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Under review as a conference paper at ICLR 2027

CyberBinGym: Can AI Agents Turn Binary Patches into Real Exploits?

Abstract

Security fixes usually reach users as compiled updates, but deployment delays leave unpatched systems exposed. During this window, comparing patched and unpatched binaries can reveal how to exploit a vulnerability, turning a defensive update into actionable information for attackers. Existing benchmarks do not measure this capability: they expose source code, rely on human-crafted challenges, or evaluate binary comprehension without requiring exploitation. We introduce CyberBinGym, a benchmark containing 100 tasks derived from real vulnerabilities in 53 widely used projects, spanning six vulnerability families and three levels of analysis complexity. Agents receive stripped vulnerable and patched binaries without source code or vulnerability information, and must combine static and dynamic analysis to recover and exploit the vulnerability. Evaluation separately measures vulnerability recovery through differential crash testing and end-to-end exploitation through flag retrieval, with trajectory audits to reject reward hacking. The strongest evaluated agent recovers the target vulnerabilities for 88% of tasks and exploits for 22%. Providing the patched binary raises its exploit rate from 15% to 30% on a matched 20-task subset; with standard binary hardening enabled, it still exploits two of its 22 previously successful tasks. These results demonstrate that current agents can turn released binary patches into working exploits in a controlled setting, although exploitation remains unreliable. These capabilities lower the barriers to targeting unpatched software and compress defenders' effective response window, increasing the urgency of timely patch deployment.

Primary area:
datasets and benchmarks
Keywords:
AI agents benchmark, cybersecurity benchmark, binary analysis and exploit generation, vulnerability analysis

Reviews

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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_Pe9VOpenReview ↗
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3
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Paper summary

The paper introduces CYBERBINGYM, a binary-only benchmark for analyzing and exploiting 1-day vulnerabilities. The authors evaluate their benchmark on three AI agents and show that, given a vulnerable and patched binary, AI agents can recover up to 88% of the vulnerabilities and successfully exploit them 22% of the time.

Critical strengths

The paper presents a useful benchmark for binary vulnerability analysis. CYBERBINGYM provides 100 tasks across 53 projects, with task selection accounting for the relative frequency of vulnerability families. By withholding source code, vulnerability descriptions, and reference PoCs, it evaluates capabilities that source-based benchmarks do not directly capture.

Practical relevance to the patch-to-exploitation window:The paper highlights how agents may accelerate vulnerability analysis once a patch becomes available. Its binary-only reproduction and exploitation results raise an important concern: attackers may require less time to turn published patches into actionable attacks, increasing the urgency of timely patch deployment.

Critical weaknesses

Insufficient evidence that the recovery metric measures the intended vulnerability: If the metric only checks exit behavior instead of vulnerability identity, an input could receive credit for triggering another bug or assertion that occurs only in the vulnerable version. This uncertainty undermines confidence in the headline the 88% recovery rate and the conclusions drawn from it.

Questions for authors
  1. Section 3.1 says accepting a PoC requires an "expected sanitizer-detected failure,” whereas Appendix A.9.2 says the oracle checks exit behavior rather than vulnerability identity. Which criteria determine the reported recovery scores, and how do they distinguish the assigned vulnerability from another bug or assertion?

  2. Have you independently checked accepted PoCs to confirm they trigger the assigned vulnerability? If so, how was this verified, and what recovery rate remains after excluding unrelated failures?

2 comments

We thank the reviewer for recognizing the benchmark's value and for the precise questions, which pinpoint a wording inconsistency we are glad to fix.

W1 / Q1 / Q2 (combined): "Section 3.1 says a PoC needs an 'expected sanitizer-detected failure', but Appendix A.9.2 says the oracle checks exit behavior rather than vulnerability identity. Which governs, how do you distinguish the assigned vulnerability from another bug/assertion, and what recovery rate remains after excluding unrelated failures?"

We understand W1, Q1, and Q2 as the same concern and answer them together; please let us know if we have misread any of them.

