acceptodds
Under review as a conference paper at ICLR 2027

Poisoning Cross-View Correspondence in Vertical Federated Learning via Consistent Latent-Cluster Reassignment

Abstract

Vertical Federated Learning (VFL) is a privacy-preserving collaborative training paradigm in which participants holding disjoint feature sets over a shared sample space jointly train a global model without exposing raw data. Although VFL security has attracted growing research interest, the literature remains heavily skewed toward targeted threats, particularly backdoor and reconstruction attacks. Byzantine attacks, a family of untargeted poisoning threats that degrade global model accuracy, have been extensively studied in horizontal federated learning but remain largely unexplored in the vertical setting. This gap is especially consequential: the classical two-party design of many VFL systems allows a single compromised passive party to unilaterally destabilize the entire system. In this paper, we introduce a novel Byzantine attack strategy for vertical settings that performs consistent cluster-based swapping, constructing a poisoned cross-view association during training. The global model gets corrupted and catastrophically fails on clean, correctly aligned data at inference time. Since existing VFL defenses fail to detect this attack without incurring substantial performance penalties, we propose a targeted defense that attributes and repairs the corrupted associations. Our findings establish untargeted Byzantine attacks as a real, underappreciated availability threat to VFL and motivate robustness mechanisms tailored to its unique cross-view learning dynamics.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
Vertical Federated Learning, Cross View Correspondence, Data Poisoning, Byzantine Attacks, Availability Attacks, Federated Learning Security, Representation Repair

Reviews

Among:
Shape:
1234this paper, Top 32%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.50 over 4 reviews, above 68% of the others.
Reviewer_w6WjOpenReview ↗
Rating
4(+1)
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper studies poisoning attacks in Vertical Federated Learning (VFL), aiming to degrade the whole model accuracy (i.e. over all samples). The attacker (called Party A) is assumed to know a small auxiliary dataset of the other party (called Server). The attack (called CCVS) consists of two phases: (1) cluster the embeddings based on feature similarity and on the auxiliary dataset (i.e. cluster similar data points with the same label) (2) report values but swap them in a cluster-level. The paper explains that cluster-level swap is essential to retain some malicious structure that the model can learn from. Moreover, for the cluster-level swap, they select the derangement that maximises the centroid distance.

The paper also proposes a defence (RGAR) that also assumes an auxiliary dataset. RGAR identifies cross-view pairs by calibrating on the auxiliary dataset. Then, during training, when a data point is provided, RGAR finds suspicious patterns by comparing the embeddings to the calibration. Using this comparison, RGAR can also repair the suspicious cross-view.

The authors evaluate on 6 datasets showing that CCVS degrades model accuracy and that their cluster-level swap technique is better than other conventional approaches. RGAR also improves model accuracy under a CCVS attack and reports high suspicion scores.

Critical strengths
  • The poisoning swaps all data points between clusters. This cluster-level swap is interesting because it creates a meaningful (yet poisonous) structure for the server model to learn.

  • Cluster swap is not random but it is specifically chosen to maximise their total distance, improving poisoning.

  • A defence for the attack is also provided that identifies malicious clients and tries to “reverse” the attack by repairing the maliciously reported values.

  • The paper is clear and well presented.

Critical weaknesses
  • CCVS and RGAR consider the classical shadow model assumption: typical in the literature but not modern. 


  • For RGAR, this assumption is less practical. First, it has to assume an initially honest Party A or a third-party auditor. Then, attested execution is necessary to get the embeddings.


  • RGAR seems to be hand-crafted for the attack. Assuming (via the “security through obscurity” argument) that the defence is known to the attacker, it remains unclear how effective RGAR is to slight variations of CCVS.

Questions for authors

Questions:

  • How does the attack perform on datasets with bigger number of classes? For example, can you provide results with CIFAR100?


  • Regarding RGAR, if attested execution is required, why not use it to verify proper execution of VFL from Party A? For example, why can’t attested execution be used to bind each sample to its actual feature row, preventing swaps?

  • How effective is RGAR for variations of CCVS? In the Appendix G.7. this is considered part of future work but can you provide evidence that RGAR remains protective even against slight variations of CCVS (for example those described in lines 1023-1024)?

4 comments
AuthorsOpenReview ↗

Responses to Reviewer w6Wj (Part 1)

Thank you very much for your thoughtful and encouraging review. We are grateful for your recognition of the structured poisoning mechanism, the distance-guided cluster selection, and the clarity of the presentation, as well as your interest in the proposed mitigation.

Your questions helped us strengthen the evaluation and clarify the assumptions. In revised manuscript and below, we present the CIFAR-100 results and address your concerns about auxiliary-data access, attested execution, and RGAR’s effectiveness.

We hope the additional evidence and explanations address your concerns and we would be very grateful if you would consider revisiting your score. Please let us know if anything remains unclear; we would be happy to elaborate.

Clarifying the shadow-model assumption in Weakness 1

We appreciate the reviewer’s concern about the auxiliary information required by CCVS and RGAR. We distinguish their assumptions from victim-model replication while acknowledging their dependence on suitable auxiliary data.

CCVS uses limited labeled examples from A’s own feature view. Its Phase-I encoder learns local structure without access to B’s features, the server’s prediction head, or the joint model’s parameters. Thus, it does not require constructing a shadow copy of the victim VFL system. The auxiliary labels provide supervision for identifying donor regions rather than reproducing the victim’s predictions.

Nevertheless, the availability and representativeness of these labels are genuine assumptions. We make their source and budget explicit and evaluate sensitivity to the label fraction.

RGAR makes a separate assumption: A trusted-reference access to authenticated, aligned reference examples rather than victim-model replication, but it restricts the deployments in which RGAR is applicable. We acknowledge that restriction and scope its recovery claims accordingly.

We therefore agree that auxiliary-data requirements deserve explicit scrutiny. Our clarification is that CCVS requires limited local supervision, whereas RGAR requires authenticated cross-view references; neither assumes a replicated victim model. We state these distinct requirements in Section 3.3 and examine their practical implications through the auxiliary-label and reference-set controls.

Q1. How does the attack perform on datasets with more classes? Can you provide results on CIFAR-100?

We thank the reviewer for recommending this extension. We evaluated CCVS on CIFAR-100, increasing the label space tenfold to 100 classes. The results show that CCVS retains a substantial effect: accuracy falls by 16.9 percentage points, exceeding the reduction from the strongest comparison attack by 9.0 points.

1. Configuration and Phase-I quality

We use a vertical split analogous to CIFAR-10, a 5% auxiliary-label budget, 100 latent clusters, and top-k donor scope 5. Clean and attacked conditions share the feature partition, architecture, and training schedule. Downstream results use three training seeds.

Phase I operates exclusively on A’s feature view and the auxiliary labels:

Phase-I metricCIFAR-100
H-ACC0.687
NMI0.554
ARI0.485
Purity0.687

A 5% budget provides 2,500 labeled examples, averaging 25 per class, to support structure recovery across 100 classes from a partial feature view.

CCVS can use the recovered structure without perfectly separating every class. Its donor construction exploits distances between latent regions and sample-level dissimilarity within destination cores. The downstream results demonstrate that these signals remain useful for poisoning in the larger label space.

2. Attack effectiveness

The following results report correctly aligned clean-test accuracy after training. All attacks use the same coverage, architecture, and training budget.

Training conditionClean-test accuracy (%) ↓Reduction from clean training (pp)
Clean training84.1 ± 0.9N/A
Round-Robin81.7 ± 0.32.4
Random Cluster76.2 ± 0.67.9
Random Sample82.3 ± 0.41.8
CCVS67.2 ± 0.616.9

Despite the 100-class setting, CCVS reduces accuracy from 84.1% to 67.2%, more than doubling test error from 15.9% to 32.8%. Its 16.9-point reduction is more than twice the 7.9-point reduction produced by Random Cluster, the strongest comparison attack.

