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- Confidence
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- Informativeness
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- Presentation
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- Soundness
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Paper summary
The paper studies the additional feature-edit cost of making existing structural attacks survive similarity-based graph defenses. It gives exact single-edge costs for binary Jaccard and one-endpoint continuous cosine thresholds, evaluates post-hoc camouflage on Metattack and PRBCD graphs, and measures edge survival with poisoned versus clean evidence while keeping victim-training features fixed. CLASP supplies jointly poisoned graphs for a broader budget sweep. The strongest contribution is the quantitative audit of inexpensive raw-feature forgery, rather than a new state-of-the-art attack.
Critical strengths
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The fixed-graph camouflage experiment is a clear mechanism test and quantitatively demonstrates cheap raw-feature forgery. On Cora, 136 copied words raise Metattack inserted-edge survival from 47% to 100%, while GCN-Jaccard's loss increases from 7.6 to 15.7 percentage points (Table 2). The exact single-edge cost characterizations help explain the mechanism under their stated assumptions.
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The study includes unusually extensive, auditable controls: feature-only and sequential attacks, matched total edit counts, matched-node random feature changes, untouched test nodes, alternative splits, and attack-seed replication. Negative findings, including CLASP's weakness on heterophilous graphs, are reported. Appendices I and J examine adaptive attacks and purifier strength, and stored graphs/results plus the full evidence/training-feature intervention grid make several claims directly checkable.
Critical weaknesses
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The proposed decomposition is interpreted too strongly. The clean-evidence intervention measures a conditional effect of changing filtering evidence, but the remaining loss is not entirely feature damage as stated in Section 5.2 and Figure 2. For the same Cora joint-10% adjacency, Table 38 gives 66.17% accuracy with clean evidence and clean training features, versus the clean-graph baseline of 77.93%; approximately 11.77 points of structural damage remain. The supplementary grid gives 40.47% with clean evidence and poisoned training features, and 36.30% with both poisoned. These support a conditional evidence effect of 4.17 points, not a complete two-way attribution of total loss. The intervention also changes retention of clean edges. Because this attribution is a central claimed contribution, the existing full grid should be used to report the structural residual and interaction, and the causal interpretation should be narrowed.
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The structural comparisons appear to mix label-access assumptions. Section 3.1 exposes training labels, whereas supplementary a_rbcd calls pass data.y together with test-node indices to PRBCD/GRBCD (unified_bench.py:151–154; extend_bench.py:143–146). This appears to provide true test labels, unlike CLASP's pseudo-label objective. Table 3 acknowledges evasion-to-poisoning transfer but does not clarify this information difference. The exact dependency behavior should be confirmed, and key comparisons should either use matched pseudo-label access or be identified as oracle-label stress tests. This affects comparative and threat-model conclusions; it does not invalidate the fact that a given stored graph can be camouflaged.
Questions for authors
Clarifications or checks that could materially change the assessment:
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Can the existing 2×2 intervention grid be used to report residual structural damage, the training-feature channel, the conditional evidence-channel effect, and their interaction separately? How will the Section 5.2/Figure 2 claim that the remaining clean-evidence loss is feature damage be revised, given the clean-feature attacked-graph condition and changes in clean-edge retention?
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Do the PRBCD/GRBCD calls consume true test labels in the exact dependency version used for the reported experiments? Please clarify this access explicitly and provide matched-information key comparisons, or label the relevant rows as oracle-label stress tests. The static call-site evidence is direct; the actual pinned implementation behavior still requires confirmation.
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What justifies the learned-evidence 'price floor'? Appendix I is a useful adaptive control, but its edits are donor words, it uses five greedy rounds, and it does not optimize through encoder training. Failure to find cheaper severe blinding with this attack does not lower-bound the best adaptive attack. Appendix J usefully addresses purifier strength. Can the broader conclusion be limited to the tested attacks/implementations, or supported by budget curves at matched damage targets?
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Under what independence conditions does Appendix M's sum of isolated cosine projection costs equal a graph-level exact minimum or floor? Appendix S correctly notes multi-edge coupling; shared moving nodes and changing opposite endpoints can invalidate a direct sum interpretation. Please state the necessary conditions or present the sum as an independent-edge reference. Also distinguish L1 moved mass, sum-of-row-L2 normalization, and median relative edge price.
The existing evidence supports cheap raw-feature forgery; these questions concern the scope of the quantitative and causal conclusions. A minor correction, not a standalone decision driver: in Appendix S, deleting a shared word at one endpoint reduces the intersection but leaves the union unchanged. The Proposition 1 conclusion still follows after correcting this case.
