acceptodds
Under review as a conference paper at ICLR 2027

CROSS: Coupled Recurrence of Latent-Symbolic Security-State for Runtime Safety Monitoring of AI Agents

Abstract

Long-horizon tool-using agents can encounter safety failures whose decisive evidence is distributed across individually innocuous actions. Earlier observations may change the safety of a later tool call, while successive actions may diverge from the user's authorized objective. Monitoring such failures requires trajectory memory, but repeatedly encoding the full history increases computation, and a fixed local window discards earlier evidence. We propose **CROSS** (**C**oupled **R**ecurrence **O**f latent-symbolic **S**ecurity **S**tates), an action-level monitor that couples recurrent neural state with a symbolic finite-state machine. The neural state summarizes contextual cross-step evidence; the symbolic state retains explicit security facts and determines auditable interventions. Symbolic state conditions the neural update, and neural predicates drive the symbolic transition, while the neural observation window remains bounded. We evaluate CROSS on synthetic risk-propagation and goal-shift tasks and on StepShield, AgentDojo, and Upward Deception. With a 1.7B backbone, CROSS achieves the highest F1 among all evaluated guards, including a baseline with a 7B backbone, on the synthetic dataset and all three public benchmarks. These results demonstrate the effectiveness of coupled recurrence for cross-step safety detection in the evaluated settings. Ablation studies further support the value of complementary security states and contextual evidence.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
Agent safety, Runtime monitoring, Recurrent security states, Neuro-symbolic system, Finite state machine

Reviews

Among:
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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_XpAoOpenReview ↗
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2
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Paper summary

This paper addresses the safety monitoring challenge for long-horizon, tool-using AI agents, where safety failures often stem from evidence distributed across multiple individually innocuous steps. The authors propose CROSS, a runtime monitoring framework that combines a recurrent neural state with an extended Finite-State Machine. The primary contribution is a novel neuro-symbolic recurrent architecture that bidirectionally couples continuous memory with discrete policy states under a bounded neural observation window.

Critical strengths
  1. CROSS effectively addresses the long-horizon context tradeoff in agent monitoring by introducing a bidirectional, coupled recurrence mechanism. Pairing continuous neural memory with deterministic FSM states allows the framework to operate within a fixed neural observation window.

  2. Despite utilizing a significantly smaller backbone, CROSS achieves state-of-the-art F1 performance across synthetic tasks and three diverse public benchmarks, outperforming stronger 4B–7B guardrail baselines.

Critical weaknesses
  1. The execution of CROSS heavily relies on JJ predefined security predicates and hand-crafted FSM rules.

  2. It remains unverified how CROSS behaves in closed-loop settings where its blocking interventions actively alter the agent's multi-turn generation trajectory.

Questions for authors
  1. In the Introduction, the author's innovation seems to be incremental, combining two methods.

  2. The description in the introduction section is obscure and difficult to understand, making it not very user-friendly for readers in non-professional fields.

3.In the introduction, the author should further clarify the key challenges or difficulties of the research question.

  1. The model architecture adopts traditional RNNs, which may lead to problems in capturing long-term dependencies. Meanwhile, this has resulted in very limited innovation in the model.

  2. The author used four indicators for evaluation. However, in areas of anomalies or safety, due to the scarcity of samples, AUROC and AUPRC are usually used to evaluate model performance more accurately.

2 comments
AuthorsOpenReview ↗

Response to Reviewer XpAo - Part 1

We thank the reviewer for recognizing CROSS's approach to the long-horizon context trade-off and its reported F1 performance against the evaluated 4B–7B guardrails. We appreciate the questions about the architecture, evaluation, and presentation, and address each below.

W1. Dependence on predefined predicates and hand-crafted FSM rules

We agree that the predicate vocabulary and FSM rules define the scope of the monitor's policy coverage. Their roles, however, differ from those of the learned component. Predicate meanings are predefined, but their values are inferred from the evolving trajectory by the neural model; they are not supplied as oracle facts during evaluation. The FSM then combines these predictions with persistent records of object bindings, provenance, and explicit authorizations to determine an intervention.

