- Rating
- 3(+1)
- Confidence
- 2
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 1
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Paper summary
The paper argues that in Byzantine FRL, the choice of which trajectory states a malicious client uses to build its poisoned update ("when") matters separately from how the update is constructed ("how"). V-BSA works in four steps:
- It computes a targeted-action log-likelihood gradient only on states whose normalized policy entropy exceeds .
- It adds this gradient to the benign update.
- It rescales the result to the benign norm.
- It clips coordinate-wise to an EMA box around the client's past updates. A binary-action result (Thm. 1) shows that entropy and Fisher trace rank states identically under a centered-isotropy assumption. Experiments use CartPole, Acrobot and LunarLander with , , against FedAvg, Median, Trimmed Mean and FedPG-BR, with and without a 5-group voting ensemble. They report:
- degradation in most settings;
- a budget-controlled comparison against random state selection (LunarLander × FedPG-BR, 1.89× mean);
- two temporal defenses that reduce but do not remove the effect.
Critical strengths
1. The question is a good one, and the core experiment design is the right one. Holding the update construction fixed and varying only which states feed the steering loss is the correct way to test the claim. The authors also report the d0 reversal in Fig. 6 rather than hiding it, which I appreciated. If the effect survives more seeds and the confound controls below, it is a useful observation for people designing or attacking FRL aggregators.
2. The paper is candid about its limits, and the theory is correct as stated. The authors report where the attack fails: the non-ensemble FedAvg sign reversal, CartPole, and continuous control. They give a counterexample against their own entropy proxy (A.5). The derivations I checked are correct (Eqs. 11, 14, 22, 25–29, 35–38, 45–54). The step-level telemetry in D.1 (split-vote and tie rates under attack) is a concrete look at how voting ensembles break, and I found it more informative than the aggregate table.
Critical weaknesses
1. The evidence that "when" is an independent attack dimension is thin and partly self-contradictory.
(a) "When" is really part of "how." V-BSA never intervenes in a trajectory. Rollouts are nominal (Sec. 4.1; Alg. 1, line 2), and {when} only decides which already-collected samples enter {steer}. That is a data-selection step inside update construction, so I don't see how it is orthogonal to "how." It also means the "intervention budget" costs a Byzantine client nothing, since it fabricates the whole update anyway. "A fraction of the interventions used by dense poisoning" is presented as an advantage, but no attacker in this threat model faces that constraint. No budget is actually imposed either: is endogenous through .
(b) The schedule comparison is confounded with steering strength. {steer} is a mean over {i,when}, and v = g + d is then norm-matched to . Changing the selected set therefore changes , the direction of after rescaling, and how much the box clips. Without , , the fraction of clipped coordinates, and FedPG-BR acceptance rates for each schedule, the dense/random/entropy gaps can't be attributed to which states were picked.
(c) The statistics are weak, and the numbers disagree with each other.
- The headline comparison rests on three runs. In Fig. 6, random selection beats entropy gating on d0 (197.86 vs 148.17), and the 1.89× mean is driven by d2 alone.
- The pilot (Fig. 2) reports budget-matched random on d0 as 91.99. Fig. 6 reports budget-matched random on the same d0 as 197.86. The motivating comparison flips on the same dynamics.
- Fig. 2 also silently mixes medians over three dynamics (dense 36.65, random 50.01, entropy 148.17) with a single d0 run (91.99).
- Every is one terminal evaluation (10 episodes at round 261) against one clean anchor. The paper itself attributes negative values to "cross-run anchor variance" (Sec. 5.3).
- The same configuration gives different numbers in two places. Table 4 reports FedPG-BR d2 at 245.4 / −125.2, while the D.1 telemetry for that configuration reports 242.50 / −66.71. To support the "orthogonal dimension" claim, I would want a sweep, random selection at several budgets, and at least 5 seeds with confidence intervals.
