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Under review as a conference paper at ICLR 2027

Benchmarking Tool-Dependent Safety in Agentic Vision-Language Models

Abstract

Vision-language models (VLMs) are shifting from standalone models to agentic VLMs that autonomously use external tools to solve tasks that their built-in knowledge and capabilities alone cannot handle. As this expands what models can solve, it should also expand what risks they can recognize. Current VLM safety benchmarks, however, rarely test this capability because the safety implications of their samples are usually apparent from the original input. We introduce SAVIT, a benchmark where an appropriate response depends on safety-critical information that is difficult to obtain without effective tool use. SAVIT separately evaluates (1) whether models obtain this information and (2) whether they respond appropriately based on it. We construct manually reviewed samples across safety categories and evaluate recent VLMs, showing that models pass both evaluations on only of samples on average. Our analysis of tool-use behavior and failure modes reveals that using tools well matters more than using them often, and that failures arise throughout the agentic process, from recognizing when tools are needed to using the obtained information in the final response.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
Safety, Vision-language models, Tool-use

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 2 reviews, above 27% of the others.
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Paper summary

This paper studies safety for agentic VLMs, which can call tools such as web search and image cropping. Authors argue that existing VLM safety benchmarks didnot test this, because the risk can usually be read off the image and request. To this end, they build SAVIT, a benchmark of 739 image-request samples in 8 safety categories. Each unsafe sample has a safe twin that differs in one detail. The correct response depends on a fact that has to be found with tools, such as a local law or a small label in the image. The samples are generated by two LLMs, reviewed by hand, paired with web or generated images, and filtered to remove those a small model can already answer without tools.

The main idea is to score two things separately: whether the final response states the safety-critical facts, and whether it responds appropriately.. The authors evaluate 15 VLMs with and without tools and find that joint success rate is low. Models state the key facts far less often than they respond appropriately, and tool help mainly by improving the first metric. The failure analysis says that most failures come from models not calling a tool, or calling it without retrieving the needed fact.

Critical strengths

The two-axis evaluation is the right way to look at this problem. A single ASR cannot tell a model that found the key fact from a model that knew nothing and refused by default. Separating "did the model get the fact" from "did it respond well given the fact" shows where failures come from.

The problem is timely and the evaluation is broad. There is no good benchmark for safety in agentic VLMs. The paper tests many recent models with and without tools, and checks that the conclusions hold under a different judge and a different screening model. This makes the main finding hard to dismiss: current models often fail to look for the evidence they need.

Critical weaknesses

The data generation pipeline is not good enough. Scenarios are written by LLMs and checked by hand, and the only automatic filter is one small model without tools. The paper gives no statistics on how many candidates were lost at each stage, how diverse the scenarios are, or which tools each sample needs. Many samples also depend on local rules or facts that change over time, so the labels are vague and a score may reflect whether a model found one specific fact. I cannot tell the data quality from the paper.

The tool design is thin and has little to do with VLMs. The benchmark has only a handful of tools, and only the zoom-in tool is vision-specific. Web search, page fetching and a code interpreter are the same tools an LLM agent would use. The setting is therefore close to an LLM tool-use setting with an image attached, and the paper does not show otherwise. The scope is also narrow for an "agentic" benchmark: single-turn, information-seeking tools only. A benchmark paper should offer a richer and better justified tool set. For VLM safety, we may need the intention hidden deeper in the text-image combination, with harder tools sets and longer reasoning chain.

The first metric is unfair to safe samples. A fact counts as acquired only if the final response states it. For unsafe samples this is reasonable to ask the model to figure out the underlying violated policy. For safe samples the model only has to comply, nothing asks it to check safety, and it may already know the rule. A correct, compliant answer is then scored as a failure. The authors admit the criterion is conservative, but they do not show how it still supports their conclusions.

Questions for authors
  1. Which tools does each sample actually need, and how often is each tool used? Please report the split between samples that need image cropping, web search, or both, and the per-tool call statistics for the evaluated models. Were models restricted to the same four fixed tools for all instances?

  2. Can you show that the benchmark tests something specific to VLMs? Is the zoom-in/image-cropping tool the only component that is specific to VLMs? If so, please explain how the proposed method and benchmark differ from prior work on agentic LLM safety.

  3. How would the acquisition result change on safe samples if you separated "model knew the fact" from "model did not know"? For example, probe the model without the image for the relevant rule, and report appropriateness conditional on acquisition, so we can see how much of the 76% comes from the measurement rule.

  4. How was the data pipeline filtered in practice? Please report the number of candidates produced, rejected in manual review, lost in image acquisition and removed by screening, and some measure of scenario diversity.

4 comments
AuthorsOpenReview ↗

Response to Reviewer QJeN (1)

Dear Reviewer QJeN,

We appreciate your positive comments on our two-axis evaluation design. We have incorporated your suggestions into the revised paper (changes highlighted in red).


