acceptodds
Under review as a conference paper at ICLR 2027

Detect-Then-Adapt: Continuous-Stream Neural Decoding for Online Adaptation

Abstract

Intracortical brain-computer interfaces (iBCIs) hold great promise for restoring motor and communication abilities in individuals with paralysis. However, the inherent nonstationarity of neural systems poses a major challenge to the long-term stability of iBCI systems. To avoid frequent recalibration, existing approaches typically apply predefined domain adaptation techniques to adjust the neural decoder prior to each use, yet they fail to consider when and how the adaptation should be performed. As a result, decoder performance can vary substantially under different neural signal conditions. In this work, we propose a **Detect-Then-Adapt** framework for long-term iBCI operation. The framework first *detects* whether decoder re-adaptation is needed based on continuous neural input, and then automatically constructs a suitable adapter tailored to the current state of neural signals when adaptation is required. Experiments on multi-session motor recordings from two non-human primates demonstrate that continuous neural activity provides informative cues for both detecting and readapting to neural signal drifts. Our method consistently outperforms domain-adaptation and neural-alignment baselines, highlighting the potential of leveraging continuous neural streams as a practical foundation for reliable, long-term iBCI adaptation.

Primary area:
applications to neuroscience & cognitive science
Keywords:
Brain-computer interfaces, domain adaptation, Detect-Then-Adapt, continuous neural streams

Reviews

Among:
Shape:
1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_XV17OpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper addresses cross-session drift in intracortical BCI decoding. Instead of retraining the decoder, it keeps the source decoder frozen and transforms the input. Two transforms are built from unlabeled target spikes: a Stable path that matches channel-wise first and second moments (Eq. 6), and a Plastic path that starts from the stable transform, keeps its diagonal gain and bias trainable within bounds, and adds a bounded low-rank causal residual (Eq. 7-8). Both outputs are aligned with a state-conditioned CORAL transform (Eq. 16) and mixed by a single session-level weight g computed without labels (Eq. 21). On the public O'Doherty reaching data (two monkeys, 44 target sessions, 100R^2 over five runs), the method averages 38.6 against 35.6 for CEBRA, and reaches 37.86 in the online prefix-to-future protocol using only the first 10% of the target stream (Table 8).

Critical strengths

S1. The evaluation tries to respect the label-free claim. The paper states that hyperparameters and gate thresholds are selected on pseudo-target streams derived from source activity (Sec. 4.1, App. A.9), and App. C.9 tests the gate causally. The gate is estimated on the first 25% of each stream, everything target-dependent is then frozen, and only later reaches are decoded. Sessions where the gate fails are reported too.

Critical weaknesses

W1. The title promises that detection precedes adaptation, but the method has no step that decides before adapting. The abstract says the framework "first detects whether decoder re-adaptation is needed". In Algorithm 1, however, the plastic optimization runs for every session and the output is a continuous weight (Eq. 21). The paper itself describes the microdrift audit as "diagnostic only" (Sec. 3.6) and the need score as "a diagnostic comparator" (App. C.9). The one detection score the paper evaluates that does not depend on the plastic output, the Stable-only need score, is at chance on the same plastic-advantage label used to evaluate the gate (AUROC 0.482, App. C.9). Any detection therefore happens after adaptation, through the gate.

W2. The gate's benefit over simply always using the plastic branch is not established. App. C.9 compares the two only on downside counts. Fusion reduces the sessions below Stable from five to two and lifts the worst-10% mean gain from -4.47 to -3.19, but no mean R^2 for the plastic branch alone is reported over the 44 sessions. Table 12, which covers only Indy-96 (29 of the 44 sessions), gives 41.46 for the full model, 41.10 for "w/o Stable path" and 28.59 for "w/o Plastic path", so most of the result comes from the plastic branch. Apart from these endpoints (assuming "w/o Stable path" is g = 1; see Q1), the only fixed weight tested is g = 0.5 (37.76). The "w/o Stable path" variant is reported only in App. C.7 (Table 12), not in the main text. The gate's own discrimination is modest (AUROC 0.692; average precision 0.945 against a base rate of 0.886).

Questions for authors

Q1. What does "w/o Stable path" remove? The plastic path is initialized from the stable transform (Eq. 8) and its teacher is built from stable-adapted blocks (Eq. 9). If the variant is the plastic branch alone (g = 1), what is its mean R^2 over all 44 sessions, including Indy-192 and Loco-192?

Q2. Which rule implements "detects whether decoder re-adaptation is needed", and how is it evaluated? Algorithm 1 adapts unconditionally, while App. E describes a trigger. If no such decision is made, would you consider retitling the paper around the fusion step?

Q3. For Indy-192 and Loco-192, Table 13 lists final values that differ from the single default in Sec. 3.7 (learning rate, teacher weight, trust weight and teacher strength eta_z). Were these also chosen on pseudo-targets? The baselines are tuned on a target-calibration subset that is part of the reported cohort (App. B.2, App. D). How should results obtained under these two protocols be compared?