2. The evaluation cannot support "substantial degradation against robust aggregators and ensemble defenses."
(a) There are no baseline attacks. Table 1 compares V-BSA only against clean training. All of these apply directly:
- ALIE, whose box is essentially Eq. 5;
- Min-Max / Min-Sum;
- the Normalized attack from Fang et al. (2025b);
- the attacks evaluated in the FedPG-BR paper. D.1 asserts that ensemble FedPG-BR filters the Normalized attack, but no such experiment appears in the paper.
(b) The setup favors the attacker.
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Every ensemble group has 2/6 Byzantine clients, so all five voters are compromised. Partition-based ensembles rely on the attacker not reaching most groups. D.1's own argument ("perturbing a minority of subgroups fails to alter the vote") does not describe the setting actually tested.
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Trimmed Mean uses against 2 attackers per group, and against 10 attackers in the non-ensemble setting. It is under-trimmed in both cases.
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The vote tie-breaking rule is never stated. Under attack, 38% of decisions are top-two ties. If ties go to the lowest index (default argmax), they resolve to action 0, which is also a target action. (c) The pattern in Table 1 is unexplained.
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The attack is weakest against plain FedAvg: negative on all three non-ensemble LunarLander dynamics, and near zero on CartPole.
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It is strongest against Median, reaching 434 on non-ensemble LunarLander. An attack that robust aggregators amplify relative to averaging suggests may be measuring the fragility of order statistics to any consistent bias. Baselines and a projection-only ablation would settle this. In addition, the clean Acrobot curves (Figs. 9, 11) swing by 150–300 across rounds, so terminal-round there largely reflects when training stopped.
Questions for authors
- What exactly are d0, d1, d2: environment variants or random seeds? Sec. 5.1 says "seeds," C.1 says "dynamic realizations," and A.6 says "dynamics seeds." How many clean runs define each anchor, and what is its run-to-run standard deviation?
- Which CartPole target rule produced Table 1? Sec. 5.1 says all attackers share target 0. App. A.6 says the main configuration is , with the shared target as a pre-registered variant. Table 1's ensemble FedPG-BR value (110.63) equals the mean of the fixed-target variant {139.5, 0, 192.4}, not the modulo run {164.9, 0, 0}. Separately: ensemble groups aggregate independently, and both attackers in a group share a target. Where, then, do opposing targets ever meet in one order statistic, as Eq. 51 and the CartPole paragraph of Sec. 5.2 assume?
- How are target actions assigned in the non-ensemble runs? Note that which vanishes at uniform for any , and the gate selects near-uniform states. If the 10 attackers target {0, 1, 2, 3, 0}, their steering largely cancels under averaging. Could this explain the FedAvg sign reversal? If so, the cancellation boundary is not binary-specific.
- Could you add the following ablations?
- Projection only ().
- Steering on low-entropy states. Lin et al. (2017), whom you cite, time their attack when action preference is strongest, so this contrast deserves discussion.
- A Gini-impurity gate. Under your own centered-isotropy assumption, Eq. 22 shows exactly for any . It is equally cheap and avoids the A.5 mis-ranking. Why use Shannon entropy?
- Does centered isotropy with state-independent hold even approximately for your MLP? The final linear layer alone contributes to , which varies with hidden activation norms. Plotting across visited states would test this directly.
- Is the ensemble damage mainly vote fragmentation caused by heterogeneous per-group targets? In the D.1 example, the four non-gated groups are confident (), and the votes [0, 1, 2, 2, 0] match for four of five groups if groups are 0-indexed. A run with a shared target across groups and random tie-breaking would separate this effect from the "when" effect.
- How do results change with random group assignment, and with Trimmed Mean using the number of Byzantine clients per pool?
5 comments
Thank you for the thorough response. The low-entropy control ( vs. ), the projection-only ablation, and the 8-seed paired comparison (8/8 wins, Wilcoxon ) address my main concern that the gap could come from steering strength rather than state selection. The tie-breaking, shared-target and trimming results also address W2(b) and Q6–Q7, and my cancellation hypothesis (Q3) was wrong.