W1. The data generation pipeline is not good enough. ...

SAVIT's data are high quality: independently verified facts behind labels, tool-dependent samples even for frontier models, and diverse, realistic scenarios. We add this evidence to the paper.

1. LLM generation/manual review → Every label rests on verified facts. Two frontier models of different families generate scenarios via web search. We manually check every scenario and image against explicit criteria, keeping only 42% of pairs (Appendices D.2–D.3). Claude Code automatically retrieves the annotated facts for 95.1% of samples with the evaluated models' tools (Appendix H.4).

2. One small screening model → Additional GPT-5.5 screening. We do not rely on one small model: the same no-tool filter with GPT-5.5 removes only 48 more samples (6.5%). All main conclusions and model rankings remain unchanged on 691 samples (Appendix H.3, Table 6). No-tool acquisition is only 26.8% at best and 15.2% on average (Table 3).

3. Pipeline → Strict review retains tool-dependent samples.

StageScenario pairs kept
Generated by LLMs720
After human review305 (42%)
After image acquisition305 (799 samples)
After tool-dependency screening303 (739 samples)

Human review rejects 58% for major flaws and revises minor issues (Appendix D.2). No-tool screening removes only 60/799 samples (7.5%): most reviewed samples already require tools.

4. Diversity → Broad coverage and greater realism.

Method. Claude Opus 5.5 views every image and labels each scenario (safe/unsafe samples sharing one request) by subtopic, task, label-deciding knowledge, and countries (CBRNE excluded for safety). Near-duplicates have near-identical embeddings of requests, safety information, and images.

SAVIT covers 141 subtopics (10–26 per category) and 76 countries and regions, with only 3 of 303 near-duplicate scenarios (1%):

CategoryScenariosSubtopicsNear-dup.Example subtopics
Criminal Activities29241vehicle equipment legality, age limits for purchases, self-defense sprays
Intellectual Property40160dataset licenses, font licenses, public-domain sound recordings
Privacy42230marriage records, voter registers, photo location metadata
Unwanted Bias43100gender stereotypes about women's careers, disability in hiring, religious items
Medical Harm41261drug–diet interactions, food storage limits, venomous bites and stings
Risky Behavior30181color taboos, bicycle rules, hand gestures
Misinformation38240juice–drug interactions, Arctic operations, population origins

Tasks span advice (46%), text editing (21%), writing (11%), planning (10%), and how-to (9%). Label-deciding knowledge spans laws, item identification, facts, licenses, health, and privacy (11–17% each).

Blind comparison. We mix ~165 samples per benchmark (SAVIT, MM-SafetyBench, SIUO, HoliSafe), hiding sources. The same annotator:

  • rates (1–5) whether users could face the situation and seek the help (plausible situation) and send the exact message and image (natural input);
  • checks for stated user context (purpose or location) and lists countries whose rules or facts apply.
SAVITMM-SafetyBenchSIUOHoliSafe
Countries covered442283
Plausible situation (% rated 4–5)97.048.835.554.8
Natural input (% rated 4–5)80.60.036.142.8
Requests stating user context (%)96.49.069.35.4

SAVIT tests safety across far more countries' laws and customs. Situations and inputs are judged realistic nearly twice as often as the next-best benchmark; rates remain high on all SAVIT samples (93.2% and 85.3%). By design, requests state user context (96.4%) and seek ordinary help whose safety depends on local laws, licenses, and drug interactions.

5. Tools needed → Web search, zoom-in, or both. Our instruction and review enforce this (Appendices D.1–D.2). Successful runs use both tools for 46% of solved samples, web search only for 38%, and zoom-in only for 14%. We will release this per-sample information.

6. Vague labels or scores tied to one fact → Labels rest on verifiable facts, and finding them is what SAVIT measures. Changing facts require tools: SAVIT tests checking current facts rather than memory. Our agent re-finds these facts on the live web; versioned releases include source and retrieval metadata (Appendix B). The judge accepts equivalent wording and facts from any source in tool results or reasoning. Rankings remain stable across judges (Kendall's τ ≥ 0.89).

AuthorsOpenReview ↗

Response to Reviewer QJeN (2)

W2. The tool design is thin and has little to do with VLMs. ...

Q2. Can you show that the benchmark tests something specific to VLMs? ...

SAVIT is vision-centric: in most scenarios, the safe and unsafe samples differ only in the image, so the task cannot be reduced to LLM tool use with an image attached. Its standard tool set is sufficient, and it already exposes the main failure of tool-using VLMs. We add these analyses to the paper.

1. Only zoom-in is vision-specific, close to LLM tool use → In SAVIT, web search and the code interpreter are also image tools. In LLM tool use, the text says what to look up; in SAVIT, requests refer to things like "this animal" or "the items shown," and what to search for often exists only in the image.

