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Withdrawn from ICLR 2027

SSP-Bench: A Hybrid Data Generation Framework for Safety, Security, and Privacy Evaluation

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Evaluation of large language models (LLMs) for safety, security, and privacy (SSP) relies heavily on static benchmarks, which suffer from score saturation, data contamination, and aggregation artifacts, and fail to capture sensitivity to linguistic variation. As a result, models that perform well on fixed test sets often fail under semantically equivalent rephrasings. We introduce SSP-Bench, a dynamic benchmarking framework that generates evaluation instances on demand while preserving domain consistency. The framework ensures label validity through externally grounded sources, enforces scope via service-specific validation, and calibrates difficulty using a multi-model steering panel. Benchmark construction is formulated as a multi-objective optimization problem over difficulty, separability, novelty, and diversity. Across 24 models and four SSP services, SSP-Bench reveals systematic failures of static evaluation, including near-zero correlation in safety rankings due to construct mixing, strong safety–over-refusal coupling, and hidden within-family regressions. These results show that static benchmarks can misrepresent model behavior, motivating dynamic, deployment-relevant evaluation.

Primary area:
datasets and benchmarks
Keywords:
Dynamic Benchmarking, Ranking Stability, Safety Alignment, Privacy Leakage

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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_1ySrOpenReview ↗
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Paper summary

The paper introduces SSP-Bench, a dynamic benchmark generation framework for evaluating LLM safety, hallucination, over-refusal, and privacy. It combines external-source grounding, service-specific validation, model-guided generation, and item selection based on difficulty, separability, novelty, and diversity. Separate model panels are used for generation feedback, benchmark assembly, and final testing. Experiments across 24 models compare the generated benchmarks with static leaderboards and examine ranking stability, selection strategies, steering-panel composition, and evaluator sensitivity. The authors report that dynamic evaluation exposes differences obscured by static aggregate scores and attribute the particularly low agreement in safety rankings to the aggregation of heterogeneous evaluation constructs.

Critical strengths
  1. A useful design for controlled dynamic benchmark construction. The framework combines source-grounded generation with validity checks and separates generation feedback, benchmark assembly, and final testing across different model panels. This is a sensible design for producing informative evaluation items while reducing direct adaptation to the models used for the final rankings.

  2. Broad evaluation with relevant validation efforts. The study covers four evaluation services and multiple model families and sizes, and includes selection-objective ablations, steering-panel substitutions, repeated generation, and human checks of safety and over-refusal items. These experiments provide a useful basis for assessing the generated data and understanding how benchmark construction choices affect evaluation.

Critical weaknesses
  1. The central explanation of construct mixing is not sufficiently supported by the stated scoring conventions. Sections 4.1 and E.2 argue that strong refusal lowers moderation scores because it produces less content for moderation classifiers to flag. However, aiXamine documents both its OpenAI Moderation and Perspective API scores as the fraction of outputs classified as safe, which appears inconsistent with this explanation. The actual score directions, transformations, and aggregation procedure need to be reconciled before attributing the near-zero static–dynamic correlation to the proposed mechanism. This directly affects one of the paper’s principal empirical contributions.

  2. The main safety results and evaluator-validation results are not consistently reported. Table 2 reports dynamic safety rates of 85.5% for Gemma-3-27B and 51.7% for Llama-3.3-70B, whereas Table 10 reports primary-judge Safeguard rates of 13.52% and 26.30%, respectively. Appendix C describes re-evaluating the safety benchmark responses, but does not explain differences in datasets, runs, or scoring settings that would account for these discrepancies. Until the results are reconciled, it is difficult to establish that the evaluator-robustness analysis validates the main reported findings.

Questions for authors

Please address the clarification requests raised in the weaknesses above, particularly the interpretation and aggregation of moderation scores, and the discrepancies between Tables 2 and 10. Please specify the datasets, model versions, and judge configurations underlying these results.

1 comment

Thank you for the careful reading of the moderation scores and of Tables 2 and 10.

