Applications of Machine Learning in NIRS-Based Assessment of Cerebral and Muscle Oxygenation for Motor Rehabilitation and Sports Training

Abstract

Machine learning (ML) applied to near-infrared spectroscopy (NIRS) signals has matured rapidly across cerebral functional NIRS (fNIRS) and muscle NIRS (mNIRS) in motor rehabilitation and sports training, but the two fields have evolved in parallel without systematic integration. We conducted a PRISMA-aligned systematic review of 42 studies published between 2012 and 2026, applying PROBAST and TRIPOD + AI risk-of-bias and reporting appraisals. Studies covered cerebral fNIRS as a single modality (24 studies), cerebral fNIRS combined with electroencephalography or autonomic biosignals (nine studies), mNIRS as a single modality (seven studies), and mNIRS combined with surface electromyography (one study). In cerebral fNIRS, physiologically grounded feature engineering, task-dependent chromophore selection, attention-based architectures aligned with hemodynamic-response timescales, and subject-independent evaluation emerged as the principal methodological levers. Deep learning outperformed the specific traditional ML algorithms tested in each study by 10 to 25 percentage points, but only where sample sizes supported transfer learning or attention; no general advantage of deep learning over traditional ML was observed across the corpus. In mNIRS, common-mode/differential-mode physiological decomposition, time-frequency band separation, and per-subject calibration emerged as muscle-physiology-specific transformations with no direct cerebral counterpart. Reported accuracies of 97% to 99% in the muscle corpus were attributable to sliding-window validation strategies that violate train-test independence and should be interpreted in light of subject-wise validation gaps. The defining empirical observation of this review is that no included study recorded cerebral fNIRS and mNIRS jointly and in co-location, despite eleven studies adopting other forms of multimodal integration. The methodological building blocks for joint cerebral-muscle ML pipelines exist across the corpus and define the open methodological frontier for the field, with concrete validation in adaptive sport, stroke and spinal cord injury rehabilitation, and BCI-controlled assistive technology as the natural next step.

Keywords

Adaptive sport / Brain-machine interface / Deep learning / Muscle oxygenation / Neurovascular coupling

1 Introduction

Human movement and sports depend on the coordinated function of the cerebral cortex and skeletal muscle, where the cortex orchestrates motor planning and execution while skeletal muscle generates force and sustains metabolic activity [1,2]. Near-infrared spectroscopy (NIRS) provides a single optical principle for non-invasively interrogating both tissues, exploiting the differential absorption of oxygenated and deoxygenated hemoglobin in the 650–1000 nm window to quantify hemoglobin chromophore changes in cerebral cortex (functional NIRS, fNIRS) and skeletal muscle (muscle NIRS, mNIRS) using the modified Beer-Lambert law [3,4]. Compared with functional magnetic resonance imaging (fMRI), positron emission tomography (PET), and magnetoencephalography (MEG), NIRS imposes substantially fewer constraints on body posture, head fixation, and laboratory environment, and it offers acceptable temporal resolution and moderate spatial resolution while tolerating the motion that movement and exercise inevitably introduce [5–7]. These properties have enabled NIRS recordings during real walking, robot-assisted training, treadmill obstacle avoidance, surgical motor-skill assessment, and competitive endurance running, contexts in which alternative neuroimaging modalities fail [8–12].

Although cerebral and skeletal muscle oxygenation are measured with the same optical principle, they differ in tissue optics, anatomical accessibility, dominant noise sources, and physiological interpretation. Cerebral fNIRS records the hemodynamic response that follows local neuronal activation through neurovascular coupling, with a canonical 4 to 6 second delay, characteristic contralateral lateralization for unilateral motor tasks, and high susceptibility to systemic-physiological confounds at the prefrontal scalp [13–15]. Cortical organization permits topographical mapping across motor, premotor, supplementary motor, somatosensory, prefrontal, and parietal regions, and supports graph-theoretical and network analyses [16–18]. mNIRS instead reflects the local supply-demand balance between oxygen delivery, capillary perfusion, mitochondrial oxidative capacity, and motor-unit recruitment, with the signal weighted toward the venous and capillary compartments and integrating contributions from both hemoglobin and myoglobin [19,20]. Muscle contraction simultaneously produces blood-flow changes that generate a positive HbO₂–HHb correlation and oxygen-consumption changes that generate a negative correlation, so signal-improvement methods developed for cerebral fNIRS can discard physiologically meaningful information when applied to muscle [21]. Spatial heterogeneity within and between muscles, adipose tissue thickness, skin pigmentation, and contraction-induced motion artifacts further distinguish the muscle-NIRS analytic problem from its cerebral counterpart [22].