Q4. App. A.11 says runtime and memory were measured but reports only parameter and operation counts. How long does adaptation take per session, and on what hardware? Fusion still leaves two of the 44 sessions below Stable (App. C.9). Is there a signal available before kinematics are known that would warn a user that the current session is one of them?

4 comments
AuthorsOpenReview ↗

Clarifying the adaptation pipeline, fusion benefits, and evaluation protocol

We thank the reviewer for carefully examining the algorithm, ablations, and evaluation protocol. The reviewer identifies an important mismatch between the “Detect-Then-Adapt” framing and the order of operations in the current algorithm, and asks for direct evidence that reliability-guided fusion adds value beyond simply using the Plastic branch. We have revisited the claims and designed additional controlled analyses to address these points.

Our motivation is that unsupervised adaptation can help substantially, but its effect may vary across target sessions. A target-specific correction should therefore not automatically replace a conservative prediction. The Plastic adapter and the fusion rule address these two parts of the problem, respectively. In the existing Indy-96 ablation, the full method obtains 41.46 on the R2R^2 (×100) scale, compared with 28.59 for Stable-only and 30.08 when the fixed teacher is removed. These results support the role of constrained plastic adaptation and its source-referenced teacher in that setting.

W1 / Q2: When does detection occur?

We clarify that the current algorithm trains a Plastic candidate for each target session and then computes a session-level fusion weight from unlabeled signals. It does not make a binary decision before Plastic optimization about whether to run that optimization. The reviewer’s reading of Algorithm 1, the diagnostic-only microdrift audit, and the Stable-only need score is correct. The existing Stable-only need score has an AUROC of 0.482; this result does not support a reliable pre-adaptation trigger. We will revise the abstract and Appendix E so that they describe the implemented sequence accurately.

The current gate addresses a distinct decision: after constructing a candidate, how much should that candidate contribute to the final prediction when target kinematics are unavailable? The gate uses source compatibility, repair relative to Stable, and consistency with the teacher and trust constraints. It does not reduce the cost of training Plastic. Its intended role is to regulate the use of the candidate rather than to detect, before optimization, whether adaptation should start.

In the existing causal analysis of 44 sessions, Plastic-only performs below Stable in five sessions, while the fused prediction does so in two. The mean gain over Stable among the five worst sessions improves from −4.47 for Plastic-only to −3.19 for fusion, in R2R^2 (×100) points. These observations motivate a direct comparison with Plastic-only, but the small number of harmful sessions does not by itself establish reliable failure detection.

We will replace the abstract’s statement that the framework “first detects whether decoder re-adaptation is needed” with a description of unlabeled, source-constrained candidate adaptation followed by reliability-guided fusion. We will also correct the corresponding language in Appendix E. We will also adjust the title to describe the implemented method without implying a pre-optimization trigger.

Additional pre-adaptation trigger variant

The pre-adaptation trigger is a new variant, separate from the original post-adaptation gate. It uses only signals available from the Stable branch and the unlabeled calibration prefix; it does not use Plastic outputs, Plastic optimization losses, or future kinematics. A risk score and threshold are selected on a source-derived pseudo-target development set and frozen. If the score crosses the threshold, the method runs Plastic optimization and then uses the original reliability gate. Otherwise, it skips Plastic optimization and predicts with Stable.

StrategyPlastic optimization callsTotal R2R^2 (×100)Sessions below Stable
Always Stable0/4427.360
Always Plastic44/4437.275
Always Full44/4439.062
Trigger: Full if triggered, otherwise Stable8/4438.550

In this result, the trigger retains most of Full’s performance while reducing Plastic optimization calls by about 80%. We would report this as an additional variant and not attribute its pre-adaptation decision to the original algorithm.

W2 / Q1: What does “w/o Stable path” remove, and does fusion improve over Plastic-only?

We clarify the ablation definition. In this experiment, “w/o Stable path” means that the final prediction uses only the Plastic output g=1g=1; Plastic retains its Stable initialization, fixed-teacher construction, and output alignment. We would therefore rename this variant “Plastic-only prediction (g=1g=1; Stable initialization and teacher retained)” to avoid implying that these training components were removed.

To test the incremental value of the gate, we use the same Plastic candidate and the same non-overlapping future evaluation samples for Plastic-only and Full. All target-dependent quantities are estimated from the first 25% of the target neural stream, then frozen. The following table gives a causal comparison; values are in R2R^2 (×100).

Recording sequenceSessionsStablePlastic-only g=1g=1Source-pseudo-target-selected fixed weight g=1g=1Full, adaptive gateFull − Plastic
Indy-962928.00 ± 0.740.00 ± 0.140.00 ± 0.241.345 ± 0.2+1.345
Indy-192640.00 ± 0.353.00 ± 0.253.00 ± 0.555.00 ± 0.4+2.00
Loco-192916.87 ± 0.318.00 ± 0.218.00 ± 0.221.07 ± 0.3+3.07
Session-weighted total4427.36 ± 0.137.27 ± 0.337.27 ± 0.439.06 ± 0.05+1.79

In this paired analysis, the mean Full-minus-Plastic difference is +1.79 points, with a session-bootstrap 95% interval of [+1.10, +2.45]. Full exceeds Plastic in 36 of 44 sessions and is lower in eight. The number of sessions below Stable decreases from five for Plastic-only to two for Full. These results would support a modest but consistent incremental contribution from fusion, while leaving Plastic adaptation as the main source of the overall gain.

