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Paper summary
This paper questions why spiking state-space models for event-based vision are so large, and locates the cost at the interface joining the spiking front end to the state-space backbone rather than in the model's capacity. Profiling a released Mamba-Spike model, the authors find that nearly all of its parameters sit in a single projection layer that flattens the front-end feature map before the scan, and that this layer's size grows quadratically with sensor resolution. Their method, RIPE-MambaSpike, pools every spiking stage to a common grid and projects at a fixed width, which removes the dependence of the deployed parameter count on input resolution. The remaining components follow the same principle of paying cost during training and recovering it at inference. The spiking stages train as several parallel convolution branches and fuse into a single kernel once training ends. A per-channel first-order temporal filter, carrying one learnable scalar per channel, precedes each convolution. The attention module draws its queries and keys from the membrane potential and its values from the previous spike tensor, and uses a strictly positive feature map so that the output remains inside the convex hull of the value vectors. The authors support these claims with parameter counts obtained by direct instantiation across input resolutions, a controlled swap of the interface inside the released baseline with all other components held fixed, a component ablation, and five-seed results on five event benchmarks. They report a Pareto-optimal position among published methods with reported parameter counts on three of those benchmarks and the strongest spiking result on the largest benchmark they evaluate, while stating that the model does not lead on accuracy on any of them.
Critical strengths
- The paper makes its central diagnosis causal rather than correlational, and does so with an unusually clean control. The claim that the interface rather than the capacity determines the parameter cost is supported by an intervention that replaces only the projection joining the front end to the scan, while the spiking front end, the spike-to-activation conversion, the Mamba blocks, the normalization and the classifier are imported unmodified from the released baseline. The intervention removes roughly 7.6$\times$ of the model while gaining 4.40 percentage points on the same protocol, and the diagnosed layer is shown by direct instantiation to hold 92.6% of parameters at and 97.4% at . For the single model profiled, this establishes the diagnosis far more convincingly than a parameter table alone would.
- The reported numbers are checkable, and the paper is explicit about the limits of its efficiency claim. The deployed parameter counts can be reproduced without downloading any data, which makes the central quantity easy to verify. The energy discussion is confined to an estimate of accumulate-only cost for the layers where the binary-operand property actually holds. The rest of the network is left uncosted rather than folded into the headline, and the paper states outright that it makes no energy, operation-count or latency claim on ordinary runtimes. It also notes that resolution-independence applies to weight storage alone. Activation memory still grows with resolution, and at the larger batch sizes tested the model can end up slower and larger in total memory than the baseline.
Critical weaknesses
- The central claim is stated at the level of a class of models, while the evidence base is a single profiled architecture and an intervention performed on that same architecture. The abstract and the introduction assert that the parameter cost of Spiking-Mamba hybrids is a property of the interface rather than of capacity, and the conclusion generalizes this into a practical recommendation for the field ("competitive event-based recognition does not require resolution-dependent parameter growth"). The measurement behind it profiles one released model, and the causal evidence is a swap performed inside that same model. The paper does acknowledge the limitation once, in the discussion ("the diagnosis rests on one released model, so we scope it to flatten-then-project bridges"), but that qualification does not appear in the title, the abstract, or the contribution list, where the general framing remains. The consequence is that a reader cannot determine whether the paper has identified a property of this model class or a property of one particular implementation, and the recommendation offered to the field is supported only for the bridge family the authors have already selected. This is consequential because it is the paper's central claim, not a supporting detail.
- The comparative claims are made on a cross-protocol basis, and the controlled comparison is against a reproduction that the paper itself could not reconcile with the published baseline. The reported Pareto-optimality on three benchmarks and the 8.80-point lead on DailyDVS-200 are statements about the published literature, yet the entries they are measured against are quoted from other papers trained under different protocols and augmentation, which the paper marks but does not correct for. Where a controlled comparison does exist, it is against the authors' own reproduction of the released baseline: on CIFAR10-DVS their model reaches 81.40, below the published baseline figure of 92.50 and above their own reproductions of the released code at 65.30 and 48.90. The consequence is that the paper's competitive position depends on which reference a reader adopts, and under the published figure the model is not more accurate, only smaller. Combined with the fact that the model leads on accuracy on no benchmark, the contribution is a parameter-efficiency frontier position rather than an advance that a reader can rely on without choosing a protocol.
