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Paper summary
The paper presents MARC for continuous hand-pose decoding from surface EMG. Its central design separates observation-driven memory updates from pose-conditioned motion prediction: predicted poses contribute to the output but do not write back into observation memory. MARC also incorporates joint-conditioned encoding and auxiliary motion and geometry objectives. Experiments on emg2pose, MANUS, and NinaPro DB8 report improvements over reproduced TDS+LSTM and EMGFormer-L baselines. Additional feedback controls and state interventions examine pose-error propagation and recovery after observation-memory reset.
Critical strengths
The separation between observation memory and pose prediction is clearly specified. The matched observation-projection control is useful because it distinguishes the source of the added information from added parameter capacity.
The evaluation covers three recording settings and includes both pose and motion diagnostics. The paper also appropriately distinguishes recovery of a model’s unperturbed output from recovery of the ground-truth pose, and acknowledges the opposing effects of feedback under the two interventions.
Critical weaknesses
The experiments do not sufficiently isolate the contribution of the proposed memory organization. MARC changes the encoder, joint representation, prediction pathway, fusion mechanism, and training objectives together. The external baseline comparisons therefore establish the performance of the complete system, but do not establish which components account for its gains. Important missing controls include the same encoder and observation memory without the prediction pathway, a conventional recurrent decoder using the same encoded features, and ablations of the auxiliary objectives. Although the feedback controls partially address the central design choice, they use only one initialization and an 18-epoch budget (Appendix F), whereas the main emg2pose recipe allows up to 64 epochs and early stopping only after 24 epochs. Participant-bootstrap intervals do not establish robustness across training runs. These limitations leave uncertainty about the necessity and reproducibility of the proposed architectural contribution.
The benchmark evidence requires stronger validation. The reproduced EMGFormer-L obtains 14.788° and 15.500° on the unseen-movement and combined emg2pose splits, respectively, whereas its original paper reports 9.28° and 12.25° (EgoEMG, Appendix D.3, Table 11). These results are not necessarily directly comparable: causal restrictions and evaluation-protocol changes may explain the discrepancy. However, the paper does not sufficiently reconcile this substantial gap to establish that the adapted baseline remains competitive. In addition, Appendix C.4 explicitly states that test comparisons informed architecture development. Selecting checkpoints on validation data does not remove potential selection bias from test-informed architectural decisions. The scope of this test-set use and the availability of an untouched final evaluation need clarification.
Missing validation in a real online system. For a method motivated by streaming myoelectric decoding and practical use, I consider evaluation with a live EMG acquisition system necessary. Experiments on prerecorded datasets establish offline decoding accuracy, but do not establish whether the proposed system can maintain accurate and timely tracking during actual operation. The timing results in Appendix G exclude acquisition, host transfer, and visualization, and therefore do not measure end-to-end latency. Likewise, manually perturbing internal states does not establish robustness to disturbances encountered during live sensing. A convincing evaluation should demonstrate sustained online tracking with synchronized reference measurements, report end-to-end latency distributions and missed update deadlines, and compare MARC with the baselines and a simplified variant on identical hardware. Without this evidence, the practical benefit of the additional memory and prediction components remains insufficiently validated.
Questions for authors
Can you report matched controls that remove the prediction pathway or replace the specialized decoder with a conventional recurrent decoder, together with auxiliary-loss ablations? Do the current memory-routing rankings persist across multiple seeds and the main training schedule?
What explains the large EMGFormer-L discrepancy on the unseen-movement and combined splits? Can you separate the effects of causalization, evaluation windows/alignment, and training objectives, and provide the exact baseline configurations?
Which architectural decisions were informed by test comparisons, and which datasets or splits were consulted? Were any final results obtained on evaluation data that had not been used during architecture development?
Can the authors include more recent and methodologically relevant baselines, particularly those incorporating explicit motion prediction or structured memory, under the same causal evaluation protocol?
5 comments
Response to Reviewer EcUc (2/2): component controls and continuous operation
Thank you for requesting complete-training controls, loss ablations and a recent structured-memory comparison. These experiments are complete.
Q1 and Q4. Prediction-free, LSTM and Gated DeltaNet controls.
