- Rating
- 2
- Confidence
- 3
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 2
Read review
Paper summary
This paper defines field-level provenance for structured tool calls as the change in the frozen model's mean log probability of a fixed field value when a candidate context source is neutralized. It proposes the Interventional Effect Decoder (IED), which learns to predict the direction and magnitude of these effects from pooled internal activations in one factual scoring pass. Experiments evaluate source identification and effect prediction on tool-use decisions, evidence-assisted repair of corrupted arguments, and a separately trained pre-execution defense model incorporating support and authorization supervision. The reported results show substantial online attribution savings, improved repair on BFCL, and a useful security–utility trade-off on three prompt-injection benchmarks.
Critical strengths
-
A concrete, measurable attribution target with a practical amortization strategy. Equations (1)–(2) hold the action fixed and define signed effects separately for each field, rather than relying on a generated explanation. The decoder moves repeated interventions offline. Tables 4 and 6 provide effect-prediction evidence, and the timing study reports approximately 5.37× lower online cost than explicit intervention at six sources. This makes the proposal potentially useful for frequent pre-execution audits.
-
The paper tests downstream usefulness and includes relevant controls. On BFCL, IED raises single-call repair recovery from 53.4% to 65.6%, with 99.7% clean retention (Table 3). Table 5 separates field supervision from influence fusion, while Appendix C.6 examines alternative neutralization strategies. These checks go beyond demonstrating that the decoder can fit its training target. The paper also reports limitations in its own results, including no repair improvement over standard review on τ²-bench.
Critical weaknesses
-
The headline source-identification metric does not directly measure recovery of the defined intervention provenance, and the evaluation boundary is insufficiently characterized. Appendix C.1 assigns the reference source according to semantic support or justification, excludes ambiguous and unsupported fields, and manually checks 10% of labels. A source that justifies a value need not be the source whose neutralization most changes the model's score. Thus Table 1's 74.6% mean accuracy is not directly an accuracy measure for recovering the highest-effect source in Equation (2). Tables 4 and 6 do provide direct effect evidence, but the paper should also report agreement with the intervention-derived top source, the fraction of fields excluded from the semantic metric, and the outcome of the annotation audit. In addition, the stated within-domain decision split does not establish whether related decisions from the same trajectory or task are kept together. These details materially affect how much the results support reliable provenance recovery on unseen decisions.
-
The security–utility comparison lacks enough protocol detail to assess generalization and operating-point fairness. The paper explicitly trains a separate defense model (Section 3.5), but Sections 4.1–4.3 and Appendix C.3 do not identify its training-set size/composition and task/attack separation from evaluation, or the blocking thresholds and their selection procedure for IED and attribution-based guards. These omissions matter because changing the blocking rule can strongly affect both attack success and task completion. Table 5 is encouraging, but its no-fusion control still uses a separately supervised defense model; it does not by itself establish comparability with the other attribution guards. A reproducible split description and thresholds selected on held-out data, ideally with a matched-utility comparison, are needed to interpret Table 2's advantage.
Questions for authors
- How often does the semantic reference source in Appendix C.1 agree with the maximum positive intervention effect? Please report intervention-derived top-source recovery, excluded-field counts, and the actual agreement/error rate from the 10% manual audit. How are cases with no positive effect handled?
- Are train/test decisions grouped by original task or trajectory, including reference-action prefixes and rollout records? Please specify the grouping and any cross-split overlap. If the current split is decision-level, does the result persist under a trajectory-disjoint split of the existing data?
- What data train the separate defense model, how are evaluation attacks/tasks excluded, and what are the exact blocking thresholds and calibration sets for each guard? Do the relative results hold at comparable benign utility?
- What common support/authorization machinery, if any, is used by the attribution-based defense baselines in Table 2? This determines whether the comparison isolates the attribution signal or compares different overall guard architectures.
- Code–paper consistency. Does the supplementary code correspond to the model and experiments reported in the paper? The decoder omits the lexical-value branch and directly regresses signed effects instead of the direction–magnitude formulation in Eqs. (7)–(10); source top-1 is evaluated against
argmax(J)rather than the stated semantic-support labels; and the defense implementation lacks the independently supervised support head and effect fusion in Eq. (11). Please reconcile these differences and identify the implementation used to produce the reported results.
5 comments
Response to Reviewer VJ3h (2/2)
How is the defense model trained, and is the test separation and threshold comparison fair? (Weakness 2 / Question 3)
The paper does not describe the training data, test separation, and threshold selection of the defense models in enough detail; we give them here. This part has five blocks: training data, test rollouts and separation, invalid samples, thresholds, and comparison at comparable benign utility.
Training data. IED reads the internal representations of context sources and call fields and forms a call risk. The training set is used for learning, the validation set for model and threshold selection, and the test set for final evaluation. All three benchmarks split train, validation, and test by task groups, and training and test tasks do not overlap. The training data are as follows, in decisions.
| Training setting | Training rows | Validation rows |
|---|---|---|
| AgentDojo | 1,873 | 327 |
| ASB | 9,600 | 3,200 |
| MCP-Tox | 2,193 | 681 |
Test rollouts and separation. The test rollouts are as follows. AgentDojo has 1,116 attack + 97 clean. ASB has 640 + 160. MCP-Tox has 249 + 249. Test separation is by task, agent, and server: AgentDojo attack test user tasks do not overlap training tasks; ASB training excludes test agents; MCP-Tox uses 27 training, 9 validation, and 9 test servers. The repair scoring model is trained with test tasks excluded, and BFCL does not participate in scoring-model training.