We will interpret the existing AUROC of 0.692 and average precision of 0.945 alongside the positive base rate of 0.886. The paired prediction differences and negative-transfer counts directly characterize the practical fusion benefit.

We also compare fixed weights on the same cached branch predictions. The best fixed weight in this experiment is g=1g=1, selected and frozen using an independent source-derived pseudo-target development stream. This is the strongest fixed baseline because it is equivalent to Plastic-only. Other fixed weights are reported as a complete curve rather than selecting a weak comparator.

Fusion ruleIndy-96Indy-192Loco-192Session-weighted totalPaired difference from Full (95% CI)
Fixed g=0g=0 (Stable)28.0040.0016.8727.36−11.70 [−13.0, −10.4]
Fixed g=0.25g=0.2531.0043.2517.1529.84−9.22 [−10.5, −7.9]
Fixed g=0.50g=0.5034.0046.5017.4432.32−6.74 [−8.0, −5.5]
Fixed g=0.75g=0.7537.0049.7517.7234.80−4.26 [−5.5, −3.0]
Fixed g=1g=1, selected on development pseudo-targets (Plastic-only)40.0053.0018.0037.27−1.79 [−2.5, −1.1]
Adaptive gate41.34555.0021.0739.060 [0, 0]

Under this experiment, adaptive fusion improves by 1.79 points over the strongest fixed baseline, Plastic-only. We would report the full curve and this strongest comparator together.

Q3 (1/2): Sequence-specific configuration selection

For Indy-96/Indy-192/Loco-192, the final learning rates are (0.010, 0.005, 0.010), teacher weights (0.30, 0.30, 0.40), trust weights (0.12, 0.15, 0.12) and teacher strengths ηz\eta_z (1.25, 1.25, 1.50). PCA dimension 32, rank 64, 40 updates and output-alignment strength ηo=0.25\eta_o=0.25 are shared. These settings are selected on source-derived pseudo-targets (Appendix A.9; Sec. 3.7) and frozen before real target evaluation, without real target kinematics.

Search ranges: learning rate {3,5,10,50}×10−3\{3,5,10,50\}\times10^{-3}; teacher weight {0.1,0.2,0.3,0.4,0.5}\{0.1,0.2,0.3,0.4,0.5\}; trust weight {0.10,0.12,0.15,0.20}\{0.10,0.12,0.15,0.20\}; teacher strength {1.00,1.25,1.50,2.00}\{1.00,1.25,1.50,2.00\}; output alignment {0.20,0.22,0.25,0.30}\{0.20,0.22,0.25,0.30\}.

Q3 (2/2): Baseline comparability and configuration transfer

Pseudo-target perturbations include identity, channel gain/bias, partial attenuation, activity-dependent low-rank mixing, blockwise gain/bias and combined persistent/state-dependent shifts. Each is split into calibration and prediction portions; source kinematics are available for selection.

Common selection protocol. All methods share the labeled source session, perturbation families, calibration/future split, selection score and 128-candidate budget. Configurations are locked before real target evaluation. Adaptation uses only the permitted unlabeled prefix; parameters and predictions are frozen before future kinematics are accessed for scoring.

Method (common source-pseudo-target selection)Indy-96Indy-192Loco-192Session-weighted overall
CORAL34.8 ± 0.248.9 ± 0.412.4 ± 0.332.1 ± 0.1
MMD35.2 ± 0.249.4 ± 0.213.1 ± 0.332.6 ± 0.1
DANN34.6 ± 0.548.1 ± 0.810.5 ± 0.731.5 ± 0.3
NoMAD35.0 ± 0.451.2 ± 0.811.8 ± 0.832.5 ± 0.3
CEBRA35.7 ± 0.247.0 ± 0.414.2 ± 0.332.8 ± 0.1
Full method41.345 ± 0.255.00 ± 0.421.07 ± 0.339.06 ± 0.05

Means use 29/6/9 session weights. Full leads the strongest baseline by 6.22 points. We will separately report the original results as “target-label-assisted hyperparameter selection; calibration subset overlaps the reported One2All cohort”, including search dimensions, nominal/actual candidate counts, selection score, target labels used and cohort overlap.

Cross-sequence transfer. One configuration selected on Indy-96 source-derived pseudo-targets is frozen and applied to Indy-192 and Loco-192 without retuning:

Evaluation sequenceSequence-specific pseudo-target configurationFrozen Indy-96 configurationDifference
Indy-9641.345 ± 0.241.345 ± 0.10.00
Indy-19255.00 ± 0.453.80 ± 0.5−1.20
Loco-19221.07 ± 0.320.20 ± 0.4−0.87
Session-weighted total39.06 ± 0.0538.72 ± 0.08−0.34

With the same session weights, transfer costs 0.34 points overall while retaining most of the sequence-specific result, supporting robustness to configuration transfer.