Each control used three runs and the main stopping rule (minimum 24 epochs, maximum 64, patience 20). Two original write controls continued training; nine other groups began from scratch. LSTM and Gated DeltaNet retain the prediction-free encoder/readout architectures and objective.
On emg2pose, prediction-free has lower mean MAE than the full architecture under the same non-future objective on two of three settings. Relative to prediction-free, the three setting means shift by −0.032 to +0.060° for LSTM and −0.007 to +0.257° for Gated DeltaNet (Table 15, p. 25). Direct state interventions complement these reconstruction controls by isolating what pose feedback changes.
Feedback has a measurable effect on error propagation and memory-loss response.
The following emg2pose results measure deviation from each model's own clean output 200 ms after intervention. Values are pose-write minus MARC, mean ± SD of three paired runs (°): positive favors MARC; negative favors pose-write.
| Intervention | Unseen users | Unseen movements | Users and movements unseen |
|---|---|---|---|
| Stored pose perturbed by ±5° | +1.303 ± 0.280 | +1.259 ± 0.184 | +1.310 ± 0.183 |
| Observation memory alone erased | −1.161 ± 0.230 | −1.761 ± 0.238 | −1.840 ± 0.113 |
All nine paired run–setting differences have the corresponding sign for each intervention. Restricting pose writes reduces the propagation of injected pose errors; allowing writes reduces clean-trajectory deviation after observation-memory loss (Figure 5, p. 7). This comparison measures trajectory deviation, not a recovery-rate advantage.
Q1. Loss ablations identify angular and spatial benefits on unseen movements.
Each row removes one loss while retaining the full inference architecture and other coefficients. emg2pose, unseen movements, mean ± SD over three runs; fingertip distance uses identical generic-hand forward kinematics for predictions and targets:
| Training objective | Angular MAE (°) | Fingertip distance (mm) |
|---|---|---|
| Full MARC | 13.217 ± 0.243 | 29.769 ± 0.676 |
| Without observation loss | 13.389 ± 0.041 | 30.096 ± 0.030 |
| Without displacement loss | 13.551 ± 0.186 | 30.634 ± 0.648 |
| Without future loss | 13.324 ± 0.614 | 30.103 ± 1.693 |
| Without geometry loss | 13.249 ± 0.253 | 30.836 ± 0.755 |
All four removals increase both metric means in this setting; their angular effects elsewhere vary. Across all three settings, removing geometry supervision increases mean fingertip error by 0.85–1.07 mm, with increases in all nine paired comparisons (Figure 6, p. 8; Table 14, p. 24).
Continuous operation and measured execution time.
Across 845 MANUS trials, maintaining state reduces mean error relative to clearing the complete streaming state every five seconds. Angular MAE (°); reduction is reset minus continuous, mean ± SD of three paired runs:
| Test setting | Five-second reset | Continuous | Reduction |
|---|---|---|---|
| Unseen users | 10.850 | 10.684 | 0.166 ± 0.015 |
| Unseen gestures | 14.336 | 14.080 | 0.256 ± 0.065 |
| Users and gestures unseen | 14.837 | 14.813 | 0.024 ± 0.030 |
This is prerecorded replay (Table 21, p. 28). On one RTX 5090, FP32/batch one, MARC's input-transfer-inclusive p95 update time is 5.703 ms, measured with 20 ms input packets and 5.88 s emg2pose context (Table 23, p. 29). Acquisition hardware was unavailable; synchronized live accuracy, sensor-to-display latency and live deadlines remain untested.
We would appreciate your reassessment of the training-budget and missing-control concerns in light of the completed comparisons, consistent spatial-supervision evidence and directly measured feedback effects.
Response to Reviewer EcUc: Follow-up on the baseline comparison and completed controls
Thank you again for your careful review. Your questions prompted us to examine the baseline reference more closely and strengthen the controlled experiments. We would particularly appreciate your view on the following evidence addressing the baseline comparison and training budget.
The EMGFormer authors' correction substantially changes the reference underlying the discrepancy raised in your review:
| Author EMGFormer-L reference: angular MAE (°) | Unseen movements | Users and movements unseen |
|---|---|---|
| Earlier, withdrawn | 9.280 | 12.250 |
| Corrected | 13.716 | 14.845 |
The author correction and our independent audit are documented in Table 22, p. 28.