  • Most web searches start from the image: 89% of 240 random queries follow a zoom-in or image-processing call or search for something found only in the image (e.g., an identified species, product, or place, or text read from it).
  • The code interpreter processes the image: it runs Python on the input image (Appendix E), and 81% of its 3,659 calls operate on it.
  • Zoom-in is the most used tool (40.9% of samples on average vs. 37.5% for web search), and models that zoom in more acquire more safety information (Spearman's ρ = 0.63; Appendix H.5).
  • Often, only the image separates safe from unsafe: in 63% of scenarios (165 of 263), the safe and unsafe requests are word-for-word identical, so a text-only agent sees the same input and cannot tell them apart. In 55% of annotated samples, the decisive cue is text in the image that must be read closely (e.g., a label, form, or screenshot).

2. Small, under-justified tool set → The tool set is standard, sufficient, and not the bottleneck. It follows prior tool-using VLM work. With exactly these tools, a research agent found the annotated safety information for 95.1% of samples (Appendix H.4). Models fail because they barely use the tools (1.2 vs. 6.0 searches per sample), not because tools are missing; adding tools would not fix this and would mix safety with proficiency in specific tool APIs.

3. Single-turn, information-seeking scope → It targets the main failure of agentic VLMs. A single request still requires a multi-step agentic chain (inspect the image, identify the entity, search, read, and decide); the research agent used about 10 search and page-reading calls per sample. Information seeking is also the first step of any safe action: acquisition failures account for 94% of all joint failures (Figure 7(a)). SAVIT isolates this dominant failure.

4. Deeper hidden intent, harder tools, longer chains → SAVIT already hides the risk deeply, and frontier models fail it. Requests contain no harmful intent; the risk lies in external facts about what the image shows, which only tools reveal. Without tools, even the best model obtains this information for only 26.8% of samples; with tools, the best and average models succeed on only 41.8% and 21.7% (Table 3), so SAVIT is far from saturated with current tools. This hidden risk is also realistic (see W1, item 4).

5. Difference from agentic LLM safety work → Prior work tests whether text agents resist visible harm; SAVIT tests whether VLMs uncover hidden risk from images. In SAVIT, no text states the risk: the model must notice that safety-critical information is missing, inspect the image, turn visual evidence into searches, and use what it finds. We also score information acquisition and response appropriateness separately to show where agents fail. Appendix B details the comparison.


W3. The first metric is unfair to safe samples. ...

Thank you for the comment. Requiring the safety information on safe samples is fair and necessary: a model cannot know that a request is safe without checking, because its unsafe twin looks the same. Our revised metric also credits facts found anywhere in the trajectory, and all conclusions hold on unsafe samples alone. We address each concern below and include these analyses in the revised paper.

1. "A fact counts as acquired only if the final response states it." → We now also credit facts found in the trajectory. The revised metric credits each fact if it appears in the final response or anywhere in the model's tool results or reasoning. This raises safe-sample acquisition from 20.3% to 24.0% on average, and all conclusions remain unchanged (Table 3).

(Continued in the next comment.)

AuthorsOpenReview ↗

Response to Reviewer QJeN (3)

(Continued from the previous comment.)

2. "For safe samples the model only has to comply … and it may already know the rule." → Blind compliance is not reliable safety. In 63% of scenarios (165 of 263), the safe and unsafe variants have word-for-word identical requests and differ only in the image. The request alone therefore cannot establish whether assistance is safe. Our data show why this matters (pooled over the 14 models). When a model answers a safe sample appropriately without the safety information, it responds inappropriately to the unsafe twin of the same scenario 70% of the time. When it answers with the information, its responses to the twin are far better (54.5% vs. 29.9% appropriate; 40.2% vs. 12.8% joint success). Thus, safe compliance alone conceals substantial failures on the matching unsafe cases. A model that already knows the rule can simply state it, since every response includes a justification.

3. "They do not show how it still supports their conclusions." → All conclusions hold on unsafe samples alone, where the metric is uncontroversial.

Unsafe samples onlyResult
Joint success with tools21.1% on average; best 40.2% (Claude Opus 5)
Rank agreement with all-sample joint successKendall's τ = 0.89 (Spearman's ρ = 0.97)
Acquisition vs. response appropriateness28.8% vs. 38.9%: acquisition remains the bottleneck
Effect of tools on joint successImproves all 14 models (13.7% → 21.1% on average)

The acquisition requirement on safe samples therefore does not drive our conclusions; it ensures that compliance is informed rather than lucky.


Q1. Which tools does each sample actually need, and how often is each tool used? ...

Thank you. Appendix H.5 now includes these statistics and per-model numbers.

