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Under review as a conference paper at ICLR 2027

Stateful Privacy-Utility Measurement for GraphRAG Evidence

Abstract

Large language models (LLMs) use GraphRAG to support structured reasoning by grounding answers in graph evidence. However, the same evidence that supports an authorized answer may also help reveal protected facts when combined with information from earlier interactions. Editing evidence to reduce this risk can change the generated answer, creating a history-dependent tradeoff between privacy and answer value. Existing work on release control, evidence transformation, and attribution leaves a gap in jointly comparing these effects for complete regenerated outputs under the same prior information. We introduce Stateful Privacy Funnel (SPriF), an offline framework for state-conditioned comparison of complete answer–evidence releases. SPriF regenerates answers for each evidence choice and a matched evidence-removal baseline while fixing the question, history, and other current evidence. A frozen LLM auditor measures incremental privacy cost from complete outputs, while a frozen reader separately measures reference-answer log-likelihood gains under the corresponding evidence contexts. Within a fixed graph-admissible inventory, the conditional funnel identifies the minimum auditor-measured cost meeting a specified reader-value requirement. Experiments on 8,206 evidence transformations across three KGQA benchmarks show that evidence-only scoring can miss minimum- cost complete releases, while relevant history can make history-free choices fail the same reader-value requirement. Under empty history and no other current evidence, post-hoc analysis examines admissible original releases with positive privacy cost and reference-hit answers. In 73.3% of these cases, lower-cost alter- natives also generate reference hits and provide positive reader value. To reduce the cost of scoring candidate releases, we evaluate partial measurement with learned or mean filling. Under a fixed 64-action measurement budget, full-inventory privacy-ranking Spearman reaches ρ ≈ 0.75 with 39.2% fewer test-time direct-scoring calls. Code is available at https://anonymous.4open.science/r/SPriF.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
GraphRAG, retrieval-augmented generation, privacy, inference leakage, knowledge graphs, privacy-utility tradeoff, evidence release, large language models

Reviews

Among:
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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_EZyMOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

The paper introduces SPriF, an offline framework for comparing GraphRAG evidence releases. It regenerates answers under the same history and uses matched evidence-removal baselines to measure incremental privacy cost from complete outputs and gains in reference-answer likelihood. It then identifies the lowest-cost release satisfying a utility requirement. Experiments on three KGQA benchmarks show that generated answers and prior history affect release comparisons, while higher likelihood-based utility does not guarantee answer correctness.

Critical strengths
  1. The evaluation method is well designed. SPriF jointly evaluates regenerated answers and evidence under the same history, accounting for privacy effects missed by evidence-only scoring. The experiments show that this can change which release has the lowest cost.
  2. The experiments are well designed and the results are clearly analyzed. Comparisons with irrelevant history and between learned and mean filling under the same measurement budget help assess each component’s contribution. The paper also distinguishes higher likelihood from correct answers, avoiding overstated claims.
Critical weaknesses

1.The paper does not verify whether lower privacy scores actually make it harder for independent attackers to infer the secret. In the control experiments, the auditor achieves 58.1% accuracy but has an average confidence of 95.4%, showing substantial overconfidence. Comparing results across models is not enough to establish that this score reliably measures actual privacy risk.

Questions for authors

Higher reference-answer likelihood does not guarantee a correct generated answer. Why is it used as the primary utility metric? What additional information does it provide beyond answer correctness, and do the experiments support this choice?

4 comments
AuthorsOpenReview ↗

Overall response to Reviewer EZyM

Thank you for your thoughtful and constructive feedback. We appreciate your positive assessment of the evaluation design and controlled comparisons. We address your comments in two replies:

  1. Comment 1 (Q1): The likelihood metric, its relation to correctness, and the additional AUROC analysis.
  2. Comment 2 (W1): Independent recovery and what the new evidence establishes about the privacy coordinate.
AuthorsOpenReview ↗

Comment 1 (Q1)

Q1: Why use reference-answer likelihood, what does it add beyond correctness, and do the experiments support this choice?