The reduction is smaller than on CIFAR-10. Fine-grained class distinctions, fewer auxiliary examples per class, and the restricted feature view make this a more demanding setting for recovering class-related donor regions.

The larger label space attenuates, rather than eliminates, the attack. CCVS retains a clear advantage over the comparison strategies, demonstrating effectiveness beyond tasks with few classes. The matched clean-to-attacked reduction separates this poisoning effect from CIFAR-100’s baseline task difficulty.

AuthorsOpenReview ↗

Responses to Reviewer w6Wj (Part 2)

Q2. Regarding RGAR, if attested execution is required, why not use it to verify proper execution of VFL from Party A?

To clarify for this - Attestation can enforce computation and binding checks, provided the correct entity-row bindings are already available. RGAR requires authenticated inputs for a limited reference set; preventing every swap requires authoritative bindings throughout the training dataset.

1. Reference queries and training contributions have different input guarantees.

For reference queries, the server keeps an immutable, authenticated copy of A’s reference features and supplies these inputs for computation. Faithful execution therefore produces embeddings of the intended reference rows. The one-time trust step establishes reference authenticity and alignment; faithful computation remains necessary as embeddings are refreshed during training.

For ordinary training contributions, A supplies the feature row associated with each entity identifier. Suppose the encoder receives entity jj’s genuine row under identifier ii. It can correctly compute fA(xj(A))f_A(x_j^{(A)}) while returning an embedding of the wrong entity. Because CCVS substitutes genuine local rows, checking feature validity or correct encoder execution alone cannot establish the intended correspondence.

Section 3.3 now makes these input guarantees explicit, and Appendix G.1 explains the associated trust boundary.

2. Preventing every swap requires an authoritative binding for every training row.

Such bindings require trusted source records, an authenticated snapshot, or an independently verified collection process. Two cases illustrate this requirement.

  • Verification by the server or an auditor. Checking all training associations requires trusted access to source records or a mechanism that certifies them. Direct server inspection would expose A’s full feature table; an auditor or privacy-preserving verification system could provide alternatives, with additional infrastructure and trust requirements. RGAR assumes this authentication for a limited reference subset.

  • A commitment to A’s table. A commitment, such as a Merkle root over identifier–row pairs, binds subsequent computation to a particular table. Its protection depends on that table’s correctness when committed. Under the training-snapshot or correspondence-connector compromise discussed in Appendix E.7, a commitment created after corruption can preserve the swapped associations. Attested execution would then faithfully enforce those incorrect bindings.

If an authenticated commitment to the correct training snapshot exists before compromise and its bindings are enforced on every contribution, we agree that CCVS can be prevented directly. Appendix G.1 explicitly acknowledges this condition. The distinction is whether trustworthy correspondence covers the complete training dataset or only the reference subset.

3. RGAR provides a recovery mechanism where complete binding enforcement is unavailable.

An independently established reference set supplies a limited trust anchor. Reference rows collected during honest onboarding or under audit, and stored separately from the mutable training snapshot, can retain their integrity when the subsequent correspondence pipeline is compromised. This requires less authenticated data than verifying every training association, while retaining the reference-access assumption stated in the paper.

The reference controls quantify recovery under a smaller trust budget. Reducing the reference fraction from 10% to 1% gives recovery accuracies of 78.9% on MNIST and 68.9% on HAR, compared with undefended baselines of 33.3% and 15.5%. Table 6 separately evaluates partial reference corruption. These controls support recovery under the tested conditions, without establishing robustness to arbitrary reference poisoning.

Restoring the data pipeline after training also leaves a recovery problem. On MNIST, the same poisoned model achieves 96.96% on poisoned training inputs but only 31.39% on those same entities after alignment is restored (Appendix E.7). Correcting correspondence therefore does not automatically undo the learned parameters. RGAR intervenes during training through reference-guided scoring, attribution, and representation repair.

The limited trusted set follows the root-dataset principle of FLTrust (Cao et al., 2021), while RGAR additionally requires authenticated cross-view references.

These clarifications address Weakness 2 and scope RGAR’s practical role. Section 3.3 and Appendix G.1 state the reference and execution assumptions; Section 6.4 and Appendix H present repair as a recovery option whose benefit depends on the dataset and trusted information. Where authenticated full-dataset bindings are enforced, direct prevention is appropriate. Where only limited correspondence can be authenticated, RGAR provides an empirically evaluated mitigation.

AuthorsOpenReview ↗

Responses to Reviewer w6Wj (Part 3)

Q3. How effective is RGAR for variations of CCVS? In Appendix G.7, this is considered part of future work, but can you provide evidence that RGAR remains protective even against slight variations of CCVS, such as those described in lines 1023–1024?

We thank the reviewer for encouraging these experiments. We examined reference-preserving poisoning and added temporal variations on UCI-HAR, including alternating submissions and gradual onset. The results establish substantial recovery against persistent poisoning even when reference samples are spared, and clarify the accuracy tradeoff under intermittent attacks.

1. Recovery already holds when the attacker preserves the reference examples.

We verified that every reference row remains correctly aligned while all eligible non-reference rows are poisoned. This directly covers the reference-sparing strategy mentioned in Appendix G.7.

DatasetUndefended accuracy (%)RGAR accuracy (%)Paired recovery (pp)
MNIST31.22 ± 1.9583.96 ± 0.94+52.74 ± 1.18
UCI-HAR15.32 ± 1.9489.15 ± 0.67+73.83 ± 2.36

These are three-seed results under the existing reference-preserving configuration, rather than an additional independent attack condition.

Sparing the trusted examples therefore leaves a strongly damaging attack outside the reference set, with substantial recovery under RGAR. The trusted examples supply cross-view relationships for constructing replacement representations; their value does not require the attacker to corrupt them.

2. Temporal variations reveal when replacement is beneficial.

On HAR, we evaluated 80-epoch schedules with five-epoch alternating blocks and gradual onset after 20 clean epochs. We tested both alternating phases so that training ends either clean or poisoned. The two alternating schedules each contain 40 poisoned epochs; static poisoning contains 80.

RGAR settings, Phase-I artifacts, donor assignments, reference sets, and training seeds are fixed across matched comparisons.

Training conditionUndefended accuracy (%)RGAR accuracy (%)
Clean97.43 ± 0.3188.44 ± 2.42
Static CCVS15.32 ± 1.9489.15 ± 0.67
Alternating, ending clean94.95 ± 0.3489.19 ± 0.86
Alternating, ending poisoned91.11 ± 0.4088.44 ± 2.27
Gradual onset93.76 ± 0.9788.35 ± 2.20

Persistent CCVS produces an 82.11-point undefended loss, against which RGAR recovers 73.83 points. Alternating and gradual schedules produce smaller final losses, and their undefended accuracies exceed RGAR’s. For the alternating schedule ending with poisoning, the paired RGAR-minus-undefended difference is −2.68 ± 1.88 points.

The current HAR configuration gives substantial weight to reference-guided replacement throughout training. Its similar accuracy across schedules therefore characterizes this replacement operating point; these measurements do not establish selective adaptation to attack onset and cessation.

3. The temporal measurements substantiate the attack variation itself.

At equal cumulative exposure, ending with poisoning produces greater damage than ending clean: undefended accuracy is 91.11% versus 94.95%. Blockwise evaluation also records repeated deterioration during poisoned intervals.

After the first poisoned block, undefended accuracy falls from 94.91% to 83.17%, while RGAR achieves 87.96%, a 4.79-point advantage. At epoch 20, its advantage is 1.44 points. These intermediate diagnostics show an early protective benefit; the final results above establish that this benefit does not persist as a net accuracy advantage over the complete intermittent schedule.

