acceptodds
Under review as a conference paper at ICLR 2027

UPCSD: Unsupervised Prefix Calibration with State-Dynamic Modeling for Long-Term Intracortical Neural Decoding

Abstract

Cross-day neural drift degrades decoding performance in intracortical brain-computer interfaces (iBCIs), challenging robust long-term decoding under practical deployment constraints. We propose unsupervised prefix calibration with state–dynamic modeling (UPCSD), which uses the first 30 s of unlabeled test-day neural activity to correct prefix-estimable first-order cross-day variation and training-time augmentation to improve robustness to residual recording variation. A state–dynamic representation separately models slowly varying neural states and fast multiscale fluctuations, which are fused and decoded by a lightweight LSTM. Chronological offline evaluation on four iBCI datasets covering center-out (CO) and random target tracking (RTT) tasks showed that UPCSD achieved the numerically highest mean daily on each dataset. Mean daily ranged from 0.62 to 0.85 within 100 days and remained 0.57 and 0.46 over the full 700- and 757-day spans of Link-CO and Link-RTT, respectively. Under strictly causal inference using only past and current neural activity, UPCSD achieved the numerically highest mean daily on these four datasets and 0.672 0.091 across 12 online test days on an additional NW-CO dataset. On the Lynxi HE200, on-chip inference closely matched GPU decoding performance while reducing active device power by approximately 92%. These results support UPCSD as a label-free approach for practical, long-term iBCI decoding.

Primary area:
applications to neuroscience & cognitive science
Keywords:
intracortical brain-computer interface, cross-day neural decoding, neural drift, unsupervised calibration, neural dynamics, long-term neural decoding, representation learning

Reviews

Among:
Shape:
1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_qvFgOpenReview ↗
Rating
1
Confidence
4
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

This paper proposes UPCSD, to use the first 30s of unlabeled neural recording to infer statistics of new days and achieve robust cross-day performance. UPCSD is evaluated offline on Link dataset over long recording days and online on edge-computing chip.

Critical strengths
  • The method is straightforward yet shows robust long-term decoding performance on public datasets.
  • Evaluation is conducted on edge-computing chip.
  • Ablation study is conducted over major components.
Critical weaknesses
  • The method section is difficult to read with many terminologies, and it is unclear what are the differences between the proposed components and common strategy like z-scoring and random noise injection.
  • The related work is lacking and more recent neural decoder models need to be compared, rather than generic models like transformer and LSTM. E.g. NDT3, POSSM, POYO and SPINT
  • The on-chip results section shows comparison between GPU and an edge-computing chip, rather than between different methods. It is unclear if benefit comes from the proposed methods or from using the chip.

[NDT3] Ye et.al. A Generalist Intracortical Motor Decoder. NeurIPS 2025

[POSSM] Ryoo et. al. Generalizable, real-time neural decoding with hybrid state-space models. NeurIPS 2025

[POYO] Azabou et.al. A Unified, Scalable Framework for Neural Population Decoding. NeurIPS 2023

[SPINT] Le et al. SPINT: Spatial Permutation-Invariant Neural Transformer for Consistent Intracortical Motor Decoding. NeurIPS 2025

Questions for authors
  1. In the ablation study why w/o State & Dynamic is close to the full model but worse than w/o State or w/o Dynamic.
  2. Please explain the difference between PFDC and z-scoring with the first 30s. Does normalization result in the drift reduction in Figure3?
  3. Are RDA doing similar augmentation as random masking and random noise injection? What are the reasons to use two white noise in RDA?
  4. Please explain the underlying motivation of state-dynamic tokenization. Why use linear mapping? And the choice of k seems arbitrary, is there hyperparameter tuning on the k?
  5. How does the recently proposed decoder models work with PFDC? All NDT3, POSSM and POYO are trained or evaluated with the similar dataset as indy-RTT.
  6. Are the benefits in GPU-HE200 comparison from UPCSD or the chip?
  7. Please define acronym at the first use, in the first section of methods.
5 comments
AuthorsOpenReview ↗

Response to reviewer qvFg (Part 1/5)

We sincerely thank the reviewer for recognizing UPCSD's long-term cross-day decoding performance, ablation studies, and on-chip deployment, and for the constructive comments on our methodological design and baseline comparisons. To address these concerns, we have conducted additional comparisons with recent neural decoders (NDT3 and SPINT), ablation studies of individual RDA perturbations, sensitivity analyses of the State–Dynamic window length, and capacity-matched experiments to further clarify the rationale behind our design choices and the contributions of individual components.

We would like to emphasize that our goal is not simply to increase model complexity, but to achieve robust long-term neural decoding through a compact, efficient, and practically deployable framework. Although PFDC and RDA employ established normalization and augmentation operations, our analyses in Figs. 1 and 3, together with cross-day decoding experiments, identify and validate the important role of these simple strategies in mitigating long-term neural drift. Furthermore, the State–Dynamic representation provides additional decoding benefits, as our supplementary experiments show.