Which description governs. A.9.2 is the accurate one: the oracle only checks exit behavior. A PoC counts iff the same input makes the vulnerable build fail (crash or non-zero exit) and the patched build exit normally, a differential crash check. It does not compare the crash against the reference vulnerability's type or location. Every recovery number in the paper uses exactly this check, so the results already match A.9.2; Section 3.1's phrase "expected sanitizer-detected failure" overstates it, and we will rewrite Section 3.1 to agree.

Why we leave vulnerability identity out of the oracle. This is deliberate, and it follows from the 1-day threat model. A released version is not a minimal single-CVE fix: one update usually bundles fixes for several distinct vulnerabilities, and the gap between the vulnerable and patched builds covers the whole release (median ~1,000 changed lines; sample 368 alone spans 86 C files). An attacker diffing the old and new releases benefits from triggering any defect the update closed, and usually can't even tell which of the co-shipped fixes a given crash belongs to, not just the one on record. So any input the patch removes is a real, actionable defect the release closed, which is the right notion of success here; demanding an exact-CVE match would undercount genuine 1-day capability. This differential check is established practice: CyberGym (Wang et al., ICLR 2026) validates PoCs by differential execution on vulnerable and patched builds, and SEC-bench (Lee et al., NeurIPS 2025) verifies its reproduced PoCs the same way (a sanitizer crash before the patch, none after). Our recovery oracle applies the same criterion.

We still checked identity directly, as validation rather than re-scoring. We checked on every accepted PoC, comparing the crash it actually produces on the vulnerable build against the task's OSS-Fuzz/ARVO ground truth. Most reproduce the specific recorded vulnerability; a minority trigger a real memory-safety defect that is not the intended bug but is genuinely present in the vulnerable build and removed by the patch. We keep those as successes, for the 1-day reason above.

AgentDiff-crash recoveryAssigned bugDifferent real bug
Codex88/1006622
Claude85/1005926
Kimi64/1005014

Recovery rates stay the same (88/100 Codex, 85/100 Claude, 64/100 Kimi), and under the stricter identity rule based on sanitizer report, 66, 59, and 50 of those respectively are the specifically-assigned vulnerability. The checker ships as appendix validation, showing the differential successes are overwhelmingly genuine memory-safety defects rather than spurious crashes; it does not change the scored metric.

References

  • Wang et al. CyberGym: Evaluating AI Agents' Real-World Cybersecurity Capabilities at Scale. ICLR 2026.
  • Lee et al. SEC-bench: Automated Benchmarking of LLM Agents on Real-World Software Security Tasks. NeurIPS 2025.

Dear Reviewer Pe9V, thank you again for your thoughtful feedback and suggestions. We would like to kindly follow up on our rebuttal and ask whether our responses have adequately addressed your concerns. We would greatly appreciate any further feedback or clarification you may have, and we would be happy to address any remaining questions.

Reviewer_cHgpOpenReview ↗
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Paper summary

This paper introduces CyberBinGym, a benchmark platform designed to evaluate whether Large Language Model (LLM)-based cybersecurity agents can identify and exploit real-world vulnerabilities, given only "patched" and "unpatched" binary files—without access to source code, vulnerability descriptions, or reference exploit code. The benchmark comprises 100 tasks derived from actual vulnerabilities in 53 open-source projects, spanning 6 vulnerability categories and 3 levels of complexity. CyberBinGym assesses two specific agent capabilities: "vulnerability reproduction" (measured via differential crash testing) and "exploit success rate" (measured by the retrieval of a "flag" within an isolated victim environment, verified through execution trace auditing). The researchers evaluated three agent configurations: Codex (based on GPT-5.6), Claude Code (based on Claude Opus 5), and Kimi Code (based on Kimi K3). Experimental results indicate that the top-performing agent achieved an 88% vulnerability reproduction rate and a 22% exploit success rate.

Critical strengths

This paper explores an important yet under-researched cybersecurity capability: whether AI agents can transform released binary patches into functional exploits without access to the source code. Unlike traditional CTF (Capture The Flag) benchmarks or source-code-based vulnerability analysis tasks, CyberBinGym utilizes real-world vulnerabilities found in widely deployed software, requiring agents to perform binary reverse engineering, differential analysis, and dynamic testing. The framework distinguishes between "vulnerability reproduction" and "successful exploitation" and incorporates a process-auditing mechanism to prevent the use of unintended "shortcuts," thereby ensuring that the evaluation results are both meaningful and credible.