Separately, our matched causal comparison shows that MARC's gains extend beyond angular accuracy. On unseen emg2pose movements, the participant-macro results are:
| Reconstruction metric | Causal EMGFormer-L | MARC |
|---|---|---|
| Angular MAE (°) ↓ | 14.788 ± 0.332 | 13.217 ± 0.243 |
| Fingertip error (nominal mm) ↓ | 34.148 ± 0.677 | 29.769 ± 0.676 |
| 100 ms displacement MAE (°) ↓ | 5.631 ± 0.061 | 5.018 ± 0.034 |
These are 10.6%, 12.8% and 10.9% reductions, respectively, with values reported as mean ± SD over three runs. The comparison therefore supports improvements in pose accuracy, spatial reconstruction and motion reconstruction within this setting (Table 2, p. 6; Figure 4, p. 7; Table 11, p. 18).
The requested prediction-free, same-encoder LSTM, Gated DeltaNet and individual-loss controls have also completed three runs under the main stopping rule (Tables 14–15, pp. 24–25). One consistent result is that removing geometry supervision increases mean fingertip error by 0.849–1.067 mm across the three test settings, with increases in all nine paired run–setting comparisons. This directly supports the spatial benefit of that training objective.
Do the corrected reference and completed controls address your concerns about baseline validity and training adequacy? If a specific comparison or protocol detail remains important to your assessment, we would be glad to clarify it. Thank you again for helping us strengthen the experimental evidence and its presentation.
Response to Reviewer EcUc (1/2): baseline audit and evaluation scope
Thank you for identifying the discrepancy with the published EMGFormer-L results. We independently checked the public reference and our evaluation. The audit explains much of the discrepancy, while the matched causal comparisons establish MARC's gains in pose and motion reconstruction.
Q2. What explains the baseline discrepancy?
The authors' correction withdraws the earlier scores: 16,831 training records had entered the unseen-movement evaluation. The checkpoint weights are unchanged. The emg2pose participant-macro angular MAE (°) is:
We independently recomputed these macro scores from released aggregates. Our own index contains 6,167 records, all test-labeled, with the corrected group counts. The apparent gap between our causal reproduction and the author reference falls from 5.508° to 1.072° for unseen movements and from 3.250° to 0.655° for the combined setting. For identical author predictions, macro versus micro aggregation changes MAE by only 0.056–0.081°.
This correction narrows the discrepancy; it does not make the protocols identical. Noncausal context, windows/alignment, normalization and training still differ, and their individual effects have not been isolated. Adapted architectures and training recipes are specified in Appendix B, pp. 13–14; the reference audit is in Table 22, p. 28.
MARC's gains come from the separate matched causal comparison. All three models below receive causal EMG inputs and use common scored timestamps and participant aggregation. emg2pose angular MAE (°), mean ± SD over three training runs:
MARC reduces MAE by 9.5–19.3% versus TDS+LSTM and 5.1–10.6% versus causal EMGFormer-L. Relative to EMGFormer-L, gains cover 19/20 unseen users, 157/158 participants on unseen movements and 19/20 in the combined setting (Table 2/Figure 3, p. 6).
The benefit also appears in hand geometry and motion. On unseen emg2pose movements, the same models give:
This corresponds to 12.8% lower fingertip error and 10.9% lower displacement error, alongside better direction consistency. These are reconstruction metrics, with motion measured between outputs 100 ms apart (Figure 4, p. 7; Table 11, p. 18; Figure 7, p. 19). The gains are therefore visible beyond aggregate angular error.
Q3. Checkpoint selection and development scope.
Validation selected run checkpoints. Earlier test comparisons informed family/capacity choices across emg2pose, MANUS and DB8, plus emg2pose state/feedback candidates, MANUS protocol variants and DB8 objectives. Final results and the added controls use these same, previously consulted test splits (Sec. 4.1, p. 5; Appendix C.4, p. 16).
We hope the independently checked correction, explicit configurations and matched results address the baseline discrepancy that motivated your concern. We would appreciate your reassessment of baseline validity on this evidence.