W1. The two central mechanistic claims are not isolated by controlled experiments.
- Metadata→body trust transfer via µ. The carrier comparison (Table 2) and the cross-agent comparison vary several things at once (invocation wrappers, loading time, context position, workflow framing, system prompts, memory-loading rules), so they cannot attribute the gain to the registry mapping alone, despite the claim that "the two carrier conditions differ only in whether the attack payload is associated with legitimate skill metadata." The clean test is a within-agent, within-model, within-payload intervention: (a) skill body loaded but metadata not placed in the high-authority listing (H ∧ ¬µ), and (b) listing retained but the description replaced by a neutral stub (H_stub ∧ µ). Equation (1)'s T(x) is only a behavioral compliance proxy and does not by itself evidence authority propagation.
- Instruction-hierarchy training as amplifier. The grouping of GPT-5.5/GLM-4.7 ("trained") vs. Qwen3.6-plus/Kimi-K2.5 ("not disclosed") conflates many model differences, and absence of public disclosure is not evidence of absent training. Wallace et al. (2024) concern earlier models and do not establish GPT-5.5's specific procedure. The within-model memory-placement contrast (privileged vs. demoted memory position across agents) is the stronger evidence and should be foregrounded; the cross-model training narrative (e.g., §5.1, Conclusion) should be narrowed to an empirical association unless a same-model position intervention is provided.
W2. "Substantive and persistent system compromise" exceeds the verification I could confirm.
The paper states that outbound classes (exfiltration, reverse shell) are judged by listener connection records. In the supplementary package I found no connection_log file and no reference to one in the evaluation toolkit (evaluate_log_based.py, listener.py). As released, success for local classes appears to reduce to "the agent generated a marker-bearing script and the OS executed it," not a verified end state (e.g., a file actually exfiltrated and received, a shell actually connected back). Issuing a command is not the same as achieving the goal: permission errors, failed calls, or absent side effects can separate the two. Please (a) specify a per-category postcondition (exit status / received connection / state diff) and release a sample of the listener records the text relies on, and (b) for persistence, give a reset checklist and a negative control that deletes the memory file before Task 2 to confirm that re-firing is attributable to memory alone and not to residual state outside the workspace.
W3. The carrier-comparison table (Table 2) is not a matched-denominator contrast. Appendix D states that "each baseline run is evaluated over its own case set," so the external and skill arms are not evaluated on the same cases, and Table 2 reports neither the per-arm n nor how invalid runs are excluded. As reported, "+36.9 / +46.4 / up to +70.5 pp" should be presented as a descriptive difference between differently-sized stimulus sets, or recomputed on matched cases with the denominators and the "valid" rule stated. The two-proportion tests in Appendix D inherit this issue and also treat per-case outcomes on a shared 306-stimulus set as independent across cells (no clustering, single run per case, no repeated seeds).
W4. The headline conditions are an upper bound, not a "most common" configuration. All results use Full-Access (auto-approve) mode, and I confirmed that 306/306 Task-1 prompts explicitly instruct the agent to use the corresponding workspace skill (case.json flags this, and the task01.md files contain the instruction). So the ASRs are measured under "user explicitly installs, auto-approves, and explicitly invokes the malicious skill." That is a legitimate and serious worst case, but the paper presents it as the prevalent real-world setting (the 93%-approval citation is about approval rate, not about disabled permissions). Please relabel these as an upper bound and add at least a small non-auto-approve / non-explicit-invocation control.
W5. Artifact, reporting, and consistency gaps.
- OpenCode panel has no producer in the released toolkit. The evaluator has no
opencode branch (the --agent option defaults to codex with no OpenCode handling), and the Sample Log/ directory contains runs only for Claude Code / Codex / Qwen Code — no OpenCode run directories. OpenCode result CSVs are present, but the toolkit and sample logs do not cover them, so the four OpenCode cells in Table 1 (one quarter of the one-shot average) and every OpenCode-based ablation/position-swap figure (Figures 3–4) cannot be traced in the artifacts. Please release the OpenCode evaluation path and sample logs, or scope the claims accordingly.
- Truncated main CSVs. Three of the 16 Main CSVs have fewer than 306 rows (Codex+GPT-5.5: 263; Codex+Kimi-K2.5: 202; OpenCode+Qwen3.6-plus: 299). Please reconcile these with the stated n = 306 per cell and Figure 5's denominators.
- Deferred definitions. The per-category ASR criterion, the Table 2 "valid" denominator, the Table 3 per-scanner detection threshold, and the Figure 4 "success" definition (which appears to differ from the main one-shot "verified-executed" criterion) are all needed in the main text.
- Table 3/Table 4 specifics. Table 3 mixes HierJack scans with SkillJect numbers taken from its paper without matched versions/thresholds/populations; in Table 4, 99 successes and 5 true defenses leave 4 of the 108 runs unaccounted for (presumably timeouts, which the caption excludes from both success and failure); please state these categories and the denominator rule, and provide per-event records behind the 443 "Rule Interceptions."
- Release hygiene. The README states that all endpoints use
*.example-cdn-sync.com. This is a registrable domain, not an RFC 2606 reserved name (.invalid/.test/.example), and should be replaced before any public release. The authors should also re-scan the package for absolute machine paths and other identifying metadata.