Moreover, real-world intracortical BCI systems require continuous, real-time decoding under constraints on computational resources, power consumption, and hardware compatibility. While more complex neural decoders may offer strong modeling capabilities, deploying their original architectures on low-power chips can require additional operator substitutions or architectural adaptations. To address these practical requirements, we developed a lightweight decoding framework with a causal, zero-look-ahead configuration, validated its real-time online decoding performance across 12 test days in macaque experiments, and successfully deployed the complete model on the Lynxi HE200 chip. We believe that achieving competitive long-term cross-day decoding performance while enabling short unlabeled calibration, real-time inference, and low-power hardware deployment represents an important contribution of this work.

Q1. In the ablation study why w/o State & Dynamic is close to the full model but worse than w/o State or w/o Dynamic.

A1. We thank the reviewer for this question. We would like to clarify that removing both the State and Dynamic branches does not eliminate temporal modeling entirely. In this ablation, the State–Dynamic tokenizer is replaced with a learnable time-step-wise projection that preserves information from the original neural activity, while the subsequent BiLSTM continues to capture temporal dependencies. Therefore, this configuration can still achieve relatively strong decoding performance.

In contrast, when only the Dynamic branch is retained, the model primarily relies on fast fluctuations relative to the slowly varying state, without access to the full slow-varying state information, leading to a noticeable performance degradation. Retaining only the State branch preserves the dominant low-frequency neural activity and generally yields better performance. The full model further integrates fast dynamic information and achieves the highest mean daily R2R^2 across all four datasets (Table 3 in the main manuscript).

Furthermore, we conducted additional experiments with a capacity-matched direct-input BiLSTM baseline. The full UPCSD achieved improvements in mean daily R2R^2 of 0.0262, 0.0046, 0.0168, and 0.0118 across the four datasets, respectively. These results suggest that the structured State–Dynamic representation provides additional decoding benefits, although the magnitude of its contribution varies across datasets.

DatasetTest DaysUPCSD (Full)Capacity-matched Baseline
Link-CO1240.5680460.541845
Link-RTT1250.4620880.457522
Indy-RTT210.5878780.571037
AuthorsOpenReview ↗

Response to reviewer qvFg (Part 2/5)

Q2. Please explain the difference between PFDC and z-scoring with the first 30s. Does normalization result in the drift reduction in Figure3?

A2. We thank the reviewer for this question. We would like to clarify that PFDC employs channel-wise normalization based on Z-scoring, and its contribution does not lie in introducing a new normalization operation, but rather in identifying and validating its effectiveness for long-term cross-day neural drift correction.

Specifically, PFDC uses only the first 30 s of unlabeled neural activity from each test day to estimate channel-wise means and standard deviations. These calibration statistics are then fixed and applied to all subsequent decoding, without requiring behavioral labels, future neural observations, or model parameter updates.

The drift reduction shown in Fig. 3A indeed results directly from this normalization procedure. More importantly, this reduction in statistical drift is accompanied by improvements in decoding performance. As shown in the ablation study in Table 3, removing PFDC decreases the mean daily R2R^2 by 0.313, 0.285, 0.302, and 0.119 across the four datasets, respectively, further supporting its contribution to robust long-term cross-day decoding.

Therefore, we emphasize that the value of PFDC lies not only in reducing cross-day statistical differences but also in improving long-term unlabeled cross-day decoding performance with minimal calibration overhead.

Q3. Are RDA doing similar augmentation as random masking and random noise injection? What are the reasons to use two white noise in RDA?

We thank the reviewer for this question. RDA is designed to simulate residual neural variability that remains after PFDC correction, thereby improving the robustness of long-term cross-day decoding. As defined in Eqs. (5)–(6), RDA combines four perturbations: channel dropout to simulate electrode channel loss, gain perturbation to simulate changes in signal amplitude, bias perturbation to simulate baseline shifts, and Gaussian noise to simulate random observation noise.

Regarding the two Gaussian terms in Eq. (6), they represent different types of neural variability rather than redundant white noise. Specifically, bcb_c represents a channel-wise random bias that remains constant within a temporal window, simulating baseline shifts, whereas ηt,c\eta_{t,c} represents time-varying random noise, simulating instantaneous observation noise.

To further evaluate the contributions of these perturbations, we conducted additional RDA ablation experiments. On Link-CO, Link-RTT, Indy-RTT, and Jango-CO, channel dropout alone achieved mean daily R2R^2 values of 0.5551, 0.4615, 0.5815, and 0.8478, respectively, approaching the performance of full RDA. In contrast, removing channel dropout reduced performance to 0.4392, 0.3830, 0.5186, and 0.8026, respectively.

DatasetFull RDAw/o RDADropout Onlyw/o Dropout
Link-CO0.56800.44810.55510.4392
Link-RTT0.46210.38710.46150.3830
Indy-RTT0.58790.50360.58150.5186
Jango-CO0.84920.80340.84780.8026

These results indicate that channel dropout is the primary contributor to RDA's performance gains, while the remaining perturbations provide smaller complementary improvements. Full RDA achieved the highest mean daily R2R^2 across all four datasets, supporting the benefit of combining different perturbation types for robust cross-day decoding.

AuthorsOpenReview ↗

Response to reviewer qvFg (Part 3/5)

Q4. Please explain the underlying motivation of state-dynamic tokenization. Why use linear mapping? And the choice of k seems arbitrary, is there hyperparameter tuning on the k?