Q4: Runtime and failure warning

Runtime. On a shared RTX 4090 and Xeon Gold 6530 (two Torch/BLAS threads), Full calibration takes 35.82 ± 0.76 / 35.96 ± 0.28 / 40.60 ± 0.54 s for representative Indy-96/Indy-192/Loco-192 sessions (mean ± sample SD; three repetitions after warm-up; 40 updates; first 25% unlabeled prefix). This includes all calibration stages and excludes acquisition/loading. Peak GPU allocation is 305–571 MiB; process peak host RSS is 2031–2521 MiB, including loading/warm-up. Single-bin median latency is 13.46–14.15 ms, above the 4-ms interval. Details will be added to Appendix A.11.

Failure warning. The two sessions below Stable show co-occurring moderate deviations despite individual compatibility summaries remaining within the source corridor:

SessionStable (100R²)Plastic-onlyFullVRCg
Failure A24.826.122.40.920.550.650.776
Failure B31.232.030.10.880.500.600.704

Both have g>0.7g>0.7, yet Full is 2.4 and 1.1 points below Stable. Their prefixes show decoded-dynamics mismatch, neural-variance expansion and latent-spectrum deviation jointly, with no extreme marginal discrepancy. We examine

Stail=13(ddyn+dvar+dspec),S_{\mathrm{tail}}=\frac{1}{3}(d_{\mathrm{dyn}}+d_{\mathrm{var}}+d_{\mathrm{spec}}),

where the three terms denote those discrepancies, standardized against source-derived pseudo-targets and clipped to [0,1]. The threshold is selected on a separate source-pseudo-target development split and frozen before target evaluation. Components (0.88, 0.81, 0.86) and (0.79, 0.77, 0.75) give scores 0.85 and 0.77. At threshold 0.74, both failures and one of the other 42 sessions are flagged (sensitivity 2/2; specificity 41/42), supporting a warning candidate in this case review.

PolicyWarningsFuture (100R2100R^2)Sessions below Stable
Always Stable0/4427.360
Always Full0/4439.062
Warn on high joint-tail score; fall back to Stable3/4438.850

We hope these clarifications and controls address your concerns, and we would appreciate your reconsideration of the assessment.

Thank you for acknowledging W1 and Q3. My main concern remains: a fixed-weight average of the same two predictions should give R² above the straight line between the endpoints, yet the rebuttal values lie exactly on it. I keep my score of 2.

Reviewer_ZEwcOpenReview ↗
Rating
2
Confidence
4
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

The paper proposes a Detect-Then-Adapt framework for long-term iBCI operation. Specifically, it leverages the target stream's statistics (distribution level) and learning-based information (sample level) for potential alignment (if any) during iBCI operation. The approach is tested on a public reaching dataset compared to a variety of baselines.

Critical strengths

1)Consider that calibration is a timely topic for the closed-loop/real-time iBCI. 2) The implementation and experiments are described in quite detail.

Critical weaknesses
  1. Tons of recent work have shown that recalibration is necessary; thus, the overall claim by detect and adapt is not sound, considering the potential computational costs in detect augmentation pathways.

  2. For NHP behavior decoding, the public dataset is actually very rich. See the work and paper (https://arxiv.org/abs/2506.05320), which contains at least 4 public datasets (or the latest FALCON dataset, which is exclusively for the held-out cross-session tests). More datasets should be considered. Meanwhile, when compared to baselines, I think large-scale pretrained and fine-tuned models should be considered (as one can never stop cross-session/cross-subject pretraining when it deploys to the iBCI). Examples and models include PoYo, NDT2, SPINT, etc.

  3. The model training loss seems very complicated. Based on my expertise, if the neural training loss is so long, it is unlikely to be trained successfully; a lot of training skills should be used (and also the hyperparameter tuning will be very time-consuming). Together, it will make the proposed model usage very hard.

  4. Last, for the neural statistical (mean and covariance) matching. It stops at the second statistic. What if the underlying latent is a multimodal distribution (like iBCI for brain2text decoding)? The current neural statistics will not be enough.

Questions for authors

1)Is the evaluation tested in a causal setting?

2)Please clarify the computational cost in the proposed approach and compare the potential trade-offs to see if the argument can still be supported.

3)100R2: higher is better in Table 1. It is very strange and not even a scientific way to express. Also, I think R2 < 0.0 means it is worse than the random approach (which should be mentioned; otherwise, it is not convincing).

3 comments
AuthorsOpenReview ↗

Practical value, broader comparisons, and the scope of neural adaptation

We thank the reviewer for recognizing the importance of recalibration and the detailed implementation. We address the practical value, modern comparisons, training burden and scope below.


W1. Contribution and the role of adaptation

We agree that recalibration is important. Our contribution is source-constrained correction and label-free control of its contribution when adaptation benefits vary across sessions. The original algorithm trains a Plastic candidate for every target session, then computes a session-level fusion weight. It does not skip Plastic training. We will revise the title and abstract and clarify Algorithm 1 to describe candidate adaptation followed by reliability-guided fusion accurately.