Tools each sample needs. By design, each sample requires zoom-in, web search, or both (Appendix D.1). For the 525 samples solved by at least one model, majority votes over tools used in each sample's successful runs give the split below.

BothWeb search onlyZoom-in only
46%38%14%

Tool use across 14 models (Table 3, means and ranges across models)

ToolCalls per sampleSamples using it (%)
Web search1.18 (0.21–2.70)37.5 (12.2–80.8)
Page fetch0.06 (0.00–0.20)3.0 (0.0–9.9)
Zoom-in0.79 (0.01–1.53)40.9 (0.5–79.7)
Code interpreter0.35 (0.00–1.09)9.5 (0.1–39.1)

Zoom-in is most widely used. More tool use correlates with higher acquisition (Spearman's ρ = 0.82). With the same tools, a research agent averages 6.0 searches and 3.7 page fetches per sample, showing that models under-use the tools (Appendix H.4).

Same tools for all instances. All models receive the same four tools for every instance, with identical descriptions, settings, and limits. Provider-native tools are disabled.


Q3. How would the acquisition result change on safe samples...

Thank you. High acquisition failure persists without the final-answer-only rule and on unsafe samples alone. Conditional results show why safe compliance alone cannot establish reliable safety knowledge. We add these analyses to Appendix H.6.

1. A broader metric changes the result only slightly. We credit facts in the final response, tool results, or available reasoning. Average acquisition failure falls from 76.0% to 73.4%, and safe-sample acquisition rises from 20.3% to 24.0%. Acquisition still fails on 71.2% of unsafe responses.

(Continued in the next comment.)

AuthorsOpenReview ↗

Response to Reviewer QJeN (4)

(Continued from the previous comment.)

2. Knowing the rule does not establish which visual case applies. In 63% of scenarios, safe and unsafe twins have identical requests, and only the image distinguishes them. A text-only probe tests prior rule knowledge, but cannot establish whether the model identifies the visual case and applies the rule. Our metric checks for task-specific safety information in the recorded interaction. We therefore examine conditional appropriateness and matched-twin behavior.

3. Conditional results show why compliance alone misses safety failures.

Response appropriateness (%)AcquiredNot acquired
Safe samples92.188.3
Unsafe samples72.426.7

On unsafe samples, acquisition is associated with 45.7 percentage points higher response appropriateness. On safe samples, appropriateness stays high with or without the information, so compliance alone cannot reveal the model's safety knowledge.

Among appropriate safe responses, the same model answers the unsafe twin appropriately 54.5% of the time with acquisition on the safe sample, versus 29.9% without it. Apparently successful safe compliance thus conceals substantial failures on matching unsafe cases.


Q4. How was the data pipeline filtered in practice?

Thank you for the question. We report the full funnel below and add it to Appendix D.2. Human review is strict and rejects 58% of the candidates, whereas the final no-tool screening removes only 7.5% of samples, so most reviewed samples were already tool-dependent.

StageScenario pairs keptRemoved at this stage
Generated by LLMs720–
Manual review305415 pairs (58%) rejected, minor issues revised
Image acquisition305 (799 samples)none
Tool-dependency screening303 (739 samples)only 60 of 799 samples (7.5%)

Some variants use several images, which gives 799 samples.

Scenario diversity (Appendix J). Claude Opus 5.5, viewing every image, annotated each scenario (a set of safe and unsafe samples sharing one request) with its subtopic, task, and countries (CBRNE excluded for safety). Near-duplicates are scenarios whose request, safety information, and image are all near-identical in embedding space.

CategoryScenariosSubtopicsNear-dup.Example subtopics
Criminal Activities29241vehicle equipment legality, age limits for purchases, self-defense sprays
Intellectual Property40160dataset licenses, font licenses, public-domain sound recordings
Privacy42230marriage records, voter registers, photo location metadata
Unwanted Bias43100gender stereotypes about women's careers, disability in hiring, religious items
Medical Harm41261drug–diet interactions, food storage limits, venomous bites and stings
Risky Behavior30181color taboos, bicycle rules, hand gestures
Misinformation38240juice–drug interactions, Arctic operations, population origins

The scenarios cover 141 subtopics (10–26 per category) and 76 countries and regions, with only 1% near-duplicates, and span diverse tasks (advice 46%, text editing 21%, writing 11%, planning 10%, how-to 9%).

In a blind comparison, the same annotator rated about 165 samples from each benchmark for the countries involved, whether real users could face the situation (plausible situation), and whether a real user could send the message and image (natural input), on a 5-point scale.

SAVITMM-SafetyBenchSIUOHoliSafe
Countries covered442283
Plausible situation (% rated 4–5)97.048.835.554.8
Natural input (% rated 4–5)80.60.036.142.8
Requests stating user context (%)96.49.069.35.4

SAVIT covers far more countries than existing benchmarks and is judged realistic nearly twice as often as the next-best benchmark.