All three reviewers noted that Tables 2 and 10 of the submission disagree. Table 10 was a separate judge comparison on a smaller, differently selected item set (details in W2 below). The revision evaluates every model under one protocol, so for each service all tables use the same items and responses.

  • Panels. 40 models from eight developers and 17 families. 14 calibration models (five developers, seven families) select the items, and 26 testing models (seven developers, ten families) play no part in selection. Static scores cover 21 testing models, and we are collecting them for the remaining five API models.
  • Selection. 2PL item information, fitted on the calibration panel alone, replaces the outcome variance as separability (details in 2iMc, W1a).
  • Robustness. An independent second judge per service (τ=.83–.95), with WildGuard replacing LlamaGuard 4 for safety because of its low recall (details in W2 below), recalibration without one or two families (τ≥.90), 100 random family splits, and a source-clustered bootstrap that keeps all 27 highlighted differences significant (Appendix D).
  • Human validation. Three blinded annotators agree on the expected behavior for 86–87% of 200 items (Gwet's AC1=.90), and the safety results hold on the items all three label unsafe (Appendix E). A human annotator sides with the primary judge on 78% of 50 safety and 82% of 50 over-refusal judge disagreements (Appendix D.3).

The main findings hold. Our safety benchmark ranks models like the static refusal tests (τ=.775), not like the static aggregate (−.153), which mixes in moderation (details in W1 below), and over-refusal and privacy spread the testing models over 48.5 and 99.2 points, against 24.9 and 42.7 for static tests. The nine testing models within two points of the best static safety score span 21.0–83.8% on our benchmark.

(W1): Score direction and construct mixing

All nine static tests report the fraction classified safe, so higher is safer throughout. Their unweighted mean is A=(7R+2M)/9, where R averages seven refusal tests and M two moderation tests. We clarified Section 4.1 and corrected the short-response explanation.

The aggregate discrepancy is arithmetic. Across the 21 testing models with static results, refusal scores have a standard deviation of 1.83 points against 23.97 for moderation, so even after the 7:2 weighting moderation contributes 3.75 times the spread. Of the 131 model pairs that the two components order differently, the aggregate follows moderation in 110 (84%). Adding moderation loses 103 pairwise agreements with dynamic safety and gains six. The aggregate therefore tracks moderation (Kendall τ=.800), while dynamic safety tracks refusal (.775), against −.354 and −.153 with moderation and the aggregate. The revision adds this decomposition to Appendix F.1. Qwen3.5 shows the divergence: 99.5–99.7% on static refusal and 94.3–96.3% on dynamic safety, but 35–41% on moderation, which puts it at the bottom of the aggregate.

The decomposition holds under WildGuard (refusal, moderation, aggregate τ=.714, −.343, −.181), on the full pool before selection (.771, −.343, −.162), within direct, framed and other requests, in all nine harm families, and when any testing family is excluded (aggregate–moderation at least .65, dynamic–refusal .66–.82). Safety-oriented language also coexists with unsafe help: a disclaimer opens 83.3% of Phi-4's unsafe answers. Refusal and moderation should therefore be reported separately.

(W2): Main results and judge robustness

Table 10 used a separate re-selection that weights difficulty five times more than our selection. With the same labels, 18 of its 20 models score lower on it, so the gap comes from the items, not the judge. In the revision Gemma-3-27B scores 10.5% under the primary judge in every table, and Llama-3.3-70B is a calibration model.

On the same responses, WildGuard flags 46.8% of Safeguard-unsafe answers against 6.7% for LlamaGuard 4, whose model card reports 69% English output-filtering recall. On safety, Safeguard and WildGuard agree at τ=.830 (ρ=.958); where they disagree, WildGuard mostly misses harm after a disclaimer or in fiction (Human validation above).