Thank you for this valuable comment. We appreciate your concern and would like to first clarify that reference-answer likelihood is used because it distinguishes releases that receive the same generated-answer correctness label, including releases that both produce an insufficient-evidence response. The reader-value coordinate ΔU\Delta U is the difference in teacher-forced, token-averaged log likelihood of the fixed reference answer between an action’s evidence context and the same case’s matched DROP context, measured in nats per reference-answer token (§4.2, p.5\color{#0969DA}{\texttt{§4.2, p.5}}). AttriBoT (Liu et al., 2025) approximates leave-one-out likelihood effects on a fixed response, while ContextCite (Cohen-Wang et al., 2024) fits a sparse surrogate to response probabilities under context ablations. These methods provide precedents for varying context while holding a response fixed. Here, the fixed target is the reference answer.

Sufficient context need not yield a correct generation (Joren et al., 2025), so we evaluate generated correctness separately. In the 61-case decision cohort, Intermediate alternatives exist in 59/61 cases (96.7%) under the likelihood criterion, but only 26/61 (42.6%) have a Hits@1-correct alternative. Of the cohort’s 2,225 Intermediate actions, 85.0% produce the insufficient-evidence response (§5.3(1), p.8\color{#0969DA}{\texttt{§5.3(1), p.8}}). A correctness label cannot distinguish these identical responses within a case, whereas reference-answer likelihood can vary with the evidence context. To address your request for empirical evidence, we have further conducted a post-submission AUROC analysis across 8,206 transformations from 112 cases. We have incorporated these results into Appendix D.1.3, Table D3, p.42\color{#0969DA}{\texttt{Appendix D.1.3, Table D3, p.42}} of the revised manuscript:

Correctness labelPooled AUROC [95% CI]Case-macro AUROC [95% CI]Evaluable cases for case-macro
Hits@10.430 [0.314, 0.584]0.768 [0.697, 0.834]66/112
Strict exact match0.701 [0.451, 0.920]0.881 [0.809, 0.940]32/112

Pooled AUROC uses all transformation rows. Case-macro AUROC equally weights cases containing both positive and negative labels. All four intervals use the same 2,000 whole-case bootstrap resamples from all 112 cases, retaining all actions within each sampled case. Each macro estimate includes only its sampled evaluable cases. Both pooled intervals include 0.5. The case-macro intervals exclude 0.5 on their respective conditional populations. We have not decomposed the difference between these estimates. The labels are the string-based diagnostics defined in D.1.3\color{#0969DA}{\texttt{D.1.3}}, rather than official benchmark evaluation. When correct generated answers are required, the paper reports an explicit correctness-constrained analysis (§5.3(3), p.9\color{#0969DA}{\texttt{§5.3(3), p.9}}). Hits@1 does not check whether the released evidence supports the answer. The case-macro results provide evidence of above-chance discrimination averaged over each label’s mixed-label cases. The experiments do not support using reference-answer likelihood as a correctness gate (§5.3(1), p.8, and §5.3(3), p.9\color{#0969DA}{\texttt{§5.3(1), p.8, and §5.3(3), p.9}}).

References

AuthorsOpenReview ↗

Comment 2 (W1)

W1: Does lower measured privacy cost correspond to lower independent recovery?

Thank you for this valuable suggestion. We agree that comparison across models alone is insufficient. We have therefore conducted a recovery evaluation with entailment labels fixed by construction, independently of either model, and incorporated it into §5.2(5), Table 1, p.8, and Appendix C.7, pp.38–39\color{#0969DA}{\texttt{§5.2(5), Table 1, p.8, and Appendix C.7, pp.38–39}} of the revised manuscript. LLM inference has been used to recover personal attributes from text (Staab et al., 2024) and to test candidate sanitizations (Pilán et al., 2025). These precedents motivate our use of LLM-based recovery as an empirical check alongside auditor scores. Auditor cost was positive in all 96 entailing views, where Gemma-3-27B-it selected the true value in every case. The synthetic test used a transcript-only five-option format. A history statement binds the target person to a route or medication, and a released key edge gives its value. Both are required to entail the protected fact. The main Qwen auditor’s costs are compared against these construction-defined labels, and Gemma’s recovery is measured separately. Across 48 case-worlds from 24 seeds, mean auditor cost in the 96 entailing views was 3.48 bits. In the 624 non-entailing views, Gemma selected “Cannot be determined from the conversation” in 616, mean cost was 0.07 bits, and 71 exceeded the 10−510^{-5}-bit tolerance.