These findings refine the scope of the mitigation contribution. RGAR provides substantial recovery against persistent, reference-preserving correspondence poisoning, using authenticated relationships without requiring the attacker’s cluster mapping or donor assignments. The temporal experiments identify conditions where the accuracy cost of replacement outweighs the attack damage.

This follows the conditional recovery claims in Section 6.4 and Appendix H. Selective intervention under changing attack intensity and optimized defense-aware attacks remain in our future work.

We hope these additional experiments and clarifications address your concerns and strengthen your confidence in the paper’s contributions. We would be grateful if you would consider revisiting your score in light of the expanded evidence and revised scope.

AuthorsOpenReview ↗

Follow-up with Reviewer w6Wj

We appreciate the time you’ve taken to consider our work and the strengths you recognized in our work. Your words motivated us to work with the remaining concerns. With the discussion period coming to a close, we hope our responses and the additional experiments have helped address the points you raised. We apologize for being a bit late in the responses. But if there is anything you would like us to explain further, we would be happy to do so while the discussion is still open.

Based on our revisions of the paper and the additional results from the new experiments we conducted, we would be very grateful if you would consider raising the score if you find our explanations satisfactory. Thank you again for your time and consideration.

Reviewer_1kGVOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

The paper studies untargeted poisoning in vertical federated learning by corrupting the correspondence between parties’ feature views. CCVS uses limited auxiliary labels to identify local clusters and consistently swaps feature rows across clusters, causing the model to learn associations that fail on correctly aligned test data. The authors also propose RGAR, which uses trusted reference data to identify and repair corrupted representations during training. Experiments on six datasets report substantial accuracy degradation at full swap coverage and recovery with the proposed defense.

Critical strengths

The paper examines a meaningful VFL vulnerability: individually plausible representations can still poison training when their correspondence with other views is corrupted. The evaluation covers several data modalities and examines relevant factors, including swap coverage, auxiliary labels, party count, and reference-set size.

Critical weaknesses
  1. The reported clustering metrics are internally inconsistent. Table 1 gives UCI-Bank an H-ACC of 0.914 and purity of 0.883, although Appendix H explicitly states that H-ACC cannot exceed purity under the provided definitions. This needs to be reconciled before the clustering evaluation can be assessed reliably.

  2. The attack comparison does not isolate the contribution of the optimized cluster mapping. CCVS changes both the mapping and donor selection, while the comparison methods use random donors. On UCI-Mushroom, there are only two clusters, so all three cluster derangements are identical; the large accuracy gap therefore cannot be attributed to the cluster mapping itself.

  3. The defense comparisons do not support the broad conclusion about existing VFL defenses. The evaluated baselines are detect-and-drop adaptations, although the paper itself identifies VFLIP as a reconstruction-based defense. Without a full reconstruction baseline or retraining on the honest view, the claimed advantage of RGAR remains insufficiently established.

Questions for authors
  1. How were UCI-Bank’s H-ACC and purity computed, and what are the corrected values under Eq. (21)?
  2. On Mushroom, what explains the gap between 32.8% accuracy for CCVS and approximately 95% for the other cluster-based attacks? Across datasets, does the maximum-distance mapping still help when donor selection and confidence filtering are held fixed?
  3. With equivalent access to trusted reference data, how does RGAR compare with an existing reconstruction defense and retraining on the honest view, in both accuracy and runtime?
6 comments
AuthorsOpenReview ↗

Responses to Reviewer 1kGV (Part 1)

Thank you very much for your thoughtful and detailed review. We are truly grateful for the strengths you recognized in our work and for your suggestions, which helped us improve the paper.

We have carefully revisited each concern and revised the manuscript to include a corrected UCI-Bank clustering evaluation, controlled ablations separating mapping and donor selection, and comparisons with VFLIP and honest-view retraining under matched trusted-reference access, including runtime measurements.

We explain these changes below and hope the additional evidence addresses your concerns. We would be grateful if you would consider revisiting your score after reviewing our responses, and we would be very happy to clarify anything further.

Q1. How were UCI-Bank’s H-ACC and purity computed, and what are the corrected values under Eq. (21)?

We thank the reviewer for the sincerity to point out a metric inconsistency that was retained in the paper due to an update of methodology in a later phase during attack development and forgetting to update the metric evaluation for a former phase. Your observation helped us identify an incomplete update in the UCI-Bank clustering-metric reporting. We have traced its cause, recomputed the clustering evaluation, and rerun the complete UCI-Bank experiments. The rerun reproduced attack results consistent with those reported in the paper, supporting the effectiveness of CCVS under the corrected evaluation.

UCI-Bank needs particular care because it uses 16 clusters for two imbalanced outcome classes. During attack development and a later phase of experiment, we adopted a many-to-one assignment for UCI-BANK, allowing several clusters to share a class tendency while preserving distinct donor regions. All reported attack experiments using this dataset used this assignment, but the clustering-metric reporting retained the earlier configuration. We therefore withdraw the incorrect H-ACC entry and explicitly distinguish the many-to-one evaluation.

Corrected evaluation and complete contingency table

The recomputed counts cover all N=36168N=36168 samples. The final column gives the balanced-accuracy-optimal evaluation assignment.

ClusterClass 0Class 1Assigned class
01,8733831
13,1451530
21,6002110
32,5213811
42,7802460
52,0001620
62,0683511
72,3892840
81,0425551
91,8571250
102,5552260
112,4141720
122,4122190
13595420
141,2111741
151,4755471
Total31,9374,231

Writing these counts as Mk,cM_{k,c}, ordinary many-to-one accuracy equals purity:

=\frac{\sum_k\max_c M_{k,c}}{N} =\frac{31{,}937}{36{,}168} =\mathbf{0.8830}.$$ To give both classes equal weight, we additionally report **optimal many-to-one balanced accuracy**: $$\mathrm{BACC}^{*} =\max_f\frac12\sum_{c=0}^{1} \frac{\sum_{k:f(k)=c}M_{k,c}}{N_c} =\frac12\sum_k\max_c\frac{M_{k,c}}{N_c}.$$ Each cluster maps to the class maximizing $M_{k,c}/N_c$. Clusters **0, 3, 6, 8, 14, and 15** map to Class 1, yielding the confusion matrix below. | Ground truth | Assigned Class 0 | Assigned Class 1 | |---|---:|---:| | Class 0 | 21,747 | 10,190 | | Class 1 | 1,840 | 2,391 | Thus, $$\mathrm{BACC}^{*} =\frac12\left(\frac{21{,}747}{31{,}937} +\frac{2{,}391}{4{,}231}\right) =\mathbf{0.6230},$$ against **0.5000** for constant-class prediction. This ground-truth-optimal mapping is an external diagnostic; **the attack uses only auxiliary-label-based class tendencies**. BACC is reported separately from Eq. (21)’s H-ACC. **Why the attack remains effective** The table reveals useful donor-selection signals: Class 1 prevalence ranges from **4.6% to 34.8% across clusters: a 7.5-fold difference**, compared with **11.7% overall**; Cluster 15 also reaches **27.1%**. These differences remain informative even though Class 0 is the absolute majority in every cluster. **CCVS needs directional signals for constructing harmful cross-view mismatches, without requiring perfectly recovered classes.** Overclustering retains finer subpopulations whose different class tendencies guide donor selection. The complete Bank rerun directly verifies that the available signals suffice to produce attack outcomes consistent with the paper on correctly aligned test data. We appreciate the reviewer’s careful observation. The revised evaluation and full contingency table clarify the clustering evidence, while the end-to-end rerun supports the reported effectiveness of CCVS.
AuthorsOpenReview ↗

Responses to Reviewer 1kGV (Part 2)

Q2: On Mushroom, what explains the gap between 32.8% accuracy for CCVS and approximately 95% for the other cluster-based attacks? Across datasets, does the maximum-distance mapping still help when donor selection and confidence filtering are held fixed?