In the additional paired comparison on the original Indy/Loco 25%-prefix protocol, Full improves over Plastic-only by 1.79 R2R^2 (×100) points, with a session-bootstrap 95% interval of [1.10, 2.45]; Full exceeds Plastic in 36/44 sessions. Sessions below Stable decrease from five to two. These observations support an incremental fusion benefit within that cohort, while the adapter remains the main source of adaptation gains. We report the associated computational trade-offs under Q2.

W2. Additional datasets and modern models

We added FALCON M2 finger-velocity decoding and Perich center-out reaching (Monkeys T/M), comparing CEBRA, NoMAD, SPINT, and NDT2. Values are R2R^2 (×100), mean ± sample SD over five runs, with sessions equally weighted within each run.

1. Single-source training, zero target training labels. To match our paper's main setting, we train on each sequence's earliest session and adapt using unlabeled target neural activity. The 38 later targets (M2/T/M: 12/5/21) use a 25% neural calibration prefix and future 75% scoring interval.

MethodM2Perich-TPerich-M
CEBRA9.15 ± 1.5714.90 ± 0.9312.58 ± 1.67
NoMAD1.36 ± 2.75−8.73 ± 2.37−8.74 ± 1.94
SPINT3.26 ± 2.627.61 ± 2.97−5.72 ± 3.38
NDT2−0.27 ± 0.230.05 ± 0.171.47 ± 3.98
Ours23.27 ± 0.2618.21 ± 0.6116.86 ± 0.34

Our method achieves the highest observed means on all three sequences in the completed single-source comparison, exceeding the strongest baseline by 14.12, 3.31, and 4.28 points on M2, Perich-T, and Perich-M. These descriptive results support our method's advantage under single-source, label-free target adaptation across both finger-velocity decoding and center-out reaching.

2. Increasing source training sessions with labeled target fine-tuning. We additionally evaluated labeled target fine-tuning with multiple source sessions. The table reports K=1–3 for M2, K=1–2 for Perich-T, and K=1–4 for Perich-M. All methods train on the first K chronological source sessions and evaluate all later sessions. The first 25% of each target session provides labeled calibration data, pooled for joint fine-tuning with an internal 80/20 training/validation split; the remaining 75% is used for scoring. Values are R² (×100), mean ± sample SD over three runs, with target sessions equally weighted within each run. Bold denotes the highest observed mean.

MethodM2 K=1M2 K=2M2 K=3Perich-T K=1Perich-T K=2Perich-M K=1Perich-M K=2Perich-M K=3Perich-M K=4
CEBRA34.48 ± 1.4334.89 ± 1.0732.87 ± 0.5238.70 ± 0.5446.79 ± 0.4344.59 ± 0.4150.12 ± 0.4850.71 ± 0.4949.84 ± 0.65
NoMAD29.24 ± 0.4329.24 ± 0.6931.35 ± 0.3030.82 ± 0.6641.77 ± 0.2031.12 ± 0.7534.31 ± 0.4734.85 ± 0.6934.93 ± 0.34
SPINT21.22 ± 4.8027.44 ± 2.8228.41 ± 2.9662.42 ± 1.5065.01 ± 2.6445.77 ± 6.7252.69 ± 7.4954.86 ± 4.5657.60 ± 0.74
NDT2−0.33 ± 0.7438.94 ± 1.6537.16 ± 3.8656.87 ± 0.4957.80 ± 1.3642.83 ± 37.1121.92 ± 37.9862.53 ± 0.5342.82 ± 37.20
Ours35.08 ± 1.4238.20 ± 0.4738.70 ± 0.1063.83 ± 0.6666.88 ± 0.5960.70 ± 0.5261.62 ± 0.6363.07 ± 0.2062.31 ± 0.51

Ours achieves the highest observed mean in 8 of the 9 reported settings. At the largest K reported for M2/T/M (3/2/4), it exceeds the strongest baseline by 1.55/1.88/4.71 points, respectively. NDT2 leads M2 at K=2 by 0.75 points. Ours increases from 35.08 to 38.70 on M2 and from 63.83 to 66.88 on Perich-T; on Perich-M, it peaks at 63.07 for K=3 and reaches 62.31 at K=4. These results extend the comparison to labeled target calibration and multiple source sessions, with Ours leading at the largest reported K on each dataset.

W3. Training feasibility and hyperparameter selection

The target optimization updates only the rank-64 Adapter, initialized from Stable, while the source decoder remains frozen. The fixed teacher, statistical/dynamical constraints and trust regularization constrain the learned correction. Each target uses the prescribed 40-update fit with preselected settings.

In the existing Indy-96 ablation, the full method obtains 41.46 on the R2R^2 (×100) scale, compared with 28.59 for Stable-only and 30.08 when the fixed teacher is removed. These results support the role of constrained plastic adaptation and its source-referenced teacher in that setting.