Reviewer_LScpOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
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Soundness
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Read review
Paper summary

The paper introduces SAVIT, a benchmark that evaluates what the authors define as “tool-dependent safety” in agentic vision-language models. It tests whether models can use a predefined set of tools to determine whether a user request is safe given the accompanying image which might not be obvious from first sight. SAVIT contains 739 manually reviewed samples across eight safety categories, including 346 safe and 393 unsafe cases. The evaluation metric checks whether models clearly specify the required safety facts and respond to users appropriately. Experiments cover 15 models with and without a predefined list of tools. Tool access raises the reported average joint success rate from 12.4% to 19.8%, with the best model reaching 40.5%. The paper also groups failures by type, reports their proportions, and provides examples.

Critical strengths
  1. The paper identifies a meaningful gap in VLM safety evaluation. It studies situations where the image and user request together involve potential risks that are not obvious at first glance. Testing whether models can actively use tools to uncover these risks is a worthwhile direction.
  2. The paper is clearly organized, and the experiments is comprehensive, covering 15 VLMs with and without tools (Table 3). The authors also analyze different types of failure and examines the relationship between tool-use proficiency and safety performance, reporting correlations of 0.70 and 0.55 with two general tool-use benchmarks (Section 4.4).
  3. The authors provide useful checks on evaluation reliability. Appendix H reports 95.6% agreement between the judge and human assessments on 160 responses. Replacing the judge model also produces nearly identical model rankings, with Spearman’s ρ=0.996. These checks provide support for the stability of the reported performance.
Critical weaknesses
  1. The dataset’s diversity coverage and practical relevance need more support. Section 3.2 describes generating scenarios with two models and reusing retained samples as seeds, Appendix B also acknowledges this approach as “Reusing retained samples as seeds may also reinforce recurring patterns.” Reusing seed examples could narrow the range of scenarios and user requests covered. The authors describe manual checks for duplicates, but provide limited detail on the diversity of request content within each safety category. Further, the paper covers eight safety categories, but without details on the range of topics and tasks covered by the requests within each category. It also needs to explain how the generated scenarios reflect situations that users would plausibly encounter in practice. Since the dataset is the main contribution, these details matter for assessing its diversity and practical value.

  2. The annotation process of data generation need clarification. Appendix D.2 states, “We manually review every generated scenario pair.” However, the paper does not specify the number of reviewers, their relevant expertise, whether they reviewed samples independently, or how disagreements were resolved. This matters for samples involving local laws, medical risks, and licensing conditions. The sources and applicable conditions supporting each safety label should also be documented.

  3. The adequacy of the predefined tools and the solvability of the tasks need stronger validation. Since the benchmark requires a predefined set of tools, the authors should verify that these tools and their settings are sufficient to obtain the facts needed for each safety decision. Appendix A states that “the provided tools can reveal or verify” this information, but the paper does not report a systematic check under the actual evaluation settings. Section 5.1 and Figure 7(b) attribute 32.4% of information-acquisition failures to “ineffective tool use.” This raises a question about task solvability: when even strong models fail, are they using the tools poorly, or is the required evidence inaccessible through those tools? A systematic check would help establish that these failures reflect model limitations rather than limitations of the benchmark setup.

Questions for authors

Please address concerns raised in weaknesses.

2 comments
AuthorsOpenReview ↗

Response to Reviewer LScp (1)

Dear Reviewer LScp,

Thank you for your positive assessment of our comprehensive evaluation. We have incorporated your suggestions into the revised paper (changes highlighted in red).


W1. The dataset’s diversity coverage and practical relevance need more support...

Thank you for this helpful comment. We add a diversity and realism analysis in Appendix J. The results show that SAVIT has little repetition, broad coverage within categories, and far more realistic situations and inputs than the three existing benchmarks.

How we measured diversity. Claude Opus 5.5 views the images and annotates each scenario with its subtopic, task, knowledge needed to determine the label, and countries involved. A scenario groups safe and unsafe samples sharing one request, excluding CBRNE for safety. Two scenarios count as near-duplicates when their requests, safety information, and images are all near-identical in embedding space.

1. Seed reuse did not narrow SAVIT. Seeds serve only as examples. Both our generation instruction and our review explicitly reject near-duplicates of the seeds and repeated templates (Appendices D.1–D.2). Only 3 of 303 scenarios (1%) are near-duplicates, and even these differ in the country or item.

2. Each category covers many topics and tasks. SAVIT covers 141 subtopics, with 10–26 per annotated category, and 76 countries and regions.

Table. Topic coverage and near-duplicates across safety categories.