(Q1): Data and evaluation configuration

The safety items come from two separately generated steering trajectories. Each model answers each item once with the system prompt "You are a helpful assistant." The primary judge is gpt-oss-safeguard-120b with the stated safety policy, high reasoning effort, temperature 0 and a 2,048-token limit, and WildGuard rates the same answers. Provider blocks count as responses of the served system, and excluding them leaves the ranking unchanged (τ=.981). The generator is gpt-4.1-mini with provider content filters disabled, the in-loop checks use gpt-oss-120b, and neither is a testing model.

Reviewer_2iMcOpenReview ↗
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2
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3
Informativeness
2
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Paper summary

The paper introduces SSP-Bench, a dynamic evaluation framework that uses LLMs to generate new evaluation items grounded in real sources. The evaluation covers the 4 categories including safety, hallucination, over-refusal, and privacy. The authors find that dynamic safety rankings are uncorrelated with the aiXamine static leaderboard. They discuss an important concept of “construct mixing” that contributes to this difference. SSP-bench also reveals some new safety findings such as Gemma3 safety inverse scaling.

Critical strengths
  • The static vs. dynamic benchmark discussion is meaningful for understanding and improving model evaluation.
  • The construct-mixing analysis is interesting and highlights an understudied issue in evaluation. The paper provides an actionable recommendation to report constructs separately to provide more insights.
  • There are over 20 models studied in the paper, and 4 different services are covered. The authors also include a collection of ablation studies.
Critical weaknesses
  • There is a big gap between the size and capability of the steering/ evaluation panel and the final test model panel. The evaluation items are selected because the older, smaller models diverge on them, but this does not necessarily generate useful evaluation data for bigger, stronger model. For example, in Table 4, the dynamic over-refusal performance is near saturate/ not separable.
  • The evaluation focuses on rank agreement, but rank disagreement alone does not suggest which benchmark is correct. The absolute score/ performance still matters a lot in actual deployment, and Table 10 shows that different judge models themselves can have very different absolute scores.
  • The benchmark novelty claim is weak. For example, the hallucination category items are LLM-written QA pairs from Wikipedia paragraphs. The static tests include datasets like SimpleQA, TriviaQA and TruthfulQA, which are written by (diverse) human writers, which carry their own styles. Therefore, the large embedding distance is not surprising. Similar critique can be made for the privacy category. Under that definition, the more “novel” the items, the more static–dynamic rank disagreement could potentially be attributed to the evaluation sets testing different things.
  • The overall presentation and clarity of the paper can be improved. Eg. clarity of main figure (Figure 1), the methodology section also sounds more complicated than it needs to be, the results tables are fully numbers without highlights.
Questions for authors
  • If you swap the models in the evaluation panel to other models, are the selected data and downstream evaluation outcome similar? This ablation is missing in the main paper.
  • Some model setup details are missing in the paper. For example, what is the generator model that creates the evaluation data? What is the LLM that does the saliency scoring pass assessment (F.1)
  • How did you check for the scope consistency requirement between static and dynamic benchmarks?
  • Appendix C states that gpt-oss-safeguard-120b is the primary safety judge, so the Safeguard column in Table 10 should match the dynamic safety rates in Table 2, but they have substantial disagreement for several models, such as Gemma-3-27B, Llama3.3-70B.
1 comment

Thank you for the questions on the calibration panel and novelty.

All three reviewers noted that Tables 2 and 10 of the submission disagree. Table 10 was a separate judge comparison on a smaller, differently selected set (details in 1ySr, W2). The revision evaluates every model under one protocol, so for each service all tables use the same items and responses.

  • Panels. 40 models from eight developers and 17 families. 14 calibration models select the items, and 26 testing models play no part in selection. Static scores cover 21 testing models, and we are collecting them for the remaining five API models.
  • Selection. 2PL item information, fitted on the calibration panel alone, replaces the outcome variance as separability (W1a).
  • Robustness. An independent second judge per service (τ=.83–.95), recalibration without one or two families (τ≥.90), 100 random family splits, and a source-clustered bootstrap that keeps all 27 highlighted differences significant (Appendix D).
  • Human validation. Three blinded annotators agree on the expected behavior for 86–87% of 200 items (Gwet's AC1=.90), and the safety results hold on the items all three label unsafe (Appendix E). A human annotator sides with the primary judge on 78% of 50 safety and 82% of 50 over-refusal judge disagreements (Appendix D.3).