A4. We thank the reviewer for this valuable question. The motivation for State–Dynamic tokenization comes from our observations of local neural dynamics. As illustrated in Fig. 3B, the slowly varying state exhibits relatively smooth temporal trajectories, whereas the dynamic component captures distinct local fluctuations. We therefore employ weighted local linear fitting to extract the underlying activity level and temporal trends, allowing these components with different temporal characteristics to be modeled separately. Local linear fitting does not assume globally linear neural dynamics, but provides a computationally efficient approximation of local activity evolution. The ablation results in Table 3 further support the additional decoding benefits of this structured representation, although the improvements are relatively modest.

Regarding the choice of window length kk, we conducted additional sensitivity analyses using 15, 31, and 45 bins. The results reveal dataset-dependent preferences: Link-RTT performs best with a shorter window, Link-CO with 31 bins, while Indy-RTT and Jango-CO show comparable performance at 31 and 45 bins. We therefore selected k=31k=31 as a unified intermediate setting, rather than optimizing the window length separately for each dataset.

Datasetk=15k=15k=31k=31k=45k=45
Link-CO (124 days)0.5450.5680.549
Link-RTT (125 days)0.4830.4660.471
Indy-RTT (21 days)0.5690.5860.588
Jango-CO (16 days)0.8480.8500.850

Furthermore, to comprehensively evaluate the decoding capability of this representation, we initially adopted a noncausal configuration that allows access to bidirectional temporal information. To meet the requirements of real-time BCI applications, we subsequently introduced causal modifications to the local fitting window, temporal convolutions, and LSTM, resulting in a strictly causal configuration that relies only on current and past neural activity. We validated this configuration through real-time online decoding experiments across 12 test days in macaques, achieving a mean daily R2R^2 of 0.672 ±\boldsymbol{\pm} 0.091 (Table 2). These results further support the feasibility of State–Dynamic representation for real-time neural decoding.

Reviewer_ZZuPOpenReview ↗
Rating
2(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
1
Read review
Paper summary

This paper proposes UPCSD for long-term intracortical neural decoding without test-day behavioral labels. It uses the first 30 seconds of unlabeled neural activity from each recording day for channel-wise normalization, applies residual drift augmentation during training, and combines slow state estimates with fast multiscale fluctuations in an LSTM decoder. The authors evaluate the method with chronological splits on four longitudinal center-out and random target tracking datasets. They also assess a causal, zero-look-ahead configuration, report online decoding over 12 NW-CO test days, and deploy the decoder on the Lynxi HE200. UPCSD achieves the numerically highest mean daily R² among the compared methods on the four longitudinal datasets; on-chip decoding closely matches GPU performance while using substantially less active device power.

Critical strengths
  1. Clear presentation and an explicit calibration protocol. The paper clearly separates test-day prefix calibration, training-time augmentation, and temporal representation learning. It specifies the 30-second unlabeled calibration budget, chronological evaluation, and exclusion of the prefix from performance measurement. This makes the deployment assumptions and the interpretation of the reported results relatively easy to follow.
  2. Validation across several relevant operating settings. The evaluation covers four longitudinal datasets, includes causal zero-look-ahead inference, and extends to 12 online NW-CO test days and on-chip HE200 inference. These settings provide useful evidence about the method’s practical applicability beyond a single offline benchmark.
Critical weaknesses
  1. Limited cross-day adaptation baselines. The noncausal baselines mostly lack dedicated test-day adaptation. NoMAD is included under the common 30-second constraint, but its weak results on several datasets—and substantial improvement with PFDC—receive little diagnostic explanation. This makes the comparative advantage difficult to assess.
  2. Unclear incremental value of the proposed modules. PFDC is prefix-based channel-wise z-scoring, while RDA uses familiar augmentations. Removing both State and Dynamic lowers mean daily R² by only 0.016–0.051. The large drop from removing State mainly shows that Dynamic-only is weak. Without a clearly defined direct-input baseline and paired uncertainty estimates, the value of the tokenizer remains unclear.
Questions for authors
  1. Why does NoMAD perform poorly on several datasets? Please report performance before and after alignment and its sensitivity to the 30-second prefix constraint.
  2. What replaces the tokenizer in “w/o State & Dynamic”? Could the authors compare against a capacity-matched PFDC + RDA + direct-input LSTM and report paired day-level differences?
3 comments
AuthorsOpenReview ↗

Response to reviewer ZZuP (Part 1/3)

We sincerely thank the reviewer for recognizing the experimental design and practical relevance of our work, as well as for the valuable suggestions regarding baseline comparisons and the individual contributions of the proposed modules.

To address these concerns, we have conducted additional analyses of NoMAD's sensitivity to calibration duration, comparisons with recent neural decoders such as SPINT and NDT3, and capacity-matched ablation studies under consistent PFDC and RDA settings to better clarify the contributions of each component.

We would like to further emphasize that, although PFDC employs relatively simple channel-wise statistical normalization, we have identified and validated its important role in correcting long-term cross-day neural drift. As illustrated in Figs. 1 and 3, using only the first 30 s of unlabeled neural activity substantially reduces cross-day differences in neural population statistics and improves decoding performance across four longitudinal datasets. Thus, our contribution lies not merely in individual components but in integrating short unlabeled calibration, residual drift augmentation, and structured temporal modeling to achieve robust long-term cross-day decoding.