(Part 1/2): Explaining the Mushroom gap.

We thank the reviewer for suggesting this decomposition. We conducted 264 controlled cross-dataset runs, together with a five-seed donor-selection study on Mushroom, to answer both parts directly. Donor selection explains the Mushroom gap under an identical mapping, while maximum-distance mapping provides additional attack strength when donor selection and confidence filtering are held fixed.

Mushroom provides a direct test of CCVS’s donor selection.

Mushroom has Kc=2K_c=2, giving only one possible cluster derangement. Maximum-distance, round-robin, and random-derangement mappings therefore select the same opposite destination cluster. This allows us to isolate donor selection while fixing the mapping, victim set, victim order, architecture, and training configuration.

We varied only the donor-selection rule over five seeds. Lower clean-test accuracy indicates a stronger attack.

Donor rule under the fixed mappingAccuracy (%) ↓Unique donorsMaximum donor reuse
Clean training97.85 ± 0.50N/AN/A
Random donors from the full destination cluster95.03 ± 1.606,5062
Random donors from the high-confidence core94.50 ± 1.105,0922
Hardest negatives from the core, diversity-capped79.80 ± 10.155,0922
CCVS hardest negatives from the core, unrestricted reuse32.78 ± 2.60691,076

This controlled experiment recovers the large separation observed in Table 2. At an identical mapping, CCVS’s donor-selection rule reduces accuracy by 62.25 ± 1.19 percentage points relative to random full-cluster donors, using paired differences across the five seeds.

The intermediate controls identify two contributions:

  • Hard-negative selection remains effective with donor diversity controlled. Random-core and diversity-capped hard-negative selection use the same number of unique donors and the same maximum reuse. Changing the selection criterion reduces accuracy from 94.50% to 79.80%.
  • Repeated selection of the hardest donors further amplifies the attack. Unrestricted selection concentrates assignments on 69 donor rows and reduces accuracy further to 32.78%.

Confidence filtering alone produces only a small change, from 95.03% to 94.50%. Moreover, victim–donor class mismatch remains between 0.90 and 0.94 across all donor rules, including those retaining approximately 95% accuracy. The large performance gap therefore depends on which feature rows are selected and how their assignments are concentrated. Simply choosing an opposite-cluster donor does not reproduce the CCVS effect.

Mushroom consequently explains the reviewer’s observation through a controlled comparison: its forced mapping removes destination choice as an explanation, isolating the contributions of hard-negative selection and donor concentration.

The revision specifies the unrestricted hardest-negative rule used for the reported CCVS result and includes the diversity-capped control. Part 2 presents the cross-dataset experiment isolating the mapping’s contribution.

AuthorsOpenReview ↗

Responses to Reviewer 1kGV (Part 3)

Q2: Across datasets, does the maximum-distance mapping still help when donor selection and confidence filtering are held fixed?

(Part 2/2): Mapping under fixed donor selection and confidence filtering

Maximum-distance mapping retains its benefit under controlled donor selection.

We crossed eight destination constructions with each applicable donor rule on MNIST, Fashion-MNIST, and UCI-HAR: the maximum-distance derangement π∗\pi^{*}, round-robin, five random derangements, and top-kk farthest-cluster pooling. This gives 264 training runs with three seeds per configuration.

Within each donor-rule comparison, the confidence threshold, swap coverage, architecture, training schedule, and victim order are fixed. Confidence filtering is disabled on UCI-HAR, allowing the mapping effect to be evaluated without that component.

The table reports mean clean-test accuracy. “Random” averages the five random derangements. The final column gives the accuracy reduction achieved by π∗\pi^{*} relative to that average.

DatasetDonor ruleπ∗\pi^{*} ↓RandomRound-robinReduction vs. random (pp)
MNISTRandom, full cluster75.2678.9681.803.70
MNISTRandom, core70.0676.8280.066.76
MNISTHardest negative41.0648.4345.477.37
MNISTHardest negative, capped61.3567.9667.316.61
Fashion-MNISTRandom, full cluster66.9972.4365.745.44
Fashion-MNISTRandom, core66.8570.8663.594.01
Fashion-MNISTHardest negative30.6546.3444.9015.69
Fashion-MNISTHardest negative, capped61.3166.9562.185.64
UCI-HARRandom, full cluster1.0639.6544.9438.59
UCI-HARHardest negative11.7435.9620.6024.22
UCI-HARHardest negative, capped0.4736.4838.5336.01

Maximum-distance derangement improves over the average random derangement in all 11 controlled comparisons, spanning all three datasets and every applicable donor rule.

Three findings directly address the reviewer’s question:

  • The mapping helps even with random donors. On MNIST and Fashion-MNIST, π∗\pi^{*} improves over average random derangements under both full-cluster and confidence-core sampling, establishing an effect beyond hardest-negative selection.
  • The benefit persists with donor diversity constrained. With diversity-capped hard negatives, the reductions relative to average random mappings are 6.61, 5.64, and 36.01 points on MNIST, Fashion-MNIST, and UCI-HAR.
  • UCI-HAR shows a particularly strong effect without confidence filtering. With random donors, changing the mapping reduces accuracy from 39.65% under average random derangements to 1.06% under π∗\pi^{*}. With diversity-capped hard negatives, the corresponding accuracies are 36.48% and 0.47%. Severe degradation therefore persists even when unrestricted donor concentration is removed.

The factorial design also reveals interactions between the components. On Fashion-MNIST, the advantage of π* over the average random mapping grows from 4.01 points with random-core donors to 15.69 points with uncapped hardest-negative donors (the Table 2 rule). Round-robin yields the stronger attack in the two random-donor conditions, while π* yields the stronger attack under both hardest-negative rules. Across all 11 dataset–rule cells, π* outperforms the average random mapping, and the two components reinforce one another.

The implemented top-kk construction receives additional support.

The Table 2 implementation uses top-kk farthest-cluster pooling. For each source cluster, the adversary selects donors from the union of its kk farthest destination cores. We evaluated this separately from the single-destination derangement π∗\pi^{*}.

Under hardest-negative selection, top-kk pooling achieves 31.22% accuracy on MNIST and 25.30% on Fashion-MNIST, the strongest attacks among all eight destination constructions evaluated on those datasets. These results further support distance-guided donor-pool construction. The revision includes the controlled ablations and specifies the donor-selection and reuse settings.

Together, the experiments establish both contributions: donor selection explains the Mushroom gap at an identical mapping, and maximum-distance mapping adds attack strength over average random mappings in all 11 controlled comparisons.

Reviewer_sTyZOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper studies untargeted poisoning by a malicious passive party in two-party vertical FL. The attack, CCVS, clusters the attacker's feature view using a 2–3% labelled auxiliary set. It then fixes a maximum-distance derangement between clusters and replaces each sample's features with those of a donor from the mapped cluster. The server thus learns a consistent but wrong cross-view association and fails on correctly aligned test data. The defense, RGAR, uses the attacker's true features on a 5–10% reference set to attribute the corruption and replace the attacker's training embeddings with reconstructions.

On six datasets at 100% swap coverage, CCVS reduces clean accuracy to 15.7–52.2%, versus 43–95% for random or round-robin swaps. Adapted Krum, FLTrust and autoencoder gates mostly fail to recover, while RGAR reaches 73.6–92.4%.

Critical strengths

Strength 1: The paper shows that a passive party without labels can severely degrade a VFL model while every embedding it sends is genuine. The effect holds on all six datasets, with standard deviations of at most 2.6 points over three seeds. Random per-sample swaps are far weaker (MNIST 89.0% vs. 32.5%), so the consistency of the swap, not the amount of corruption, drives the effect.