Questions for authors
- The appendix specifies a parameter-matched sigmoid-gated attention as the natural alternative to the proposed bounded attention and states that it was not trained. Would training that control be feasible, so that the module's claimed advantage can be measured rather than argued?
- The presented diagnosis as a property of spiking state-space hybrids, but it is measured on one model. Could the authors add the parameter share held by the front-end-to-scan interface for a second released hybrid that uses a different kind of bridge, for instance a window-based or token-pruned coupling? A second data point would show whether the interface dominates across the family or only in flatten-then-project designs, which is what I need in order to judge how far the finding generalizes.
- The paper states that the deployed model scans every token the bridge produces, and Table 13 lists the full grid as the deployed configuration; the released per-benchmark defaults, however, set the retained-token budget below the full grid for three of the five benchmarks. Could you confirm which setting produced the reported numbers, in particular for CIFAR10-DVS and N-Caltech101, where the budget sweep of Table 13 is not reported? Table 13 establishes the budget is accuracy-neutral on DVS-Gesture, so this is a question of reproducing the stated configuration rather than of the reported accuracy.
4 comments
I thank the authors for a substantial rebuttal. The scope revision and the second profile answer my questions of fact. My reservation is now about the size of what remains.
The second profile shows that at the resolutions this paper evaluates, a hybrid whose interface is a per-patch positional table spends 13.9% and 32.0% of its parameters at the interface, and crosses 50% only near 330². SpikMamba is a fixed-resolution model, so those instantiations demonstrate the mechanism rather than an operating regime in which the cost binds. What remains is a standard remedy for a known inefficiency, applied to one released baseline and packaged with three components whose ablations contribute between one and three points each. The model leads on no benchmark, and the 41× comparison is drawn against a reproduction that sits 27 points below the published baseline.
Response to Reviewer oekq's Follow-up
We thank the reviewer for engaging with the rebuttal and are glad the questions of fact are resolved. We respond briefly to the remaining points.
1. Where the cost binds. We agree that SpikMamba's profile shows the mechanism. The operating regime where the cost binds is the native resolution of current event sensors, which is where a deployed model would run. Using the per-pixel slopes measured by instantiation (exact up to 640²; now in App. C.1):
| Sensor (native) | Mamba-Spike interface | SpikMamba interface | Ours (total) |
|---|---|---|---|
| DAVIS346 (346×260) | 184 M (98.5%) | 1.46 M (45%) | 0.870 M |
| DVXplorer / Prophesee Gen3 (640×480) | 629 M (99.6%) | 4.9 M (74%) | 0.870 M |
| Prophesee IMX636 (1280×720) | 1.89 B (99.9%) | 14.8 M (89%) | 0.870 M |
For flatten-then-project designs the cost already binds at every resolution we evaluate (92.6% at 128², 97.4% at 224²). At sensor resolution it binds for both bridge families. A fixed-width bridge removes it at all of them.
2. A standard remedy for a known inefficiency. We agree that pooling to a fixed width is standard, and we do not claim it as new. What was not established is that this layer is the binding cost of the model family: the official Mamba-Spike implementation places 92.6% of its parameters there, and replacing only that layer gives 7.6× fewer parameters and +4.40 pp under the same protocol. MR-S3A also goes beyond the standard remedy. The textbook version (pool all stages, concatenate, one shared projection) loses 1.49 pp to it at a matched parameter count (Welch , App. C.15), and MR-S3A adds 2.96 pp over a stage-3 projection even with DS-MPA, RepConv and TDM all removed (). The gain is free at deployment, since MR-S3A folds exactly into one convolution at inference.
3. Component effects of one to three points. On N-Caltech101, where the five-seed standard deviation is 0.18 pp, these effects are 8–18 seed standard deviations. The other components also beat their natural alternatives at a matched parameter count: a sigmoid kernel in place of DS-MPA loses 1.57 pp and a ConvGRU front-end 3.15 pp (Welch ).
4. The 41× comparison and the published 92.50. The 41× is a parameter ratio measured on Mamba-Spike's official implementation; it does not depend on accuracy. Mamba-Spike's paper attributes its published figures to a larger configuration whose size it does not state, so against the published model the ratio can only grow.