Furthermore, lightweight design and hardware deployment compatibility are also key objectives of our work. To meet the requirements of real-world intracortical BCIs for real-time processing, low power consumption, and limited computational resources, UPCSD adopts a compact and efficient architecture while maintaining stable decoding performance. We further demonstrate its practical applicability through real-time online decoding across 12 test days and deployment on the Lynxi HE200 chip. The on-chip decoding results closely match those obtained on the GPU, while the measured device inference power is reduced by approximately 92%, highlighting the potential of UPCSD for resource-constrained intracortical BCI systems.

Weakness 1. The noncausal baselines mostly lack dedicated test-day adaptation. NoMAD is included under the common 30-second constraint, but its weak results on several datasets—and substantial improvement with PFDC—receive little diagnostic explanation. This makes the comparative advantage difficult to assess.

Response 1. We thank the reviewer for this valuable suggestion. To strengthen the comparison with recent neural decoders and cross-day adaptation methods, we have conducted additional experiments with SPINT and NDT3.

All methods were evaluated using strictly chronological data splits, with approximately the earliest 20% of recording days used for training and validation and the remaining 80% reserved for cross-day testing, avoiding potential information leakage from random splits. On Link-RTT, SPINT, using its own 30-s unlabeled calibration strategy, achieved a mean daily R2R^2 of 0.1147±0.16440.1147 \pm 0.1644, compared with 0.4621 ± 0.1779 for UPCSD. On Indy-RTT, SPINT achieved 0.0060±0.17270.0060 \pm 0.1727, whereas UPCSD achieved 0.5879±0.24600.5879 \pm 0.2460. We also evaluated NDT3 on Indy-RTT, where it achieved an R2R^2 of 0.400, compared with 0.5879 for UPCSD.

We note that SPINT is computationally expensive, requiring approximately 8 hours for a single training and evaluation run on Link-RTT using our current hardware. Consequently, extensive hyperparameter tuning was limited by the available computational resources.

Regarding NoMAD, we further investigated its sensitivity to calibration duration. Extending the alignment window from 30 s to 120 s increased the mean daily R2R^2 from 0.2909 to 0.3072 on Link-RTT and from 0.8451 to 0.8504 on Jango-CO, indicating only modest improvements on these datasets. Moreover, NoMAD requires additional unsupervised parameter optimization on each test day, whereas UPCSD does not require test-day gradient updates.

These additional experiments further support the effectiveness of UPCSD for long-term cross-day decoding under strictly chronological evaluation and short unlabeled calibration constraints.

AuthorsOpenReview ↗

Response to reviewer ZZuP (Part 2/3)

Weakness 2. PFDC is prefix-based channel-wise z-scoring, while RDA uses familiar augmentations. Removing both State and Dynamic lowers mean daily R2R^2 by only 0.016–0.051. The large drop from removing State mainly shows that Dynamic-only is weak. Without a clearly defined direct-input baseline and paired uncertainty estimates, the value of the tokenizer remains unclear.

Response 2. We thank the reviewer for this valuable comment. While PFDC and RDA employ established normalization and augmentation operations, the contribution of our work lies in identifying and systematically validating their effectiveness for long-term cross-day drift correction and integrating them into a lightweight decoding framework for real-world iBCI application.

Through our analysis of cross-day neural activity, we found that channel-wise shifts in mean and scale account for an important component of cross-day statistical differences, which can be effectively mitigated using a short unlabeled prefix. As shown in Figs. 1 and 3, only 30 s of neural activity is sufficient to substantially reduce cross-day differences in neural population means. Building on this finding, we developed PFDC, which requires no test-day gradient updates, and integrated it with RDA and the State–Dynamic tokenizer to improve long-term decoding robustness while maintaining low model complexity.

To further clarify the independent contributions of these components, we conducted additional comparisons with BiLSTM and Transformer under the same PFDC + RDA settings, as well as a capacity-matched direct-input BiLSTM baseline. The results show that the full UPCSD consistently achieves additional performance gains, although the benefits of the tokenizer vary across datasets.

DatasetBiLSTM + PFDC + RDATransformer + PFDC + RDAUPCSD (Full)
Link-CO0.53010.51770.5680
Link-RTT0.45080.41290.4621
Indy-RTT0.52800.54150.5879
Jango-CO0.83960.80920.8492

Furthermore, lightweight design and hardware deployment compatibility are also important methodological objectives of our work. The existing software stack of the Lynxi HE200 supports only a subset of neural network operators, making some complex decoding architectures difficult to compile and deploy directly without additional operator substitutions or architectural adaptations. In contrast, UPCSD was designed with hardware-supported operations in mind and has been successfully deployed in its entirety on the chip, achieving decoding results highly consistent with GPU inference while reducing measured device inference power by approximately 92%. Moreover, UPCSD requires no test-day gradient-based optimization, further reducing the calibration overhead during long-term use. These results demonstrate that our contribution extends beyond decoding accuracy to the development of a practically deployable framework for long-term unlabeled neural decoding on resource-constrained hardware.