Remaining points:
The 8-seed results cover only LunarLander × Ensemble FedPG-BR. The rest of Table 1 is still three runs, and clean runs alone vary substantially (208.4 ± 35.2). Please report uncertainty in Table 1 or scope the claims. Per Q5, centered isotropy fails in the LunarLander gated regime (–), so Thm. 1 motivates rather than explains the main result. The paper should say so. Since only reduces backward compute (W1a), the "intervention budget" framing should be revised. The τ sweep requested under W1(c) is still missing.
Two corrections: the 284.87 cited in Q7 is non-ensemble Acrobot in Table 1 (LunarLander is 434.35), and the Ensemble FedAvg in W2(b) doesn't match Table 1 (79.90). Which configuration is it from?
I am keeping my rating at weak reject, mainly because the multi-seed evidence covers a single configuration.
Follow-up to Reviewer 9Y3m: Existing τ-Sweep Results, Numerical Clarifications, and Manuscript Framing Updates
Thank you for your follow-up and for noting that the low-entropy control, projection-only ablation, and 8-seed paired comparison address your main concern regarding steering strength, while the tie-breaking, shared-target, and trimming audits address the corresponding questions. Below we point to the existing -sweep results in Appendix D.4, clarify the two numerical points, and summarize the updates in the revised PDF.
1. Existing Sweep (Appendix D.4, Table 7, p. 28)
We apologize if this result was not sufficiently visible in our previous response. The requested sensitivity analysis is included in Appendix D.4 (Table 7, p. 28) across five seeds (s0–s4, clean anchor 208.2, LunarLander-v2 Ensemble FedPG-BR):
- : ,
- : ,
- (default): ,
- : , Compared with dense poisoning ( on s0–s4; on s0–s7), high degradation holds across before vanishing at .
2. Clarifications on the Two Numerical Points
- Q7 Median value: Thank you for catching that typo—284.87 is indeed non-ensemble Coordinate-wise Median on Acrobot in Table 1, whereas the corresponding LunarLander value is 434.35 (further reinforcing the vulnerability of median aggregation on LunarLander).
- Ensemble FedAvg (65.6 to 99.7 vs. 79.90): Both metrics report terminal degradation for the same Ensemble FedAvg configuration (default targets, d0–d2), differing only in evaluation protocol: 79.90 is Table 1's logged 10-episode evaluation mean, whereas 65.6 to 99.7 is the offline 50-episode tie-breaking re-evaluation of the saved round-261 checkpoints pooled over d0–d2 (65.6 under deterministic lowest-index argmax vs. 99.7 under uniform random tie-breaking, with a 47.0% tie rate; clarified in Appendix D.4, p. 28).
3. Manuscript Framing & Table 1 Updates
We have updated the revised PDF to address each of your remaining points:
- Table 1 uncertainty & scope (p. 7): We added the 3-realization dispersion (SD across d0–d2) directly to Table 1 and explicitly scoped our multi-seed statistical inference to the primary LunarLander Ensemble FedPG-BR benchmark (Table 6, p. 27), framing the 3-realization grid as cross-environment and cross-aggregator trends.
- Role of Theorem 1 (Sections 4.2 & 5.2, pp. 5, 8): We revised the text to state that Theorem 1 motivates the entropy gating proxy under idealized binary centered isotropy rather than explaining multi-action MLP performance where state-dependent Jacobian norms vary.
- Terminology ("intervention budget"): Throughout the paper, we replaced "intervention budget" with "steering-sample fraction" (or "rate-matched") to accurately reflect that measures the fraction of nominal rollout states backpropagated through the steering loss.
Response to Reviewer 9Y3m: 8-Seed Controls, Telemetry Audits, Mechanism Ablations, and Numerical Reconciliations
We thank Reviewer 9Y3m for the thorough audit, verifying our proofs, and highlighting App. D.1. We reconciled Fig. 2 and Table 1 and added 8-seed baselines, ablations, and telemetry in App. D.4 (Tables 6–8).
1. Weaknesses 1(a)–(c): Decomposition & Statistics
2. Weaknesses 2(a)–(c): Baselines & Setup
3. Questions 1–7