This separation allows contextual interpretation to remain learned while making policy decisions reproducible and inspectable. For example, a neural prediction cannot itself create an authorization: the FSM requires a matching explicit grant. Defining this interface also does not require enumerating every possible attack sequence. Nevertheless, missing predicates, incorrect predictions, or incomplete rules can limit coverage. We will clarify these assumptions and the engineering required to adapt the predicate vocabulary and rule set to a new policy domain. The component ablations support the value of complementary states; they do not establish robustness to arbitrary predicate or rule errors.

W2. Behavior under closed-loop interventions

We agree that closed-loop behavior remains unverified. Our experiments evaluate recorded trajectories without regenerating the agent's subsequent actions after a block. The synthetic timely-blocking analysis reports 74.30% for CROSS versus 67.97% for StepGuard, the strongest baseline on this metric. Success requires blocking at the first unsafe action, with all unsafe trajectories as the denominator. This provides evidence about intervention timing during replay.

A live intervention can change later observations, trigger retries, or cause the agent to seek approval or abandon the task. The existing results do not measure these consequences. We will state this distinction explicitly. A direct evaluation would use paired interactive rollouts on the same tasks and agent seeds, measuring safety violations, legitimate task completion, unnecessary blocks, and recovery after intervention.

Q1. Is the contribution an incremental combination of two existing methods?

The contribution is the specific coupling of two persistent security states at the action boundary. At each event, the symbolic state conditions the neural update; a predicate head maps the updated latent representation to security predicates; and these predicates update the symbolic records that govern both the current intervention and subsequent neural updates. This recurrent information flow connects ambiguous contextual evidence with explicit permissions and object bindings while keeping the neural observation window bounded.

The component results reported in Section 5.4 support this design: synthetic F1 is 91.51% for CROSS, compared with 77.26% for Symbolic-Only, 66.59% for Neural-Only, and 60.48% for Stateless. These controls retain current-event computation while changing cross-event persistence. They therefore support complementary contributions from the two persistent states, although they do not isolate bidirectional coupling against every alternative fusion design. We will sharpen the Introduction around this contribution and distinguish it from the established ideas of neural recurrence and finite-state monitoring.

Q2. Accessibility of the Introduction

We appreciate this feedback and will revise the Introduction to explain the monitoring problem through a concrete example before introducing the architecture. An agent may read sensitive information early in a task, perform several benign actions, and later propose an external write. The write's safety depends on its relationship to the earlier information and the applicable authorization. This example will make the roles of contextual memory and explicit security records clear to readers outside agent-safety research. We will also define the main terms at first use and introduce the mechanism in plain language before presenting its formalization.

AuthorsOpenReview ↗

Response to Reviewer XpAo - Part 2

Q3. Clarifying the key research challenges

We will organize the motivation around three concrete challenges: retaining distant security evidence without repeatedly processing an expanding history; connecting ambiguous semantic evidence to exact object bindings and permissions; and producing auditable action decisions from these two forms of information. A short observation window can lose earlier evidence, latent compression does not by itself provide explicit authorization semantics, and symbolic rules require context-sensitive predicates. CROSS addresses these challenges through recurrent neural memory, persistent symbolic records, and the predicate-and-feedback interface between them. The revision will connect each challenge directly to its corresponding design choice.

Q4. Use of traditional RNNs and long-term dependencies

CROSS uses a Transformer-based event encoder with recurrence across agent events. The Transformer receives the current event, learned memory tokens carrying earlier evidence, and an embedding of the symbolic state. Learned query outputs and a fast–slow gated projector then update the memory for the next event. Thus, the architecture does not replace contextual encoding with a vanilla RNN; its recurrent state carries information between successive Transformer computations.

The fast–slow update is designed to balance retention and adaptation, while symbolic records preserve explicit facts and authorizations. We agree that compressed neural memory can still lose long-range evidence. The history and sequence-order analyses examine this issue in the evaluated settings, but do not establish lossless retention over arbitrary trajectory lengths or prove that the projector prevents forgetting. The novelty claim concerns the coupled security-state architecture, rather than recurrence or gating in isolation.