Strength 2: In two-party VFL, removing the suspected party discards an entire feature view, so repairing rather than discarding is the right goal. The paper also states RGAR's trust assumptions openly.

Critical weaknesses

Weakness 1: The attack is essentially label flipping. At full coverage, every sample in cluster s, which approximates a class, receives A-features from cluster π(s), while labels and B's features stay unchanged. From A's view this is class-permutation label flipping (e.g., Tolpegin et al., ESORICS 2020), a connection the paper never discusses. The paper also does not explain how flipping only one view behaves. At 75% coverage, MNIST, F-MNIST and HAR stay at 93.5/85.7/93.0%, and they collapse only at 100% (Table 7). The paper attributes this to an aligned majority, but aligned samples are a 25% minority at 75% coverage. On Mushroom (K_c = 2), CCVS, Round-Robin and Random Cluster use the same derangement, yet CCVS gives 32.8% versus 95.2% and 94.7%. The gap must therefore come from donor selection rather than mapping geometry. This weighs most in my assessment because the contribution rests on the attack.

Weakness 2: RGAR is not compared with the simple alternatives its assumptions allow. The paper reports neither training without Party A, even though App. I says RGAR's cost should be compared with that option, nor training only on R, which holds 3k–6k clean MNIST samples. Cosine Gate flags 97–100% of poisoned samples on MNIST, F-MNIST and HAR yet reaches only 46.9/13.3/61.2%. This may reflect a train/test mismatch in the baseline protocol. On Bank, RGAR's 85.3% is below the roughly 88% majority-class rate.

Questions for authors
  1. How does CCVS differ from label flipping, and what does flipping a single view add?
  2. Could you add a coverage sweep between 75% and 100% and report test accuracy with A or B zeroed out? Could you also add an ablation that separates the cluster mapping from donor selection and explains the Mushroom result?
  3. What accuracy do you get from training on B alone, and from training on R alone, over three seeds? What do the gate baselines feed the head at test time?
  4. Does CCVS still collapse HAR and Bank under balanced partitions? For Bank, please report balanced accuracy or AUC.
  5. In what deployment would A poison training but send true features at inference? Would held-out aligned validation data reveal the attack?
7 comments
AuthorsOpenReview ↗

Responses to Reviewer sTyZ (Part 1)

We thank the reviewer for the thoughtful and detailed review. We are grateful for the strengths recognized in our work and for the careful examination of the attack and defense mechanisms.

In response, we conducted additional coverage and view-zeroing experiments, controlled mapping/donor ablations, three-seed honest-view and reference-only comparisons, and balanced-partition experiments. We also examined gate-baseline inference behavior and attack visibility under held-out aligned evaluation.

We hope these results address your concerns. We would be grateful if you would consider revisiting your score after reviewing the additional evidence, and would be happy to clarify anything further.

Q1. How does CCVS differ from label flipping, and what does flipping a single view add?

We agree with this observation that Under perfectly class-aligned clusters and a bijective permutation, A’s marginal feature-label relationship admits a class-permutation label-flipping interpretation, as suggested through Tolpegin et al. (ESORICS 2020). The distinction concerns the joint VFL example, attacker capabilities, and donor selection. Revised Section 4.2 explicitly discusses this relationship.

1. CCVS corrupts correspondence while preserving honest-view supervision. Label flipping

(xA,xB,y)→(xA,xB,y′)(x_A,x_B,y) → (x_A,x_B,y')

CCVS

(xA,xB,y)→(xA,j(i),xB,y)(x_A,x_B,y) → (x_{A,j(i)},x_B,y)

B’s features and the server label still describe the original entity, while A supplies another entity’s genuine feature row. Under the ideal class-permutation interpretation, the views provide conflicting class evidence; relabeling the complete example cannot reconcile both.

The passive attacker cannot edit server labels or B’s features and has only limited auxiliary labels. Hash checks confirm that labels and B remain byte-identical; only A changes. CCVS therefore exploits entity correspondence under passive-party constraints. A’s marginal interpretation omits the preserved B–label relationship participating in the same loss.

2. Class permutation alone does not explain the attack strength.

CCVS pools distant destination cores and selects donors separately for each source sample, allowing reuse and controlling donor concentration beyond the class-level mapping.

Mushroom isolates this contribution because its two clusters admit only one derangement. With mapping and training fixed, five-seed results are:

Donor ruleAccuracy (%)Unique donorsCross-class donor fraction
Random, full cluster95.03 ± 1.606,5060.8986
Random, confidence core94.50 ± 1.105,0920.9340
Hardest negative, diversity-capped79.80 ± 10.155,0920.9361
CCVS, unrestricted reuse32.78 ± 2.60690.9159

The identical mapping yields approximately 95% accuracy or severe degradation depending on donor selection. CCVS causes greater damage despite a lower class-mismatch fraction than random-core selection.

With unique-donor count and maximum reuse held equal, hard-negative selection reduces accuracy from 94.50% to 79.80%. Unrestricted selection further reduces it to 32.78%, giving a paired 62.25 ± 1.19-point reduction relative to random full-cluster donors.

Archived configurations reinforce this beyond Mushroom. On MNIST, mismatch fractions 0.974/0.984 accompany accuracies 84.48%/31.22%; on Fashion-MNIST, fractions 0.991/0.996 accompany 79.37%/25.30%. Thus, class mismatch alone does not determine attack strength.

Section 6.5 summarizes these findings; Appendix B, Table 7 reports the Mushroom ablation; and Appendix E.2 specifies unrestricted reuse and consistency across epochs.

3. Single-view poisoning induces harmful dependence despite an intact honest view.

Zeroing A’s embedding immediately before the head, without retraining, gives the following three-seed results:

DatasetNormal aligned inference (%)A zeroed (%)
MNIST31.22 ± 1.9568.73 ± 0.39
Fashion-MNIST25.30 ± 1.9664.95 ± 1.94
UCI-HAR15.32 ± 1.9454.89 ± 0.91
UCI-Mushroom32.84 ± 3.4477.54 ± 4.26

Removing A hurts clean-trained models but substantially improves CCVS-trained models. A’s useful contribution becomes harmful after correspondence poisoning, despite correct labels and an intact B-view. Section 6.5 summarizes this finding; Appendix E.6 and Table 13 provide the inference-intervention results.

These findings address Weakness 1 beyond the marginal label-flipping analogy. At an identical mapping, donor selection changes Mushroom accuracy from approximately 95% to 32.8%; view-zeroing then exposes harmful dependence on A. They also depict the importance of selected feature rows and persistent cross-view assignments beyond a class permutation.

AuthorsOpenReview ↗

Responses to Reviewer sTyZ (Part 2)

Q2 (Part 1/2). Could you add a coverage sweep between 75% and 100% and report test accuracy with A or B zeroed out?

As per the suggestions made, we added high-coverage measurements, test-time view-zeroing experiments, and controlled mapping/donor ablations. These address the coverage interpretation and the source of attack effectiveness raised in Weakness 1. We present coverage and view-zeroing here, followed by the component ablations in Part 2.

1. Substantial degradation occurs before full coverage.

The reviewer is correct that aligned samples constitute a 25% minority at 75% coverage. We have corrected the “aligned majority” explanation. Remaining aligned examples may constrain learning even as a minority.

The expanded coverage results are:

Dataset0%75%85%90%95%100%
MNIST96.58 ± 0.0993.70 ± 0.1582.17 ± 0.6068.82 ± 1.5157.02 ± 1.1531.22 ± 1.95
Fashion-MNIST87.24 ± 0.5685.45 ± 0.2673.53 ± 0.4165.94 ± 1.1556.62 ± 0.3225.30 ± 1.96
UCI-HAR97.43 ± 0.3193.05 ± 0.7379.92 ± 1.4961.76 ± 1.4043.54 ± 1.0115.32 ± 1.94

Accuracy is reported in percent as mean ± standard deviation over three seeds.