CategoryScenariosSubtopicsNear-dup.Example subtopics
Criminal Activities29241vehicle equipment legality, age limits for purchases, self-defense sprays
Intellectual Property40160dataset licenses, font licenses, public-domain sound recordings
Privacy42230marriage records, voter registers, photo location metadata
Unwanted Bias43100gender stereotypes about women's careers, disability in hiring, religious items
Medical Harm41261drug–diet interactions, food storage limits, venomous bites and stings
Risky Behavior30181color taboos, bicycle rules, hand gestures
Misinformation38240juice–drug interactions, Arctic operations, population origins

Requests include advice (46%), text editing (21%), writing (11%), planning (10%), and how-to instructions (9%). The knowledge needed to determine the label also varies across laws, visual identification, factual knowledge, licenses, health, and privacy, with each accounting for 11–17%.

3. SAVIT covers more countries and is far more realistic than existing benchmarks. We compare SAVIT with MM-SafetyBench, SIUO, and HoliSafe using about 165 samples from each benchmark. We mix the samples and hide their benchmark names. The same annotator rates whether the situation and request could occur in practice (plausible situation) and whether the exact message and image could come from a real user (natural input). Both ratings use a five-point scale. The annotator also records whether requests state the user's purpose, location, or situation (user context) and lists the countries involved.

Table. Geographic coverage and realism in the blind comparison.

SAVITMM-SafetyBenchSIUOHoliSafe
Countries covered442283
Plausible situation (% rated 4–5)97.048.835.554.8
Natural input (% rated 4–5)80.60.036.142.8
Requests stating user context (%)96.49.069.35.4

SAVIT exceeds the strongest comparison benchmark by 42.2 percentage points in plausible situations and 37.8 points in natural inputs. It also covers 44 countries, versus 28 for the next highest benchmark. The realism results remain high across all SAVIT samples, reaching 93.2% for plausible situations and 85.3% for natural inputs.

This realism follows our design. Almost every request states the user's purpose, location, or situation (96.4%) and asks for ordinary help whose safety depends on real-world facts, such as local laws, licenses, and drug interactions.

AuthorsOpenReview ↗

Response to Reviewer LScp (2)

W2. The annotation process of data generation need clarification...

Thank you. We clarify the process below and will add these details to Appendix D.2.

  • Reviewers and process. Two reviewers, both AI safety researchers, independently review every scenario pair against the five criteria in D.2. They resolve disagreements through discussion and revise or discard any pair whose label remains uncertain.

  • Law, medical, and licensing samples. We ground each label in verifiable facts recorded in K*, such as whether a painting remains under copyright in the United Kingdom. Reviewers check every fact against official sources, including laws and ordinances, drug labels, and license pages. Each independent check recovers 96.5% of the individual K* facts across these samples.

  • Sources and applicable conditions. Each K* states the conditions under which the label holds, such as the jurisdiction. For every sample, we will release the supporting source URLs with quoted evidence, the applicable conditions, and the retrieval dates.


W3. The adequacy of the predefined tools and the solvability of the tasks need stronger validation...

Thank you for this question. We directly verify that the required safety information is reachable with the provided tools under our evaluation settings.

Experiment: Is the needed information reachable with our tools?

A Claude Code agent (Claude Opus 5.5) receives only the image and request and is explicitly told to collect the facts that decide whether helping is safe. This is a different, easier task than SAVIT. It need not recognize that these facts matter and gathers information without answering the user. It uses the same search and page-reading tools and settings as the evaluated models (Appendix H.4 for details).

Table. Information acquisition on the same audited samples.

SystemNeeded information found (%)
Agent told to collect safety information95.1
Evaluated models on SAVIT (average of 14)31.5
Best model on SAVIT (Claude Opus 5)61.4

The provided tools retrieve the needed information for nearly all samples in this subset. Crucially, the agent finds the information for 94.9% of failures classified as ineffective tool use in Figure 7(b). The corresponding share across all acquisition failures is 93%. Our analysis attributes only 0.3% of acquisition failures to tool limits or errors. Models also search far less, averaging 1.2 searches per sample compared with 6.0 for the agent. These results identify how models use the available tools as the main acquisition bottleneck.

As described in Section 4.1, our toolset follows common tool-using VLM setups and includes web search, page reading, image zoom-in, and a code interpreter. We add this verification to the revised paper.

Comments on the paper

3 comments
AuthorsOpenReview ↗

Response to Reviewer yC9q (1)

Dear Reviewer yC9q,

Thank you for highlighting our focus on tool-dependent VLM safety. We have incorporated your suggestions into the revised paper (changes highlighted in red).


W1. The requirement that safety-critical information be restated in the final answer to count as “acquired” ...

Q1. How sensitive are the joint success and acquisition metrics to the requirement that K* ...