The original four-option task allowed outside knowledge. Prespecified exclusions retained 35 of 68 matched-history cases. With no conversation shown (subject, relation, and options only), Gemma selected the true value in 28/35 cases. Empty-history DROP also yielded 28/35, with 26 shared successes. At least one action differed from DROP in only 4/35, 2/35, and 1/35 cases under empty, relevant, and irrelevant histories. The relationship between cost rankings and recovery success among transformed actions on the original workload remains unvalidated. The calibration error identified in your review also remains. In the synthetic setting, both auditor cost and recovery distinguish the entailing and non-entailing groups, with the exceptions reported above.

References

AuthorsOpenReview ↗

A Kind Request for Your Further Consideration

Dear Reviewer EZyM,

Thank you again for your time and thoughtful feedback on our paper. In our response, we clarified the definition and purpose of the likelihood-based reader-value coordinate and reported both pooled and case-macro AUROC results with confidence intervals (Appendix D.1.3, Table D3, p.42\color{#0969DA}{\texttt{Appendix D.1.3, Table D3, p.42}}). We also added recovery evaluations with a different model family, including a synthetic test with entailment fixed by construction, and explained the remaining limitations of recovery-based validation (§5.2(5), Table 1, p.8, and Appendix C.7, pp.38–39\color{#0969DA}{\texttt{§5.2(5), Table 1, p.8, and Appendix C.7, pp.38–39}}).

As the discussion period is drawing to a close, we would greatly appreciate it if you could review our responses and let us know whether they address your concerns. We would be very happy to answer any further questions.

For verification, the supplementary results, frozen inputs, model-output ledgers, and analysis scripts are available under post_submission/ in our anonymous repository. The overview and reproduction instructions are in post_submission/README.md.

Thank you once again for your time and consideration.

Best regards,
The Authors

Reviewer_7DwKOpenReview ↗
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2
Confidence
2
Informativeness
2
Presentation
3
Soundness
3
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Paper summary

This paper introduces an offline, stateful measurement framework for GraphRAG evidence release. Conditional on a fixed interaction history, query, and other evidence from the same round, the framework enumerates KEEP, DROP, minimization, and graph-substitution actions. It regenerates the complete answer and evidence, then measures changes in an auditor model’s posterior over a protected proposition relative to the DROP baseline. Using reference-answer likelihood as reader value, the paper constructs empirical privacy–utility frontiers over a finite action inventory and studies history effects, correct-answer preservation, and inexpensive scoring approximations.

Critical strengths

The evaluation object is carefully defined. Scoring only evidence can miss information disclosed by the generated answer. Regenerating and evaluating the complete output, while conditioning on history and same-round evidence, is therefore a valuable measurement choice .

The paper distinguishes graph membership, answer correctness, reference-answer likelihood, and auditor-relative incremental disclosure. It also retains ties and unattainable states rather than obscuring them. Importantly, the work is framed as offline measurement, not an online release controller, a differential privacy mechanism, or a formal confidentiality guarantee.

Critical weaknesses

W1. The central privacy coordinate has not been independently validated against protected-fact recovery.

In the balanced-label control experiment, the primary auditor has overall MAP accuracy of 58.1%, mean MAP confidence of 0.954, and ECE_true of approximately 0.385. Its accuracy on entailed exposure E2 is only 50.8%. Poor calibration alone does not necessarily invalidate action rankings. However, the cross-model analysis does not resolve this concern. On the frozen 12-case subset, the mean within-case Spearman correlations for raw privacy between Qwen and GLM/Gemma are 0.1653/−0.0609. For the clipped policy coordinate, the corresponding values are 0.6278/0.2281, with different valid-case fractions. A low measured cost may therefore reflect a particular auditor’s failure to recognize the protected fact, rather than a lower ability of an information recipient to recover it. The paper appropriately acknowledges model dependence, but this remains central to interpreting the “privacy” coordinate and differences expressed in bits.

A useful addition would be an independent fact-judgment or recovery evaluation on a prespecified subset of actions. The key question is whether lower measured costs, and especially the selected minimum-cost actions, correspond to lower recovery success. This is a construct-validity check, not a request for a formal security guarantee.

W2. Likelihood-based utility can select actions that do not preserve correct answers.