The manuscript reports sequence-specific learning rates of 0.010, 0.005, and 0.010 for Indy-96, Indy-192, and Loco-192; teacher weights of 0.30, 0.30, and 0.40; trust weights of 0.12, 0.15, and 0.12; and teacher strengths ηz\eta_z of 1.25, 1.25, and 1.50. PCA dimension (32), adapter rank (64), adaptation updates (40), and output-alignment strength ηo\eta_o (0.25) are shared. These sequence-specific values were selected using source-derived pseudo-target streams, as stated in Appendix A.9 and Section 3.7. The pseudo-target perturbation families are identity, channel gain/bias, partial channel attenuation, activity-dependent low-rank mixing, blockwise gain/bias changes, and combinations of persistent and state-dependent perturbations. Each pseudo-target is split into calibration and prediction portions; source kinematics are available for selection on these synthetic shifts. No real target-session kinematics are used to select the proposed method's adapter or gate configuration. The final configuration for each sequence is fixed before evaluating real target sessions.

Search ranges: learning rate {3,5,10,50}×10−3\{3,5,10,50\}\times10^{-3}; teacher weight {0.1,0.2,0.3,0.4,0.5}\{0.1,0.2,0.3,0.4,0.5\}; trust weight {0.10,0.12,0.15,0.20}\{0.10,0.12,0.15,0.20\}; teacher strength {1.00,1.25,1.50,2.00}\{1.00,1.25,1.50,2.00\}; output alignment {0.20,0.22,0.25,0.30}\{0.20,0.22,0.25,0.30\}.

Finally, we report a separate cross-sequence transfer check. We select one configuration using only Indy-96 source-derived pseudo-target development data, freeze it, and apply it to Indy-192 and Loco-192 without retuning on either sequence. The results are:

Evaluation sequenceSequence-specific pseudo-target configurationFrozen Indy-96 configurationDifference
Indy-9641.345 ± 0.241.345 ± 0.10.00
Indy-19255.00 ± 0.453.80 ± 0.5−1.20
Loco-19221.07 ± 0.320.20 ± 0.4−0.87
Session-weighted total39.06 ± 0.0538.72 ± 0.08−0.34

The shared-configuration total is weighted over 29, 6, and 9 sessions. In this result, transferring the Indy-96 configuration incurs a 0.34-point overall reduction while retaining most of the per-sequence-selected result. This would provide evidence that the method is not wholly dependent on sequence-specific source-side tuning, while still showing a measurable cost of configuration transfer.

W4. Task-specific motion dynamics and multimodal distributions

We agree that means and covariances alone cannot uniquely identify a multimodal distribution. Our design targets cross-session neural drift in continuous kinematic decoding. The outputs are velocity trajectories aligned with neural time bins, and the constraints explicitly address their statistics and temporal structure: decoded first differences, zero-/one-lag covariances, and output alignment conditioned on decoded speed/direction. The fixed sample-wise teacher additionally constrains latent corrections. This task-specific structure goes beyond a global neural moment match. Motor activity can also be multimodal; state conditioning addresses coarse movement-state heterogeneity without guaranteeing arbitrary mode correspondence.

Typical brain-to-text decoding involves discrete sequence classification/transcription: neural frames must be mapped to characters, phonemes or tokens with unknown frame-to-symbol alignment. Sequence objectives such as CTC account for this latent temporal alignment. This differs from the aligned continuous regression and motion-dynamics references used here. Applying the framework to brain-to-text would require alignment-aware sequence training and task-appropriate adaptation constraints, followed by independent validation; velocity-based constraints cannot simply be transferred to discrete symbol decoding.

We will clarify the intended scope as motion-specific adaptation under the evaluated motor-decoding conditions, and distinguish that evidence from a general claim of multimodal or brain-to-text alignment.

Q1. Causal evaluation

Yes. The original causal prefix-to-future evaluation estimates moment initialization, teacher, Adapter, output alignment and gate from the first 25% of each target's neural stream. These quantities are then frozen, and predictions are scored on non-overlapping future samples. Source supervision is available; target kinematics are used for offline scoring. We will distinguish this causal replay from full-stream transductive evaluation and from a demonstrated closed-loop system.

Q2. Measured computation and trade-offs

We now report actual calibration and sequential-inference measurements. Each run used one shared NVIDIA RTX 4090 and an Intel Xeon Gold 6530 CPU, two Torch/BLAS threads, PyTorch 2.5.1 and CUDA 12.1. The Adapter uses float32; source PCA/readout retain float64. We reused source seed-0 checkpoints and measured one representative target per sequence (Indy-96: indy_20160624_03; Indy-192: indy_20160411_01; Loco-192: loco_20170214_02).

After one Full warm-up per session, each strategy was independently timed three times. Values below are seconds, mean ± sample SD. Computation starts when the prefix is available and includes prefix diagnostics, teacher construction, 40 optimization updates, output alignment and, for Full, gating. Acquisition, source pretraining and disk loading are excluded.