6 comments
Response 2
W1 and Q1, continued. Why the camouflage experiment is separate
The criticism above is about the joint condition, where the feature budget is 10% of the non-zero entries and the two channels genuinely mix. The camouflage experiment of Table 2 is a different setting, and it has a direct control that we should have placed in the main text. On Cora, with Metattack's stored graph and the 136 copied words:
- the copies alone, with no structural attack, leave an undefended GCN at 80.60, against 80.14 on the clean graph;
- structure together with the copies leaves the undefended GCN at 66.87, against 66.90 for structure alone;
- GCN-Jaccard's loss rises from 7.63 to 15.67 points;
- the filter prunes 572 edges, which is what it prunes on the clean graph.
Since the copies do not measurably change an undefended model, either alone or in combination with the structural attack, we think the 8.03 point rise in the defended loss can only be acting through the filter. The pattern is the same in all six camouflage cases: copies-only accuracy stays within 0.69 points of the clean GCN, the undefended loss moves by at most 0.67 points, and GCN-Jaccard loses an extra 8.03, 4.07 and 8.33 points on Cora and 1.13, 2.97 and 4.13 points on CiteSeer under Metattack, PRBCD and CLASP. Read off the grid, the training-feature channel in the camouflage rows lies between -0.73 and 0.60 points, which is the same statement.
What our text did not do, and what the reviewer is right to object to, is keep these two experiments apart. The revision reports the joint condition as a four-way decomposition with no causal attribution beyond the conditional effect, and lets the camouflage experiment carry the causal claim, with the control above moved into the main text.
W2 and Q2. Label access in the PRBCD and GRBCD calls
Review: "The structural comparisons appear to mix label-access assumptions. Section 3.1 exposes training labels, whereas supplementary a_rbcd calls pass data.y together with test-node indices to PRBCD/GRBCD ... This appears to provide true test labels, unlike CLASP's pseudo-label objective."
Response: The reviewer has read the code correctly. Both call sites are
a.attack(data.x.float(), to_ei(A0), data.y, budget=B,
idx_attack=data.test_mask.nonzero().flatten())
so the attack receives the true labels of the attacked test nodes, while CLASP optimises a surrogate's pseudo-labels. We should have stated this rather than leaving it to be found in the code. The effect is to make the baselines stronger than the threat model of Sec. 3.1 allows, so the structural comparison was conservative with respect to CLASP, but it is not a matched comparison.
Revised text, Sec. 3.1: "One departure from this is worth stating plainly: PRBCD and GRBCD are run through their reference implementation, which scores the attacked nodes against their true labels, so those rows give the baselines oracle labels on the attacked set, while CLASP optimises a surrogate's pseudo-labels. Those rows are therefore oracle-label stress tests and are marked as such in App. Q."
This does not affect the results that take a stored poisoned graph as input and price the feature edit on it. Those are Table 2, the edge-level survival counts, the intervention grid and Props. 1 and 2, none of which depend on how the graph was produced. We are rerunning PRBCD and GRBCD with the information CLASP is given, which is true labels on the training split and the surrogate's argmax elsewhere, and will post the matched rows in this thread. We expect the attack to become weaker or to stay where it is.
A related point, since the reviewer raised matched information. CLASP's homophily
switch is set from labels. A control in the supplementary material
(pseudo_homophily.json) shows that homophily estimated from the surrogate's
pseudo-labels on the unlabelled nodes selects the same rule as the true
homophily on all six graphs, cross-class on Cora, CiteSeer and PubMed and
same-class on chameleon, squirrel and actor. That access can be removed at no
cost, and the revision says so.
The remaining points are in the next comment.
Response 3
Q3. What justifies the learned-evidence price
Review: "What justifies the learned-evidence 'price floor'? Appendix I is a useful adaptive control, but its edits are donor words, it uses five greedy rounds, and it does not optimize through encoder training. Failure to find cheaper severe blinding with this attack does not lower-bound the best adaptive attack."
Response: We accept this and have removed the word floor. App. I gives an upper bound on the price paid by the strongest adaptive attack we were able to construct, and we agree it does not lower-bound the best adaptive attack that exists. The limitations the reviewer identifies are the right ones. The appendix's own numbers suggest the attack is not at a limit: under Metattack, 140 of 263 inserted edges on Cora and 110 of 227 on CiteSeer bought nothing at all, and between 22 and 62 edges reached the five-word cap. The gap bought is 1.67 to 2.47 points for 0.22 to 0.85% of the non-zero entries.
The conclusion is now scoped to the attacks and implementations we tested: across every adaptive attack and every purifier cut we tried, the copies bought at most 2.47 points, and we make no claim about what a stronger adaptive attack could do. App. J supports that scoping rather than a bound, since sweeping the keep fraction from 0.90 to 0.50 leaves the gap between -1.00 and 2.17 points on all four graph and attack pairs. We agree that budget curves at matched damage targets are the right comparison and we are running them.