At 90% coverage, CCVS reduces accuracy by 27.76 points on MNIST, 21.30 on Fashion-MNIST, and 35.67 on HAR. At 95%, the reductions increase to 39.56, 30.62, and 53.89 points, respectively. Noticeable damage therefore occurs while correctly aligned training pairs remain available.

Full coverage is a deliberate operating point of the attack. The malicious party controls its complete training feature block and can reassign every local row without modifying server labels or accessing B’s features. Applying the strategy consistently across this block exploits the correspondence corruption available within the threat model.

The accelerating degradation is consistent with the mechanism. Partial coverage retains aligned pairs that can anchor the learned relationship; their influence need not require a numerical majority. Full coverage reinforces the fabricated correspondence throughout A’s training contribution. The sweep quantifies this coverage dependence and shows that severe degradation extends below exactly 100%. Section 6.5 summarizes these findings, and Appendix E.4, Table 11 reports the expanded sweep.

2. View-zeroing reveals harmful dependence on A.

We evaluated the trained models normally and with either party’s embedding zeroed immediately before the fusion head, without retraining:

DatasetNormal inference (%)A zeroed (%)B zeroed (%)
MNIST31.22 ± 1.9568.73 ± 0.3937.00 ± 1.93
Fashion-MNIST25.30 ± 1.9664.95 ± 1.9434.93 ± 1.68
UCI-HAR15.32 ± 1.9454.89 ± 0.9124.30 ± 0.19
UCI-Mushroom32.84 ± 3.4477.54 ± 4.2623.65 ± 2.79

These CCVS-trained results use three seeds.

Removing A improves every attacked model shown, whereas the same intervention reduces accuracy in the corresponding clean-trained models. A provides useful information under clean training, but its contribution becomes harmful after correspondence poisoning. Correct server labels and an intact B-view therefore do not prevent the fused model from learning damaging dependence on A.

Zeroing intervenes on an already-trained joint model. The separately trained B-only models in Q3 evaluate learning again without A. Appendix E.6, Table 13 reports the view-zeroing results and the accompanying clean-model comparison.

AuthorsOpenReview ↗

Responses to Reviewer sTyZ (Part 3)

Q2 (Part 2/2). Could you add an ablation that separates cluster mapping from donor selection and explains the Mushroom result?

We conducted a five-seed fixed-mapping Mushroom study and 264 controlled cross-dataset runs. Together, they distinguish the two contributions: donor selection explains Mushroom’s gap, while distance-guided mapping adds attack strength when donor selection and confidence filtering are held fixed.

1. Mushroom isolates the donor-selection contribution.

We agree with the reviewer that Mushroom’s two clusters admit only one derangement. This makes it particularly informative for isolating donor selection. We fixed the mapping, victim set, victim order, architecture, and training configuration and varied only the donor rule over five seeds:

Donor ruleAccuracy (%) ↓Unique donorsMaximum reuse
Random, full destination cluster95.03 ± 1.606,5062
Random, high-confidence core94.50 ± 1.105,0922
Hardest negative, diversity-capped79.80 ± 10.155,0922
CCVS hardest negative, unrestricted reuse32.78 ± 2.60691,076

At an identical mapping, CCVS reduces accuracy by 62.25 ± 1.19 percentage points relative to random full-cluster donors, using paired differences across seeds.

The intermediate controls explain the gap. With unique-donor count and maximum reuse held equal, hard-negative selection reduces accuracy from 94.50% to 79.80%. Unrestricted selection concentrates assignments on 69 donor rows and further reduces accuracy to 32.78%.

Cross-class donor fractions remain between 0.90 and 0.94, including the near-clean random-donor conditions. The damage therefore depends on the selected rows and their concentration beyond simply choosing donors from the opposite cluster.

Section 6.5 summarizes this decomposition, and Appendix B, Table 7 reports the controlled donor ablation. Appendix E.2 specifies unrestricted donor reuse and fixed assignments across epochs; Appendix E.3 states the comparison strategies.

2. Maximum-distance mapping contributes independently across datasets.

We additionally conducted 264 training runs, crossing eight destination constructions with applicable donor rules on MNIST, Fashion-MNIST, and HAR, using three seeds per configuration. The constructions comprise maximum-distance derangement π∗\pi^{*}, round-robin, five random derangements, and top-kk pooling.

Within each donor-rule comparison, confidence filtering, coverage, architecture, training schedule, and victim order are fixed. With hardest-negative selection:

Datasetπ∗\pi^{*} ↓Average random derangementRound-robin
MNIST41.0648.4345.47
Fashion-MNIST30.6546.3444.90
UCI-HAR11.7435.9620.60

Maximum-distance derangement improves over average random mappings in all 11 tested dataset–donor conditions, including random-donor and diversity-capped conditions. With hardest-negative selection, its advantage is 7.37, 15.69, and 24.22 points on MNIST, Fashion-MNIST, and HAR.

The benefit also persists with donor diversity constrained: capped hard-negative selection gives advantages of 6.61, 5.64, and 36.01 points, respectively.

HAR provides a particularly direct comparison because confidence filtering is disabled. With random donors, maximum-distance mapping reaches 1.06%, compared with 39.65% under average random mappings. With capped hard negatives, the corresponding accuracies are 0.47% versus 36.48%. Severe degradation therefore persists without unrestricted donor concentration.

3. The implemented top-kk construction receives additional support.

The Table 2 implementation pools the cores of each source cluster’s kk farthest admissible destinations. We evaluated this separately from the single-destination derangement π∗\pi^{*}.

With hardest-negative selection, top-kk pooling reaches 31.22% on MNIST and 25.30% on Fashion-MNIST, the strongest attacks among the eight destination constructions tested on those datasets.

Appendix B, Table 8 reports the controlled mapping comparisons, while Appendix E.1 distinguishes pooled donor construction from the single-destination derangement. Section 6.5 summarizes the findings.

Mushroom establishes the donor-selection contribution under an identical mapping; the cross-dataset factorial establishes an additional mapping benefit under fixed donor rules. We hope these results resolve the component-attribution concern in Weakness 1.

Reviewer_2BNEOpenReview ↗
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4
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2
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Paper summary

This paper studies poisoning of cross-view correspondence in vertical federated learning. A malicious passive party has access only to its own features and a small stratified auxiliary labeled set, but can submit a local feature from another sample under a given sample ID during training. The proposed Consistent Cross-View Swap (CCVS) first learns a semi-supervised representation and clusters the adversary’s local view. It then constructs a maximum-distance cluster derangement and selects hard-negative donors from the destination clusters. The resulting feature reassignment is fixed across epochs, so the server trains on a persistent but false association between the malicious view, the honest view, and the label. At test time, correctly aligned clean views are restored, and accuracy drops.

The paper also proposes Reference-Guided Attribution and Reconstruction (RGAR). Before training, the server stores a small authenticated reference set containing the malicious party’s true features. RGAR uses class and joint prototypes, diagonal Mahalanobis distances, and EMA drift to score suspicious pairs and accumulate party-level evidence. After attribution, it reconstructs or replaces the suspicious party’s representation instead of dropping the whole view. Experiments cover multiple datasets, with comparisons to Round-Robin, Random Cluster, Random Sample, Krum, Cosine Gate, and AE Gate. The paper reports that, with two parties and 2–3% auxiliary labels, CCVS reduces clean-test accuracy substantially across all six datasets.

Critical strengths
  1. A VFL-specific attack surface. CCVS explicitly targets cross-view sample correspondence rather than treating VFL as ordinary client-update aggregation. It needs no test-time trigger or label modification and exploits a structural property of VFL.