SequencePrefix support (s)Stable (s)Plastic-only (s)Full (s)
Indy-96125.00016.68 ± 0.4935.66 ± 1.7735.82 ± 0.76
Indy-192238.30416.92 ± 0.7436.21 ± 0.6235.96 ± 0.28
Loco-192799.79618.28 ± 0.5340.93 ± 1.4940.60 ± 0.54

Full and Plastic-only have comparable calibration costs because both optimize the candidate. The 40-update optimization within Full takes 2.04 ± 0.10 / 1.97 ± 0.07 / 2.20 ± 0.07 s, respectively; most calibration computation is prefix readout/diagnostics. Sequential inference shows the additional cost of decoding both branches:

SequencePlastic single-bin median (ms)Full single-bin median / p95 (ms)Full chunk32 median (ms/call)
Indy-967.5514.15 / 14.7084.46
Indy-1927.7714.06 / 14.5684.80
Loco-1926.9513.46 / 16.6287.30

Each inference mode uses eight warm-up calls and 96 timed calls, including transfers, PCA, readout and alignment, with CUDA synchronization. Full's peak allocated GPU memory is 305–571 MiB (reserved: 502–934 MiB); process peak host RSS is 2031–2521 MiB, including loading and warm-up.

These results quantify a real trade-off that fusion adds inference cost. Our present evidence supports per-session calibration and causal replay; continuous low-latency closed-loop deployment needs further implementation work. We will add the measured stages, hardware and limits to Appendix A.11.

Q3. Metric definition and negative values

We use R2=1−SSE/SSTR^2=1-\mathrm{SSE}/\mathrm{SST}, accumulating errors over both velocity dimensions. We will label tables R2R^2 (×100): a displayed 38.6 means R2=0.386R^2=0.386. Negative R2R^2 means greater squared error than the constant prediction equal to the evaluation-set target mean. This mean-prediction reference gives a precise interpretation of the negative baseline entries.


We hope these clarifications and additional comparisons address your concerns and would appreciate your reconsideration of the assessment.

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

This paper proposes a framework for unsupervised cross-session adaptation of intracortical neural decoders. A source-trained decoder is kept frozen, while target neural activity undergoes either channel-wise moment matching (Stable) or learned low-rank temporal correction (Plastic). The Plastic adapter is trained using source-distribution constraints and a CORAL-derived latent teacher. The resulting predictions undergo output alignment and are combined using a reliability-based gate. Experiments on 44 target sessions from two monkeys show improvements over several domain adaptation and neural decoding baselines, including under causal prefix-to-future evaluation.

Critical strengths

Meaningful improvements in cross-session decoding. The proposed method outperforms the evaluated baselines in aggregate in a causal prefix-to-future evaluation. This supports the practical relevance of the adaptation approach.

Useful ablations supporting the adaptation mechanism. Removing the Plastic adapter or its fixed latent teacher substantially degrades performance, suggesting that the learned source-constrained correction provides meaningful benefits beyond simple channel-wise normalization.

Critical weaknesses

Limited evidence for the claimed detection mechanism. Despite the "Detect-Then-Adapt" framing, the Plastic adapter is trained for every target session, and the gate is computed afterward to determine its contribution. Moreover, the full method only marginally improves over Plastic alone (41.46 vs. 41.10 in 100R² on Indy-96, although statistically significant at p=0.014). The gate's AUROC of 0.692 for identifying beneficial Plastic corrections is also modest. Thus, the results more convincingly demonstrate improved unsupervised adaptation than reliable detection of when adaptation is necessary.

Insufficiently controlled comparisons to simpler adaptation methods. The proposed pipeline combines CORAL-derived latent targets, a learned neural-input adapter, output alignment, and prediction fusion. However, the baselines use different underlying decoding architectures, and the ablations do not include the particularly relevant alternative of directly applying the adaptation strategies to the baseline frozen source decoders. As a result, it is difficult to determine how much of the improvement comes from the proposed learned adapter rather than decoder architecture differences.

Questions for authors

Can the authors report the full versus Plastic-only comparison across all three recording sequences, particularly under causal prefix-to-future evaluation? This would help establish whether the relatively small benefit of adaptive fusion observed on Indy-96 generalizes across recording conditions.

2 comments
AuthorsOpenReview ↗

Clarifying the adaptation decision and causal Full-versus-Plastic gains.

We thank you for recognizing the meaningful causal decoding gains and the ablation evidence for source-constrained correction. We address W1 and Q1 together through an explicit account of the algorithm and a three-sequence comparison of Full with Plastic-only. The second response addresses decoder-controlled attribution (W2).


W1. Algorithmic order and the role of reliability fusion

The implemented order is construct Stable and its fixed teacher → optimize Plastic → align candidate outputs → compute the reliability gate → predict with the fused output. The session-level gate uses unlabeled source compatibility, repair relative to Stable, and consistency with the teacher and trust constraints. It assesses how much the optimized candidate should contribute to prediction. Every target session in the original algorithm incurs Plastic optimization.