Among the 61 disclosure-positive decision cases, 96.7% admit an Intermediate alternative under the likelihood-based definition, but this falls to 42.6% when Hits@1 correctness is required. Across all Intermediate actions, 85.0% produce the predefined insufficient-evidence response. Among cases with a correct Intermediate action, 53.8% have only incorrect actions among their minimum-cost Intermediate choices. These results do not invalidate the descriptive framework. They do mean that a high prevalence of low-cost alternatives should not be interpreted as widespread preservation of useful answers. The paper already includes correctness-constrained analyses and KEEP/DROP mixture references. My concern is therefore not that these comparisons are absent, but that the current evidence does not establish a robust cost advantage at matched average correctness. The two reported mean differences on p. 48 are approximately 0.0307 and 0.0604 bits, without paired uncertainty intervals for those differences.

The correctness-constrained results should play a more prominent role in the main conclusions. Absolute exposure should also accompany incremental cost: a small increase relative to DROP may simply mean that DROP already reveals substantial information, rather than that the complete interaction is safe.

W3. The independent sample units and conditional scope of the reported proportions should be more prominent.

The 8,206 transformed actions are not 8,206 independent queries. Table B1 reports 112 cases in the complete transformation census, 61 cases in the main decision subset, and 49 cases for which all three groups are nonconstant in the history-ranking comparison. All 113 privacy-evaluable holdout propositions are YES by construction; balanced positive and negative labels appear only in the separate control experiment (Table B1 and Section B.4). For example, the statement that 73.3% of cases admit a correct alternative is conditional on the 30 cases in which KEEP is itself correct: 22/30, not 73.3% of all 61 decision cases or of general GraphRAG queries (p. 41, Table D3). Denominators and conditioning events should accompany the main proportions, and conclusions should remain tied to the evaluated proposition and case distributions.

Questions for authors
  1. On a prespecified action subset, does the privacy coordinate predict independent protected-fact recovery? Are minimum-cost selections stable under that evaluation?
  2. Using the existing frozen outputs, can you report paired intervals for cost differences against the KEEP/DROP mixture at matched correctness, together with absolute exposure under DROP and the selected action?
  3. Which main conclusions remain when restricting analysis to cases where the available witness directly supports the protected fact? Can the principal percentages consistently report their case counts and conditioning subsets?
8 comments
AuthorsOpenReview ↗

Overall response to Reviewer 7DwK

Thank you for your insightful and constructive feedback. We appreciate your recognition of the value of evaluating complete outputs conditioned on history and of the distinction between likelihood, answer correctness, and incremental disclosure. Your suggestions guided the additional recovery evaluations, uncertainty estimates, and clarifications discussed in the three replies below:

  1. Comment 1 (W1, Q1): Independent recovery on the original and synthetic cohorts, including what these evaluations establish about minimum-cost selections.
  2. Comment 2 (W2, Q2): Paired cost-difference intervals at matched mean Hits@1, absolute exposure on the same decision cohort, and the greater prominence given to correctness in the revised manuscript.
  3. Comment 3 (W3, Q3): Direct witness support, the scope of the reported percentages, and their denominators and conditioning subsets.
AuthorsOpenReview ↗

Comment 1 (W1, Q1)

Q1 (W1): Does the coordinate predict independent recovery, especially for minimum-cost selections?

Thank you for this valuable suggestion. We agree that cross-model agreement alone does not establish recovery-based validity. We have therefore conducted an additional recovery evaluation with Gemma-3-27B-it: on synthetic facts whose entailment is fixed by construction, auditor cost was positive in all 96 entailing views, where Gemma recovered the true value in every case. On the original workload, the minimum-cost ranking remains unresolved. We have incorporated these experiments into §5.2(5), Table 1, p.8, and Appendix C.7, pp.38–39\color{#0969DA}{\texttt{§5.2(5), Table 1, p.8, and Appendix C.7, pp.38–39}} of the revised manuscript.

We used Gemma-3-27B-it in a multiple-choice recovery task, distinct from the main Qwen auditor’s YES/NO scoring task. Prespecified exclusions retained 35 of 68 matched-history cases, with DROP, KEEP, and up to two MINIMIZE and two REPLACE actions per case. The original four-option task allowed outside knowledge. With no conversation shown (subject, relation, and options only), Gemma selected the true value in 28/35 cases. Empty-history DROP also yielded 28/35, with 26 shared successes. At least one evaluated action differed from DROP in 4/35, 2/35, and 1/35 cases under empty, relevant, and irrelevant histories. This limited action discrimination leaves little information about whether minimum-cost selections reduce recovery success.