  2. Broad attack evaluation and useful ablations. The paper studies six public datasets and reports the effects of auxiliary-label fraction, swap coverage, party count, and donor scope. It also reports training-seed variation conditional on a fixed Phase I partition.

  3. A repair-oriented defense objective. In two-party VFL, dropping a suspicious party removes a complete feature view. RGAR’s use of a trusted relationship to reconstruct that view is a reasonable alternative to detect-and-drop defenses.

Critical weaknesses
  1. Metric validity and comparison protocol issues affect the main evidence. Appendix H defines H-ACC as a one-to-one cluster-to-class Hungarian mapping and states that (\mathrm{H\text{-}ACC}\leq\mathrm{Purity}). Yet UCI-Bank has (K_c=16) and two classes, for which a one-to-one cluster-to-class mapping is not defined, and Table 1 reports H-ACC (=0.914) while Purity is (0.883), violating the stated inequality. The authors must clarify whether a many-to-one mapping, padding, or another metric was actually used and recompute Bank H-ACC. More broadly, CCVS is reported over three VFL seeds, while Round-Robin, Random Cluster, and Random Sample are single-seed point estimates; Phase I clustering is also run only once. RGAR hyperparameters are selected from training diagnostics rather than a common validation protocol, and the threshold/tuning procedures of the baselines are not specified symmetrically. It is therefore difficult to determine whether the reported advantage comes from the mapping itself or from method-specific tuning and randomness.

  2. RGAR’s applicability and security boundary are much narrower than the main narrative suggests. RGAR requires the server to store 1–10% of the malicious party’s true raw features before the attack and assumes that these reference features are unpoisoned, the party faithfully executes forward passes on server-supplied references, the server has training labels, and the party cannot forge reference responses. This is a substantial trust and privacy concession beyond standard VFL. The reference-corruption experiment does not cover an attacker that knows and spares the reference set, drifts slowly, forges forward responses, or colludes with another party. RGAR is enabled only during training and is disabled at inference; its results remain below clean accuracy, and for tabular data it uses class-prototype replacement rather than the same reconstructor. The conclusions should therefore be restricted to conditional training-time repair under the trusted-reference, single-malicious-party threat model.

  3. Attack realism and baseline coverage are limited. The image experiments use left/right pixel splits, which are controlled views rather than typical institution-level heterogeneous features. UCI-Bank uses attack-specific 16 donor regions and a class-aware destination rule. The attack is evaluated only as a fixed training-time row reassignment, without adaptive attacks, slow/intermittent swapping, reference avoidance, cryptographic ID/integrity checks, or collusion. The defense comparison also consists mainly of the authors’ adaptations of detect-and-drop methods and lacks unified clean false-positive, precision/recall, and adaptive-attack evaluation.

Questions for authors
  1. Please correct and explain UCI-Bank H-ACC. With (K_c=16) and two classes, how is the one-to-one cluster-to-class Hungarian mapping defined? Why is H-ACC (0.914) larger than Purity (0.883), contrary to Appendix H? Please provide the contingency table and recomputed result.

  2. Please run CCVS, Round-Robin, Random Cluster, Random Sample, RGAR, and all defense baselines with the same set of Phase I and VFL random seeds, and report means, uncertainty, detection precision/recall/FPR, and whether thresholds were selected on an independent validation set. The current single-seed baseline results are insufficient for claims such as “only CCVS produces collapse” or “RGAR is the only method that recovers.”

  3. Does RGAR fundamentally require raw malicious-party features and true labels in the reference set? Please evaluate frozen reference embeddings, a reference set known to and selectively spared by the attacker, and forged reference responses. These cases determine whether the defense applies under standard VFL privacy and integrity assumptions.

  4. Can the authors add adaptive attacks against RGAR, such as slow drift, non-reference-only swapping, alternating clean/poisoned submissions, and forged forward passes, as well as at least one multi-party or colluding setting? If these are out of scope, please state the trusted-reference and single-malicious-party boundary explicitly in the main claims.

  5. Please report clean accuracy, training cost, communication overhead, and privacy cost in a unified comparison. RGAR takes approximately 3165 seconds on MNIST versus 47 seconds for naked poisoned training, and sharing 1–10% of raw features should be clearly distinguished from the standard VFL setting.

8 comments
AuthorsOpenReview ↗

Responses to Reviewer 2BNE (Part 1)

Thank you very much for your thoughtful and detailed review. We appreciate your recognition of the VFL-specific attack surface, the breadth of the evaluation, and the motivation for representation repair. Your questions helped us strengthen the experimental controls and clarify the assumptions underlying our results.

We address each concern below and identify the corresponding revisions. We hope these results address your concerns. We would be grateful if you would consider revisiting your score after reviewing the additional evidence, and would be happy to clarify anything further.

Q1. Please correct and explain UCI-Bank H-ACC. With 16 clusters and two classes, how is the one-to-one Hungarian mapping defined? Please provide the contingency table and recomputed result.

We thank the reviewer for bringing this to our notice. We have reconciled UCI-Bank’s clustering evaluation with its attack configuration, recomputed the metrics, and rerun the complete Bank pipeline. The rerun reproduced attack outcomes consistent with those reported in the paper.

UCI-Bank uses 16 latent donor regions for two imbalanced outcome classes. During attack development, we adopted a many-to-one class-tendency assignment, allowing several clusters to share a class tendency while preserving their individual identities for donor selection. All reported Bank attack experiments used this configuration. The clustering-metric reporting retained an earlier configuration, producing the inconsistent H-ACC entry. We have withdrawn 0.914 and clarified the evaluation conventions.

1. Complete contingency table

The recomputed counts cover all 36,168 training samples.

ClusterClass 0Class 1Assigned class
01,8733831
13,1451530
21,6002110
32,5213811
42,7802460
52,0001620
62,0683511
72,3892840
81,0425551
91,8571250
102,5552260
112,4141720
122,4122190
13595420
141,2111741
151,4755471
Total31,9374,231—

2. Clarifying the matching convention

An injective assignment of all 16 clusters to two classes is impossible. The rectangular Hungarian convention instead finds a maximum-weight partial matching, with each cluster and class appearing at most once. Equivalently, padding with zero-valued dummy class columns gives unmatched clusters zero contribution.

To characterize class information across all 16 donor regions while accounting for imbalance, we separately report optimal many-to-one balanced accuracy. Each cluster is assigned to the class maximizing its count divided by that class’s total population. This maps Clusters 0, 3, 6, 8, 14, and 15 to Class 1 and gives:

Ground truthAssigned Class 0Assigned Class 1
Class 021,74710,190
Class 11,8402,391

The resulting balanced accuracy is

0.5(21747/31937+2391/4231)=0.6230,0.5(21747/31937 + 2391/4231) = 0.6230,

compared with 0.5000 for a constant-class assignment. The attack constructs its class tendencies using only the stated auxiliary-label budget.

3. Why these donor regions remain useful for CCVS

Class 1 constitutes 11.7% overall, but its prevalence varies from 4.6% in Cluster 1 to 34.8% in Cluster 8, approximately a 7.5-fold difference. Cluster 15 contains 27.1% Class 1 samples. These differences reveal class-related structure even though Class 0 remains the majority in every cluster.

CCVS uses this partial structure to guide donor selection and cross-view reassignment. Perfect class recovery is unnecessary when distinct donor regions already provide different class tendencies. Retaining multiple regions also preserves subpopulation distinctions that would disappear if the partition were collapsed into two classes.

The clustering evaluation establishes the available donor signals, and the complete Bank rerun verifies their downstream attack effect on correctly aligned test data. This connects the corrected evaluation to the reported effectiveness of CCVS.

The revised Table 1 removes the outdated Bank entry, Section 6.2 summarizes its separate evaluation, and Appendix I.1, Table 22 provides the contingency table and metric definitions. We will also include the rectangular Hungarian calculation explicitly in Appendix I.1 to make the requested convention and numerical result directly reproducible.