Q4. The conditions under which App. M's sum is exact
Review: "Under what independence conditions does Appendix M's sum of isolated cosine projection costs equal a graph-level exact minimum or floor? ... Please state the necessary conditions or present the sum as an independent-edge reference. Also distinguish L1 moved mass, sum-of-row-L2 normalization, and median relative edge price."
Response: The reviewer is right that we left the conditions implicit. The sum equals the graph-level minimum when no two rejected edges share a moving endpoint, and no moving endpoint is also the fixed endpoint of another rejected edge, so that moving one node cannot change another edge's target. We did measure how often this holds but reported it as a remark. Table 2 gives it.
Table 2: share of moves that can be priced in isolation, PubMed
| cosine threshold | 0.01 | 0.05 | 0.1 | 0.2 |
|---|---|---|---|---|
| PRBCD | 1.000 | 0.941 | 0.922 | 0.908 |
| CLASP | 0.974 | 0.917 | 0.896 | 0.885 |
At the threshold where the forgery is cheapest the condition holds exactly, since all 140 moving nodes carry exactly one rejected edge. At the higher thresholds the revision presents the sum as an independent-edge reference and not as a graph-level minimum.
We have also separated the three quantities. Normalising by the sum of row L2 norms, 7680.26 on PubMed, the exact L2 cost of Prop. 2's minimiser is 0.0036% of the mass at a threshold of 0.01 and rises to 1.51% at 0.2. The feasible interpolation that App. M also reports moves 0.074% of the L1 mass at 0.01 and overpays the exact minimiser by a factor of 16.68, falling to 1.40 at 0.2. The median relative price of a single edge is 0.0038 at 0.01 and 0.1533 at 0.2. These are labelled separately in the revision.
The minor correction in App. S
Review: "in Appendix S, deleting a shared word at one endpoint reduces the intersection but leaves the union unchanged. The Proposition 1 conclusion still follows after correcting this case."
Response: Thank you, the case was stated wrongly and the correction is the reviewer's. Deleting a word both endpoints share removes it from the intersection but leaves it in the union, so the flip takes i to i-1 with U unchanged and the ratio falls.
Revised text, App. S: "it deletes a shared word, so i falls by one while U is unchanged, since the other endpoint still has the word, and the ratio falls".
Only copying a word the other endpoint has and deleting a word it lacks can help, so the argument and the bound are unaffected.
Response 1
We thank the reviewer for a review that engaged with the appendices and with the code, and whose points have led to real changes in the paper. We hope our revisions and responses merit reconsideration of a higher evaluation.
W1 and Q1. The decomposition of the loss
Review: "The proposed decomposition is interpreted too strongly. The clean-evidence intervention measures a conditional effect of changing filtering evidence, but the remaining loss is not entirely feature damage as stated in Section 5.2 and Figure 2 ... the existing full grid should be used to report the structural residual and interaction, and the causal interpretation should be narrowed."
Response: The reviewer's arithmetic is correct and our wording was too strong. Table 1 gives the four cells for the Cora joint 10% graph, against GCN-Jaccard's 77.93 on the clean graph.
Table 1: the intervention grid, Cora joint 10%, GCN-Jaccard
The total loss of 41.63 points decomposes into a structural residual of 11.77, a training-feature channel of 25.70, an evidence main effect of 3.13 and an interaction of 1.03. The conditional evidence effect as deployed is 4.17, which is the quantity we reported. CiteSeer at the same budget gives 11.27, 31.37, 4.97 and -1.87 against a total of 45.73, with a conditional effect of 3.10. The revision reports all four components at every budget, and reports the clean-edge retention change the reviewer noticed, which is the 657 against 432 in Table 1.
The causal wording is narrowed in three places.
Revised text, Sec. 5.2: "What it measures is the conditional effect of changing the filter's evidence while the victim's training features stay poisoned. The rest of the defended model's loss survives filtering, and it is not feature damage alone: with the filter's evidence and the victim's training features both clean, the attacker's edges still cost the defended model accuracy (App. P), so the residual combines structural damage with feature poisoning, and the two channels interact."
Revised text, Fig. 2 caption: "the gap between the curves is the conditional effect of corrupting the filter's evidence, and the rise of the dashed curve is the loss that survives filtering, which combines structural damage with feature poisoning that no edge filter was built to stop."
Revised text, Contributions: "The gap is the conditional effect of corrupting the evidence; what it does not explain is the loss that survives filtering, which combines structural damage with feature poisoning that no edge filter was designed to stop."
The remaining points are in the next comment.