A post-hoc variant prohibited outside knowledge, restricted recovery to the conversation, and added “Cannot be determined from the conversation” as a fifth option. Under empty history, Gemma selected the true value in 6/35 cases with KEEP and 1/35 with DROP. The KEEP-minus-DROP difference in the true option’s log probability was 9.05 nats, 95% CI [7.18, 11.11] (Appendix C.7, p.38\color{#0969DA}{\texttt{Appendix C.7, p.38}}). Neither the original cross-family correlations nor clipping establishes recovery-based validity of the minimum-cost selections.

The synthetic test used the same five-option format. A history statement binds the target person to a route or medication, and a released key edge supplies its value. Both are required for entailment. Across 48 case-worlds from 24 seeds, mean auditor cost in the 96 entailing views was 3.48 bits. In the 624 non-entailing views, Gemma selected “Cannot be determined from the conversation” in 616, mean cost was 0.07 bits, and 71 exceeded the 10−510^{-5}-bit tolerance. The prespecified four-cell interaction on the auditor’s raw p(YES)p(\mathrm{YES}) was positive in all 48 case-worlds, with mean 0.81, 95% CI [0.67, 0.94]. Its sign agreed in every case-world with the same interaction computed on Gemma’s true-option probability (Appendix C.7, p.39\color{#0969DA}{\texttt{Appendix C.7, p.39}}).

AuthorsOpenReview ↗

Comment 2 (W2, Q2)

Q2 (W2): Paired intervals at matched correctness and absolute exposure

Thank you for this valuable suggestion. We fully agree that this comparison needs paired uncertainty estimates and absolute exposure on the same cohort. We have now completed both analyses on the same 61 cases and incorporated the paired cost-difference intervals into Table D10, p.50\color{#0969DA}{\texttt{Table D10, p.50}} and the absolute exposure results into Table D11 (p.51)\color{#0969DA}{\texttt{Table D11 (p.51)}} of the revised manuscript. None of the four paired intervals establishes a cost advantage for either rule over the KEEP/DROP mixture at matched mean Hits@1. The absolute exposure analysis reports auditor-assigned true-proposition probabilities for DROP, KEEP, and each rule’s selected action. The main analysis re-matches mean Hits@1 within each resample. The difference is mixture cost minus rule cost, and rr is the KEEP weight in the mixture.

RuleDifference (bits)Re-matched 95% CIFixed-rr 95% CI
R-lik0.0307[−0.225, 0.340][−0.156, 0.205], r=7/30r=7/30
R-nonsentinel0.0604[−0.344, 0.480][−0.129, 0.278], r=2/3r=2/3

For R-nonsentinel, one of 2,000 resamples had more rule hits than KEEP hits and could not be matched by a KEEP/DROP mixture. The re-matched interval therefore uses 1,999 resamples. All four intervals include zero. Matching the aggregate hit rate also does not enforce each case’s likelihood constraint.

The absolute probabilities are:

ReleaseMedianMeanFraction ≥ 0.90Mean paired difference from DROP [95% CI]
DROP0.1480.2603.3%Baseline
KEEP0.6220.56231.1%+0.302 [0.233, 0.372]
R-lik selected0.1190.3084.9%+0.048 [−0.002, 0.103]
R-nonsentinel selected0.2940.45123.0%+0.191 [0.118, 0.267]

Rule rows use the final selected action, including KEEP fallback. These are auditor probabilities, not independent recovery rates. The DROP median and fraction at or above 0.90 agree with the decision-cohort row of Table C17 (p.30)\color{#0969DA}{\texttt{Table C17 (p.30)}}. Table D11\color{#0969DA}{\texttt{Table D11}} additionally reports means and paired differences. In the full census, the DROP fraction at or above 0.90 is 6.2% (Table C17\color{#0969DA}{\texttt{Table C17}}).