Critical weaknesses

I believe the paper has several notable shortcomings:

  1. The benchmark is constructed based on historical vulnerabilities found in open-source software, utilizing existing datasets and artifacts from CyberGym, OSS-Fuzz, and ARVO. Although the agents are not explicitly provided with the source code or descriptions of the vulnerabilities, these underlying vulnerabilities—along with their corresponding patches—may have long been publicly documented and included in the pre-training data of the models being evaluated.
  2. The paper compares Codex, Claude Code, and Kimi Code; however, these configurations differ in terms of both their underlying language models and their agent infrastructure (harness). Consequently, any significant disparities in success rates for vulnerability patching and exploitation cannot be attributed solely to the reasoning capabilities of the models themselves. Factors such as tool-use strategies, context management, available integrated tools, and execution policies could all exert a substantial influence on performance.
Questions for authors

No

2 comments

We thank the reviewer. Both weaknesses are important and we address them directly; we hope the clarifications and added analyses warrant reconsideration.

W1: "Underlying vulnerabilities and patches may be in the models' pretraining data (contamination)."

This is the right concern for any benchmark built on historical CVEs, and we have several lines of evidence that performance is not explained by memorization:

  • The task is binary-only, stripped, and recompiled. The agent never receives source, CVE text, commit messages, or reference PoCs (Section 3.3). Any memorized source-level knowledge must be re-grounded in a specific stripped binary layout: recovering types, offsets, and reachability from disassembly is the hard part, and it is build-specific.
  • Exploitation depends on this build's runtime state (heap layout, addresses, object lifetimes observed live in GDB), which is not memorizable from public text.
  • Giving the vulnerability description does not reliably help. In our description ablation (Figure 4, Table 9), adding the natural-language description, which would most strongly cue any memorized knowledge, changes Codex's recovery only from 90% to 86% and its exploitation from 26% to 20% on the 50-task subset. If agents were recalling memorized solutions, the description should help substantially; instead it does not help at all. This is concrete, in-paper evidence against a memorization explanation.
  • The absolute exploit rates are low (Codex 22%, Kimi 0%). If the agents were simply reproducing publicly-documented exploits from pre-training, we would expect far higher success; the low rates are hard to reconcile with a memorization account.
  • The paper already reports that we observed no apparent memorization in inspected trajectories, and that stripping/recompiling mitigates direct contamination (Discussion).

Taken together, these points (binary-only stripped/recompiled inputs, the description ablation not helping, low absolute exploit rates, and no memorization signal in the inspected trajectories) are evidence that memorization alone is unlikely to explain the observed performance. We also note the binary-obfuscation study already listed as future work as a further guard against residual contamination.

W2: "Codex/Claude/Kimi differ in both model and harness, so success differences can't be attributed to model reasoning alone."

We agree, and we do not claim to isolate pure model reasoning. Two responses:

  • Framing. CyberBinGym evaluates deployed agent systems (model + harness), which is the realistic threat model: a real attacker uses an off-the-shelf agent, not a disembodied model. The contribution is a benchmark and a threat-model finding ("current agents can turn binary patches into exploits"), not a pure-model leaderboard. We will state this scope explicitly and soften any model-attributed language.
  • Additional ablation study. To pull the harness apart from the model, we run a plain ReAct agent on the 20-task subset: the standard react agent from Inspect AI (UK AI Security Institute), a single fixed reasoning loop with two bash tools and no agent-specific scaffolding, driven by GPT-5.6 (the model behind Codex). Running the same model and tasks through this neutral harness, and comparing against Codex's own harness, is what isolates the harness's effect. First results:
MetricReAct harness GPT-5.6 (new)Codex harness GPT-5.6 (ref)
Recovery (crash)13/20 = 65%12/20 = 60%
Exploitation1/20 = 5%2/20 = 10%

Using the same model with a simpler ReAct agent gives similar recovery results (65% vs. 60%), while exploitation remains low in both settings (5% vs. 10%). This suggests that the recovery performance of GPT-5.6 is not specific to the Codex harness on this subset. However, the experiment does not isolate model effects across different agents, so we continue to report the main results as system-level comparisons.