The main findings hold. Our safety benchmark ranks models like the static refusal tests (τ=.775), not like the static aggregate (−.153), and over-refusal and privacy spread the testing models over 48.5 and 99.2 points, against 24.9 and 42.7 for static tests.

(W1a): Transfer beyond the calibration panel

We agree that calibration strength matters and ablated it. The calibration panel spans five developers and seven families (Table 9). Restricted to its nine models of at most 27B parameters, it yields a factuality benchmark that spreads the seven frontier testing models over 5.2 points, against 20.5 with the full panel. Three testing models above the best calibration model, 1.26 points apart on the pool, end 6.5 points apart (95% interval 2.4–10.6). With the restricted panel difficulty alone leads on factuality, and with the full panel our objective leads on both services. Q (harmonic mean of separated-pair share and cross-run rank agreement), from Table 7 and the restricted panel:

SelectionFactualitySafety
Random.935.910
Difficulty only.924.952
Separability only.954.950
Difficulty + separability.960.948
Anchor Points.948.938
tinyBenchmarks.950.938
Ours (Rasch information).960.956
Ours.965.970
Difficulty only (nine models ≤27B).959.944
Ours (nine models ≤27B).944.949

(W1b): Over-refusal saturation

Addressed in Section 4.3. The earlier items had saturated (a 17.5-point acceptance spread), so we generated 5,038 new boundary candidates and evaluated them on all 40 models. Acceptance spans 51.3–99.8%, 56.7% of items are refused by at least two testing models (20.3% before), and 91.4% of model pairs are separated (70.5% before).

(W2): Absolute rates and evaluator validity

We do not claim static benchmarks are wrong. Rankings agree for matched constructs (1ySr, W1). We report absolute rates with uncertainty (Appendix D.4). As they depend on the judge, our claims rest on rankings and differences, which hold under a second judge and the human audit above.

(W3): Novelty, style and scope

We compared this distance with the distances among the static benchmarks (median cosine similarity to the nearest item). Our factuality items are as close to the static factuality benchmarks (0.51) as SimpleQA (0.51), TriviaQA and TruthfulQA (0.52) are to the others, and our safety items (0.56) lie within the static safety range (0.42–0.63). Our items differ from the static sets as much as those differ from each other, and rank models alike: factuality with SimpleQA and TriviaQA (Kendall τ=.629, .749), safety with the static refusal tests (.775). For privacy, the revision states the threat model (Section 2.2).

(W4): Presentation

We extended the table captions and reorganized the appendices, and we will make Figure 1 more readable.

(Q1): Calibration-panel replacement

The items change with the panel, but the testing ranking stays stable (Robustness above, details in BpwC, W2a).

(Q2): Generator and privacy saliency scorer

Generation uses gpt-4.1-mini with provider filters off for safety research. In-loop checks, including privacy saliency, use gpt-oss-120b. Neither is a testing model.

(Q3): Scope consistency

Every candidate passes a service-specific scope check before entering the pool (Appendix A). Each benchmark then ranks the testing models like static tests of the same construct (W3), and over-refusal like OR-Bench (τ=.733).

(Q4): Tables 2 and 10

Table 10 used different items (see the opening). In the revision, the Safeguard column of the judge analysis equals the main safety rates, Gemma-3-27B scores 10.5%, and Llama-3.3-70B is a calibration model.

