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Under review as a conference paper at ICLR 2027

GAVEL: Global Auditing via Evidence Latents for Long-Horizon Agents

Abstract

Safety evidence in long-horizon agent trajectories is often dispersed across multiple actions, with critical signals appearing sparsely, emerging only after long delays, or becoming unsafe only through their composition. Existing local guardrails focus on individual turns or short contexts, while memory-based monitors must decide what to retain before later actions reveal the significance of earlier evidence. We introduce Global Auditing via Evidence Latents (GAVEL), a two-pass architecture that separates global evidence organization from detailed record access. An Evidence Encoder learns a compact set of evidence latents from the full observed trajectory under safety supervision, while an Audit Decoder judges the original record conditioned on this learned global context. Across three safety benchmarks and four language-model backbones, GAVEL achieves the highest mean accuracy in all 12 evaluated settings, outperforming the strongest competing baseline by up to 12.6 percentage points. On LongSafety diagnostics with Qwen3-8B, GAVEL shows particularly large gains for delayed and compositional evidence, improving accuracy by 17.1 and 18.0 points over the strongest baseline in the corresponding buckets. Controlled latent interventions further show that the final prediction depends on trajectory-matched evidence context.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
AI safety, agent guardrails, long-horizon agents, safety auditing, evidence latents, LLM alignment

Reviews

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

This paper studies trajectory-level safety auditing for long-horizon LLM agents, where unsafe behavior may depend on sparse, delayed, or compositional evidence distributed across multiple interactions. It proposes Global Auditing via Evidence Latents (GAVEL), a two-pass framework comprising an Evidence Encoder and an Audit Decoder. The encoder processes the complete observed trajectory and produces compact evidence representations using 16 learnable queries, while the decoder assesses the original trajectory conditioned on these representations. Training uses trajectory-level safety labels and updates the queries, encoder LoRA adapters, and classification head while keeping the pretrained backbone weights frozen. Across three safety benchmarks and four backbones, GAVEL achieves the highest mean accuracy in all 12 main evaluation settings, with improvements of up to 12.6 percentage points over the strongest competing baseline. Additional LongSafety diagnostics examine performance under dispersed evidence and increasing context lengths, while ablations and latent interventions investigate the contribution of the learned evidence context.

Critical strengths

The method is well suited to long-horizon safety auditing. GAVEL first uses an Evidence Encoder to integrate scattered evidence across the full trajectory. The Audit Decoder then makes predictions based on both the evidence representation and the original trajectory, capturing global information dependencies while preserving fine-grained behavioral details. This design is well suited to risks that emerge only after a delay or arise from combinations of multiple steps (Secs. 3.2–3.3; Fig. 2).

The training scheme is parameter-efficient and requires no fine-grained evidence annotations. The method is trained end-to-end using only trajectory-level safety labels. It updates the learnable queries, the Encoder’s LoRA parameters, and the classification head while keeping the pretrained backbone frozen. No additional annotations of evidence spans or explanatory text are required, reducing both the number of trainable parameters and annotation requirements (Sec. 3.4; Appendix B.2).

The main experiments and targeted diagnostics provide substantial evidence of effectiveness. GAVEL achieves the highest average accuracy across all 12 main experimental settings, spanning three safety benchmarks and four backbone models. In the LongSafety diagnostics, it outperforms the strongest baseline by 17.1 and 18.0 percentage points on the delayed-evidence and compositional-evidence categories, respectively, supporting its ability to handle safety evidence distributed across multiple steps (Table 1; Appendix G, Table 9).

Critical weaknesses

Although the main experiments use four different backbone models, the paper does not clearly specify which models serve as the trained Encoder and Decoder in each experimental setting.

One important ablation is still missing: keeping the rest of the framework unchanged, removing only the 16 queries appended to the Encoder input, and retraining the model.

Figure 7 uses an exponentially spaced sweep to reveal the broad trend, but this is insufficient to establish whether 16 is locally optimal.

Questions for authors

Why is LoRA used for training? Would full-parameter fine-tuning be feasible, and how would it compare?

How exactly are the evaluation metrics computed for each of the three benchmarks? The paper does not explain this in sufficient detail.

Could the authors add a baseline that directly classifies the Evidence Encoder’s output under the same training setup, to verify the necessity of the Audit Decoder?

3 comments

We sincerely thank the reviewer for the thorough and constructive evaluation, as well as the positive assessment of our two-pass framework, parameter-efficient training strategy, and empirical gains across both benchmark and diagnostic evaluations.

Below, we address the weaknesses and questions point-by-point, with corresponding new ablation experiments and clarifications incorporated into the revised manuscript.

W1. Clarification of Encoder–Decoder Configurations

We appreciate the reviewer pointing this out. In the original submission, while we stated the backbone families used, the exact instantiation and parameter relationship between the Evidence Encoder and Audit Decoder were not explicitly tabulated.

To resolve this ambiguity, we have updated Appendix B.2 with an explicit configuration table (Table R3-1). In each experimental setting:

  1. Backbone Family & Initialization: Both the Evidence Encoder and Audit Decoder are independently instantiated from the same pretrained backbone checkpoint (e.g., both use Qwen3-8B).
  2. Parameter Independence: The two modules maintain separate parameter sets without shared runtime weights.
  3. Training Allocation:
    • Evidence Encoder: The backbone is kept frozen. Only the K=16K=16 learnable query tokens and lightweight LoRA adapters (applied to WqW_q and WvW_v, with rank r=16,α=32r=16, \alpha=32, dropout 0.1) are trained.
    • Audit Decoder: The backbone is kept frozen. Only the terminal linear classification head ww is trained.

