W1. The "fine-grained" claim has no fine-grained component and no fine-grained metric.
The paper motivates itself on "insufficient modeling of fine-grained forgery cues" (Sec. 1) and attributes poor generalization to that deficiency. No proposed component operates at that granularity. The four mechanism experts take the global SigLIP embedding phi(x) as input (Eq. 4), and the mixture network also estimates its coefficients from global features. The only region-aware branch is a frozen Xception sidecar over eight MediaPipe-aligned regions, and the paper states explicitly that it "does not contribute to the computation of S(x)" (Sec. 3.2.1), so it cannot affect detection. No localization metric (region IoU, pixel-level AUC, point-wise accuracy) is reported anywhere in the main paper or appendix. The diagnostic claim and the proposed mechanism therefore do not meet: whatever improves cross-domain accuracy, it is not fine-grained cue modeling as the paper defines the problem.
W2. Hallucination is declared the central problem and then never measured.
"Hallucination" appears four times in the paper, entirely in the introduction and related work. No hallucination rate, faithfulness rate, unsupported-claim rate, or human evaluation is reported, and Appendix L states verbatim: "No human evaluation is reported." What actually constrains the output is an output contract, not the proposed knowledge mechanism: the decision field is copied verbatim from upstream (Eq. 2), region and cue names are drawn from a closed 9-region x 12-cue vocabulary (Appendix K.7), the forgery type is one of four fixed closing sentences (Table 22), and a repair prompt is triggered on contract failure. This is a legitimate design, but it means the anti-hallucination credit belongs to constrained decoding. The paper's thesis is that retrieval-grounded knowledge makes explanations reliable, and that thesis is left unmeasured. The one non-LLM faithfulness metric that is freely available, forgery-type accuracy over the closed four-way label, is not reported, even though the labels are derivable from the source-method mapping in Table 5.
W3. GraphRAG is not retrieval in any falsifiable sense, and its contribution is not identifiable.
The knowledge base contains 260 nodes in total (Table 9: 21 regions, 27 cues, 88 rules, 11 categories, 3 authenticity patterns, 4 caution policies), all authored by the authors, with no external corpus and no cited provenance for the 88 rules. Retrieval is a deterministic scoring function with hand-set weights, lambda = (2.0, 1.5, 1.5, 1.0, 0.8, 0.8, 0.5) (Appendix D.4), with no learned retriever and no embedding index. The query is a function of (y-hat, eight region indices, arg-max mechanism, uncertainty), so the reachable retrieval space is finite and small. Functionally this is weighted prompt-template assembly. The naming carries a claim the mechanism does not support, and the empirical support is weaker than the name suggests. Table 4 uses one fixed SFT checkpoint and ablates only inference-time inputs, so it never tests whether training with the graph matters. Its pointwise scores are non-monotonic: full model 4.18/4.75, w/o F-FKGs 4.08/4.48, w/o F-FKGs and regions 4.12/4.57. Removing strictly more information improves the score, and the offered explanation is post hoc. The decisive missing control is a vocabulary-only condition: the graph injects exactly the 21-region and 27-cue terminology, so removing the graph also removes the vocabulary. Without that control, "structured knowledge helps" and "more forensic-sounding tokens help" are not separable, and the ELO ordering (1126.7 > 972.8 > 900.4) cannot be interpreted.
W4. The explanation evaluation cannot separate the method from the instrument.
Four confounds, all verifiable in the appendix. (a) Teacher is judge: the SFT targets are generated by Kimi (Appendix K, Category D), and Kimi-K3 is simultaneously the pointwise and pairwise judge, so the student is optimized toward Kimi's style and then graded by Kimi. (b) Asymmetric same-family correction: Appendix L removes the Qwen2.5-VL-7B base from the Qwen3.7-Plus column "due to suspected same-family preference" but retains MEGRA in that column, although MEGRA is exactly Qwen2.5-VL-7B plus QLoRA; the concern applies with at least equal force to the fine-tuned model. (c) Effect size is not larger than instrument noise: the judge-to-judge spread for MEGRA (4.18 under Kimi vs 4.75 under Qwen, 0.57) is essentially the same as the claimed method gap (4.18 vs 3.59 under Kimi, 0.59). (d) The reported ELO is a deterministic monotone transform of the pairwise win rate (Appendix L: Delta = 400 log10(P/(1-P))), fitted as a star graph with MEGRA as the only hub and no baseline-baseline pairings, so 1723.3 corresponds to a 92.5% win rate against VERITAS. A 92.5% win rate and a 0.59 point difference on the same 1000 images are not mutually consistent unless the pairwise judge is responding to surface form rather than reasoning quality. The rubric compounds this: it rewards "creativity, comprehensiveness, and granularity" (Appendix K.1), and in a paper whose thesis is anti-hallucination, rewarding creativity and comprehensiveness is misaligned with the stated objective, since neither instruction penalizes unsupported claims.
W5. The paper's own ablation contradicts its central generalization claim.
Removing the mechanism experts (Table 3) costs 13.3 points on ID, 10.5 on CM, 5.2 on CF, but only 1.25 on CD. The component named after mechanism-aware generalization decays to almost nothing precisely on the split that measures generalization. Conversely, the frozen experts, which alone reach 52.14-62.17% average accuracy (Table 17; six-model stack 62.93%), are the ones carrying the CD gain (removing them costs 5.8 points there). The open-world improvement is therefore delivered largely by a six-model ensemble of off-the-shelf detectors that are individually close to chance on this benchmark, whose marginal contribution is 3.58 points, while the proposed mechanism machinery contributes mostly in-domain capacity. This should be reported as the finding, not as support for the current framing.
W6. The state-of-the-art claim has no paired significance test against the only competitive baseline.
The margin over VERITAS is 0.39 points on the reported average and 0.52 on OOD, while the standard deviation across the 18 OOD subsets is 6.88. Appendix H explicitly restricts its tests to lesions: "These tests concern the internal detection-module lesions only." No test of MEGRA against VERITAS is reported. The quoted confidence interval [90.77, 91.42] is computed over images rather than over subsets, so it is far narrower than a claim resting on cross-distribution generalization requires. The comparison is also asymmetric across columns: MEGRA loses on ID (95.5 vs 97.3) and by 5.2 points on FFIW (73.3 vs 78.5), and the reported average mixes denominators between rows with and without an ID entry (footnoted, but load-bearing for the SOTA sentence).
W7. The system is an ensemble compared against single models, with no cost accounting.
MEGRA runs six frozen detectors, four MLP experts, a SigLIP-LoRA channel, two calibrated residual channels, an Xception region sidecar, and a 7B QLoRA-tuned MLLM with graph retrieval. Baselines in Table 1 are single models. No inference cost, parameter count, or latency comparison appears in the main paper to justify a +0.5 point OOD gain at this complexity. The 2-expert variant collapsing to 75.92 (Table 18), while the uniform average of the same experts rises, further suggests the stacking head is highly sensitive to pool composition, which weakens the mechanism-aware interpretation of the gain.
W8. No limitations section. Appendix N is titled "Additional Qualitative Examples and Limitations" but contains no limitations.