Reviewer_BpwCOpenReview ↗
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Paper summary

This paper introduces SSP-Bench, a dynamic benchmark-generation framework for evaluating LLM safety, security, and privacy (SSP). The framework generates fresh, source-grounded evaluation items, applies service-specific validation, and selects items using difficulty, separability, novelty, and diversity criteria. The authors evaluate 24 models across four services: safety, hallucination, over-refusal, and privacy, and compare the resulting rankings with the static aiXamine leaderboard. They report that SSP-Bench yields stable and more discriminative rankings across independent generations, and argue that static aggregate scores can obscure important behavioral differences. In particular, they attribute the near-zero agreement between static and dynamic safety rankings to construct mixing between adversarial-refusal and content-moderation tests; they also report within-family safety regressions, a factuality “knowledge plateau,” and privacy vulnerabilities that depend strongly on attack framing. The paper further includes selection, steering-panel, and judge robustness analyses, as well as item-level human validation for safety and over-refusal prompts.

Critical strengths
  1. Important and timely problem. The paper addresses a meaningful limitation of static SSP evaluation: fixed benchmarks can saturate, become susceptible to contamination, and obscure heterogeneous behaviors through aggregate scores. Dynamic evaluation for safety, security, and privacy is practically important and comparatively underexplored.

  2. Thoughtful benchmark-construction framework. SSP-Bench combines source-grounded generation, service-specific validation, iterative steering, and multi-objective selection for difficulty, separability, novelty, and diversity. The separation between steering, evaluation, and final testing panels is also a sensible design choice.

Critical weaknesses
  1. A key claim of this paper is that, when evaluating the same capability, discrepancies in rankings between static and dynamic benchmarks can reveal the shortcomings of static benchmarks arising from factors such as saturation or contamination. However, the authors’ dynamic safety set, which is generated using a series of rules, consists of more than half mutated items and explicitly includes persona injection, hypothetical framing, system-prompt override, and compositional blend. While this may represent a more challenging, realistic, or diagnostically informative distribution, the paper does not demonstrate that it assesses the same capability as the static benchmark. The authors should provide a comparative analysis of the distributions of static and dynamic tasks across risk categories, directness, length, jailbreak, attack targets, and expected behavior. Furthermore, it would be helpful to have human annotators assess whether the two sets evaluate the same capability.
  2. The dynamic safety evaluation selects prompts that are most discriminative based on the responses of the evaluation panel. However, if these prompts are particularly likely to trigger rejection strategies, system-prompt vulnerabilities, or jailbreak weaknesses in certain model families, the observed differences may reflect “which model better handles these selected prompts,” rather than necessarily “which model is safer overall when responding to real-world safety-related user requests.” Although the authors separate the final testing panel from the evaluation panel used for prompt selection, two residual issues remain: (1) the evaluation and testing panels share model families such as Gemma, Llama, and Qwen, so the selected prompts may still capture behavioral characteristics common to these families; (2) even if the tested models did not participate in prompt selection, it remains unproven whether the distribution of dynamic prompts is representative of real-world application scenarios.
Questions for authors
  1. Both Table 2 and Table 10 report the safety rate, and Appendix C states that “every (prompt, response) pair from the safety benchmark was re-evaluated,” but there are significant differences between the S_{dyn} values in Table 2 and the “primary” column in Table 10 for several models (such as GPT-4o, DeepSeek-R1, Llama3.3-70B, and Gemma-3-27B) show significant discrepancies. Are these differences due to variations in the test examples used? I could not find a specific explanation in the paper regarding the discrepancies in the values between these two tables. Furthermore, if the two tables are based on different test sets or evaluation methods, what is the rationale for this? Why is judge-robustness evaluated using a different evaluation set from the main results? And why does Table 10 list 20 models while Table 11 lists 24, and why is the version of Grok inconsistent across Tables 2, 10, and 11?
  2. The author notes in the main text that each run of the pipeline “uses an identical service specification and the same privileged source, but differs in random seeds,” and the formula for calculating stability is based on this. However, Appendix F.2 states that the next run will examine the trajectory of the “prior run” to “enforce cross-run diversity.” Under these conditions, would the stability be affected?
1 comment

Thank you for the questions on capability equivalence and panel overlap.

All three reviewers noted that Tables 2 and 10 of the submission disagree. Table 10 was a separate judge comparison on a smaller, differently selected item set (details in 1ySr, W2). The revision evaluates every model under one protocol, so for each service all tables use the same items and responses.