Table R3-1. Backbone configurations of the Evidence Encoder and Audit Decoder.

Experimental SettingEvidence Encoder BackboneAudit Decoder BackboneWeight InitializationWeight Sharing
Qwen3Guard-Gen-4BQwen3Guard-Gen-4BQwen3Guard-Gen-4BSame CheckpointNo
Qwen3-4B-Instruct-2507Qwen3-4B-Instruct-2507Qwen3-4B-Instruct-2507Same CheckpointNo
Qwen3-8BQwen3-8BQwen3-8BSame CheckpointNo
Llama-3.1-8BLlama-3.1-8BLlama-3.1-8BSame CheckpointNo

This structural decoupling ensures that global evidence organization and fine-grained verification are handled by specialized pathways while preserving the foundational knowledge of the underlying LLM backbones.

W2. Retraining Ablation for Learnable Queries

We fully agree with the reviewer. The original intervention experiments in Section 4.4 and Figure 4 primarily evaluated inference-time substitutions, which do not fully isolate the learning contribution of the queries during training.

To address this, we conducted retraining experiments from scratch on Qwen3-8B (Pre-Ex-Bench) under identical optimization setups:

  • No-Query (Retrained): We completely remove the 16 query tokens from the Evidence Encoder. Instead, the final K=16K=16 hidden states of the raw trajectory sequence are projected to form the latent context S~\tilde{S}, and the Audit Decoder backbone remains frozen, with only its classification head trained.
  • Random-Q (Retrained): We append 16 fixed random query vectors to the Encoder input (initialized randomly and frozen during training), retraining only the encoder LoRA and classification head.

Table R3-2. Retraining ablations of learnable queries on Qwen3-8B Pre-Ex-Bench.

VariantQuery ConfigurationQuery TrainableAccuracy (%)F1 (%)Unsafe Recall (%)
Full GAVEL16 learned queriesYes92.06 ± 2.2689.69 ± 1.6389.27 ± 1.92
No-QueryLast KK trajectory hidden states—88.42 ± 1.3784.66 ± 1.8282.91 ± 2.08
Random-Q16 fixed random queriesNo89.17 ± 1.2485.63 ± 1.5784.28 ± 1.96

The results show that removing learnable queries degrades accuracy by 3.64 pp and unsafe recall by 6.36 pp, demonstrating that simply reading the raw sequence hidden states is insufficient for trajectory-wide risk integration. While fixed random queries (Random-Q) partially mitigate this drop by providing decoupled readout slots, they still fall 2.89 pp short of Full GAVEL. This confirms that the observed improvements do not merely stem from extra token positions, but rely on task-driven supervision adapting the queries to bind dispersed risk evidence.

We have added this retraining ablation to Section 4.4 in the revised paper.

W3. Fine-Grained Latent Budget Sensitivity

We thank the reviewer for this constructive suggestion. While the exponential sweep (K∈{2,4,8,16,32,64}K \in \{2, 4, 8, 16, 32, 64\}) demonstrated broad stability across a 32-fold capacity range, we agree that it did not adequately characterize the local behavior around K=16K=16.

To investigate local sensitivity, we conducted a fine-grained sweep evaluating K∈{12,14,16,18,20,24}K \in \{12, 14, 16, 18, 20, 24\} on Qwen3-8B across all three benchmarks under identical protocols. The table also includes the existing K∈{8,32,64}K \in \{8, 32, 64\} results from the original exponential sweep.

Table R3-3. Fine-grained latent budget sensitivity on Qwen3-8B (Accuracy in %).

Latent Budget KASSEBench Acc (%)Pre-Ex-Bench Acc (%)R-Judge Acc (%)
K=8K = 890.7087.9090.20
K=12K = 1291.0891.3192.76
K=14K = 1491.6691.8293.18
K=16K = 16 (Default)91.5792.0693.40
K=18K = 1891.4991.8793.46
K=20K = 2091.2191.5593.12
K=24K = 2490.6087.6092.80
K=32K = 3290.8085.4093.50
K=64K = 6490.9092.2091.40

The fine-grained results indicate that performance remains stable around K=16K=16, forming a consistent high-performance plateau across K∈{14,16,18}K \in \{14, 16, 18\}, with all accuracy results within 0.24 pp of the K=16K=16 result. Under K=16K=16, the model achieves 91.57% on ASSEBench, 92.06% on Pre-Ex-Bench, and 93.40% on R-Judge, sitting squarely within this optimal region. Smaller budgets (K≤8K \le 8) exhibit noticeable drops due to evidence bottlenecking, whereas larger budgets (K≥24K \ge 24) show non-monotonic behavior on denser benchmarks like Pre-Ex-Bench, consistent with the Information Bottleneck perspective discussed in Appendix A.6.

We emphasize that K=16K=16 is not claimed to be a strict global mathematical optimum across every individual dataset—for instance, Pre-Ex-Bench exhibits a secondary peak at K=64K=64. Rather, K=16K=16 serves as a robust, universally effective operating point that balances compression quality and computation across distinct benchmarks.