AuthorsOpenReview ↗

Response to reviewer ZZuP (Part 3/3)

Q1. Why does NoMAD perform poorly on several datasets? Please report performance before and after alignment and its sensitivity to the 30-second prefix constraint.

A1. We thank the reviewer for this valuable suggestion. To clarify NoMAD's performance differences across datasets, we further examined its adaptation mechanism and sensitivity to calibration duration. NoMAD relies on unsupervised alignment using target-day neural activity, whereas our evaluation applies a consistent 30-s unlabeled calibration constraint.

Notably, NoMAD performs well on Jango-CO, achieving an R2R^2 of 0.846 when combined with PFDC. On Link-RTT, incorporating PFDC improves its R2R^2 from 0.028 to 0.294, highlighting the importance of correcting cross-day differences in input statistics.

To investigate the effect of calibration duration, we further extended NoMAD's alignment window to 60 s and 120 s. On Link-RTT, the mean daily R2R^2 increased from 0.2909 (30 s) to 0.3025 (60 s) and 0.3072 (120 s). On Jango-CO, the corresponding values were 0.8451, 0.8447, and 0.8504, respectively. These results indicate that longer alignment windows provide only modest improvements, suggesting that the 30-s calibration constraint alone cannot fully explain NoMAD’s performance gap on Link-RTT.

Dataset30 s60 s120 s
Link-RTT0.29090.30250.3072
Jango-CO0.84510.84470.8504

Furthermore, NoMAD's performance may be influenced by the compatibility between dataset characteristics and its modeling assumptions. In particular, the Link datasets use spike-band power (SBP) rather than raw spike counts, whereas NoMAD employs a Poisson reconstruction objective and relies on source-day latent dynamics for target-day alignment. These differences may contribute to its limited cross-day adaptation performance on Link-RTT.

Q2. What replaces the tokenizer in “w/o State & Dynamic”? Could the authors compare against a capacity-matched PFDC + RDA + direct-input LSTM and report paired day-level differences?

A2. We thank the reviewer for this valuable suggestion. We clarify that the "w/o State & Dynamic" configuration does not directly feed the raw 96-dimensional neural signals into the LSTM. Instead, it replaces the State–Dynamic tokenizer with a learnable time-step-wise projection (Linear(96,64) → GELU → Dropout → Linear(64,64) → LayerNorm), removing local state fitting, dynamic decomposition, and multiscale temporal convolutions while retaining PFDC, RDA, the original two-layer bidirectional LSTM, and the regression head. This configuration contains 621,634 trainable parameters, compared with 692,034 in the full UPCSD, resulting in a difference in model capacity.

To control for this difference, we conducted additional experiments with a capacity-matched PFDC + RDA + direct-input BiLSTM baseline. Specifically, we expanded the time-step-wise projection to Linear(96,501) → GELU → Dropout → Linear(501,64), while keeping the remaining architecture unchanged and excluding State–Dynamic decomposition. This baseline contains 691,991 trainable parameters, differing from the full UPCSD by only 43 parameters (0.0062%).

All models were evaluated using identical data splits, PFDC/RDA settings, and optimization protocols. Each model was trained for 40 epochs, with model selection based on source-domain validation loss. Under identical prediction lags and post-30-s evaluation conditions, the full UPCSD achieved higher mean daily R2R^2 than the capacity-matched baseline, with improvements of 0.0262, 0.0046, 0.0168, and 0.0118 on Link-CO, Link-RTT, Indy-RTT, and Jango-CO, respectively.

DatasetTest DaysUPCSD (Full)Capacity-matched Baseline
Link-CO1240.5680460.541845
Link-RTT1250.4620880.457522
Indy-RTT210.5878780.571037

These results demonstrate that the State–Dynamic tokenizer provides additional decoding benefits even after controlling for model capacity, although the magnitude of improvement varies across datasets and is relatively small on Link-RTT.

Reviewer_wrbGOpenReview ↗
Rating
2
Confidence
3
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

This paper proposes UPCSD, a framework for long-term intracortical neural decoding under cross-day distribution shifts. The approach combines four components: Prefix-Based First-Order Drift Correction (PFDC), which normalizes neural recordings using statistics estimated from the first 30 seconds of each recording day; Residual Drift Augmentation (RDA), which introduces synthetic recording perturbations during training; state–dynamic tokenization, which separates slowly varying neural states from faster temporal fluctuations; and an LSTM-based sequence decoder. The authors evaluate the approach on four longitudinal datasets and an additional online dataset. They report improvements over several baselines, including NoMAD, and demonstrate deployment on resource-constrained hardware.

Critical strengths

Some of the major strengths of the paper:

  1. Extensive evaluation on longitudinal neural datasets. The paper evaluates UPCSD across multiple intracortical neural decoding datasets with varying recording durations and behavioral tasks.

  2. Component-level ablations and practical deployment. The authors make an effort to evaluate the contributions of different components through the ablation experiments in Table 3. The hardware deployment experiments are also useful for assessing the practical feasibility of the proposed approach, especially since the authors include evaluations of practical factors such as power consumption and latency (even though in the Appendix).