Dear Reviewer cHgp, thank you again for your thoughtful feedback and suggestions. We would like to kindly follow up on our rebuttal and ask whether our responses have adequately addressed your concerns. We would greatly appreciate any further feedback or clarification you may have, and we would be happy to address any remaining questions.

Reviewer_QBosOpenReview ↗
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Paper summary

The paper suggests a benchmark for evaluating whether AI agents can identify and exploit real software vulnerabilities using only vulnerable and patched binaries, without access to source code or vulnerability descriptions. The benchmark contains tasks derived from real vulnerabilities across multiple open-source projects, covering six vulnerability categories and three complexity levels. Three AI agents are evaluated on two capabilities: vulnerability recovery and successful exploitation. The main results indicate that Codex achieves an 88% vulnerability-recovery rate and a 22% exploitation rate, outperforming the other agents. Additional experiments examine the benefits of having access to patched binaries, reasoning effort, repeated attempts, and binary hardening.

Critical strengths
  • The paper investigates a relevant cybersecurity threat - the ability of AI agents to generate exploits by comparing patched and vulnerable binaries.

  • Evaluation done using real vulnerabilities in open-source projects and evaluates different factors, including the availability of patched binaries, vulnerability descriptions, reasoning effort, repeated attempts, and binary hardening.

Critical weaknesses
  • Evaluation uses simplified scenario or exploitation which might not reflect real scenario.

  • The paper measures vulnerability recovery using differential crash testing. However, generating an input that crashes the vulnerable version but not the patched version does not necessarily demonstrate that the agent identified or understood the intended vulnerability.

  • The main evaluation appears to rely on one trajectory per agent and task, although agent behavior can vary substantially between independent attempts. The repeated-attempt experiment demonstrates this variability, showing that exploitation success improves from 13.3% to 30% across three attempts on a 20-task subset. However, repeated experiments are not reported across the entire benchmark, and confidence intervals or statistical significance analyses are absent. Similarly, the patched-binary ablation uses only 20 tasks, where the increase from 15% to 30% represents three additional successful cases.

  • The paper evaluates three AI agents, but does not compare their performance against conventional automated vulnerability-discovery or binary-analysis approaches.

Questions for authors
  • The exploitation success rate drops significantly when common binary-hardening mechanisms are enabled. Why was the main evaluation conducted without the full set of these protections? Could the authors evaluate hardened configurations on all 100 tasks rather than only the 22 previously successful cases?

  • How does the evaluation distinguish between an agent that correctly identifies and triggers the intended vulnerability and one that generates a different crash specific to the vulnerable binary? C

  • How representative is the benchmark's standardized victim interface and privileged flag-retrieval helper of realistic environments?

  • How does CyberBinGym performance compare with traditional binary-differencing, fuzzing, or vulnerability-discovery techniques that do not use LLM agents? Such a comparison would help quantify the contribution of AI-driven reasoning beyond conventional automation.

5 comments

We thank the reviewer for a careful, concrete review. We address each weakness and question below; several are already answered by analyses added since the reviewed draft.

W1 / Q3: "Simplified scenario; how representative are the standardized victim interface and the privileged flag-retrieval helper?"

The victim environment is deliberately standardized, but it is realistic and preserves what the exploitation metric is meant to measure.

  • The interface is realistic. The victim exposes the target's standard input/output over socat (Appendix A.3), which is how a large class of real targets actually consume untrusted input: network-facing parsers, document/image processors, and protocol handlers run as services. This matches the setup used by other real-software agent benchmarks (e.g. ExploitGym (Wang et al., NeurIPS 2026) and The Last Ones (Folkerts et al., NeurIPS 2026)).
  • Invoking the flag helper is equivalent to arbitrary command execution. Over the network interface the agent cannot run the helper directly: it must first turn the memory-corruption bug into control-flow hijack and code execution inside the victim process. Once it can execute the helper, it can execute any command with the victim's privileges, i.e. it has achieved remote code execution (RCE). A captured flag therefore certifies a full RCE, the standard end goal of real-world exploitation.
  • The flag helper is a success oracle, not an assist. The Set-UID helper (under a randomized path in /opt/cybingym, Appendix A.3) only standardizes the success signal, a single auditable objective ("read a root-owned secret") that stands in for an arbitrary post-exploitation action. It does not lower the bar: the agent must already have obtained genuine code execution to invoke it, and the trajectory audit rejects flags obtained via (a) direct environment access or (b) the target's own built-in command-execution features (Section 3.1; Figure 2 audit panel). So reaching the flag is possible only after real exploitation.