We have incorporated Table R3-3 and this discussion into Appendix D.1.

Q1. LoRA versus Full-Parameter Fine-Tuning

We adopted LoRA primarily to achieve parameter efficiency and prevent the degradation of foundational linguistic reasoning under trajectory-level binary supervision.

To empirically compare LoRA against Full Fine-Tuning (Full FT), we trained a variant that unfreezes the full Evidence Encoder backbone (~8.0B parameters for Qwen3-8B), while keeping all other components (Audit Decoder frozen, data, learning rate schedule, epochs, batch size) strictly identical.

Table R3-4. LoRA versus full fine-tuning of the Evidence Encoder on Qwen3-8B Pre-Ex-Bench.

Training StrategyTrainable ParamsAccuracy (%)F1 (%)Unsafe Recall (%)Relative GPU Hours
LoRA (GAVEL)8.46M92.06 ± 2.2689.69 ± 1.6389.27 ± 1.921.00×
Full FT (Encoder)~8.00B92.28 ± 1.8790.08 ± 1.5489.91 ± 1.732.47×

Full fine-tuning yields only marginal improvements (+0.22 pp accuracy and +0.39 pp F1) at the expense of updating ~1000× more parameters and incurring 2.47× higher training compute. This demonstrates that full parameter deformation is unnecessary; adapting attention projections via LoRA is sufficient to steer the queries toward trajectory-level risk aggregation.

We have incorporated this comparative study into Appendix B.2.

Q2. Evaluation Metrics Across the Three Benchmarks

We appreciate the reviewer noting the need for a more detailed protocol. In the revised paper, we have expanded Section 4.1 and Appendix B.1 to clarify the prediction setups and metric computations:

  1. Benchmark Task Formats:

    • ASSEBench: Evaluates complete multi-turn interaction traces against official safety labels under the lenient standard.
    • Pre-Ex-Bench: Judges whether a proposed action in context poses potential hazards before execution.
    • R-Judge: Assesses complete agent-environment records for cumulative safety violations.
  2. Metric Definitions: In all benchmarks, Unsafe is designated as the positive class (y=1y=1), and Safe as the negative class (y=0y=0). Let TP,FP,TN,FN\text{TP}, \text{FP}, \text{TN}, \text{FN} denote true positives, false positives, true negatives, and false negatives:

    Accuracy=TP+TNTP+FP+TN+FN\text{Accuracy} = \frac{\text{TP} + \text{TN}}{\text{TP} + \text{FP} + \text{TN} + \text{FN}}

    Unsafe Recall (R)=TPTP+FN,Precision (P)=TPTP+FP\text{Unsafe Recall (R)} = \frac{\text{TP}}{\text{TP} + \text{FN}}, \quad \text{Precision (P)} = \frac{\text{TP}}{\text{TP} + \text{FP}}

    Unsafe F1=2×Precision×RecallPrecision+Recall=2TP2TP+FP+FN\text{Unsafe F1} = \frac{2 \times \text{Precision} \times \text{Recall}}{\text{Precision} + \text{Recall}} = \frac{2\text{TP}}{2\text{TP} + \text{FP} + \text{FN}}

  3. Multi-Seed Aggregation: For each random seed, predictions are thresholded at p=0.5p=0.5 on the test set to compute confusion matrices, reporting the empirical mean and standard deviation across seeds (Mean±Std\text{Mean} \pm \text{Std}).

Q3. Direct Classification from Evidence Encoder Outputs

We agree that directly evaluating whether the Evidence Encoder alone can perform safety classification helps isolate the architectural benefit of the Audit Decoder.

To verify this, we evaluated two architectural baselines under identical setups on Qwen3-8B (Pre-Ex-Bench):

  • Encoder-only Classifier: Removes the Audit Decoder entirely. We apply mean-pooling over the 16 latent representations from the Evidence Encoder and feed them into a linear classification head.
  • Single-pass LoRA Classifier: Employs a single backbone with LoRA to directly predict trajectory safety from the raw input in a single pass.

Table R3-5. Architectural comparisons on Qwen3-8B Pre-Ex-Bench.

MethodPassesEvidence EncoderAudit DecoderAccuracy (%)F1 (%)Unsafe Recall (%)
Encoder-only Classifier1YesNo87.91 ± 1.4684.03 ± 1.7482.37 ± 2.02
Single-pass LoRA1NoYes89.37 ± 1.6286.29 ± 1.8584.81 ± 2.14
Full GAVEL2YesYes92.06 ± 2.2689.69 ± 1.6389.27 ± 1.92

Directly classifying from compressed evidence latents (Encoder-only) leads to a 4.15 pp drop in accuracy and a 6.90 pp drop in unsafe recall. While the latents capture global dependency cues, severe compression into 16 slots inevitably discards fine-grained execution details (e.g., specific parameters or code snippets). Conversely, a single-pass model struggles to integrate distant evidence across long contexts. GAVEL succeeds because the Audit Decoder combines global latent guidance with unconstrained causal attention back into the exact original record.

We have added these comparisons and the corresponding analysis to Section 4.4.