Critical weaknesses

The paper demonstrates that the complete UPCSD pipeline works reasonably well on the evaluated datasets. What is less convincingly demonstrated is why this particular combination of established techniques is necessary, and whether its architectural contributions are responsible for the improvements.

The key weaknesses of the current version of the draft and UPCSD are as follows.

  1. My primary concern is the limited methodological novelty of the proposed approach. Most of the individual techniques employed in UPCSD are already well established. PFDC essentially performs channel-wise normalization using the mean and standard deviation estimated from a 30-second calibration window. RDA combines familiar augmentation techniques, including channel dropout, multiplicative gain perturbations, additive bias, and Gaussian noise. The state–dynamic tokenizer, which appears to be the main architectural contribution, employs local weighted linear fitting, temporal trend/residual decomposition, multiscale 1D convolutions, and feature fusion. Finally, decoding is performed using a conventional LSTM.

While combining established techniques into an effective framework can certainly be valuable, I find that the paper does not sufficiently justify why this particular combination is necessary or establish what fundamentally distinguishes its representation from existing temporal signal-processing and representation-learning approaches.

Several architectural choices also appear somewhat ad hoc, without sufficient theoretical or empirical justification.

  1. Some of the major questions regarding the PFDC. a. I wonder what would happen if the authors used running statistics instead of keeping the mean and standard deviation fixed after the first 30 seconds. Several test-time adaptation approaches update normalization statistics as new observations arrive.

For example, the authors could consider running normalization or an exponential moving average (EMA):μt=(1−α)μt−1+αxt.\mu_t=(1-\alpha)\mu_{t-1}+\alpha x_t.

Such approaches could respond to distribution shifts that occur after the initial calibration window. They would also remain strictly causal, as they only require past and current observations.

b. In Section 4.2, Figure 3a, the authors investigate calibration durations ranging from 1 to 120 seconds and justify choosing 30 seconds based on the observed drift reduction. However, Figure 3a evaluates the reduction in cross-day mean drift rather than downstream neural decoding accuracy. These are not necessarily equivalent. I would like to see how decoding R2R^2 varies across calibration durations of 10, 20, 30, 40, 60, and 120 seconds. This would help establish whether the selected duration is appropriate for the actual decoding task, rather than primarily for statistical alignment.

  1. Some of the major questions regarding the RDA. a. Appendix B, Table 7 provides the augmentation hyperparameters, but it is unclear how these values were selected. For example, the channel dropout probability is 0.30 for three datasets and 0.35 for Jango-CO. What motivates these particular values? Were they selected through validation, based on measured characteristics of the neural recordings, or chosen heuristically? b. Table 7 reports an augmentation application probability of 1.0. Together with Equation (7), this suggests that every training input is passed through the stochastic augmentation operation, rather than explicitly training on both clean and augmented versions. I would appreciate clarification of this design choice. Have the authors investigated whether mixing unaugmented and augmented observations during training affects decoding performance? c. According to Equation (5), the four corruption mechanisms are combined within the augmentation operation. Although Table 3 demonstrates that removing RDA reduces performance, the experiments do not establish which individual perturbations are responsible for these improvements. For example, would channel dropout alone provide most of the benefit? Are the gain, bias, and noise perturbations all necessary? I would encourage the authors to evaluate the individual augmentation components and their most relevant combinations.

  2. Some of the major questions regarding the dynamic-state tokenization. a. The authors propose separating slowly varying neural states from fast temporal fluctuations using weighted local linear fitting. However, the rationale behind the selected temporal windows is insufficiently developed. For example, why is a 31-bin window, corresponding to approximately 620 ms, appropriate for capturing slowly varying neural states across different datasets and behavioral tasks? b. The main motivation for state–dynamic tokenization is that neural activity contains information evolving at different temporal scales. However, this is a well-established signal-processing problem, and several conventional approaches are available for separating temporal components. For example, why not consider low-pass/high-pass filtering or Discrete Wavelet Transform (DWT) as alternative feature-extraction strategies? ICA could also be explored as an alternative form of signal decomposition, although I acknowledge that its objective is to recover statistically independent components rather than to specifically separate slow and fast temporal variations. c. I appreciate the authors' efforts to provide the ablation results in Table 3. However, several questions remain. First, does removing the state and/or dynamic branches substantially change the number of trainable parameters? If so, some performance improvements could potentially arise from increased model capacity rather than the proposed decomposition itself. Parameter-matched comparisons would help clarify this. Second, are the reported improvements statistically significant? For example, on Link-RTT, the improvement from including the full state–dynamic representation, compared with removing both branches, is only (+0.016) in mean daily R2R^2. This is apparently a small improvement, so a paired statistical test will help determine whether it is significant.