Q5. Why report decision metrics rather than AUROC and AUPRC?

We agree that AUROC and especially AUPRC would provide useful complementary evidence under class imbalance. Their relevance applies to safety detection as well as anomaly detection. Our evaluation reports ACC, precision, recall, and F1, with FPR in the ablations, because an action-level monitor must ultimately make an intervention decision. Recall measures missed unsafe cases; precision measures the fraction of alerts that are correct; and FPR measures the fraction of benign cases incorrectly flagged. These metrics characterize the evaluated operating point.

They do not replace threshold-swept evaluation. Even an exact confusion matrix cannot recover the score ordering needed for ROC or precision–recall curves, and rounded summary metrics generally do not uniquely determine integer confusion counts. We will revise the evaluation discussion to make this scope explicit. AUROC/AUPRC and recall at a specified low FPR are valuable extensions, but require suitable continuous scores or a clearly defined threshold-varying policy. For CROSS, evaluating its auxiliary neural risk score alone would not evaluate the complete FSM-based intervention policy. The current results support performance at the reported operating points.

We thank the reviewer again for recognizing the importance and promise of the work and for the constructive, detailed feedback. We will incorporate these explanations, the additional baseline results, and the identified reporting improvements into a future version.

Reviewer_DRnqOpenReview ↗
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1
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Paper summary

The paper proposes CROSS, a monitoring scaffold for LLM agents that decides at each step whether to allow, escalate, or block the agent’s next action. It features "memory across steps": a small learned latent state, maintained by a Qwen3-1.7B model, and an explicit rule-based state machine that tracks security facts such as sensitive objects, permissions, and untrusted instructions. The paper tests this on a synthetic dataset of risk-propagation and goal-shift trajectories and on three public benchmarks (StepShield, AgentDojo, Upward Deception), comparing it against four 4–7B guardrail models by binary detection metrics.

Critical strengths
  • The paper is clearly written and easy to follow, and the figures are well designed and informative.
  • The problem of monitoring long agent trajectories, where the safety of an action depends on earlier evidence, is important and timely.
Critical weaknesses
  • Origin of the evaluated trajectories (Table 2). The paper does not state which agent produced the trajectories evaluated on StepShield, AgentDojo, and Upward Deception, how they were sampled, or what the evaluation unit is (trajectory or step). This matters a lot for interpreting the results. In the AI control literature [1], the central difficulty is the capability gap between the trusted monitor and the untrusted agent it oversees: weak-to-strong monitoring is a hard problem. Here, a 1.7B monitor is evaluated on trajectories whose source is never described. I would like to see trajectories generated by agents of different capability (and ideally different families), and an analysis of when and why the monitor, and the baselines, fail as the agent gets stronger.

  • Trivial baselines outperform the evaluated methods. The authors kindly report metrics with two decimals, which is precise enough to recover integer TP/FP counts for every method. Reconstructing the evaluation sets in this way gives ~2,670 samples with 108 positives (4.0%) on StepShield, 1,088 samples with 278 positives (25.6%) on AgentDojo, and 200 samples with 103 positives (51.5%) on Upward Deception. On Upward Deception, the constant "always unsafe" classifier achieves F1 = 68.0, higher than CROSS (56.7) and every baseline. On StepShield, the constant "always safe" classifier achieves 95.96% accuracy, higher than every evaluated method.

  • AgentDojo is used as a static classification dataset. AgentDojo involves an attacker, a target agent, and, in this setting, a monitor; it distinguishes clean runs (benign utility), static attacks (utility under attack, targeted ASR), and adaptive attacks against the defense. The paper reports a single classification number and does not explain what it corresponds to (which agent, which suites, which attacks, what counts as unsafe). Could the authors report the standard AgentDojo metrics, i.e., benign utility, utility under attack, and ASR, with the monitor in the loop? With 65.6% precision, roughly a third of blocks are FPs, and their effect on task utility is never measured. A closed-loop evaluation in a realistic environment would also allow comparison with established defenses such as CaMeL [2], which enforces information-flow rules conceptually very close to the proposed FSM.