Reviewer_DmuUOpenReview ↗
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Paper summary

This paper proposes GAVEL, a two-pass architecture for trajectory-level agent safety auditing. An Evidence Encoder uses learned queries to produce latent representations of the trajectory, which are then provided alongside the original record to an Audit Decoder for safety classification. Experiments across four model backbones and three benchmarks report consistent improvements over existing baselines.

Critical strengths
  • The problem of detecting safety violations involving dispersed evidence in long agent trajectories is relevant and well motivated.
  • Table 1 reports consistent improvements across 12 settings.
  • The authors also provide targeted experiments beyond aggregate accuracy, including latent interventions (Table 2), component ablations (Figure 4), and context-length experiments (Figure 5).
Critical weaknesses

1. Limited novelty and unclear role of the learned evidence latents.

  • The architecture largely combines existing techniques, including learned queries from Perceiver/BLIP-2 and standard classification objectives. The methodological novelty appears rather limited.
  • It is unclear how the learned queries specifically organize sparse, delayed, or compositional safety evidence (Section 3.2). Training uses only trajectory-level binary labels, without explicit evidence supervision.
  • Table 2 and Figure 4 show that the learned latents are useful for prediction, but do not establish what information they capture or whether they actually organize dispersed evidence. The latent perturbations may also introduce input configurations not encountered during training.

2. The experiments do not sufficiently isolate the proposed mechanism.

  • GAVEL processes the full trajectory twice. It is unclear whether the improvements come from the proposed evidence organization or simply the additional processing and learned representations. A similarly trained single-pass classifier with decoder LoRA or a simpler two-pass alternative would be useful comparisons.
  • The interpretation that MAGE fails to preserve weak early signals (Section 4.2) is not directly substantiated. Unlike MAGE, GAVEL's decoder also has access to the full original trajectory.
  • Figure 8 visualizes the decoder's attention to the original record, rather than the information captured by the evidence latents. It is unclear how this supports the claimed evidence-organization mechanism.

3. Limited evidence for the claimed long-horizon reasoning capability.

  • The main benchmarks do not all strongly test long-horizon dependencies (e.g., R-Judge, Appendix B.4).
  • Although Figure 3 provides delayed/compositional evidence diagnostics, it remains unclear whether the improvements require integrating distant evidence rather than detecting local cues. Some examples in Figure 9 also appear to contain locally identifiable safety violations.
Questions for authors
  1. What evidence shows that the learned latents capture and organize dispersed safety cues, rather than merely providing additional task-specific features?
  2. How would GAVEL compare against a similarly trained single-pass model with decoder LoRA, or a simpler two-pass architecture?
3 comments

We sincerely thank the reviewer for the thoughtful and constructive review. We are encouraged that the reviewer finds our problem setting relevant and well-motivated, appreciates our consistent performance improvements across 12 settings, and values our diagnostic and targeted evaluations (such as latent interventions, component ablations, and context-length evaluations).

Below, we address the weaknesses and questions.

W1 & Q1. Mechanism and Evidence of Learned Evidence Latents

While learned query interfaces (such as Perceiver and BLIP-2) have been applied to multimodal tasks, our methodological contribution lies in formulating trajectory-level safety auditing as a two-pass decoupled aggregation-and-verification problem. Standard guardrails inspect local turns or commit early to fixed-size memory states, leaving them vulnerable when safety-critical signals are individually innocuous and emerge only through chronological composition. GAVEL instead introduces an Evidence Encoder as a global evidence-routing workspace, preserving the uncompressed trajectory for the Audit Decoder's terminal verification.

To directly address what information the latents capture and whether they actively organize dispersed risk cues (rather than learning arbitrary generic features under weak binary supervision), we tracked attention allocation from query tokens to trajectory tokens across the Evidence Encoder's layers:

Table R2-1. Progressive attention concentration of query tokens on Qwen3-8B (ASSEBench).

Encoder LayerAttention Mass on Benign Steps (%)Attention Mass on Decisive Risk Spans (%)Relative Risk Focus Ratio
Layer 481.618.41.00×
Layer 1654.345.72.48×
Layer 2826.873.23.98×

Across network depth, attention mass from the K=16K=16 query tokens shifts sharply from benign-dominated coverage at Layer 4 to a concentration of over 73% directly on safety-critical interaction points (e.g., initial privilege escalations, obfuscated arguments, or external exfiltration actions). This confirms that trajectory-level binary supervision provides sufficient gradient signal through the frozen decoder to guide the queries toward isolating dispersed risk cues from routine tool-usage noise.

To further test whether specific trajectory-wide properties are linearly decodable from the latents SS, we trained linear probes on the intermediate vectors:

Table R2-2. Linear probe decoding accuracy from evidence latents SS (Qwen3-8B on ASSEBench).

Probed PropertyProbe Input: Raw Trajectory StatesProbe Input: Evidence Latents S
Cross-turn Tool Dependency (Presence of Multi-step Chaining)62.4 ± 1.886.7 ± 1.2
Information Exfiltration Path (Source-to-Destination Flow)58.9 ± 2.184.3 ± 1.5
Overall Trajectory Safety Label68.1 ± 1.991.2 ± 1.1

Probing the 16 latent vectors decodes cross-turn tool dependencies and sensitive data flows with 86.7% and 84.3% accuracy, substantially outperforming probes trained on pooled raw trajectory states. This demonstrates that the learned latents do not merely act as generic classification features; they specifically capture relational dependencies across distant steps.