To give correctness a more prominent role, §5.3(1), p.8\color{#0969DA}{\texttt{§5.3(1), p.8}} now opens with the 26/61 Hits@1-correct alternative result, and the Conclusion, p.10\color{#0969DA}{\texttt{Conclusion, p.10}} now states that the correctness constraint uses reference-answer labels offline. Among those 26 cases, a post-hoc comparison finds that 14/26 (53.8%) have only incorrect actions among their minimum-cost Intermediate choices (§5.3(2)\color{#0969DA}{\texttt{§5.3(2)}}).

Reviewer_ZYJ2OpenReview ↗
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2
Confidence
2
Informativeness
2
Presentation
1
Soundness
2
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Paper summary

This paper proposes SPriF, an offline framework for GraphRAG that compares a privacy-utility tradeoff when the evidence for an answer is edited. The prior conversation history is taken into account, since the same evidence edit can have a different privacy cost depending on what the user has already seen. For each evidence edit candidate, the answer is regenerated and compared with the output where the evidence is removed. Privacy cost is measured by a fixed LLM auditor, and answer value is measured by another fixed LLM reader. SPriF identifies the minimum privacy cost that satisfies a given value requirement. Through the extensive experiments, the authors show that evidence-only evaluation can miss the minimum-cost output and that history can change the selection. They also evaluate a partial-measurement scheme that directly measures only some candidates and fills in the rest.

Critical strengths
  1. The motivation addresses a potentially overlooked issue. Editing the evidence in GraphRAG can alter the answer itself, and privacy risks vary depending on the preceding conversation.
  2. The argument that the entire output, including both the evidence and the regenerated answer, should serve as the unit of evaluation is compelling.
  3. The experiments are conducted carefully, and the statistical treatment is thorough.
  4. The work demonstrates a high level of reproducibility and transparency. The authors also report negative results and acknowledge that their measurements are model-relative rather than absolute guarantees.
Critical weaknesses
  1. While understandable considering the amount of experiments, the main claim should be clearly visibile in the main text for readablity wihtout relying on the appendix pages. For example, how the relevant/irrelevant histories are constructed is not described in the main text.

  2. The evidence retrieval process is not described in the main text. It can only be inferred from a single sentence in L400 stating that SubgraphRAG supplies 88.5% of the transformed actions.

  3. The writing is hard to follow. Nearly every sentence carries many conditions (admissible, attainable, evaluable cohort, post-hoc, etc.), making it hard to identify the core claims.

  4. Too many analyses weaken the core claims. The analyses are spread over different cohorts, conditions, and thresholds, and many of them are post-hoc or exploratory. No single decisive experiment supports the core claim.

  5. The LLM auditor, which determines the privacy cost, is not reliable. Its overall accuracy is 58.1%, its ECE is about 0.385, and its accuracy on entailing exposure is 50.8%.

  6. The auditor's measurements are not validated against actual privacy risk. The authors themselves state that the rankings have not been validated against independent fact recovery.

  7. There is no experimental comparison with existing methods (e.g., OCELOT, MNC, CQE).

  8. The protected facts are not private. They are chosen deterministically from a public benchmark (Freebase), so the experiments measure how much more an LLM believes an already public fact. The auditor's prior knowledge may also affect the results.

  9. The conclusions depend heavily on how utility is defined. Lower-cost alternatives exist in 97% of cases under the likelihood-based criterion, but only in 18% when the generated answer must exactly match the reference (Fig. 3).

Questions for authors
  1. What is the single key result that best supports the main claim, and can it be presented in the main text without relying on the appendix?

  2. What evidence shows that the auditor's measurements reflect actual privacy risk?

  3. How does SPriF compare with existing methods in terms of actual release decisions?

  4. Do the conclusions hold when the protected facts are genuinely private and not part of the auditor's prior knowledge?

  5. Which utility definition do the authors consider appropriate in practice, and do the conclusions hold under it?

6 comments
AuthorsOpenReview ↗

Overall response to Reviewer ZYJ2

Thank you for your detailed feedback on our paper. We appreciate your recognition of the motivation for evaluating complete outputs. We address your questions and describe the corresponding revisions in three replies below:

  1. Comment 1 (Q1–Q2, W4–W6): The key history-ranking result and the evidence connecting auditor cost to independent recovery.
  2. Comment 2 (Q3–Q5, W7–W9): Comparisons with existing methods, synthetic facts and model priors, and the choice of utility criterion when answer correctness is required.
  3. Comment 3 (W1–W3): The history-construction and candidate-source descriptions added to the main text, and the placement of the correctness-constrained result at the start of the main analysis.
AuthorsOpenReview ↗

Comment 1 (Response to Questions 1-2 and Weaknesses 4-6)

Q1 (W4): What is the single key result?