  • The synthetic dataset. I looked at the released synthetic dataset, and it is not a set of agent trajectories but a templated symbolic simulator. Events are JSON records over two tools ("tool_a", "tool_b"), twelve operation types, and sequential numeric object IDs, with only four distinct text strings across all 14,700 events (the "prompt injection" is always the literal string "approved success granted"). Trajectories have 5–13 events, which hardly qualifies as long-horizon. This raises further concerns about what kind of generalization is possible when training on such data, and how it translates to real agentic settings.

  • Missing natural baselines. The paper lacks (i) a prompted LLM monitor given the full trajectory, and (ii) the same Qwen3-1.7B backbone fine-tuned on the same data as a plain full-history classifier. Without (ii), it is impossible to tell whether the gains come from the proposed architecture or from in-distribution training that the off-the-shelf baselines never received.

[1] R. Greenblatt, B. Shlegeris, K. Sachan, F. Roger. AI Control: Improving Safety Despite Intentional Subversion. arXiv:2312.06942, 2023.

[2] E. Debenedetti, I. Shumailov, T. Fan, J. Hayes, N. Carlini, D. Fabian, C. Kern, C. Shi, A. Terzis, F. Tramèr. Defeating Prompt Injections by Design. arXiv:2503.18813, 2025.

Questions for authors
  1. Where do the trajectories in Table 2 come from: which agent model(s), which subsets, how were they sampled, and is the evaluation unit a trajectory or a step?
  2. Why do the evaluated methods, including CROSS, underperform a constant baseline (on Upward Deception in F1, on StepShield in accuracy), and how should Table 2 be interpreted in light of this?
  3. Is CROSS intended as a defense? If so, how does it behave under adversarial pressure, e.g., adaptive prompt injections designed to avoid triggering the "untrusted instruction" predicate, or an agent that is aware of the monitor?
  4. Were the baselines trained or adapted on the synthetic data, or used off the shelf?
  5. On the public benchmarks, where do the event metadata (permissions, object bindings) required by the FSM come from, and was CROSS trained on any of these benchmarks?
  6. How was the synthetic dataset generated, and what role did GPT-5.6-sol play, given that the released data appears template-based?
  7. The paper motivates bounded-window monitoring by cost; can the authors report latency and compute compared with a full-history monitor?
  8. Could the authors explain more clearly why this direction is interesting in the first place? What is the motivation for building a small (1.7B) monitor inside a fairly elaborate scaffold (latent memory, predicate head, hand-written FSM), rather than using a stronger prompted or fine-tuned monitor with the full trajectory in context? And why do the authors expect this approach to work in covert settings, where a capable agent deliberately hides its intent and spreads a harmful plan across individually benign-looking steps, given that the FSM can only act on the predicates the small model manages to extract?
3 comments
AuthorsOpenReview ↗

Response to Reviewer DRnq - Part 1

We thank the reviewer for recognizing the clarity of the presentation and the importance and timeliness of the problem. We clarify the evaluation protocols below and use the component controls, intervention-timing results, and additional same-backbone comparisons to address the concerns about architectural value and monitoring cost.

W1 / Q1: Trajectory provenance and weak-to-strong monitoring

The architectural evidence extends beyond comparing models of different sizes. Within CROSS, synthetic F1 rises from 60.48% without persistent state to 66.59% with neural persistence, 77.26% with symbolic persistence, and 91.51% with both. These controls support complementary security memory independently of the parameter counts of external guards.

We will clarify the public evaluation sources and units:

  • StepShield: 216 held-out trajectories; 2,670 labeled post-observation steps, including 108 first-divergence positives. The source paper describes trajectory generation using GPT-4 and Claude-3.
  • TS-Bench–AgentDojo: 1,088 scored current-action records, including 278 positives, from 1,220 publisher records across four suites; 132 exceed the input limit. ToolSafe reports collection with GPT-4o and Qwen3-30B-A3B-Instruct-2507. These records are action views, rather than independent episodes.
  • Upward Deception: Locally adapted public tasks executed using the configured endpoint gemini-3.7-flash. Of 256 majority-labeled examples, 200 meet the common scoring limit. Labels concern the final reply's observable source-provenance risk. All 56 excluded labeled examples are positive; the scored subset mixes development and test roles and is not an independent held-out estimate.