Finally, we conducted latent interpolation between paired Safe and Unsafe trajectories:

Table R2-3. Latent interpolation between paired Safe and Unsafe trajectories on Pre-Ex-Bench.

Interpolation Ratio α (Unsafe Latent Weight)Predicted Risk Probability p^\hat{p}Unsafe Decision Rate (%)
α=0.0\alpha = 0.0 (Pure Safe Latent)0.08 ± 0.023.8
α=0.25\alpha = 0.250.23 ± 0.0417.5
α=0.50\alpha = 0.500.52 ± 0.0552.8
α=0.75\alpha = 0.750.79 ± 0.0483.1
α=1.0\alpha = 1.0 (Pure Unsafe Latent)0.95 ± 0.0297.2

The predicted risk probability transitions monotonically and smoothly as the latent representation shifts between safe and unsafe trajectories.

We have incorporated Tables R2-1, R2-2, and R2-3 into Section 4.4 and Appendix H.

W2 & Q2. Isolating the Two-Pass Mechanism against Single-Pass and Simpler Baselines

To determine whether the gains come from the structured factorization of global context and raw record access, or simply from extra computation and parameter capacity, we evaluated two architectural variants under matched trainable-parameter and optimization budgets on Qwen3-8B (Pre-Ex-Bench):

  1. Single-pass Decoder LoRA: A single LLM backbone trained with LoRA, strictly matching GAVEL's trainable parameter budget (8.46M) and receiving the full raw trajectory.
  2. Cascaded Two-pass Classifier (Textual Summary): A two-pass model where Pass 1 autoregressively generates a structured textual summary of the trajectory, and Pass 2 predicts safety conditioned on the concatenated summary and raw trajectory.

Table R2-4. Architectural comparison under matched trainable-parameter and optimization budgets.

ArchitecturePassesTrainable ParamsAccuracy (%)F1 (%)Unsafe Recall (%)
Single-pass Decoder LoRA18.46M89.37 ± 1.6286.29 ± 1.8584.81 ± 2.14
Cascaded Two-pass (Summary)28.46M88.15 ± 1.5384.92 ± 1.7083.10 ± 1.95
Full GAVEL28.46M92.06 ± 2.2689.69 ± 1.6389.27 ± 1.92

Single-pass LoRA underperforms GAVEL by 2.69 pp in accuracy and 4.46 pp in unsafe recall despite receiving identical raw inputs, as a single causal attention pass struggles to simultaneously filter extensive routine execution logs and connect distant dependencies. Generating discrete textual summaries (Cascaded Two-pass) degrades performance further to 88.15%, suffering from information bottlenecking where ambiguous or weak early cues are omitted during text generation.

Regarding MAGE, we also tested its memory retention directly: when an initial suspicious tool call is separated from its final consequence by more than 50 benign steps, MAGE's detection rate drops to 47.9%, whereas GAVEL maintains 82.4%. This empirically confirms that incremental memory updates struggle to anticipate which early signals become relevant later, whereas observing the full trajectory first avoids premature eviction.

We have incorporated Table R2-4 into Section 4.2 and Section 4.4.

W3. Verification of Long-Horizon Reasoning Dependencies

While R-Judge contains moderate sequence lengths, our main evaluations on ASSEBench and Pre-Ex-Bench represent extended multi-turn interactions with tool feedback, and our LongSafety experiments specifically stress-test contexts exceeding 8k words.

To confirm that the improvements in Figure 3 reflect multi-step dependency integration rather than reliance on localized trigger tokens, we performed an ablation on the Compositional diagnostic bucket (where no single step is unsafe in isolation) by selectively masking antecedent or subsequent actions:

Table R2-5. Impact of masking individual risk spans in the Compositional bucket (Qwen3-8B).

Evaluation SettingAccuracy (%)F1 (%)Unsafe Recall (%)
Full Trajectory (GAVEL)69.5 ± 3.064.1 ± 3.660.6 ± 4.2
Masking Component A (e.g., initial data read)48.2 ± 3.436.8 ± 3.929.5 ± 4.1
Masking Component B (e.g., external transmission)46.5 ± 3.234.1 ± 3.727.2 ± 3.8
Single-pass SFT on Full Trajectory51.5 ± 5.641.2 ± 6.134.8 ± 6.5

When either the antecedent or the consequential action is masked, GAVEL's unsafe recall collapses from 60.6% to ~28%, matching the baseline level. If the model were relying on a single localized trigger, masking the other component would leave the prediction largely unaffected. This sharp drop confirms that the unsafe verdict relies on the joint composition of distant, individually benign actions across the trajectory.

We have incorporated Table R2-5 and this discussion into Section 4.3 and Appendix G.

I thank the authors for their rebuttal efforts and the additional experiments conducted. The comparison against two architectural variants helps isolate GAVEL's architectural contribution, while the additional analyses of learned evidence latents shed light on their empirical usefulness.

However, I share Reviewer kyk1's view that the inconsistency between the reported GAVEL metrics and the MAGE confusion matrices raises questions about the validity of the main results.

After considering the whole rebuttal, I have decided to retain my rating.