W2 / Q2: "Differential crash testing need not show the agent identified the intended vulnerability."

We agree that a differential crash does not necessarily mean the agent has recovered the exact vulnerability recorded in the original report. However, we argue that requiring an exact match would not fully reflect the 1-day threat model we study.

A software release may fix multiple vulnerabilities. Unlike a single vulnerability-fixing commit, a released version often includes several security fixes and other code changes. In our benchmark, the difference between vulnerable and patched versions covers a median of around 1,000 changed lines. For example, sample 368 contains changes across 86 C files. In a real 1-day scenario, an attacker comparing two releases is interested in finding any vulnerability that can be triggered in the old version but is no longer present in the new one. Whether that vulnerability matches the one originally reported is less important from the attacker's perspective. Requiring an exact match would therefore exclude valid findings that are relevant to the threat model we aim to evaluate.

Our recovery metric reflects this setting. We consider a PoC successful if the same input causes the vulnerable binary to crash while the patched binary executes normally. This measures whether the agent can identify a behavioral difference between the two versions and construct an input that triggers it. We do not require the crash to match the reference vulnerability's type or location, and we will clarify this distinction in the paper.

This evaluation approach is also consistent with existing benchmarks. CyberGym (Wang et al., ICLR 2026) validates PoCs by differential execution on vulnerable and patched builds, and SEC-bench (Lee et al., NeurIPS 2025) verifies its reproduced PoCs the same way (a sanitizer crash before the patch, none after). We apply the same differential criterion in a binary-only setting.

W3: "One trajectory per task; no confidence intervals / significance; repeats and the patched-binary ablation only on 20 tasks."

We agree statistical reporting was missing. We have computed it from the released data snapshot and add it to the revision.

The 20-task scaling/ablation subsets are matched subsets spanning the difficulty levels. They are 20 tasks because one extra full-benchmark pass of Codex costs about \2.8kandabout213agent−hours,andthreerepeatsoverall100taskswouldbeabout2.8k and about 213 agent-hours, and three repeats over all 100 tasks would be about \\8.4k for Codex alone; we therefore scope the repeated-attempt and patched-binary findings to the matched 20-task subset and do not run additional full-benchmark repeats.

To quantify uncertainty on the subset, we repeated Codex three times per task and estimate each task's success probability with its own Beta posterior, then propagate (merge) the per-task posteriors into the subset rate (truncated/infrastructure-failed runs are treated as missing, not failures):

Metric (Codex, 20-task subset, 3 runs/task)Rate95% CI (seed)95% CI (as benchmark sample)
Recover vuln.72.5% (14.5/20)[65, 80]%[59, 85]%
Exploit17.5% (3.5/20)[11, 23]%[7, 29]%

The seed interval is the re-run uncertainty with the 20 tasks held fixed; the benchmark-sample interval additionally treats the 20 tasks as a sample of the full suite. A variance decomposition shows run-to-run (seed) uncertainty is the smaller component (~ ±4 pp) while between-task difficulty heterogeneity is larger (~ ±8 pp): individual tasks are seed-dependent (about one-third of recovery outcomes flip across the three runs), but these flips average out, so the subset-level rate is reproducible to ~ ±4 pp under reruns. These intervals rest on only 2–3 completed runs per task and are reported as approximate bounds.

As shown in Figure 5, the patched-binary ablation's recovery effect is large and robust (55% to 90%, i.e. 11 to 18 of 20; exact paired, one-sided p ≤ 0.033 across all feasible pairings), whereas the exploitation delta (15% to 30%, 3 to 6) is suggestive but not individually conclusive, which is why we corroborate it with the patch-influence audit (17 direct among the 26 trajectories audited so far) rather than resting on the 20-task delta alone.