These heterogeneous units require explicit reporting, and corpus-level model names cannot substitute for per-example capability analysis. Our present contribution is a compact recurrent monitoring architecture. Oversight of stronger, monitor-aware agents remains a direction for future research.

W2 / Q2: Constant baselines and the interpretation of Table 2

The numerical comparisons are correct, but a higher score on one metric does not establish better safety monitoring. Always-safe achieves 95.96% accuracy on StepShield while detecting none of its unsafe steps; CROSS detects 98.15%. The accuracy advantage therefore comes at the cost of eliminating unsafe-action detection.

On Upward, always-unsafe achieves 67.99% F1 versus CROSS's 56.68%, but also has 100% FPR. CROSS achieves 63.10% precision and 59.50% accuracy, compared with 51.50% for both under always-unsafe. Its FPR, derived from the reported confusion counts, is 31.96%: it correctly accepts 68.04% of labeled benign replies, whereas always-unsafe accepts none.

As an additional view of class discrimination, balanced accuracy derived from the same counts is 94.29% on StepShield and 59.75% on Upward, compared with 50% for either constant classifier. These derived metrics do not replace F1; they demonstrate that the constants do not dominate CROSS across detection and false-alarm criteria.

We will include constant baselines and confusion matrices. Our ranking claim concerns the four evaluated learned guards; the choice among operating points also depends on the costs of missed violations and unnecessary blocking.

W3 / Q3: Offline detection, intervention timing, and closed-loop defense

The evaluation provides evidence about intervention timing as well as classification. In the synthetic timing experiment, CROSS blocks exactly at the first unsafe action on 74.30% of unsafe trajectories, compared with 67.97% for StepGuard, the strongest baseline on this measure: a 6.33-point improvement.

On TS-Bench-AgentDojo, CROSS improves precision from StepGuard's 59.15% to 65.56%, with recall changing from 100% to 99.28%. On the common cohort, the reported counts correspond to 145 rather than 192 false alerts, a 24.48% reduction, while detecting 276 rather than 278 unsafe actions. Thus, the results support improved selectivity with high unsafe-action coverage; the false-alert fraction alone omits this comparison.

These results concern recorded trajectories. They do not measure how an intervention changes task completion, retries, or subsequent attacks. Benign utility, utility under attack, targeted ASR, and adaptive attacks remain complementary closed-loop evaluations. CaMeL is a relevant comparison under matched acting models, tasks, environments, and documented intervention capabilities.

AuthorsOpenReview ↗

Response to Reviewer DRnq - Part 2

W4 / Q6: Why the synthetic controls are informative

The restricted vocabulary enables a controlled test of state dependence. The simulator deliberately constructs safe and unsafe variants with the same final action, length, and lexical multiset. Resolving the target therefore requires earlier evidence and its relationships, such as whether a grant remains valid for the relevant object. Limited linguistic diversity constrains generalization claims, but does not eliminate this diagnostic value.

Separately, the manuscript's synthetic configuration and order controls test the use of historical evidence: removing persistence reduces F1 from 91.51% to 60.48%, and shuffling the same historical content reduces F1 by 9.17 points. Order-marginalized voting recovers most of the shuffled loss, remaining 1.92 points below the original order. Together, these results support the value of historical content and an additional benefit from its ordering. The release and each evaluation panel will be identified separately.

Retention was also tested beyond the release's 5–13-event sequences. In a separate historical development stress test, 8, 32, or 64 neutral events were inserted before the unchanged target event. On state-required cases, timely-block recall was 89%, 88%, and 88%, respectively. At 64 events, retaining state improved this rate by 18 points over resetting it (95% cluster-bootstrap CI: 12.67–23.67). This experiment uses an at-or-before blocking criterion, rather than the exact-boundary criterion above. It supports evidence retention across controlled gaps, rather than robustness to arbitrary strategic concealment.