Invalid samples. We do not set a separate exclusion layer; the denominator of each benchmark is all attempted rollouts, and parse failures or no-action samples are counted as failures and not removed.
Blocking thresholds. Blocking thresholds are selected on the validation (calibration) set of each benchmark and fixed before test; for IED they are .97 on AgentDojo, .95 on ASB, and .97 on MCP-Tox. AP, CC, and lexical reuse the same IED guard, with the same data split; the three baselines only provide attribution scores, and the guard makes the allow-or-block decision, so the difference comes only from the front-end attribution signal. When the risk score exceeds the threshold, the candidate call is not executed; the system returns feedback and lets the agent replan; after the budget is reached, the action is still not allowed. Other complete defenses keep their native mechanisms.
Comparison at comparable benign utility. The MCP-Tox results are as follows.
| Method | ASR↓ | UA↑ | BU↑ |
|---|---|---|---|
| IED | 0.4% | 31.3% | 48.6% |
| AP | 0.4% | 15.7% | 49.0% |
| CC | 0.4% | 12.1% | 47.8% |
| Lexical | 0.4% | 16.9% | 49.0% |
| PI Detector | 8.0% | 29.3% | 48.2% |
All methods have BU between 47.8% and 49.0%. IED has the same ASR as AP, CC, and lexical, and UA is 15.6, 19.2, and 14.4 points higher, respectively; compared with PI Detector, IED has lower ASR and higher UA at similar BU. The task-completion advantage in the original table is not mainly obtained by lowering clean task completion.
Do the attribution-based defense baselines use the same support/authorization machinery? (Weakness 2 / Question 4)
The attribution-based defense baselines in Table 2 do share the same support/authorization machinery. AP, ContextCite, and text methods themselves provide source attribution information; to use them for defense, we connect their attribution scores to the same IED guard. AP, CC, and lexical reuse the same guard checkpoint, with the same data split. Therefore the comparison isolates the front-end attribution signal, not different defense architectures. TextEmb is trained separately with the same S/A labels.
The IED in the three benchmarks uses the same source-field modeling and support/authorization judgment process, only adapting to each tool format and context organization; the three are trained on their own data and determine operating points on their own validation sets.
Does the supplementary code correspond to the models and experiments in the paper? (Question 5)
We apologize that the supplementary code we provide is not complete, because we are still in the review stage. The code we provide is part of our iterative code, and these methods are also part of our ablation study. We will release the complete code later.
All our code is based on the paper, and the code and experiments correspond to the paper.
Thank you for the detailed rebuttal and the additional experiments. The intervention-based evaluation, task-disjoint results, and clarifications on the defense protocol address my concerns for now.
Response to Reviewer VJ3h (1/2)
We thank the reviewer for the comments on source definition and evaluation protocol. We add intervention-target evaluation and task-disjoint results, and check the defense data, calibration, and shared components.
We will include these experiments and changes in the final revised version.
Semantic source vs. intervention source: agreement, annotation and exclusion rules (Weakness 1 / Question 1)
Thank you for helping us find this issue: the labels in Table 1 are indeed semantic reference scores given by a large language model, and they are not the intervention provenance defined in Eq. (2).
To address this, we re-evaluated the original IED model with the intervention provenance as the reference. Our three-domain top-1 mean is 80.5%, compared with 75.5% for Activation Patching. This shows that under the definition of Eq. (2), the intervention-derived top-source recovery still holds, and the advantage is clearer than under the LLM labels.
Table 1 in the paper has 6,216 test fields: 2,269 operation fields (tool names) and 3,947 argument fields. By Appendix C.1, only argument fields are evaluated. Among the argument fields, 2,835 have a positive intervention effect (max J>0.05) and form the IED denominator of the original Table 1; the three datasets in the main text share 2,797 (the 38 positive fields of AgentDojo have only one source and are not included); the other 1,112 argument fields have no positive intervention effect and are not forced to have a positive source.
The semantic-label audit batch is counted separately: from the 2,835 positive fields, we remove 191 S=1 deterministic fields and 3 fields that did not enter the batch, leaving 2,641; adding 200 control fields without positive J gives 2,841 audited fields. The overall agreement between the multi-judge semantic reference labels and the intervention provenance is 60.7%.
60.7% shows that the two definitions are not equivalent, so semantic labels cannot be used directly as intervention-provenance recovery. But the two are not unrelated, and semantic labels still have reference value for the main dataset. For the manual audit, we randomly sampled 280 of the 2,841 semantic-label fields (about 10%) and had three human annotators score them: 269 agree with human judgment and 11 do not, giving a correct rate of 96.1% and an error rate of 3.9%; we corrected the 11 inconsistent labels. Semantic labels reflect attribution direction, but they are not the ground truth of intervention effect and cannot replace intervention-provenance evaluation. The paper will report the two settings separately and correct the reference-source note and table caption.
Train/test separation by task or trajectory (Weakness 1 / Question 2)
Thank you for the correction. The split of Table 1 is decision-level: decisions of the same task or trajectory can appear in both the training and test sets, so there is overlap. We therefore add a task-disjoint split at the task/trajectory level: grouped by scene and normalized task key, the scene and normalized-task overlap across sets is zero, and the train/dev/test sizes are 5,208/1,336/1,028.
The results under the new split are as follows.
IED is higher than AP and TextEmb under the task-disjoint setting, so the main source-ranking result holds on unseen tasks. The old split is re-evaluated at 80.5%, and the task-disjoint setting is 79.6%, a difference of about 0.9 points.
Downstream repair and attack evaluations are also separated by task groups; details are in Question 3.