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Paper summary
This paper proposes STFSFormer, a spiking Transformer for EEG emotion recognition. It combines HELIF neurons with differential drive and refractory feedback, a multi-decay-branch encoder, and local spiking attention, and selects the attention multiplication order based on matrix dimensions. The authors conduct within-subject evaluation, cross-subject evaluation, and component ablations on SEED, SEED-V, and DREAMER, and report model complexity and FPGA synthesis energy estimates.
Critical strengths
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The paper considers both the representation ability for time-varying EEG and inference cost, and combines neuron dynamics with local attention into a fairly complete model design.
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The authors first split complete trials and then generate non-overlapping windows, avoiding windows from the same trial entering different data sets; the LOSO evaluation also clearly isolates the test subject and all their sessions.
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Besides recognition performance, it also includes component ablations, hyperparameter sensitivity, firing rate, and complexity analysis. The HELIF and attention replacement experiments show that both components contribute under the current configuration.
Critical weaknesses
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The main text says it uses window-level Accuracy and Macro-F1, but in Table 1, Brain-GRL on DREAMER-Arousal reports 85.27% and 87.05% for the two metrics. For the same set of binary predictions, same sample weights, and a consistent aggregation method, standard Macro-F1 should not exceed Accuracy. Similar cases appear in other baselines, so the metric definitions, aggregation method, or table values need clarification.
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Choosing between two equivalent multiplication orders based on dimension is essentially a deterministic computation-order optimization. The default configuration and the reported block-length sweep both satisfy , so the same branch is always used, and there is no empirical validation of the benefit of switching branches. The existing ablations are also not enough to separate the contributions of the local window, spike representation, and multiplication-order selection.
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SEED LOSO accuracy improves over Spikformer by only 0.59 percentage points, and some DREAMER metrics are lower than EEGNet. The paper does not report per-subject paired analysis or confidence intervals, so it is impossible to tell whether these gains are stable.
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The HELIF ablation removes both the differential path and refractory feedback at the same time, so the contribution of each part cannot be determined; the lack of frequency-response and noise-robustness analysis also makes it hard to tell whether the enhanced variations correspond to useful EEG information. In addition, there remains a gap between offline zero-phase filtering and whole-trial normalization and continuous online deployment.
Questions for authors
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In Table 1, how are Accuracy and Macro-F1 aggregated across windows, subjects, and random seeds? Can you provide the evaluation code and corresponding confusion matrices to explain the cases where binary Macro-F1 is higher than Accuracy?
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Can you add attention controls under the same local window, similar parameter count, and comparable compute budget, and separately measure the actual latency and memory cost of fixed token-first, fixed feature-first, and the dimension-selection strategy?
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Can you report per-subject LOSO results, paired differences, and confidence intervals, and add stronger EEG emotion recognition baselines to verify the generalization advantage?
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What device, frequency, numerical precision, and power analysis flow are used for the FPGA estimates? Which memory and data movement costs are included in the energy accounting, and do all baselines use comparable implementation optimizations?
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Can you separately ablate differential drive and refractory feedback, and validate performance under causal filtering, online normalization, and noise perturbation, to support the neuron mechanism and continuous deployment motivation?
We thank the reviewer for recognizing the trial-before-window split, strict subject isolation, and the combined evaluation of representation and efficiency. We address the reporting inconsistency first, followed by the attention controls and online preprocessing.
Corrected Table 1 and metric aggregation
We thank the reviewer for identifying the inconsistency between Accuracy and Macro-F1. The cause was a logging error in our result-saving script: during an earlier hyperparameter-tuning run, the script wrote the Accuracy value into the Macro-F1 field, and these stale entries were carried into Table 1. We have fixed the script, regenerated the affected entries from the correct evaluation logs, and updated the PDF. The corrected values are computed from the same pooled predictions, so no experimental results or conclusions change.
For each seed, we pool the test windows from all subjects and compute Accuracy and Macro-F1 once from that pooled prediction set, without trial voting or an equal-subject average. Accuracy is the fraction of correctly classified windows, and Macro-F1 is the unweighted mean of class-wise F1 scores. Table 1 reports the mean and standard deviation of the five seed-level values. This aggregate is window-weighted: subjects with more test windows contribute more observations.
Attention controls and measured execution cost
We compare fixed token-first, fixed feature-first, and dimension selection using the same checkpoint, inputs, and batch. The supplementary measurements use one A10 with batch=128, T′=100, L=3, and dh=64:
The isolated token-first and feature-first cores take 0.145 and 1.589 ms, respectively. At the equal-core-MAC boundary L=dh=64, the two orders have similar core latency and both use 32 MiB. These measurements show that dimension selection primarily reduces core computation and memory requirements, while complete-model forward latency remains similar in the tested configuration. The benefit is an execution-cost optimization, rather than an accuracy improvement from reordering mathematically equivalent products.
Separate neuron mechanisms and online preprocessing
The additional ablations separately remove differential drive and refractory feedback, reducing average accuracy by approximately 3.22 and 2.35 percentage points, respectively. These controls address the contribution of each mechanism beyond the original combined HELIF/LIF replacement.
The original pipeline uses offline zero-phase filtering, within-trial normalization, and state resets at each EEG window. Replacing only the zero-phase filter with a causal filter reduces accuracy by approximately 0.95 percentage points. Introducing 1-second EMA online normalization gives a drop of approximately 13.72 points. Lengthening the EMA time constant to 10 seconds improves accuracy by approximately 4.08 points relative to the 1-second configuration. These results identify online normalization as an important remaining gap between the offline evaluation and continuous deployment.
On trial-isolated SEED, 20-45 Hz narrow-band noise at 0 dB reduces accuracy by approximately 0.30 percentage points, while EMG-like bursts cause a drop of 1.29 points. EOG-like and step artifacts produce larger drops of 5.93 and 8.67 points, respectively. These results indicate greater sensitivity to the tested EOG-like and transient disturbances than to the narrow-band noise condition. If accepted, we will incorporate these controls and distinguish efficient model inference from a validated continuous EEG acquisition and preprocessing system.
The FPGA device, clock configuration, numerical precision, power-analysis flow, and memory-accounting scope are addressed in the shared FPGA response under General Response.