Thank you for this valuable comment. We appreciate your concern and would like to first clarify that the key result is the three-arm history comparison reported in the submitted main text: relative to the empty-history ordering, relevant history produces +0.130 greater measured action-ranking displacement than the matched irrelevant-history control, 95% CI [0.074, 0.189] (§5.2(2), p.7\color{#0969DA}{\texttt{§5.2(2), p.7}}). Table C12 (p.28)\color{#0969DA}{\texttt{Table C12 (p.28)}} gives the unrounded estimate, +0.1296, 95% CI [0.0741, 0.1887], across 49 cases with nonconstant clipped costs in all three arms. The history construction and primary estimator were fixed before the corresponding additional scoring runs (Appendix B.8\color{#0969DA}{\texttt{Appendix B.8}}). The alternative-availability and minimum-cost selection comparisons discussed under Q3–Q5 are post-hoc. The three-arm result shows that the auditor-measured cost ordering of releases changes with relevant prior history.

Q2 (W5–W6): What evidence connects the coordinate to independent recovery?

Thank you for this valuable suggestion. We appreciate your concern about whether the coordinate corresponds to independent recovery. To examine this relationship, we have further evaluated releases with Gemma-3-27B-it, a different model family from the main Qwen auditor. We have incorporated these additional experiments into §5.2(5), Table 1, p.8, and Appendix C.7, pp.38–39\color{#0969DA}{\texttt{§5.2(5), Table 1, p.8, and Appendix C.7, pp.38–39}} of the revised manuscript. On synthetic facts whose entailment is fixed by construction, auditor cost was positive in all 96 entailing views, and Gemma selected the true value in each of them. In the synthetic test, a history statement binds the target person to a route or medication, and a released key edge gives its value. Both are required to entail the protected fact. Gemma answered from the conversation alone, choosing among four candidate values and “Cannot be determined from the conversation”. Across 48 case-worlds from 24 seeds, mean auditor cost in the 96 entailing views was 3.48 bits. In the 624 non-entailing views, Gemma selected the fifth option in 616, mean cost was 0.07 bits, and 71 exceeded the 10−510^{-5}-bit tolerance.

The original four-option task allowed outside knowledge. Among 35 cases retained from 68 under prespecified exclusions, Gemma selected the true value in 28/35 cases with no conversation shown (subject, relation, and options only), and in 28/35 with empty-history DROP. The two conditions shared 26 successes. Across the evaluated actions, at least one outcome differed from DROP in 4/35, 2/35, and 1/35 cases under empty, relevant, and irrelevant histories. The calibration figures cited in W5 are those reported in §5.2(4)\color{#0969DA}{\texttt{§5.2(4)}} and remain unchanged. Privacy cost is the positive part of the change in the log2 probability assigned to the true label, relative to the same case’s matched DROP view (§4.2, p.5\color{#0969DA}{\texttt{§4.2, p.5}}). It measures an auditor-relative increment, not calibrated recovery risk. Neither subtracting DROP nor clipping resolves the calibration errors. Fine-grained rankings among transformed actions on the original workload remain unvalidated. In the synthetic task, auditor cost and recovery both differ between entailing and non-entailing views under the stated construction and recovery format.

AuthorsOpenReview ↗

Comment 2 (Response to Questions 3-5 and Weaknesses 7-9)

Q3 (W7): How do actual release decisions compare with existing methods?

Thank you for this valuable comment. We appreciate your concern about comparison with existing methods. As discussed in §2\color{#0969DA}{\texttt{§2}}, OCELOT, MNC, and CQE do not evaluate the privacy cost of a disclosure jointly with an LLM answer regenerated from it. We have therefore not conducted a head-to-head implementation comparison with these methods. SPriF evaluates each candidate’s complete output after regenerating the answer. CQE enforces logical confidentiality policies. OCELOT calibrates disclosure-operator costs and accumulates them in a budget ledger, and MNC selects task-sufficient disclosures under risk and budget constraints.