The released data are nevertheless simulator-generated, and we will describe them accordingly.

W5 / Q4 / Q7: Same-training baselines and the cost of full history

The four competing guards were adapted on a unified dataset; they were not evaluated solely as off-the-shelf models. CROSS also used available training data from the three public benchmarks. We will state the adaptation and split protocols explicitly.

More directly, our additional FULL-H control uses the same 1.7B backbone and training data as CROSS, fine-tuned as a plain full-history classifier. This addresses the requested control for task-specific training:

DatasetFULL-H F1 (%)CROSS F1 (%)Measured latency speedupGFLOPs reduction
Synthetic91.7391.511.84×65.3%
StepShield48.3146.193.31×88.2%
TS-Bench–AgentDojo78.4378.977.17×93.6%
Upward Deception60.3456.683.95×87.1%

This comparison makes the architectural trade-off concrete. On synthetic data, CROSS is within 0.22 F1 points of full history at 1.84× speedup. On AgentDojo, it achieves 0.54 points higher F1 at 7.17× speedup. Across all four datasets, latency falls by 45.7–86.0% and memory by 0.05–0.55 GiB; StepShield and Upward incur F1 reductions of 2.12 and 3.66 points.

Compared with a 265-token sliding window, CROSS improves F1 by 31.03, 18.90, 35.59, and 15.90 points, respectively, with lower latency and computation throughout. Memory is slightly higher than Window 265, by 0.02–0.16 GiB. The advantage is therefore supported by an explicit quality–cost comparison, rather than an assumption that a small model must be efficient.

These results answer the same-backbone fine-tuned-baseline concern. A stronger prompted full-history monitor remains a further comparison; the present evidence does not establish superiority over every larger monitor.

Q5: Training exposure and FSM metadata

CROSS used available training data from all three public benchmarks, and all four guards received dataset adaptation. The public results therefore concern adapted systems, rather than zero-shot transfer.

For metadata, the simulator supplies typed operations, object identifiers, and explicit grants. Public adapters expose recorded observations, tool arguments, and environment fields, which must be distinguished from inferred predicates and trusted authorization records. A textual claim of permission does not constitute an authenticated grant.

The current documentation does not establish a complete field-level mapping for every scored public cohort. We will provide the adapter mappings, trust assumptions, and missing-field behavior in the Appendix.

AuthorsOpenReview ↗

Response to Reviewer DRnq - Part 3

Q8: Why use a compact recurrent monitor with an FSM?

The extra state has a measurable contribution. Full CROSS reaches 91.51% synthetic F1, compared with 77.26% for symbolic persistence alone and 66.59% for neural persistence alone. Relative to Symbolic-Only, it raises recall by 14.02 points while lowering FPR from 18.06% to 4.72%. The improvement therefore cannot be explained simply by triggering more alarms.

The separate available-history panel provides another test: increasing retained history from one to four prior events raises recall from 35.00% to 80.67% at the same 9.00% FPR. Together with the matched FULL-H comparison, these results motivate carrying useful context in recurrent state while preserving explicit, inspectable policy decisions.

The target is distributed observable evidence: an earlier sensitive read, revocation, or commitment may change the safety of a later action. Neural memory retains contextual cues, while symbolic records preserve bindings and constraints. This does not make wholly concealed intent observable. Adaptive concealment and weak-to-strong oversight remain directions for future research, while the reported controls already support the value of persistent security state in the evaluated settings.

We thank the reviewer again for recognizing the importance and promise of the work and for the constructive, detailed feedback. We will incorporate these explanations, the additional baseline results, and the identified reporting improvements into a future version.

Reviewer_NrLhOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
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Soundness
2
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Paper summary

This paper proposes CROSS, a runtime safety monitor for AI agents that combines recurrent latent representations with symbolic finite-state machines to detect cross-step safety violations. Experiments on synthetic datasets and three public benchmarks demonstrate improved F1 over existing guardrails, with ablations supporting the complementary roles of neural and symbolic states.