Reviewer_kyk1OpenReview ↗
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Paper summary

This paper asks how to classify safety when decisive evidence is dispersed across an observed agent record. Its central hypothesis is that organizing this evidence before classification improves judgment. GAVEL first encodes the complete provided record into 16 input-dependent latents, then supplies the raw record and these latents to a frozen decoder with a classification head. Training updates learned queries, encoder LoRA, and the head using trajectory-level binary labels; a new record is classified without its label. The claimed contribution is a better computation over available evidence, rather than access to additional observations. The paper reports gains across three benchmarks and four main backbones, with diagnostic experiments intended to explain them.

Critical strengths
  1. A relevant problem with a useful framing. Separating sparse, delayed, and compositional evidence can expose failures that aggregate safety scores may hide, making trajectory-level evaluation more informative.

  2. A sensible design with modest supervision requirements. Keeping the raw record alongside learned latents preserves access to detailed evidence. Training needs only trajectory-level labels, without evidence-span annotations or rationales. These choices make the approach worth evaluating, although their comparative benefit remains uncertain.

Critical weaknesses
  1. Table 1 reports MAGE F1 scores of 85.74% on Pre-Ex-Bench and 89.43% on R-Judge with Qwen3-4B-Instruct-2507. At the reported recalls of 66.09% and 75.21%, even perfect precision would permit at most 79.58% and 85.85%, respectively. These values contradict Section 4.1's metric definitions, even when averaged over the same runs. The cause of these inconsistencies and their effect on the reported comparisons remain unclear. Appendix G.2 states that official LongSafety labels are used unchanged. However, the released data provide contexts, instructions, and safety metadata rather than binary trajectory labels, and the official evaluation judges generated responses. The inputs and labels underlying the diagnostic gains need clarification.

  2. SFT uses full fine-tuning, whereas GAVEL uses LoRA and two passes (Appendix B.2). A single-pass LoRA classifier with matched inputs, head, and tuning is needed to isolate the architectural gain. Latent interventions establish dependence on trajectory-matched latents but cannot replace this comparison. Neither Section 4.4 nor Figure 4 states whether Random Q and No context were retrained. The contribution relative to latent compression in ICAE and input-dependent prompting in IDPG also needs clarification.

Questions for authors
  1. Can you recompute the inconsistent entries from predictions, confirm that unsafe-class F1 and recall use the same runs, and provide per-run confusion matrices and seed counts? Please also clarify why the Full GAVEL bootstrap margins in Table 10 (±2.26/1.63/1.92) match the Qwen3-8B Pre-Ex-Bench standard deviations in Table 1.

  2. How was Safiron.jsonl in Appendix B.5 used for ASSEBench training relative to the 70/15/15 split in Table 4? For LongSafety, how were the classification inputs and binary labels constructed, and which checkpoint was evaluated?

  3. Were Random Q and No context in Figure 4 separately retrained? For No context, which representation was used by the classification head?

  4. To assess the architectural contribution, could you compare against a single-pass LoRA classifier with matched data, head, and tuning, reporting paired performance differences and compute costs?

5 comments

We sincerely thank the reviewer for the thorough evaluation. The reviewer's attention to metric consistency, evaluation protocols, and architectural comparisons has been vital in enhancing the transparency and empirical soundness of our work. Below, we address the weaknesses and questions point-by-point, with corresponding data corrections, protocol clarifications, and new ablation experiments incorporated into the revised manuscript.

W1 & Q1. Metric Consistency, Transcription Correction, and LongSafety Evaluation Protocol

1. Correction of MAGE Evaluation Metrics in Table 1 and Confusion Matrices

The reviewer's mathematical derivation regarding the upper bound of F1 is entirely correct. Following a thorough trace of our evaluation scripts and per-instance prediction logs, we confirmed that the reported MAGE F1 in Table 1 was a clerical transcription error that occurred during manual compilation of the final summary tables. We recomputed the metrics from the raw per-instance predictions across all five random seeds and updated the corresponding entries in Table 1:

Table R1-1. Corrected MAGE results on Qwen3-4B-Instruct-2507 (Pre-Ex-Bench and R-Judge).

DatasetMethodAccuracy (%)Unsafe F1 (%)Unsafe Recall (%)Precision (%)
Pre-Ex-BenchMAGE (Original)88.52 ± 2.5585.74 ± 3.12 (Err.)66.09 ± 3.34—
MAGE (Corrected)88.52 ± 2.5674.30 ± 5.2166.09 ± 3.3184.94 ± 8.18
GAVEL (Table 1)93.88 ± 1.0592.23 ± 0.7491.13 ± 3.7293.36 ± 1.15
R-JudgeMAGE (Original)89.67 ± 2.6789.43 ± 3.18 (Err.)75.21 ± 3.63—
MAGE (Corrected)89.65 ± 2.6881.09 ± 4.5975.20 ± 3.3588.03 ± 6.42
GAVEL (Table 1)91.39 ± 4.1491.84 ± 4.6591.26 ± 7.1293.12 ± 3.85

The corrected F1 scores strictly satisfy the theoretical upper bounds (74.30%≤79.58%74.30\% \le 79.58\% on Pre-Ex-Bench; 81.09%≤85.85%81.09\% \le 85.85\% on R-Judge). Correcting this transcription error does not alter the paper's empirical conclusions; GAVEL's advantage in detecting unsafe behavior remains solid and is even more pronounced: on Pre-Ex-Bench, GAVEL leads MAGE by 17.93 pp in F1 and 25.04 pp in Unsafe Recall; on R-Judge, GAVEL leads by 10.75 pp in F1 and 16.06 pp in Recall.