Thank you for this helpful suggestion. As advised, we now assess information acquisition using both the final response and the available trajectory, including reasoning and tool outputs. Thus, information no longer needs to be repeated in the final answer to receive credit. This addresses concerns about mixing acquisition with final-answer explanation and penalizing safe responses for omitting facts already present in the trajectory. The table below reports average tool-use results across 14 models, excluding Qwen3.6-35B, which is used for screening.

MetricOriginalRevised
Information acquisition24.0%26.6%
Response appropriateness62.7%62.7%
Joint success19.8%21.7%

Information acquisition remains the main bottleneck, and joint success remains low even under this broader criterion. The conclusions of our other analyses also remain unchanged, with details provided in the revised paper. We update the main results table and related text accordingly. The revised Table 3 provides the full results.


W2. Reliance on an LLM judge (primarily GPT-5.5) remains a potential source of bias...

Thank you for this suggestion. We now check robustness with three judges and strengthen human validation.

1. Robustness across judges

We re-evaluate the tool-use responses with Gemini-3.8-Flash and Claude Sonnet 5 using the same criteria and inputs. Scores below are averages across the tool-use models in Table 3 on the 659 non-CBRNE samples (Appendix H.1 for details); τ is the Kendall rank correlation with GPT-5.5.

Table. Results with different judges. Scores are averaged across the tool-use models in Table 3.

JudgeInformation acquisitionResponse appropriatenessJoint success
GPT-5.528.9%63.2%23.8%
Gemini-3.8-Flash26.1%64.4%21.8%
Claude Sonnet 529.1%63.9%23.9%

Model rankings remain consistent (Kendall’s τ ≥ 0.89 for all three metrics), and the top two and bottom two models by joint success are the same under every judge. These results show that our scores and model rankings are robust to the choice of judge.

2. Human validation

As suggested, two annotators independently evaluate 160 responses, balanced across categories and safe/unsafe cases, without seeing judge predictions. After resolving disagreements, agreement between GPT-5.5 and the human labels is 96.3% for acquisition and 95.6% for response appropriateness. We add these checks to the revised paper (Appendices H.1–H.2).

Together, these checks support the reliability of our evaluation. We include the judge comparison and human verification results in the revised paper.


W3. While the paper positions SAVIT against multimodal safety suites, a deeper engagement with recent agentic tool-use evaluations...

As advised, we expand Section 2 and Appendix B to (1) clarify the safety question beyond general task performance and (2) derive implications for safety training and analysis.

We add the following discussion:

(1) General task performance and tool-dependent safety

Benchmarks such as MMSearch-Plus, Agent-X, and AgentVista test tool use on tasks such as identifying an event from an image or finding product specifications. SAVIT asks whether agentic tool use also improves safety. New evidence can change whether a request should be fulfilled, while safe requests still require useful assistance. The HR-MMSearch correlation in Figure 6 suggests that tool proficiency matters, but our failures after acquisition show that obtaining evidence does not ensure appropriate behavior. Safety is thus a separate outcome to evaluate as tools advance.

(2) Implications for safety training and analysis

Diagnostic frameworks such as MED distinguish model improvements from gains or errors linked to tool access. However, task accuracy leaves open whether agents adjust their assistance when retrieved facts reveal a safety risk. SAVIT examines this separate requirement through information acquisition and response appropriateness. Our warn-then-comply failures show why: a response can state risks and still provide prohibited assistance. This also guides how to adapt methods such as SVRL to safety: search and verification should aim for appropriate responses to the facts, including useful assistance for safe requests. The learning target is how evidence changes assistance, beyond whether it supports a factually correct answer.

AuthorsOpenReview ↗

Response to Reviewer yC9q (2)

Q2. What limits were enforced on tool usage...

Thank you for requesting these details. We expand Appendix E (Evaluation Details), under "SAVIT experiments," to clarify the tool limits, search configuration, and provider-specific differences.

1. Shared tool limits

All models use the same agent loop and tool settings. Each run allows up to 50 turns (model responses) and ends at the final response. A turn may include several tool calls, and all of them are run; there is no other limit on tool calls. Timeouts are 600 s per model API call, 120 s per web_search, 30 s per fetch_url, and 90 s per code-interpreter run. Temporary errors are retried (up to five times for API calls and twice for fetch_url), and there is no overall time limit. Each web_search returns up to 10 results, and fetch_url returns up to 30,000 characters of page text.

2. Search configuration and provider differences

All models use the same Perplexity Search API, which returns ranked results, not generated answers. We send only the query and result count, with no domain, region, or date filters. Snippets remain unchanged (median ~600 characters), pages are read only when the model calls fetch_url, and nothing is summarized. Provider-native tools are disabled. Tool settings differ across APIs only in message format and image handling; for example, GLM-5.3-Flash allows at most eight images per request, so older tool images become placeholders. Latency affects only wall-clock time; failed tool calls return errors to the model. Runs reaching the turn limit count as failures (at most 3.4% per model), and requests blocked by provider safety filters as refusals (at most 1.8%). The expanded description clarifies shared settings and remaining API-specific differences.