Across both tissues, NIRS produces data that are simultaneously high-dimensional, contaminated by multiple noise sources, and substantially variable across individuals [23–25]. Modern arrays now reach 60 to 100 optical channels, and feature spaces routinely exceed 200 candidate variables per recording [16,26]. Raw signals contain physiological oscillations from cardiac activity, respiration, and Mayer waves, instrumental drift, motion artifacts, and superficial-tissue contributions that share frequency content with the task-related signal [13,27,28]. Inter-individual variability in skull thickness, optical path length, adipose tissue thickness, and skin pigmentation further modulates the measured signal, and the canonical hemodynamic response function may be misspecified for individual subjects and disrupted in clinical populations [17,22,29]. Conventional analysis pipelines that rely on block-averaged amplitude statistics or general linear modelling against a canonical hemodynamic response function were developed for cued, stationary, group-level paradigms and struggle with the dimensionality, non-stationarity, and individual variability of NIRS data acquired during dynamic movement [12].

Machine learning (ML) addresses these limitations by offering principled approaches to high-dimensional pattern recognition, automatic feature learning, multimodal fusion, individualized modelling, and continuous-output prediction [23,30]. Applications have matured rapidly. Early classical-ML feasibility studies between 2012 and 2018 established that support vector machines (SVM), artificial neural networks, and hidden Markov models could decode motor execution and motor imagery from cerebral fNIRS and classify peripheral oxygenation patterns from mNIRS [28,29,31]. Between 2018 and 2022, deep learning architectures including convolutional and recurrent neural networks began to outperform classical ML on the same datasets, hybrid electroencephalography (EEG)-fNIRS and surface electromyography (sEMG)-fNIRS systems extended the measurable repertoire, and interpretable models with shapley additive explanations (SHAP) and saliency-based attribution emerged [5,14,32,33]. Since 2022, attention-based architectures, multilayer brain networks with neurovascular-coupling-defined inter-layer edges, and clinically translatable digital-therapeutic pipelines have proliferated, and the populations under study have expanded from healthy young adults to stroke, Parkinson’s disease, multiple sclerosis, cerebral palsy, spinal cord injury, transhumeral amputees, older adults, and competitive athletes [12,17,26,34,35]. Across studies, deep learning has typically outperformed classical ML when sample sizes are sufficient, although simple linear models can perform comparably on standard benchmarks, and headline accuracy figures often reflect optimistic evaluation rather than genuine generalization [24,36]. Movement science and motor-task rehabilitation require physiologically plausible, transparent, and clinically actionable models rather than black-box predictors, making interpretability a central concern alongside predictive accuracy.

Existing reviews have addressed substantial parts of this landscape, with separate syntheses of fNIRS deep learning [23], fNIRS in clinical diagnostic ML [24], fNIRS in exercise-cognition science [13,37], and muscle oximetry in sports science [20,38]. These reviews share a single-tissue scope: each treats either cerebral fNIRS or mNIRS in isolation, leaving three questions unaddressed that this review takes as its remit. First, which ML strategies developed for cerebral fNIRS transfer to mNIRS, and which fail because cerebral analytical assumptions discard physiologically meaningful information at the muscle site? Second, what is the methodological state of ML applied to each tissue separately, given that motor rehabilitation and sports training depend on the coordinated function of cortex and muscle, not on either compartment in isolation? Third, which methodological components distributed across the separate cerebral and muscle literatures could constitute a joint cerebral-muscle ML pipeline, in which co-located cerebral fNIRS and mNIRS recordings are analyzed together to characterize the brain-muscle axis directly? This review therefore investigates how ML has been applied to NIRS-based cerebral and muscle oxygenation research to advance the assessment, prediction, and support of motor-task rehabilitation and sports training in humans. Within this primary objective, we pursue three sub-objectives. First, we characterize ML applications to cerebral fNIRS in human movement and exercise contexts and identify the algorithmic, feature-engineering, and interpretability strategies that respect cerebral-tissue physiology. Second, we characterize ML applications to mNIRS in human movement and exercise contexts and identify the strategies that respect skeletal-muscle physiology. Third, we synthesize across both sub-objectives to identify the methodological convergences and divergences between cerebral and mNIRS-ML, to identify the methodological components distributed across the two separate literatures that could constitute a future joint cerebral-muscle pipeline, and to propose an integrated framework for such a pipeline: simultaneous co-located cerebral fNIRS and mNIRS recording paired with ML-based fusion. Because the corpus contains no study recording both tissues jointly, this third sub-objective is necessarily constructive rather than descriptive.