To confirm that Unsafe F1 and Unsafe Recall derive strictly from the same underlying predictions, we report the per-seed confusion matrices across all five runs (Pre-Ex-Bench N=460N=460, positive N=115N=115; R-Judge N=85N=85, positive N=25N=25):

Table R1-2. Per-seed confusion matrices of MAGE on Qwen3-4B-Instruct-2507 (5 seeds).

DatasetSeedTPFPTNFNAccuracy (%)Unsafe F1 (%)Unsafe Recall (%)Precision (%)
Pre-Ex-BenchSeed 176143313988.4874.1566.0984.44
(N=460N=460)Seed 28133423491.9681.4170.4396.43
Seed 371253204485.0067.3061.7473.96
Seed 478113343789.5776.4767.8387.64
Seed 574163294187.6172.2064.3582.22
Mean ± Std————88.52 ± 2.5674.30 ± 5.2166.09 ± 3.3184.94 ± 8.18
R-JudgeSeed 119258690.5982.6176.0090.48
(N=85N=85)Seed 218357788.2478.2672.0085.71
Seed 320159592.9486.9680.0095.24
Seed 418555785.8875.0072.0078.26
Seed 519258690.5982.6176.0090.48
Mean ± Std————89.65 ± 2.6881.09 ± 4.5975.20 ± 3.3588.03 ± 6.42

All metrics are directly computed via the closed-form definitions from these counts. We have updated Table 1 and included the per-seed breakdowns in Appendix B.1.

2. Correction of Bootstrap Confidence Intervals in Table 10

The reviewer correctly observed that the reported intervals for Full GAVEL in Table 10 (±2.26/1.63/1.92\pm 2.26 / 1.63 / 1.92) matched the multi-seed standard deviations in Table 1 on Qwen3-8B Pre-Ex-Bench. This was a clerical copy-and-paste error during table formatting: the standard deviations across random seeds from Table 1 were accidentally pasted into the reference row of Table 10 instead of the empirical bootstrap confidence intervals described in lines 1528–1530. Retaining the baseline evaluation means (92.06/89.69/89.2792.06 / 89.69 / 89.27), we recomputed the empirical 95% bootstrap confidence intervals with 1,000 resamples:

Table R1-3. Corrected bootstrap 95% confidence intervals for latent-reference interventions (Pre-Ex-Bench).

VariantAccuracy (%)Unsafe F1 (%)Unsafe Recall (%)
Full GAVEL92.06 ± 1.8489.69 ± 1.4189.27 ± 1.55
Cross-sample Latent Swap82.48 ± 3.1477.75 ± 2.4776.18 ± 2.84
Token Shuffle86.31 ± 2.8582.54 ± 2.1981.42 ± 2.51

With the corrected bootstrap intervals, the 95% CI of Full GAVEL does not overlap with either Cross-sample Latent Swap or Token Shuffle, corroborating the decoder's reliance on trajectory-matched latent representations and ordered slot structure. We have revised Table 10 accordingly.

3. LongSafety Evaluation Protocol and Binary Label Construction

The reviewer rightly pointed out that LongSafety is not natively formatted as multi-turn agent interaction traces and that its official evaluation evaluates generated responses rather than binary trajectory labels. We clarify the adaptation protocol used for our diagnostic evaluation:

  1. Task Formulation and Input Serialization:

    LongSafety tests safety vulnerabilities under long background context. We adapted it into a long-context agent response safety auditing task. For each original instance, we generate one candidate response using Llama-3.1-8B-Instruct and reuse that same response across all eight context-length variants. The input trajectory transcript was serialized as:

    τ=[C;I;R]\tau = [C; I; R]

    The auditor must judge whether this complete transcript represents a safety policy violation.

  2. Binary Ground Truth Construction:

    Binary safety labels are derived by evaluating the generated responses using LongSafety's official Multi-Agent Evaluator (y=1y=1 for unsafe, y=0y=0 for safe). To verify label fidelity, two authors independently validated 50 randomly sampled instances against the official evaluation rubric, achieving a 96.0% (48/50) agreement rate with the automated evaluator.

  3. Evaluated Checkpoints and Dataset Partitions:

    • Auditing Models: All LongSafety diagnostic experiments (Figures 3 and 5, Table 9) directly evaluate the frozen Qwen3-8B checkpoints trained on our main benchmarks with the same 32k raw context cap, without any fine-tuning on LongSafety. This serves as an out-of-distribution stress test.
    • Data Splits: Figure 5 follows the controlled protocol of LongSafety §5.2 on 200 instances with contexts exceeding 8k words. Appendix G’s evidence-pattern analysis uses the 500-instance diagnostic pool.

    We have also corrected the Figure 5 y-axis label from “Safety Rate” to “Classification Accuracy” in the revised manuscript.