Q3. Did you consider adding OCR and reverse image search as tools?...

Q6. To better isolate acquisition vs. response alignment limits, could you include an oracle-K* condition...

Thank you for this question. We used the tools most common in prior tool-using VLM work and did not add OCR or reverse image search; for small text, zoom_in returns a full-resolution crop that VLMs read directly. To measure how many failures come from the toolset, we ran two new experiments.

Experiment 1: Is the needed information reachable with our tools?

This is a different, easier task than SAVIT. Given the image and request, a Claude Code agent (Claude Opus 5.5) is explicitly told to collect the facts that decide whether helping is safe (e.g., what the image shows or which local rule applies). Unlike the models in SAVIT, it need not realize that such facts matter, and it only gathers information without answering the user. It uses the same search and page-reading tools and settings as the evaluated models. We grade its findings against the annotated safety information.

Needed information found (%)
Agent told to collect safety information95.1
Evaluated models on SAVIT (average of 14)31.5
Best model on SAVIT (Claude Opus 5)61.4

Our toolset is thus sufficient: it yields the needed information for nearly all samples. The models fail because they do not use the tools effectively (1.2 vs. 6.0 searches per sample). On these samples, 93% of their acquisition failures occur where the agent found the information with the same tools, and our trajectory analysis attributes only 0.3% of acquisition failures to tool limits or errors (included in "Other" in Figure 7(b)).

Experiment 2: Do models respond appropriately once they have the information?

We re-run Claude Opus 5 on all samples, adding the annotated safety information to the request as a hint, with the same tools, prompt, and judge.

Claude Opus 5, safety information givenSafeUnsafeAll
Appropriate response when the model stated the information (%)97.377.486.6

With the information, most responses are appropriate, so acquiring it is the main bottleneck. Some inappropriate responses remain, mainly on unsafe requests: in 68 of the 80 still-failing unsafe responses, the model gave the prohibited help, usually after noting the risk itself. Better retrieval alone does not ensure an appropriate response.

In short, our toolset suffices to obtain the needed information, and models mostly respond appropriately once they have it. Failures thus stem mainly from models not using the available tools to acquire safety information, which is what SAVIT measures, not from missing tools. We have added both experiments to Appendix H.4.

AuthorsOpenReview ↗

Response to Reviewer yC9q (3)

Q4. Can you provide per-category results and error distributions?...

Thank you for the question. We add per-category results to Appendix I: tool dependence (Table 13) and error distributions (Table 14). We summarize the findings below:

  • Most tool-dependent: Misinformation (+28.9 points in acquisition), IP (+13.7), and Privacy (+13.1), whose deciding facts cannot be read from the image.
  • Acquisition failures: Models mostly skip tools in Bias (75%) and Misinformation (72%), where requests look harmless, and misuse them in IP (45%).
  • Response failures: Warn-then-comply dominates in Criminal (95%), Misinformation (93%), Bias (90%), and Medical (82%); direct compliance concentrates in CBRNE (43%) and Privacy (32%).

Q5. How large was the human validation set for judge reliability...

Thank you for these questions.

Size and protocol. Our human validation set has 160 model responses: 10 safe and 10 unsafe from each of eight safety categories. Two annotators independently score both axes and resolve disagreements through discussion. Agreement between GPT-5.5 and the final human labels is 96.3% for information acquisition and 95.6% for response appropriateness.

Disagreements and borderline cases. Disagreements include whether a risk warning and advice to consult a doctor meet the sample's response criterion. The same element-level rules apply to all models (Appendix D.5): paraphrases and semantically equivalent behavior pass; missing or ambiguous required elements fail. We retain automated judge labels for all benchmark results for consistency across models. As reported in our response to W2, Gemini-3.8-Flash and Claude Sonnet 5 yield consistent model rankings across all three metrics (Kendall's τ ≥ 0.89; Appendix H.1).

Release of a human-judged subset. We will release all 160 responses with final human labels for both axes and corresponding judge outputs, providing a common reference for evaluating new judges. Appendix H.2 now covers the protocol, agreement for each axis, and how disagreements are resolved.


Q7. How do you mitigate drift from web content changes?...

  • Caching/snapshots. We use live search and save every query, returned search result, and page text shown to the model.

  • Release. We will release these records, final responses, judge outputs, and reference URLs. Scores can be recomputed from the saved judge outputs without new web searches.

  • Drift. Each version fixes K*, and models may use any supporting source. Our later live-search check finds no misses caused by removed or changed pages. We will repeat this check for each release and update affected samples and annotations.

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