The post-hoc descriptive comparisons in D.5–D.6\color{#0969DA}{\texttt{D.5–D.6}} evaluate four structural rules, KEEP/DROP mixtures, and two offline rules using measured costs and reader values. On the same 61 cases, KEEP has mean cost 1.7515 bits and Hits@1 49.2%. R-lik has mean cost 0.3780 bits and Hits@1 11.5%. R-nonsentinel has mean cost 1.1073 bits and Hits@1 32.8% (Table D9, p.49\color{#0969DA}{\texttt{Table D9, p.49}}). The two offline rules were fixed after inspecting existing outcomes, as stated in D.6\color{#0969DA}{\texttt{D.6}}. Both re-matched paired cost-difference intervals against mixtures matched to mean Hits@1 include zero (Table D10, p.50\color{#0969DA}{\texttt{Table D10, p.50}}). These estimates do not establish a cost advantage for either rule over a KEEP/DROP mixture at matched mean Hits@1. SPriF is an offline framework for comparing candidate releases, and the paper does not evaluate online controller performance (Appendix G.2, p.72\color{#0969DA}{\texttt{Appendix G.2, p.72}}). These comparisons describe release-rule choices within the evaluated candidate inventory.

Q4 (W8): What about genuinely private facts and model priors?

Thank you for this valuable suggestion. We appreciate your concern about the role of model priors. To address it, we have further evaluated synthetic facts involving newly constructed entities and no public benchmark entity. We have added this evaluation to Appendix C.7, p.39\color{#0969DA}{\texttt{Appendix C.7, p.39}} of the revised manuscript. On Freebase, subtracting matched DROP measures an increment but does not eliminate model dependence. In the original recovery task, Gemma selected the true value in 28/35 cases with no conversation shown (subject, relation, and options only), against a chance level of 1/4. This is Gemma’s baseline and does not identify the source of Qwen’s responses.

In the synthetic task, a history statement binds the target person to a route or medication, and a released key edge gives its value. Both are required for entailment. Auditor cost was positive in all 96 entailing views, and exceeded the 10−510^{-5}-bit tolerance in 71 of the 624 non-entailing views. These facts also show history-dependent cost: mean KEEP cost was 3.41 bits higher under the target person’s own binding history than under another person’s binding, with a 95% seed-bootstrap CI of [2.57, 4.22]. The prespecified four-cell interaction on the auditor’s raw p(YES)p(\mathrm{YES}) was positive in all 48 case-worlds. Generalization to real sensitive facts is untested.

Q5 (W9): Which utility definition should be used when correctness matters?

Thank you for this valuable comment. We appreciate your concern and would like to first clarify that the submitted paper evaluates correctness requirements by adding a Hits@1 condition to the likelihood criterion, and a lower-cost Intermediate alternative then exists in 26/61 cases (42.6%), against 59/61 (96.7%) under the likelihood criterion alone and 11/61 (18.0%) under strict exact match (§5.3(1), p.8\color{#0969DA}{\texttt{§5.3(1), p.8}}). Conditional on KEEP being Hits@1-correct, the rate is 22/30 (73.3%, 95% CI [56.7%, 86.7%]) (Table D4, p.43\color{#0969DA}{\texttt{Table D4, p.43}}). The three-arm history-ranking result under Q1 orders actions by clipped privacy cost and does not use a utility threshold or correctness criterion.

In a separate full-inventory analysis over 113 privacy-evaluable cases, the Hits@1 constraint is attainable at u=0u=0 in 71 cases (62.8%). The mean of the casewise minimum costs over those 71 attainable cases is 0.7830 bits (§5.3(3), p.9, and Appendix D.3, p.44\color{#0969DA}{\texttt{§5.3(3), p.9, and Appendix D.3, p.44}}). Correct lower-cost alternatives exist in a subset of cases. The higher 96.7% rate applies to the likelihood criterion alone. The string-based correctness diagnostics also do not verify evidence support. Section 5.3(1), p.8\color{#0969DA}{\texttt{Section 5.3(1), p.8}} now opens with the 26/61 Hits@1-correct alternative result. The Conclusion (p.10)\color{#0969DA}{\texttt{Conclusion (p.10)}} now states that the correctness constraint uses reference-answer labels offline.

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