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Paper summary
The paper argues that a web world model can predict a plausible future for a candidate action while leaving out the information needed to decide whether the action should be taken, and calls the needed property safety sufficiency. In SafeWebWorld (30,000 / 1,000 / 3,000 train / development / test examples from existing benchmarks and a synthetic set), a model receives a goal, policy, observation, and candidate action, and outputs a predicted future, security evidence, consequence, risk, and an EXECUTE, ASK, or BLOCK decision. In a human study, 86.1% of 3,000 sampled futures are judged plausible, while several models almost never choose ASK. After fine-tuning (SA-SFT), Llama’s Evidence Recall rises while its ASK recall falls to almost zero (Authorisation-Policy Collapse). The LAR analysis shows that recalibrating the decision scores recovers much of the accuracy and that combining two backbones (DCPF) reaches 96.23% balanced accuracy, while fine-grained checks remain poor.
Critical strengths
The three-way decision is a useful lens. Separating ASK from BLOCK and including safe controls exposes behavior that a binary safe/unsafe metric hides: WebSynthesis-Qwen3-8B almost never executes unsafe actions (0.08% false safe) but never chooses ASK when it is required, and GPT-5.6, Claude Opus 4.8, and Gemini 2.5 Pro reach only 4.88%–14.63% ASK recall (Table 2).
The paper does not over-claim from its aggregate results. It tests DCPF within a mixed-label risk family and on matched EXECUTE/ASK/BLOCK triplets and reports that it drops to 35.55% balanced accuracy and 8.89% exact-triplet accuracy (vs. 73.33% for base Llama). This honest reporting is valuable.
Critical weaknesses
The central claim, that plausible futures omit policy-decisive evidence, is not measured directly. The model sees the full observation and policy and writes the future, evidence, and decision in one call, so the decision does not need to rely on the future. Evidence Recall is word overlap between the predicted security-evidence field and the reference (Eq. 14), not a check on the future, and the human study judges only plausibility; as the authors note, it “does not annotate policy-evidence omission at the individual prediction level” (line 1767). The two key numbers thus come from different output fields. The rise in Evidence Recall after SA-SFT (e.g., 28.68% to 93.32% for Qwen) may also mostly reflect learning the annotation wording. The input-source ablation in Appendix F.5, which decides from the predicted future alone, is the closest direct test and should be the main experiment.
Label quality limits what the numbers mean. The test labels were checked by a single reviewer without inter-annotator agreement (line 866), 54.2% of the test set is synthetic with no description of how it was generated, and the authors’ own probes show that risk family, unigrams, and templates predict the labels (line 897). Models trained on this data may learn these patterns, which fits the large gap between DCPF and zero-shot models and DCPF’s drop within a family. It is therefore unclear whether the low ASK recall of strong models is a real failure or a mismatch with this benchmark’s labeling convention.
Questions for authors
For Llama, the ASK collapse already appears in the “supervised foundation” checkpoint before SA-SFT (Table 28). What data and loss were used for this checkpoint, and was the class imbalance (66.4% BLOCK, 13.6% ASK in training) handled? If the collapse comes from imbalance, recalibration fixing it is expected, and Authorisation-Policy Collapse may be specific to this training recipe.
Response to Reviewer nB75
Thank you for examining the evaluation protocol, dataset construction and checkpoint lineage. We have clarified the measurement scope, brought the existing future-usefulness result into the main discussion and added verified foundation-training details.
W1. Joint prediction versus direct evidence-omission measurement
The main evaluation is a joint structured-prediction interface: all five fields are generated in one autoregressive response, and the decision can access the original input and preceding output tokens. It does not impose a future-only bottleneck. Section 3.1 now makes this explicit. ER measures the evidence field, while the human study evaluates future plausibility; neither directly measures individual future-text omissions. The Introduction and Section 3.5 now make that distinction explicit, Figure 1 is labelled illustrative, and Sections 2.1 and 3.4 describe the diagnostics used to study aspects of safety sufficiency.
We now highlight the existing input-source ablation from Appendix F.5 in Section 5.2. Under this separate offline decision protocol, Llama’s BA is 90.366% with original context X, 54.284% with frozen future F and 74.732% with X+F. Adding F to X lowers BA by 15.634 points (paired-bootstrap 95% CI [−17.529, −13.804]); Qwen’s X+F gain has a CI including zero. These are decision-usefulness results, not lexical-overlap measurements. F also removes the policy and other context, and X+F does not isolate a specific missing cue. The result therefore supports the conclusion that these futures are neither sufficient substitutes for context nor uniformly beneficial additions under this protocol, without identifying evidence omission as the cause of each error. We retain the joint benchmark as the main evaluation and use F.5 as a separate test of future usefulness, since they answer different questions.
W2. Labels and shortcut sensitivity
Appendix A.4 already describes the annotation and manual review of all 3,000 TEST records by one author. With no independent annotators, inter-annotator agreement was not measured. Section 3.3 now highlights the audit description, and Section 6 identifies the agreement limitation. The policy-conditioned contract in Section 3.2 distinguishes unresolved authorisation from prohibition; low ASK recall is measured against that contract.
We have expanded Appendix A.3 to explain how the synthetic examples were generated and processed. Python templates construct the scenarios, policies, reference futures and evidence, with explicit rules assigning labels and decisions. An AI coding assistant helped develop the code; individual examples are generated without LLM calls. Public inputs are deduplicated, synthetic examples fill the required risk-category counts, and a fixed seed assigns the splits. Later text revisions preserve split membership and gold targets. Final checks cover missing fields, duplicates, cross-split instance overlap and visible answer markers.
Appendix A.5 reports lexical, template and family regularities that predict labels. Group-aware and source-transfer checks do not eliminate these concerns. The existing Section 5.5 and Appendix K.3 show the limit of aggregate recovery: on the matched-authorisation diagnostic, DCPF achieves 8.89% exact-triplet accuracy versus 73.33% for base Llama. We therefore do not interpret high pooled performance as evidence of shortcut-free authorisation reasoning.
Q1. Foundation training, imbalance and onset of degradation
Appendix K.1 now specifies the checked foundation used to initialise the three Llama SA-SFT runs. It completed two epochs over all 30,000 frozen training messages: 6,000 EXECUTE, 4,080 ASK and 19,920 BLOCK. Training comprised 7,500 optimiser updates with batch size one and gradient accumulation eight, using full-conversation causal-LM loss with labels equal to input IDs. No class weighting, class-dependent resampling or decision-specific weighting was applied. Final SA-SFT instead uses response-only supervision and ten optimiser updates.
Table 29 reports emitted decisions on DEV-1000: ASK recall falls from 48.94% to 4.26% before final SA-SFT, then to 0.00%. The Abstract, Introduction, Section 5.3 and Conclusion now reflect this timing. A training-recipe explanation remains possible; these comparisons do not isolate imbalance or supervision format as the cause. The frozen-score recovery analysis consequently tests recoverability on the evaluated distribution, not a universal collapse mechanism or robust authorisation understanding.