2 Methods

2.1 Protocol and registration

This systematic review was conducted in accordance with the Preferred Reporting Items for Systematic Reviews and Meta-Analyses (PRISMA) 2020 statement [39]. Because the present review searches a heterogeneous, rapidly evolving methodological literature spanning biomedical, engineering, and computer-science databases, where reproducibility of the search itself is a known weakness, we additionally followed the PRISMA-S extension [40] to ensure transparent and reproducible reporting of database-specific syntax, controlled vocabulary, and filters. The protocol was prospectively registered with the International Prospective Register of Systematic Reviews (PROSPERO; registration number: CRD420261380936) prior to the start of screening.

2.2 Eligibility criteria

Because this review evaluates prediction models rather than therapeutic interventions, eligibility was defined using the PICOTS framework (Population, Index model, Comparator, Outcomes, Timing, Setting) recommended by CHecklist for critical Appraisal and data extraction for systematic Reviews of prediction Modelling Studies (CHARMS) [41] for the systematic appraisal of prediction-model studies. PICOTS is better suited than the conventional PICO scheme for ML/prediction-model reviews because it explicitly captures Timing (concurrent decoding vs. prospective prediction) and Setting (laboratory, clinical, or sport-specific recording context), both of which are central to determining whether a NIRS-based ML model is generalizable to motor-task rehabilitation and sports training.

Inclusion criteria include: (i) Population: human participants of any age, including healthy individuals, clinical populations relevant to motor rehabilitation, and athletes; (ii) Prediction models: classical, deep, or interpretable machine-learning models applied to continuous-wave, frequency-domain, or time-domain NIRS measurements of cerebral cortex (fNIRS) and/or skeletal muscle (mNIRS as defined above), with multimodal recordings (e.g., EEG-fNIRS, sEMG-NIRS) eligible provided NIRS contributed to the model input; (iii) Comparator: any or none; (iv) Outcomes: at least one quantitative model-performance metric (e.g., accuracy, sensitivity, specificity, F1, AUC, RMSE); (v) Timing: concurrent decoding and prospective prediction both eligible; (vi) Setting: laboratory, clinical, or sport-specific recordings during human movement, motor tasks, motor imagery, or exercise; and (vii) Study design: original peer-reviewed empirical studies in humans, published in English from database inception to April 2026.

Exclusion criteria include: studies using animal, in vitro, or simulation-only data; NIRS applied outside cerebral or skeletal-muscle oxygenation (e.g., tumor spectroscopy, agricultural NIRS); analyses without ML; resting-state, cognitive, or affective paradigms without a motor or exercise component; reviews, editorials, commentaries, conference papers, theses, and book chapters (used only for citation tracking); studies with no retrievable full text after two author-contact attempts; and preprints or otherwise non-peer-reviewed manuscripts.

2.3 Search strategy

Searches were executed across six databases: PubMed, Embase, Web of Science, Scopus, IEEE Xplore, and the Cochrane Library. The strategy combined three concept blocks with Boolean AND, with terms within each block joined by OR. Block 1 (NIRS modality) included “near-infrared spectroscopy”, “near infrared spectroscopy”, NIRS, fNIRS, “functional near-infrared”, mNIRS, “muscle oximetry”, “tissue oximetry”, “cerebral oximetry”, “muscle oxygenation”, SmO₂, StO₂, TOI, and TSI. Block 2 (computational approach) included “machine learning”, “deep learning”, “artificial intelligence”, “neural network*”, “convolutional neural*”, CNN, RNN, LSTM, transformer, “support vector*”, SVM, “random forest*”, XGBoost, “gradient boost*”, “hidden Markov*”, “explainable AI”, XAI, SHAP, “attention mechanism”, and “graph neural network*”. Block 3 (movement and exercise context) included motor, movement, gait, walking, running, cycling, exercise, training, rehabilitation, “motor imagery”, “motor execution”, “brain-computer interface”, BCI, “brain-machine interface”, neurorobotic, athlete*, and sport*. Searches were filtered to humans, English language, and journal articles. Database-specific syntax (MeSH, Emtree, and controlled vocabulary with field tags) is provided in full in Supplementary Appendix S1, following PRISMA-S [40].