  3. (Major Concern) This is one of my most significant experimental concerns. Appendix C (under Interpretation of fairness) explicitly states that the BiLSTM and Transformer baselines do not receive training-time data augmentation. However, RDA is an important component of UPCSD. The ablation results in Table 3 show that removing RDA causes substantial performance degradation. Interestingly, when RDA is removed, UPCSD performs worse than the strongest PFDC-enabled baseline across all four datasets (Compare the baseline+PFDC results in Table 1 with the w/o RDA results in Table 3). This raises an important question: How much of UPCSD's improvement over the baselines is attributable to the proposed architecture, and how much to the additional training-time augmentation? The current comparison changes both the architecture and the training procedure simultaneously, making it difficult to isolate their respective contributions. I would strongly encourage the authors to include additional comparisons, such as: (i) BiLSTM + PFDC + RDA, (ii) Transformer + PFDC + RDA, (iii) UPCSD + PFDC + RDA.

  4. A similar concern also appears while comparing causal versus noncausal decoding performance. Comparing Tables 1 and 2, performance decreases noticeably on the two long-term Link datasets when moving from the noncausal to the causal UPCSD configuration. However, the causal and noncausal implementations differ not only in their access to future neural observations but also in their LSTM architectures and in the prediction–target temporal alignment. Therefore, it is difficult to determine how much of the performance difference is specifically attributable to causality.

While the separate causal and online evaluations are appreciated, the noticeable performance degradation on the two long-term Link datasets suggests that a practically deployed causal decoder may achieve substantially lower accuracy than the more impressive noncausal results indicate. I would like the authors to discuss this discrepancy and its implications for real-world deployment.

Some other comments.

  1. Finally, I felt that some of the terminology unnecessarily complicates relatively straightforward operations. For example, Prefix-Based First-Order Drift Correction is essentially channel-wise normalization based on statistics estimated during an initial calibration window. Similarly, Residual Drift Augmentation largely consists of conventional training-time data augmentation. The terminology is not incorrect, but clearer descriptions of these operations would improve accessibility and help readers distinguish established techniques from the paper's actual methodological contributions. (Authors may choose to ignore this comment).
Questions for authors

I would suggest that the authors review the detailed weaknesses of the key questions in the current version of the work and the draft.

6 comments
AuthorsOpenReview ↗

Response to reviewer wrbG (Part 1/6)

We sincerely thank the reviewer for the careful evaluation of our manuscript and the detailed, constructive comments regarding methodological novelty, experimental fairness, and the rationale behind our design choices. We address each concern point by point below.

Q1. My primary concern is the limited methodological novelty of the proposed approach. Most of the individual techniques employed in UPCSD are already well established. PFDC essentially performs channel-wise normalization using the mean and standard deviation estimated from a 30-second calibration window. RDA combines familiar augmentation techniques, including channel dropout, multiplicative gain perturbations, additive bias, and Gaussian noise. The state–dynamic tokenizer, which appears to be the main architectural contribution, employs local weighted linear fitting, temporal trend/residual decomposition, multiscale 1D convolutions, and feature fusion. Finally, decoding is performed using a conventional LSTM.

A1. We thank the reviewer for this valuable comment. We acknowledge that several individual operations in UPCSD are based on established techniques. However, their combination is motivated by the distinct yet interconnected challenges of long-term cross-day neural decoding, rather than simply assembling existing methods.

During long-term BCI operation, neural recordings exhibit substantial cross-day variability, while behavioral labels are generally unavailable for recalibration. PFDC first corrects statistical drift using a short segment of unlabeled neural activity, providing an inexpensive adaptation mechanism without updating model parameters. However, short-term statistical calibration cannot fully account for changes in recording conditions. RDA therefore complements PFDC by exposing the model to residual variability during training, improving robustness without additional inference overhead. Beyond recording variability, neural activity contains both slowly varying states and rapid temporal fluctuations that are relevant to decoding. State–Dynamic tokenization addresses this separate temporal modeling challenge by explicitly extracting local activity levels, trends, and fluctuations across multiple temporal scales.

Thus, the three components are designed to work together: PFDC reduces observable statistical drift, RDA improves tolerance to residual variability, and State–Dynamic tokenization captures task-relevant temporal structure. This division of roles provides the rationale for their integration rather than treating them as interchangeable techniques.

Importantly, practical intracortical BCIs require continuous real-time decoding under limited computational and power budgets. We therefore adopt a relatively simple LSTM architecture to support lightweight and hardware-compatible deployment. The contribution of UPCSD lies not in introducing entirely new primitive operations, but in combining these complementary mechanisms to achieve robust long-term cross-day decoding with short unlabeled calibration and practical deployment capability. The subsequent responses provide additional experimental evidence supporting these design choices.

AuthorsOpenReview ↗

Response to reviewer wrbG (Part 2/6)

Q2. Some of the major questions regarding the PFDC. a. I wonder what would happen if the authors used running statistics instead of keeping the mean and standard deviation fixed after the first 30 seconds. Several test-time adaptation approaches update normalization statistics as new observations arrive. For example, the authors could consider running normalization or an exponential moving average (EMA):μt=(1−α)ut−1+αxt\mu_t=(1-\alpha)u_{t-1}+\alpha x_t. b. In Section 4.2, Figure 3a, the authors investigate calibration durations ranging from 1 to 120 seconds and justify choosing 30 seconds based on the observed drift reduction. However, Figure 3a evaluates the reduction in cross-day mean drift rather than downstream neural decoding accuracy. These are not necessarily equivalent. I would like to see how decoding R2R^2 varies across calibration durations of 10, 20, 30, 40, 60, and 120 seconds. This would help establish whether the selected duration is appropriate for the actual decoding task, rather than primarily for statistical alignment.