Critical strengths

Effective architecture: Combining latent recurrence with explicit symbolic states is a meaningful approach to long-horizon safety monitoring. The component ablations provide evidence that both mechanisms contribute to performance.

Promising empirical results: CROSS achieves the highest F1 across all evaluated benchmarks despite using a smaller 1.7B backbone. Improvements on StepShield (+8.60 pp), AgentDojo (+4.64 pp), and Upward Deception (+10.69 pp) are encouraging.

Critical weaknesses

Limited validation of practical efficiency: Although bounded neural memory is a central motivation, the paper lacks direct comparisons of inference latency, memory consumption, and computational overhead against full-history or sliding-window monitors.

Insufficient evidence for real-world reliability: The evaluation focuses on offline detection rather than closed-loop agent execution. Some results remain concerning for deployment, including 30.20% precision on StepShield and 51.46% recall on Upward Deception. Moreover, the comparisons are not parameter-matched, and statistical uncertainty is not reported.

Questions for authors

How does CROSS compare with full-history and sliding-window baselines under matched inference budgets, particularly as trajectory length increases?

Can the authors report statistical variance across runs and evaluate the impact of false blocking on legitimate task completion in an interactive agent environment?

How sensitive is performance to predicate extraction errors and the design of the FSM rules?

2 comments
AuthorsOpenReview ↗

Response to Reviewer NrLh - Part 1

We thank the reviewer for recognizing the value of coupling latent and symbolic states for long-horizon monitoring, and for highlighting the component ablations as evidence that both contribute. We also appreciate the reviewer's acknowledgment that CROSS achieved the highest F1 among the evaluated guardrails across all four benchmarks with a 1.7B backbone.

W1 and Q1. What does CROSS gain at a comparable inference budget, and how does trajectory length matter?

Setup. The cost comparison uses Qwen3-1.7B (FP16, batch size one, V100). Full history re-encodes the visible prefix at each decision. Window 265 and CROSS share a 265-position input ceiling. The window retains recent events, while CROSS uses up to 256 current-event tokens plus four memory slots, one symbolic-state slot, and four query slots. Costs are per event on a separate synthetic sample, per post-observation event on StepShield, per current action with history already processed on TS-Bench-AgentDojo, and per event on Upward Deception (F1 scores the final reply). In a separate replay on synthetic dataset, we inserted 8, 32, or 64 neutral events before the unchanged final event of 600 trajectories. With three fixed checkpoints and a common threshold, we compared retaining both states with resetting them each step. On 100 unsafe trajectories requiring earlier evidence, recall counted a block at or before the first unsafe action.

Results. At the shared token cap, CROSS gains 15.90–35.59 F1 points over Window 265, with lower reported latency and fewer backbone FLOPs on all four datasets. Relative to full history, CROSS reduces latency by 45.7–86.0% and backbone FLOPs by 65.3–93.6%, with F1 differences ranging from −3.66 to +0.54 points. Memory savings are smaller (0.05–0.55 GiB relative to full history). In the controlled replay, recall was 89% at an 8-event gap and 88% at both 32 and 64 events. At 64 events, retaining state improved recall by 18 points over resetting it (paired 95% cluster-bootstrap CI [12.67, 23.67]).

DatasetMonitorF1 (%)Latency (ms)Memory (GiB)Backbone GFLOPs
SyntheticFull history91.731163.941,028.56
Window 26560.48753.86542.74
Window 51280.891053.90893.74
Window 102491.731163.941,028.56
CROSS91.51633.89356.56
StepShieldFull history48.311494.011,422.96
Window 26527.29833.86632.03
Window 51230.121213.921,089.93
Window 102439.351473.991,394.55
CROSS46.19453.88167.98
TS-Bench–AgentDojoFull history78.433874.284,260.64
Window 26543.38593.75346.35
Window 51250.89863.87666.09
Window 102459.661984.012,009.46
CROSS78.97543.91272.92
Upward DeceptionFull history60.342174.442,233.60
Window 26540.78783.86572.49
Window 51245.171133.90993.31
Window 102451.521524.031,458.72
CROSS56.68553.89287.21

W2. What do the public scores and model-size comparisons establish?