2.4 Study selection

Records were exported to EndNote and deduplicated. Title/abstract and full-text screening were each performed independently in duplicate by two reviewers (J.L. and Y.D.), blinded to each other’s decisions in separate EndNote libraries and reconciled in a master library after each stage. Disagreements were resolved by discussion, with the corresponding author (Y.-K.J.) adjudicating any unresolved cases.

2.5 Data extraction

A standardized Microsoft Excel form was used. Two reviewers (J.L. and W.C.C.) extracted data independently in duplicate, with discrepancies resolved by discussion and Y.-K.J. adjudicating. Study authors were contacted by email (up to two attempts, two weeks apart) when key methodological information was missing; unresolved items were recorded as “not reported.”

Extracted variables spanned eight domains: (i) study identification (identifier, first author, year, journal, country); (ii) review classification (NIRS modality: cerebral fNIRS, mNIRS, or hybrid; section assignment; tissue site); (iii) population and exercise context [population type, sample size, age/sex, exercise or motor task, task context, timing of prediction (concurrent decoding vs. prospective prediction), and recording setting (laboratory, clinical, or sport-specific)]; and (iv) NIRS acquisition hardware (CW/FD/TD mode, device, emitter/detector counts, source-detector separation, wavelengths, sampling rate, channel layout, bimodal synchronization); (v) NIRS signal processing [modified Beer-Lambert conversion with reported DPF, bandpass and motion-artifact parameters, short-separation regression, signal-improvement transforms [correlation-based signal improvement (CBSI), differential-based signal improvement (DBSI)], signals used (ΔHbO, ΔHbR, ΔHbT, TOI, TSI, StO₂, SmO₂)]; (vi) machine-learning approach and implementation (task type, target outcome, algorithm family, architecture specification with layer types, kernel sizes, attention dimensions, and parameter count, input features, loss function, optimizer with learning rate and batch size, regularization, validation strategy with subject-wise versus window-wise splitting, hyperparameter tuning, training time, inference latency, code availability); (vii) performance, interpretability, and deployment (metrics with values and confidence intervals, comparator algorithms, XAI method, tissue-level insight, real-time feasibility against sampling period, computational cost); and (viii) synthesis-level annotations (methodological strengths and limitations, relevance to simultaneous cerebral-muscle measurement, key findings).

Timing and Setting, the T and S elements of the PICOTS framework specified in Section 2.2, were extracted from the full texts of all 42 included studies following the primary extraction round. Timing was coded as concurrent decoding where the target label was measured within the same session as the NIRS recording, and as prospective prediction where the target label was measured at a later, separate time point; studies reporting separate models of each kind were coded as both. Diagnostic classification of an existing group or disease status was treated as concurrent decoding rather than prospective prediction. Setting was coded from the stated physical recording location as laboratory, clinical, sport-specific, mixed, or not reported. Recruitment source, ethics-approval institution, and author affiliation were not treated as evidence of recording setting. Where a study described the recording environment without naming it institutionally, and participants were volunteers tested under university ethics approval with no clinical care involved, Setting was coded as laboratory; where no recording location could be established, Setting was recorded as not reported.

2.6 Risk of bias and methodological quality appraisal

Risk of bias was assessed using The Prediction Model Risk of Bias Assessment Tool (PROBAST) [42] across its four domains (Participants, Predictors, Outcome, Analysis), with low/high/unclear judgments per domain and overall. To capture ML-specific reporting elements outside PROBAST’s scope, a complementary 10-item checklist informed by TRIPOD + AI [43] was applied alongside PROBAST. Items addressed: (i) participant flow and sample-size justification, (ii) missing-data handling, (iii) train/validation/test splitting (subject-wise vs. trial-wise), (iv) class balance and chance-level baseline, (v) feature engineering and dimensionality reduction, (vi) hyperparameter tuning, (vii) comparator models, (viii) external validation, (ix) calibration and uncertainty reporting, and (x) interpretability or explainability methods. The full checklist and scoring rubric are provided in Supplementary Appendix S2.