A2. We thank the reviewer for these valuable suggestions.

a) Fixed versus running statistics. Running normalization and exponential moving averages (EMA) are reasonable causal adaptation strategies, particularly for tracking within-day distribution shifts. Our study primarily focuses on long-term cross-day drift. As shown in Fig. 3A, a fixed 30-s calibration prefix reduces approximately 90% of cross-day population mean drift, while improving decoding performance across four longitudinal datasets. This approach requires estimating normalization statistics only once per day, avoiding continuous parameter updates during inference and reducing the potential influence of short-term behavioral fluctuations on calibration statistics. We acknowledge the potential benefits of dynamic normalization under substantial within-day nonstationarity and will discuss this as a direction for future work.

b) Calibration duration and decoding performance. We agree that reducing statistical drift does not necessarily translate into improved decoding accuracy. We therefore conducted additional experiments evaluating decoding performance with calibration durations of 10, 20, 30, 40, 60, and 120 s, as summarized below.

Dataset10 s20 s30 s40 s60 s120 s
Link-CO0.53820.55100.56110.56690.57270.5785
Link-RTT0.44000.45630.46340.46640.46840.4698
Indy-RTT0.55230.57630.59020.59310.59990.6016
Jango-CO0.81140.83650.84840.85010.85290.8527

Across all four datasets, decoding performance improves substantially within the first 30 s, with diminishing gains from longer calibration. Extending calibration from 30 to 120 s increases mean daily R2R^2 by only 0.0174, 0.0064, 0.0114, and 0.0043 on Link-CO, Link-RTT, Indy-RTT, and Jango-CO, respectively. These results are consistent with the drift reduction trend in Fig. 3A and further demonstrate the effectiveness of short-prefix calibration for downstream decoding. We therefore selected 30 s as a practical trade-off between calibration time and decoding performance, rather than optimizing solely for maximum decoding accuracy.

AuthorsOpenReview ↗

Response to reviewer wrbG (Part 3/6)

Q3. Some of the major questions regarding the RDA. a. Appendix B, Table 7 provides the augmentation hyperparameters, but it is unclear how these values were selected. For example, the channel dropout probability is 0.30 for three datasets and 0.35 for Jango-CO. What motivates these particular values? Were they selected through validation, based on measured characteristics of the neural recordings, or chosen heuristically? b. Table 7 reports an augmentation application probability of 1.0. Together with Equation (7), this suggests that every training input is passed through the stochastic augmentation operation, rather than explicitly training on both clean and augmented versions. I would appreciate clarification of this design choice. Have the authors investigated whether mixing unaugmented and augmented observations during training affects decoding performance? c. According to Equation (5), the four corruption mechanisms are combined within the augmentation operation. Although Table 3 demonstrates that removing RDA reduces performance, the experiments do not establish which individual perturbations are responsible for these improvements. For example, would channel dropout alone provide most of the benefit? Are the gain, bias, and noise perturbations all necessary? I would encourage the authors to evaluate the individual augmentation components and their most relevant combinations.

A3. We thank the reviewer for these constructive suggestions.

a) Augmentation hyperparameters. The RDA hyperparameters were selected through preliminary hyperparameter searches and validation performance comparisons rather than arbitrary choices. To limit dataset-specific tuning, we adopted largely consistent augmentation settings across the four datasets, with a slightly higher channel dropout probability for Jango-CO (0.35 versus 0.30 for the other datasets).

b) Augmentation application probability. We set the augmentation application probability to 1.0 to expose the model to diverse recording perturbations throughout training. Importantly, this does not mean that all training samples receive identical perturbations, as the corruption parameters are randomly sampled for each augmentation. To examine this choice, we compared application probabilities of 0, 0.5, and 1.0, corresponding to no augmentation, mixed clean and augmented training, and stochastic augmentation of every training sample, respectively.

Datasetp = 0p = 0.5p = 1.0
Link-CO0.44810.51390.5680
Link-RTT0.38710.44620.4621
Indy-RTT0.50360.56410.5879
Jango-CO0.80340.83510.8492

Mixed training improved cross-day decoding performance, while increasing the application probability from 0.5 to 1.0 further improved mean daily R2R^2 by 0.0541, 0.0159, 0.0238, and 0.0141 on Link-CO, Link-RTT, Indy-RTT, and Jango-CO, respectively. These results support our choice of applying stochastic augmentation to every training sample.

c) Contributions of individual perturbations. We further conducted component ablations to examine the contributions of different RDA perturbations.

DatasetFull RDAw/o RDADropout Onlyw/o Dropout
Link-CO0.56800.44810.55510.4392
Link-RTT0.46210.38710.46150.3830
Indy-RTT0.58790.50360.58150.5186
Jango-CO0.84920.80340.84780.8026

The results show that channel dropout accounts for most of the improvement in cross-day robustness, while the combined gain, bias, and noise perturbations provide smaller additional benefits. Full RDA achieves the highest mean daily R2R^2 across all four datasets, supporting the use of complementary perturbations rather than relying on channel dropout alone.

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

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