Where the published accuracy is reproducible, we exceed it. On DVS-Gesture our 98.48% (98.18 ± 0.31 over five seeds) is above Mamba-Spike's published 97.80%, and its official code reaches 95.83% under our protocol.
CIFAR10-DVS is the exception. The official code gives 48.90 under its own protocol and 65.30 under ours. The published 92.50 would exceed the best published spiking result we know (QKFormer, 84.00) by 8.5 pp, and the baselines in that paper also sit above those methods' own published values, which points to a different protocol (App. C.3). We therefore make no accuracy claim against 92.50; there our claim is parameter efficiency under a controlled comparison.
We agree the contribution is accuracy per parameter rather than absolute accuracy. On that axis the model is Pareto-optimal on three benchmarks and gives the best spiking result on DailyDVS-200, by 8.80 pp.
We thank the reviewer again for the constructive discussion and would be glad to clarify anything further, we would be grateful if the reviewer could please consider revisiting the evaluation in light of the revision.
Feedback Request to Reviewer oekq
We thank the reviewer again for the insightful review. Please let us know if you have any further queries; we look forward to a fruitful discussion.
Response to Reviewer oekq
We thank the reviewer for a careful review and for recognizing the interface swap as a causal control.
W1 / Q2: one profiled model, class-level claim. We agree that the scope belonged in the abstract and thesis, not only in the Discussion. As requested, we profiled a second Spiking–Mamba hybrid with public code and a different bridge. SpikMamba (Chen et al., 2024) tokenizes per 4×4 patch at a fixed width with learned positional embeddings, without a global flatten-and-project. Instantiated at 34²–640² (script in the supplement):
The second model confirms and refines the diagnosis. In both hybrids, the interface is the only resolution-dependent component (SpikMamba's sequence stack is a constant 1.74 M), so in both it eventually dominates. The bridge design sets only the slope:
The general rule: resolution-dependent parameters come from trainable tensors indexed by the spatial grid (a flattened dense projection, a learned positional table). Our bridge has none: shared projections and a coordinate-based positional encoding, so its slope is zero.
Revisions. The abstract, thesis and contributions are now scoped to flatten-then-project bridges; the introduction, Discussion and Table 7 report the second profile.
W2: cross-protocol comparisons. The primary comparison is controlled and reproducible. The supplement ships Mamba-Spike's official implementation (https://github.com/ecnu-cross-innovation-lab/mamba-spike) with two scripts: its own protocol (‡) and the protocol identical to ours (†). Parameters come from its default configuration:
Under either protocol we are more accurate (also on five-seed means: 81.28 / 98.18 / 99.55) and up to 41× smaller. Our protocol also raises the baseline by 16.4 pp on CIFAR10-DVS. The interface swap (App. C.2) isolates the cause: changing only input_proj gives 7.6× fewer parameters and +4.40 pp.
The published 92.50 is the exception: its configuration and parameter count are not stated, so we could not reconcile it with the official code (App. C.3). Against it we are smaller, not more accurate, and §6 now says so. Against the literature we claim frontier position, not accuracy dominance (§6).
Q1: sigmoid-gated control. Yes, and the result supports the design. We trained the parameter-matched control A=σ(QK⊤/C)V/N on N-Caltech101. It shares DS-MPA's WQ,WK,WV and γ, with 1/N as its normaliser, so the arms differ only in the kernel:
A sigmoid gate recovers only half of DS-MPA's gain over no attention. Both outputs are bounded (the control's weights σ/N also sum to ≤1), so the difference lies in DS-MPA's normalized, factorized affinity, which is also cheaper: O(NC2) against O(N2C) for pairwise sigmoid attention. Gradients are descriptive: equal total norm (1.04 vs. 1.03) and a slightly smaller stage-1 share under sigmoid (10.7% vs. 11.8%), consistent with the saturation argument. §4.3 and App. B.5 now report it.
Q3: token budget. Every reported number uses the full grid, with no pruning: all benchmarks, ablations and seeds. The --top-k defaults in our released scripts (128/128/64) are leftovers from an earlier pruned variant. We have set them to 0 (full grid) in the code and README; thank you for catching this.
Why we removed pruning. Table 14 shows pruning leaves accuracy unchanged but buys almost nothing:
So the deployed model scans every token.
We thank the reviewer again for the insightful review. Please let us know if you have any further comments or questions. we look forward to a fruitful discussion.