Both tools were applied independently in duplicate by two reviewers (J.L. and W.R.), with discrepancies resolved by discussion and Y.-K.J. adjudicating. PROBAST judgments are visualized as traffic-light and summary bar plots using the robvis R package [44] and reported alongside the synthesis (Section 2.7). Risk of bias is incorporated as a moderator in the narrative synthesis rather than used as an exclusion criterion.

2.7 Data synthesis

Results were synthesized narratively in three layers mirroring the three sub-objectives. Quantitative pooling was not undertaken because expected heterogeneity in target outcomes, performance metrics, validation strategies, and populations renders a common effect estimate uninterpretable; descriptive quantitative summaries (e.g., median performance by algorithm family stratified by population and task) complement the narrative where appropriate.

The first layer maps cerebral fNIRS studies across populations, paradigms, algorithm families, and interpretability strategies, identifying feature-engineering and architectural choices that respect cerebral-tissue physiology (neurovascular coupling, hemodynamic delay, lateralization, systemic-physiology confounds). The second layer maps mNIRS studies analogously, identifying strategies that respect skeletal-muscle physiology (supply-demand balance, capillary-venous weighting, adipose and skin-pigmentation effects, contraction-induced motion artifacts, and simultaneous flow and oxygen-consumption signal sources). Within each of the first two layers, studies were additionally characterized along two cross-cutting methodological dimensions: whether models were evaluated subject-dependently, training and testing on data from the same participants, or subject-independently, testing on participants held out entirely from training; and whether evaluation was offline, online, or pseudo-online. The third layer synthesizes across both to articulate convergent methodologies, tissue-specific divergences, and the methodological components that could constitute a joint cerebral-muscle ML pipeline for personalized motor-task rehabilitation and sports training. This layer was specified to inventory any studies recording cerebral and mNIRS jointly and the approaches used to integrate them; in the event that no such study was identified, the layer instead assembles the constituent components from the separate literatures and proposes an integrated framework.

Synthesis is supported by structured tables (study-level characteristics, ML methodology, interpretability and validation) and figures (temporal evolution of ML approaches in NIRS movement/exercise research; distribution of populations and tasks across algorithm families; a conceptual diagram of the joint cerebral-muscle pipeline). Risk-of-bias judgments from Section 2.6 are overlaid on the synthesis as moderating context rather than as quantitative weights.

3 Results

3.1 Study selection and characteristics

The database search retrieved 1711 records from PubMed (n = 131), Web of Science (n = 718), Scopus (n = 255), Embase (n = 126), IEEE Xplore (n = 472), and the Cochrane Library (n = 9). After removal of 584 duplicates and 231 ineligible publication types, 896 records underwent title and abstract screening, of which 761 were excluded. The remaining 135 reports were assessed in full text, and 93 were excluded with documented reasons, most commonly insufficient or absent machine-learning methodology, missing performance metrics, or non-eligible populations or paradigms. Forty-two studies met all eligibility criteria and were included in the qualitative synthesis. The full selection process is summarized in Fig. 1.

The 42 included studies, summarized in Table 1, were published between 2012 and 2026, with 83.3% (n = 35) appearing from 2020 onward. First-author institutions were concentrated in China (n = 18) [12,17,18,21,26,34,35,45–55] and the United States (n = 6) [6,8,10,33,56,57], with the remaining studies distributed across 17 other countries or multinational collaborations [5,7,9,11,14–16,28,29,31,32,58–64].