We agree that the absolute precision and recall matter for deployment. On StepShield, CROSS raises precision from StepGuard's 23.25% to 30.20% at the same 98.15% recall. This is a gain in selectivity, although about seven in ten alerts still concern benign steps. On Upward Deception, 51.46% recall is 9.71 points above the best competing recall, and nearly half of the labeled positive replies are still missed. These results support improved detection on recorded trajectories. They also explain our caution about unattended blocking.

The parameter-count concern applies to the comparison between complete systems. The four competing guardrails use 4B–7B backbones and CROSS uses 1.7B. To assess the contribution of recurrence, the more informative comparison is within CROSS. On the main synthetic evaluation, F1 was 60.48% when both states reset between events, 66.59% with neural persistence alone, 77.26% with symbolic persistence alone, and 91.51% with both. Adding neural persistence to symbolic persistence raised recall by 14.02 points and reduced the false-positive rate from 18.06% to 4.72%. Both changes support the reviewer's reading that the states contribute complementary evidence.

AuthorsOpenReview ↗

Response to Reviewer NrLh - Part 2

Q2. How variable are the results, and what do false blocks imply for task completion?

The main benchmark F1 values are point estimates. We can quantify checkpoint variability for a separate synthetic replay of 200 unsafe and 400 benign trajectories. It counted a block at or before the first unsafe action. Relative to resetting both states, the full monitor changed this rate by +10.0, −17.5, and −11.5 percentage points across three fixed checkpoints (mean −6.33, sample SD 14.46 points). On benign trajectories, retaining state reduced false blocking from 36.00% to 4.50%. The paired 95% cluster-bootstrap intervals were [−11.67, −1.00] points for the change in unsafe blocking and [−35.94, −27.11] for the change in benign false blocking. These intervals describe uncertainty across task clusters for the three checkpoints. In this replay, fewer benign interruptions came with lower overall unsafe coverage.

The paper's timing experiment asks a different operational question. CROSS blocked exactly at the first unsafe action on 74.30% of unsafe synthetic trajectories, compared with 67.97% for StepGuard, the strongest baseline on this measure. Together, the two replays quantify intervention timing and benign interruptions. We agree that a benign interruption and a failed task are distinct outcomes. An agent may recover after a block. Replaying a fixed trace cannot show how that intervention would change the agent's subsequent actions or its chance of completing the task. Preserving legitimate task completion and enabling recovery after an erroneous block are priorities for future closed-loop work.

Q3. How sensitive is CROSS to predicate errors and FSM rule choices?

An error audit located a concrete failure mode. In an earlier synthetic development study, each of three folds contained 75 benign and 75 unsafe trajectories. With learned predicates, the frozen monitor raised six false alarms in one fold. All six triggered the rule for sensitive data reaching an external destination. The other two folds had no classification errors. With annotated predicates and the auxiliary risk input fixed at zero, the recurrent finite-state machine (FSM) classified all 150 trajectories correctly in each fold. Resetting the FSM at every event, with the same predicates and rules, produced 15 false alarms and 30 misses per fold. Even with accurate current-event predicates, these decisions depended on facts retained from earlier events.

A separate rule test used 13 hand-authored cases with independently specified decisions. The original FSM passed all 13. Each of 11 deliberate rule changes caused its targeted case to fail. For example, removing the actor check made a permission granted to one actor usable by another. These tests identify decisions that depend on specific rules. The effect of broader policy changes on benchmark F1 and robustness to unfamiliar predicate errors remain directions for future improvement.

We thank the reviewer again for recognizing the architectural contribution and for the constructive questions about practical use. In the next version, we will incorporate the efficiency comparison, explain how the token budget and the two intervention criteria are defined, and clarify what the checkpoint and rule diagnostics establish. We will also make the limits of the deployment evidence explicit wherever we discuss task completion.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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