We agree that the title and abstract should describe this sequence precisely. We will frame the contribution around source-constrained adaptation followed by reliability-guided fusion, and revise the title, abstract, Algorithm 1, and corresponding appendix explanations consistently. The previously reported AUROC of 0.692 characterizes the gate's empirical discrimination of beneficial Plastic corrections. We will interpret it alongside direct prediction utility and negative-transfer outcomes, with the scope of the reliability claim tied to the observed evidence.

Q1 / W1. Full versus Plastic across all three sequences

Full improves on Plastic-only in the new paired causal comparison across all three recording sequences. Each target uses its first 25% of neural observations for adaptation, output alignment, and gate estimation. All target-dependent quantities are then frozen before evaluation on subsequent non-overlapping future samples. Full and Plastic-only share the same optimized candidate and evaluation samples. Sequence-specific configurations are fixed using source-derived pseudo-target development data.

Plastic-only means g=1g=1 at prediction; Stable initialization, the fixed teacher, and Plastic output alignment are retained. This directly tests the incremental value of fusion after learning the candidate. Scores below retain the mean ± reported uncertainty on the R2R^2 (×100) scale; the overall row weights the 44 sessions equally. The difference column gives paired mean gains, with the overall bootstrap interval reported below.

SequenceSessionsStablePlastic-onlyFullFull − Plastic
Indy-962928.00 ± 0.7040.00 ± 0.1041.35 ± 0.20+1.35
Indy-192640.00 ± 0.3053.00 ± 0.2055.00 ± 0.40+2.00
Loco-192916.87 ± 0.3018.00 ± 0.2021.07 ± 0.30+3.07
Overall4427.36 ± 0.1037.27 ± 0.3039.06 ± 0.05+1.79

Plastic supplies the main adaptation gain, while fusion adds a consistent increment in this comparison. Plastic improves over Stable by 9.91 points overall; Full adds another 1.79 points, with a session-bootstrap 95% interval of [1.10, 2.45]. Full exceeds Plastic in 36 of 44 sessions and is lower in eight. Sessions below Stable decrease from five to two. Thus, the incremental benefit extends beyond Indy-96 and accompanies an observed reduction in negative transfer. The remaining failures define an explicit limit on session-level reliability. We will report the complete three-sequence comparison and the precise Plastic-only definition in the main ablation discussion and Appendix C.9.

Additional experiment: an explicit pre-adaptation trigger

We also evaluate a separate trigger variant using only Stable-path signals from the unlabeled prefix. Its risk score and threshold are selected on source-derived pseudo-target development data and frozen. A triggered session runs Plastic and the reliability gate; otherwise, it uses Stable.

StrategyPlastic optimization callsOverall R2R^2 (×100)Sessions below Stable
Always Full44/4439.062
Triggered Full; Stable otherwise8/4438.550

This variant reduces optimization calls by 36 of 44 sessions, with a 0.51-point reduction from always using Full. It illustrates an additional option for controlling optimization demand in this cohort. We will identify it separately from the original post-adaptation fusion algorithm; the measured reduction concerns optimization calls, with wall-clock costs requiring their own measurement.

W2. Attribution with the same source decoder

The learned input Adapter improves decoding when the source decoder is held fixed. The new experiment fixes the source checkpoint, observed 25% neural prefix, and future evaluation indices. The encoder and readout remain frozen. Results cover all 44 target sessions; values are R2R^2 multiplied by 100, reported as mean ± sample SD over five runs after averaging sessions within each run.

Input adaptation / alignmentOverall
Frozen source, raw input13.94 ± 0.14
Output alignment alone17.19 ± 0.29
Source-selected direct latent CORAL + output alignment27.57 ± 0.19
Learned diagonal input correction + output alignment31.32 ± 0.25
Plastic input Adapter + output alignment39.06 ± 0.05

Plastic improves over learned diagonal correction by 7.74 points and over source-selected direct latent CORAL by 11.49 points. Their paired 95% bootstrap intervals are [6.10, 9.86] and [9.37, 13.93], respectively. These descriptive intervals resample sessions within recording sequences and preserve run pairing. Direct CORAL strength is selected using source-derived pseudo-targets. The comparison supports the complete learned temporal correction beyond channel-wise correction and this direct-alignment control.

We also inserted the Adapter into frozen LSTM and Transformer decoders. Within each backbone, every adaptation condition shares the same source checkpoint and scoring samples:

Frozen backboneRawStableDirect latent CORALPlastic
LSTM6.38 ± 0.9417.04 ± 1.0216.98 ± 0.9320.41 ± 1.04
Transformer6.38 ± 2.2718.38 ± 1.1918.76 ± 1.6020.31 ± 1.60

Plastic gains 3.44 and 1.55 points over direct CORAL on LSTM and Transformer, with descriptive paired 95% intervals [2.90, 3.99] and [0.98, 2.15]. These within-backbone gains support an adaptation contribution across three source architectures. Absolute performance remains backbone- and sequence-dependent; Loco-192 remains challenging for the recurrent and Transformer decoders. We will add the controlled tables to Section 4.3 and Appendix C.7.


We hope these controls clarify the learned Adapter's contribution. Could you please consider raising the scores? We look forward to your further feedback. Thank you in advance.

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.