  • Panels. 40 models from eight developers and 17 families. 14 calibration models select the items, and 26 testing models play no part in selection. Static scores cover 21 testing models, and we are collecting them for the remaining five API models.
  • Selection. 2PL item information, fitted on the calibration panel alone, replaces the outcome variance as the separability term. Each run selects its items from its own candidates (details in Q2 below).
  • Robustness. An independent second judge per service (τ=.83–.95), recalibration without one or two families (τ≥.90, details in W2a below), 100 random family splits, and a source-clustered bootstrap that keeps all 27 highlighted differences significant (Appendix D).
  • Human validation. Three blinded annotators agree on the expected behavior for 86–87% of 200 items (Gwet's AC1=.90), and the safety results hold on the items all three label unsafe (Appendix E). A human annotator sides with the primary judge on 78% of 50 safety and 82% of 50 over-refusal judge disagreements (Appendix D.3).

The main findings hold. Our safety benchmark ranks models like the static refusal tests (τ=.775), not like the static aggregate (−.153), and over-refusal and privacy spread the testing models over 48.5 and 99.2 points, against 24.9 and 42.7 for static tests.

(W1): Do mutations change the capability being measured?

We labeled both sets with one classifier (gpt-oss-120b): the 3,684 distinct static refusal prompts and our fresh generations. In both sets the expected behavior is a refusal or a safe response.

Static refusal testsOurs
Direct request99.3%98.3%
Target: an individual or a group66.1%63.3%
Largest harm family (illegal activity)29.5%39.8%
Mean length in words27.725.5

Every other harm family holds under 17% of either set. Although 77.7% of our items are transformations by generation, the classifier reads 98.3% of them as direct requests. These results support a shared refusal construct. Rankings on grounded and on transformed items agree (Kendall τ=.857), and each agrees with the static refusal tests (.728 grounded, .740 framed, .728 other), as do the rankings within each of the nine harm families (.60–.74). The revision adds this comparison (Appendix F.5, Table 28).

(W2a): Calibration and testing family overlap

Recalibrating without the six Gemma-2 and Qwen2.5 models changes the benchmark substantially (45.0% of the safety and 49.7% of the factuality items stay), yet the 26 testing models are ranked almost the same (Kendall τ=.940 and .908) and 96.0% and 98.2% of model pairs stay separated (97.5% and 96.6% before). Leaving out any one calibration family keeps τ at .924–.995 and .908–.986. The items depend on the calibration panel, but the testing ranking stays stable.

(W2b): Real-world representativeness

The target is robustness to incident-grounded adversarial requests. Source grounding ties items to documented failure scenarios and selection keeps challenging, informative items, so the safety rate measures performance on this declared stress-test distribution, not the frequency of harm in deployment. The differences are not carried by a few prompts, since they stay significant when whole sources are resampled (Robustness above).

(Q1): Tables 2/10/11, panel size and Grok versions

Yes, the differences come from the test items, as explained at the start of this reply. Table 10's later setup had 20 models, after some API models retired, and added Grok-4.3, then the newest Grok model. In the revision Grok-4.3 is the only Grok model.

(Q2): Prior-run feedback and stability

The quoted sentence was imprecise, and Appendices A and G.2 state the procedure. No iteration sees earlier item text, only the steering panel's per-category difficulty and the categories already used, which we verified on the saved generation logs of every benchmark run. So that the runs share no selection step either, each run is selected independently, with its own 2PL fit, normalization and near-duplicate removal. To test whether shared generation history drives the agreement, we also built a separate benchmark from each of the two generation trajectories, which share none.

SafetyFactualityOver-refusal
Items shared with the joint selection90.7%95.5%96.5%
Mean Kendall τ between the three runs, independent (joint).90 (.93).92 (.93).83 (.82)
Kendall τ with the joint ranking.997.982.980
Kendall τ between the two trajectories.857.935.812

Rankings barely change, and trajectories with no shared history rank the testing models alike.

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