AuthorsOpenReview ↗

Responses to Reviewer 2BNE (Part 2)

Q2 (Part 1/2). Please evaluate all methods with matched Phase-I and VFL seeds, report uncertainty and detection precision/recall/FPR, and clarify independent validation and threshold selection.

We thank the reviewer for emphasizing these controls. We expanded the evaluation with 264 controlled mapping/donor runs, a five-seed Mushroom donor study, reconstruction-defense comparisons, and three-seed honest-view and reference-only controls. These experiments directly test whether CCVS’s advantage persists when its components and training conditions are controlled. We also clarify which sources of uncertainty the reported results cover.

1. Matched controls isolate the mapping and donor-selection contributions.

The factorial study crosses eight destination constructions with four donor rules on MNIST and Fashion-MNIST and three on HAR, using three VFL seeds per configuration. Within each donor-rule comparison, the Phase-I artifacts, confidence filtering, coverage, victim order, architecture, and training schedule are fixed.

With hardest-negative donors, mean clean-test accuracy is:

DatasetMaximum-distance derangementAverage random derangementRound-robin
MNIST41.0648.4345.47
Fashion-MNIST30.6546.3444.90
UCI-HAR11.7435.9620.60

The random column averages five random derangements, each evaluated over three training seeds. Maximum-distance derangement improves over the average random mapping in all 11 dataset–donor conditions, including random-donor and diversity-capped conditions. The result therefore extends beyond the original single-seed strategy comparison.

The implemented top-k pooling construction is evaluated separately. Under hardest-negative selection, it achieves 31.22% on MNIST and 25.30% on Fashion-MNIST, the lowest accuracies among the eight destination constructions tested on those datasets.

Mushroom supplies a complementary control because its two clusters permit only one derangement. Holding that mapping and training configuration fixed gives:

Donor ruleAccuracy (%)Unique donorsMaximum reuse
Random, full cluster95.03 ± 1.606,5062
Random, confidence core94.50 ± 1.105,0922
Hardest negative, diversity-capped79.80 ± 10.155,0922
Hardest negative, unrestricted reuse32.78 ± 2.60691,076

These five-seed results show a paired 62.25 ± 1.19-point reduction relative to random full-cluster donors. Hard-negative selection also improves attack strength when unique-donor count and maximum reuse are held equal.

Section 6.5 and Appendix B, Tables 7–8 report these controls. They support distinct contributions from distance-guided destination construction, donor selection, and donor concentration.

2. The defense comparison now includes broader recovery alternatives.

Under matched trusted-reference access and fixed poisoned views, we evaluated both an original-procedure VFLIP port and a training-time adaptation. RGAR achieves higher observed mean accuracy than both variants on all five tested datasets:

DatasetVFLIP-original (%)VFLIP-adapted (%)RGAR (%)
MNIST10.53 ± 0.7344.84 ± 0.8183.96 ± 0.94
Fashion-MNIST11.90 ± 3.1372.82 ± 1.3873.72 ± 0.55
UCI-HAR15.86 ± 0.0017.37 ± 5.7688.23 ± 1.43
UCI-Mushroom69.67 ± 8.6242.00 ± 3.2796.54 ± 2.88
UCI-Bank11.71 ± 0.0146.61 ± 36.9381.34 ± 3.50

VFLIP uses three seeds; RGAR uses three on MNIST/Fashion-MNIST and five on the tabular datasets. We state these counts explicitly. Appendix H.3, Table 20 additionally reports B-only and R-only training using three seeds.

These controls support the revised, conditional recovery claim. Honest-view and reference-only training are competitive on several datasets, while RGAR offers benefits on HAR and class-sensitive Bank metrics. Section 6.4 and Appendix H discuss these comparisons and avoid interpreting RGAR as uniformly superior to retraining.

AuthorsOpenReview ↗

Responses to Reviewer 2BNE (Part 3)

Q2 (Part 2/2). Please evaluate all methods with matched Phase-I and VFL seeds, report uncertainty and detection precision/recall/FPR, and clarify independent validation and threshold selection.

3. Additional controls strengthen the comparison, and the revision makes their statistical scope explicit.

We appreciate the reviewer’s emphasis on separating method effects from randomness and tuning. The additional studies address this directly through 264 controlled mapping/donor runs and a five-seed fixed-mapping Mushroom experiment.

For these comparisons, methods share the same Phase-I artifacts, coverage, victim order, architecture, and training schedule. Reusing the partition provides a common input for isolating the attack components. The error bars measure VFL training variability conditional on that partition; variation across independently fitted Phase-I partitions remains an extension. Section 6.1 and the “Sources of variation” discussion state this distinction, and original single-seed baseline entries remain marked.

The matched experiments provide quantitative evidence beyond the original baseline rankings. Maximum-distance derangement improves over average random mappings in all 11 dataset–donor conditions. With hardest-negative donors, the three-seed mean accuracies are:

DatasetMaximum-distance derangementAverage random derangementReduction (pp)
MNIST41.0648.437.37
Fashion-MNIST30.6546.3415.69
UCI-HAR11.7435.9624.22

The random column averages five random derangements, each evaluated over three training seeds. The mapping advantage also persists under diversity-capped donor selection, giving reductions of 6.61, 5.64, and 36.01 points, respectively. HAR uses no confidence filtering, so its comparison additionally establishes a mapping effect without that component.

On Mushroom, where the two-cluster mapping is identical for every strategy, random full-cluster donors yield 95.03 ± 1.60%, compared with 32.78 ± 2.60% for CCVS’s unrestricted hardest-negative donors. The paired reduction is 62.25 ± 1.19 points over five seeds. Controlling unique-donor count and maximum reuse, hardest-negative selection still reduces accuracy from 94.50 ± 1.10% to 79.80 ± 10.15%. Section 6.5 and Appendix B, Tables 7–8 provide these component controls.

The expanded defense evaluation also tests meaningful recovery alternatives. Under matched trusted-reference access, RGAR achieves higher observed mean accuracy than both evaluated VFLIP variants on all five datasets. The additional three-seed controls show that, on HAR, RGAR reaches 89.15 ± 0.67%, compared with 81.49 ± 0.39% for B-only retraining, a 7.66-point advantage. In the separately reported matched Bank evaluation, RGAR achieves 81.46% balanced accuracy and 89.13% AUC, compared with 50.59% and 51.16% for B-only training. These comparisons establish specific predictive benefits while the R-only and B-only results identify settings where simpler alternatives are competitive (Section 6.4 and Appendix H).

Threshold selection and detection metrics are now distinguished from predictive recovery. Hyperparameters were selected using training diagnostics; a shared independent-validation tuning protocol was not used. The VFLIP adaptation calibrates its threshold at the 95th percentile of authenticated-reference scores, which is reference calibration rather than independent validation.

The gate audit further establishes that the original baselines suppress contributions during training but feed unmodified embeddings to the head at inference. Appendix H.4 documents this protocol, and the revised interpretation recognizes that inference handling contributes to baseline accuracy. Detection or suspicion rates alone cannot establish successful recovery. A unified clean FPR and precision/recall comparison remains incomplete, so our comparative conclusions rely on the measured predictive outcomes and controlled component experiments.

We have accordingly rescoped the categorical claims highlighted by the reviewer. The revised account emphasizes substantial correspondence-poisoning damage, independently measured contributions from mapping and donor selection, and conditional benefits of reference-guided recovery. The additional evidence makes these contributions more directly assessable, while the manuscript explicitly identifies the remaining Phase-I variability, tuning, and detection-metric boundaries.

We hope the stronger controls and more precise interpretation address the reviewer’s concern and strengthen confidence in the contributions supported by these experiments.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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