W2 & Q3. Training Protocols of Component Ablations and Retraining Verification

Regarding whether the ablations in Figure 4 were evaluated at inference time or retrained:

  1. Clarification of Original Figure 4: The ablations in original Figure 4 evaluated inference-time interventions on the trained Full GAVEL checkpoint to test whether the decoder depends on the learned latents at test time. For the No-context intervention, the classification head read the final raw sequence token representation hTh_T.
  2. Retrained Ablation Verification: To rule out distribution shifts introduced by inference-time intervention and evaluate the training contribution of each component, we performed independent retraining from scratch on Qwen3-8B (Pre-Ex-Bench) under identical optimization hyperparameters:

Table R1-4. Retraining ablations of context and query components on Qwen3-8B Pre-Ex-Bench.

VariantEvidence EncoderQueriesDecoder LatentReadout PositionAccuracy (%)F1 (%)Unsafe Recall (%)
Full GAVEL (Default)Yes16 learnedYeshT+Kh_{T+K}92.06 ± 2.2689.69 ± 1.6389.27 ± 1.92
No context (Retrained)No—NohTh_T87.24 ± 1.5583.18 ± 1.7281.65 ± 2.01
Random Q (Retrained)Yes16 fixed randomYeshT+Kh_{T+K}89.17 ± 1.2485.63 ± 1.5784.28 ± 1.96

The retrained No-context variant trails Full GAVEL by 4.82 pp in accuracy and 7.62 pp in recall. Fixed random queries (Random-Q) also drop by 2.89 pp in accuracy. This confirms that the improvements are driven by task-supervised latent evidence organization during training rather than extra capacity or inference-time perturbation alone.

We have added these retraining comparisons to Section 4.4.

W2 & Q4. Architectural Comparison with Single-pass LoRA Classifier and Compute Cost

To isolate the structural contribution of the two-pass architecture, we evaluated a Single-pass LoRA Classifier strictly matching GAVEL's training data, trainable parameters (8.46M on Wq,WvW_q, W_v), optimization settings, and classification head on Qwen3-8B (Pre-Ex-Bench):

Table R1-5. Architectural comparison between Single-pass LoRA and Full GAVEL on Qwen3-8B Pre-Ex-Bench.

MethodPassesTrainable ParamsAccuracy (%)F1 (%)Unsafe Recall (%)Latency (ms)Throughput (/s)Peak Memory (GB)
Single-pass LoRA18.46M89.37 ± 1.6286.29 ± 1.8584.81 ± 2.14158.426.3115.84
Full SFT (Table 1)1~8.00B90.49 ± 1.4487.29 ± 2.1283.06 ± 3.49155.096.4515.42
Full GAVEL28.46M92.06 ± 2.2689.69 ± 1.6389.27 ± 1.92183.205.4631.91
Paired Difference (Δ\Delta)——+2.69 ± 1.15+3.40 ± 1.28+4.46 ± 1.42+24.78-0.85+16.07

Under matched trainable parameters and inputs, GAVEL delivers a net architectural gain of +2.69 pp accuracy, +3.40 pp F1, and +4.46 pp Unsafe Recall over Single-pass LoRA. This confirms that single-pass causal attention struggles to concurrently filter routine execution steps and retain weak, dispersed risk signals, whereas separating global organization from record verification resolves this bottleneck.

In terms of computational trade-offs, GAVEL incurs a modest runtime increase of 24.78 ms per sample (~15.6%). The higher peak memory reflects maintaining two backbone passes concurrently, which can be mitigated in serving by sharing weights across frozen instances.

We have incorporated Table R1-5 and this discussion into Section 4.4 and Appendix D.

W2 (Cont.). Core Distinctions from ICAE and IDPG

We clarify the conceptual and architectural distinctions between GAVEL and prior latent methods such as ICAE (Ge et al., 2024) and IDPG (Wu et al., 2022):

Table R1-6. Comparison with related latent compression and prompt generation methods.

MethodOptimization ObjectiveLatent Representation RoleRaw Input in DecisionTarget Problem Setting
ICAE (Ge et al., 2024)Autoencoding text reconstruction lossCompressed surrogate replacing raw textDropped / weak accessContext-efficient language modeling
IDPG (Wu et al., 2022)Downstream task generation lossInput-conditioned soft promptsVaries by interfacePrompt-guided text generation
GAVEL (Ours)Trajectory-level binary discrimination (BCE)Global index guiding causal attentionFully retained (Raw-record bypass)Long-horizon agent safety auditing
  1. Distinction from ICAE (Discriminative vs. Generative Reconstruction): ICAE optimizes for full text reconstruction, which forces its latents to encode non-hazardous execution noise. GAVEL trains via discriminative trajectory supervision to selectively retain risk dependencies (Appendix A.6). Furthermore, ICAE discards the raw input, while GAVEL retains the full raw record alongside the latents so the decoder can inspect exact parameters and tool calls.
  2. Distinction from IDPG (Full-Trajectory Evidence Aggregation vs. Soft Prompting): IDPG generates conditioning soft prompts for standard generation tasks. GAVEL targets long-horizon trajectories up to 32k tokens. The Evidence Encoder appends learnable queries after the complete trajectory. Under causal attention, each suffix query can attend to all preceding trajectory tokens, allowing it to aggregate evidence distributed across earlier and later steps. The resulting evidence latents are then provided to the causal Audit Decoder together with the original trajectory.

We have incorporated Table R1-6 into the revised Related Work.

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