W4 / Q4: "No comparison with conventional binary-differencing / fuzzing / vulnerability-discovery."

Our main target is exploitation, and the solver gets only the stripped vulnerable and patched binaries: no source, no vulnerability description, no reference PoC. Conventional (non-agent) tools for this kind of task come in two families. For each family we take the strongest open, widely-used tool and give it advantages the agent never gets, so every gap below is a lower bound on the agents' real edge.

  • Fuzzing feeds a program many inputs to find one that crashes it, the conventional analog of our recovery metric. The standard tool is AFL++ (Fioraldi et al., USENIX WOOT 2020), the successor to AFL and the default engine in Google's OSS-Fuzz and the FuzzBench benchmark. We run it in QEMU mode (the usual way to fuzz closed-source software), and we also build a patch-directed variant, the binary-only analog of directed greybox fuzzing (AFLGo; Böhme et al., ACM CCS 2017, later folded into OSS-Fuzz), aimed straight at the patched code.
  • Symbolic execution / automatic exploit generation reasons about a crash to build a working exploit, the conventional analog of our exploitation metric. The standard open tool is angr (Shoshitaishvili et al., IEEE S&P 2016), the binary-analysis framework and symbolic engine behind Shellphish's exploitation system in the DARPA Cyber Grand Challenge. We hand it a real crashing input, so it skips the hard part, finding the crash, and only has to turn that crash into control of the instruction pointer.

Every baseline runs on the same binaries we give the agent in CyberBinGym, and is scored by the benchmark's own differential oracle.

BaselineAdvantage we grant it over the agentResultAgents (ref)
AFL++, QEMU mode (undirected)— (same input the agent gets)6/10088/100
Patch-directed AFL++ (ghidriff targets + angr-CFG block distance → custom-mutator seeds)told the patched code locations to steer toward7/10088/100
angr symbolic execution (v10.0.5), controllability analysisgiven a ground-truth crashing PoC0/2222/22

Each baseline gets an advantage, and all three still fall far short. Fuzzing finds shallow bugs that crash easily, but not the deep, structured input needed to reach the patched defect, which is exactly what the benchmark measures. The agents' own traces show the same limit: Codex runs AFL on 34 tasks, and only 6 of those lead to an exploit (Section 4, Appendix A.5). Patch direction adds one task and loses none; the gain is small because the patches are spread out (ghidriff finds a median of 35 changed functions per task), so locating the target is not the bottleneck. And angr, even when handed the crash, never reaches a control-flow hijack on any task: its symbolic search blows up (path explosion). Our setting is strictly harder, since the agent starts with no crash at all.

Directing the fuzzer on binaries alone took one step that source-level tools like AFLGo avoid: those tools rebuild from source with the distance measure compiled in. We cannot rebuild, so our distance map is keyed to the recovered CFG and has to be matched against the program's runtime execution trace instead.

No off-the-shelf system handles our binary-only, no-PoC setting end to end. Surveying the directed-fuzzing and AEG literature confirms it: every candidate needs heavy adaptation.

SystemWhy it does not fit (binary-only, no source / description / PoC)
1dFuzz (Yang et al., ISSTA 2023)pre/post-patch directed differential fuzzing, but not open-source
UAFuzz (Nguyen et al., RAID 2020)use-after-free only; needs a prior UAF trace
AFLGo (Böhme et al., ACM CCS 2017)source-level; rebuilds with distance instrumentation
Rex (Shellphish Mechanical Phish, DARPA CGC; Shoshitaishvili et al., IEEE S&P Mag. 2018)starts from a crash; targets its own exploit models
HEXP (Liu et al., IEEE TIFS 2025)binary-level exploit generation, but requires an existing PoC; heap-only

That gap is itself part of the finding. Conventional automation does not cover the binary-patch-to-exploit task the agents perform, which is why we report a fuzzing floor for recovery and no conventional number for exploitation.

Comments on the paper

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Thank you for your time and contributions!
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