only on the original 70% ALE part, is needed.
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Claims of scalability and of advantages over prior work are not tested. The introduction says that whole-trajectory LLM judging (as in AgentDAM and ConVerse) "is not scalable" and that AgentLeak-style detection is "not suitable for long-horizon scenarios." Neither claim is tested: no baseline detector is run on MAPLEBench trajectories, and no runtime, cost, or accuracy comparison is given. Table 1 is a feature checklist, not empirical evidence.
Questions for authors
See weaknesses above
5 comments
Response 2/5
Cascaded detector design
We thank the reviewer for bringing this concert into light. We would like to clarify a subtle but important detail of our cascaded detection pipeline that may not have been clearly stated in the manuscript. The cascade operates at the sensitive atom+interaction pair level rather than filtering the entire interaction. Consequently, while an atom-interaction combination will not be investigated repeatedly, the same interaction will be investigated for other atoms. For instance, if an interaction includes an explicit email and a semantically disclosed medical condition, the former will be detected in tier 1 and the latter in tier 3. Therefore, cascade design does not undercount co-occurring disclosures. Instead, it will avoid invoking tier 3 for detecting the phone number in the interaction. We have fixed the description in the revised manuscript in Section 2.3 and Appendix D.3.
Response 3/5
On findings being artifacts of the benchmark structure
Late leakage:
We acknowledge that the temporal distribution of violations is influenced by the task structure where the output generation usually happens towards the end of the trajectory. In fact, this is strongly exhibited in Figure 10 (Figure 14 in the revised version) in Appendix E.3, which shows that most of the violations occur after the first output write. However, we would also like to clarify that output file writes are not the only mode of leakage and violations can occur within other tool calls such as exec and web search. We have added a clarifying statement to RQ2 in Section 3.2.1 of the revised manuscript.
Time to first use vs information resurfacing
We thank the reviewer for highlighting the difference between delayed first detection vs information resurfacing. We agree that the dormancy fraction in Eq. (4) (Eq. 15 of the revised version) measures the delay until first detection and consequently Figures 4 and 11 plot the same. We have clarified this in detail and changed the terminology in the revised manuscript (see Section 3.2.1 RQ3 and Appendix E.3). In order to directly observe information resurfacing along the trajectories, we conduct additional analyses as follows. For each trajectory+sensitive-atom pair with ordered distinct detection positions , let the normalized maximum detection-free gap be
$ \frac{1}{L}\max \left( \{ 0 \} \cup \{ \tau_i-\tau_{i-1}-1:2\le i\le K \} \right), $
where is the observed trajectory length (pairs without separated detection episodes receive zero). We plot the cumulative distribution function (CDF) of the normalized maximum detection-free gap in Figure 5 of the revised manuscript. We observe that among 661 pairs with repeated detections, around 20% have gaps exceeding 25% of the trajectory length. Approximately 6% of the pairs exceed 50% of the trajectory length. This provides clear evidence of information resurfacing after extended periods without detection.
Moreover, we observe that these repeated detections contribute to a significant number of CI verdict flips (i.e., when the current detection's CI verdict differs from that of the next detection), as evident from the transition analysis presented in Figure 11 (Appendix E.3) of the revised manuscript. This shows that an atom that was handled appropriately in one instance can subsequently be disclosed inappropriately, even with extended gaps between the events. For instance, among all reappearances with a 30–40% gap length, more than 11% of transitions are from benign to violation. These observations reveal a privacy risk specific to long-horizon trajectories, where sensitive information can cross contextual boundaries and cause CI violations across widely separated interactions. Together with our original study on the delay to first detection, these findings establish a distinct privacy phenomenon specific to long-horizon trajectories.
Privacy-utility trade-off
The benchmark intentionally incorporates subtasks requiring agents to handle sensitive information, reflecting realistic workflows where sensitive data must sometimes be processed to complete a task successfully. Our contextual-integrity evaluation distinguishes appropriate disclosures from those that violate the information's intended use or destination. For example, including a required sensitive identifier in an authorized output artifact can be contextually appropriate, whereas revealing that identifier to an unrelated third party may constitute a violation. Therefore, the inclusion of privacy-sensitive subtasks does not imply that successfully completing them must increase the number of CI violations. Nevertheless, we acknowledge that benchmark-specific scoring requirements and differences across tasks or models may influence the observed relationship between task reward and violations.
Response 1/5
Interpretation and validation of the Leakage Estimator
We agree that Theorem 2.1 establishes an information-theoretic bound for the true conditional distributions, whereas Eq. (1) uses LLM-estimated probabilities and therefore does not retain a formal lower-bound guarantee. In Section 2.3 under Leakage Estimator of the revised manuscript, we have clarified that the implemented estimator is an information-theoretically motivated proxy for trajectory-conditioned information gain in detail. Nevertheless, from the practical standpoint, the Leakage Detector provides complementary information particularly on partial disclosures and cumulative leakage.
The KL-based formulation is intended to capture changes across the entire answer distribution, including partial information that eliminates possible sensitive values without uniquely identifying the correct answer. Nevertheless, we acknowledge that confidently incorrect predictions can produce high KL divergence. The log-likelihood ratio (LLR) of the correct answer could be informative in such scenarios as per the reviewer's suggestion. However, the LLR of the correct answer is not universally better than using KL divergence, particularly when the goal is to capture partial information disclosures.
As a simple example, consider the without-trajectory prior distribution of (0.4→correct,0.2,0.2,0.2) where a slightly higher probability has already been assigned to the correct answer (potentially due to pre-trained knowledge of the model, patterns in distractors, etc.). Now, assume that the trajectory carries additional information concentrating more probability mass on the first two examples and the distribution shifts to (0.4→correct,0.4,0.1,0.1). In this scenario, the log-likelihood ratio of the correct answer will be 0 while the KL divergence will capture the distribution shift.
Investigating this matter deeper relevant to the empirical performance of the Leakage Estimator, we plot the computed average correct-answer LLR vs. the average KL divergence in Figure 22 (Appendix E.6) of the revised manuscript. The plots show a very high linear correlation (Pearson = 0.62 over all questions and Pearson = 0.93 over good questions only), indicating that both metrics would provide similar results. In the revised manuscript, we also clarify the estimator's hyperparameters in Appendix E.6.