Per-study methodological characteristics for the 42 included studies are catalogued in Table 2. Cerebral functional NIRS dominated the corpus, used either as a single modality (n = 24) [5–8,10,11,15,16,18,29,33–35,45–47,50,52,54,57,60–64] or in hybrid pipelines combined with EEG (n = 8) [12,14,17,32,49,53,56,58] or autonomic biosignals (n = 1) [28]. mNIRS appeared as a single modality in seven studies [9,21,31,48,51,59,65] and in one further hybrid pipeline combining mNIRS with sEMG [26]; one additional study paired cerebral functional NIRS with sEMG of the biceps [61], representing the only included study with simultaneous cerebral and muscle physiological recording, although muscle activity was captured by electromyography rather than near-infrared spectroscopy. No included study reported a fully co-located cerebral-plus-mNIRS recording.

Healthy adults were the most common population (n = 23) [5,10–12,14,16,26,28,29,32–35,45–47,49,52,53,57,60,63,64], followed by clinical cohorts (n = 15) spanning stroke (n = 7) [15,17,18,21,51,54,62], Parkinson’s disease (n = 2) [50,56], multiple sclerosis (n = 1) [8], spinal cord injury (n = 1) [58], cerebral palsy (n = 1) [7], peripheral arterial disease (n = 2) [31,59], and limb amputation (n = 1) [61], with athletes (n = 2) [9,65] and older adults (n = 2) [6,48] represented in smaller numbers. Sample sizes ranged from 7 to 451 participants. Upper-limb motor and brain-computer-interface paradigms accounted for over half of the studies (n = 23) [14,15,17,18,21,28,29,32–35,47–49,53,54,56–61,64], followed by gait and locomotion paradigms (n = 11) [5–8,11,12,45,46,50,52,63], with the remainder examining cycling and endurance exercise (n = 4) [9,31,51,65], fatigue (n = 1) [26], postural control (n = 1) [16], multimodal rehabilitation (n = 1) [62], and surgical motor-skill tasks (n = 1) [10]. The distribution of NIRS modalities, populations, and motor-task paradigms across the 42 included studies is summarized in Fig. 2.

3.2 ML applications to cerebral fNIRS

Twenty-four studies applied ML to cerebral functional NIRS as a single modality [5–8,10,11,15,16,18,29,33–35,45–47,50,52,54,57,60,62–64]; nine further studies combined cerebral fNIRS with EEG [12,14,17,32,49,53,56,58] or autonomic biosignals [28] and are addressed in Section 3.4.

3.2.1 ML task taxonomy

Binary classification of motor states was the dominant formulation, encompassing walking versus rest [11,52,63], left-versus-right hand movement [29], hand-movement direction [64], hand opening versus closing [15], and self-paced walking-intention onset [46]. Two studies recast clinical-population stratification as a binary problem (Parkinson’s disease versus controls during dual-task walking [50]; FMA-UE severity in chronic stroke [62]), and two further studies dichotomized continuous outcomes for prediction of rehabilitation responders, using a 75-point modified Barthel index cutoff [54] and a 9-point ΔFMA-UE threshold [18]. Multi-class classification appeared in seven studies, ranging from three-class motor execution and imagery [6,35], three-class finger-opposition [60], and tri-class velocity discrimination [57] up to four-class gait-adjustment intentions [45], four-class sensory conditions [16], and five-class fine-motor complexity [34]. Sommer et al. introduced a novel multi-label formulation in which left and right motor cortex labels were each independently assigned one of three finger-tapping frequencies [33]. Continuous regression appeared in four studies, predicting GMFM-88 motor function in children with cerebral palsy [7], FMA-UE scores at discharge in stroke [18], surgical FLS scores [10], and continuous gait parameters [52]. A separate axis cut across all formulations. The first dimension is subject-dependent versus subject-independent modelling: subject-dependent models are trained and tested on data from the same participants, whereas subject-independent models are tested on participants entirely held out from training, and therefore characterize performance on new users without per-user retraining. This contrast was explicit in four studies [10,29,35,60]. The second dimension is online or pseudo-online evaluation: online evaluation classifies the signal as it streams during the recording session, while pseudo-online evaluation replays previously recorded data through the classification pipeline in simulated real time, preserving causal access to past samples only. Five studies implemented one or the other [11,29,45–46,63].

3.2.2 Algorithm families

Three regularities about which algorithm families work for which conditions emerge from the cerebral fNIRS corpus and inform the methodological choices reported below. First, low-capacity classifiers [linear discriminant analysis (LDA), kernel SVM] outperform deep architectures when sample size falls below approximately 30 subjects, because higher-capacity models lack the data to learn task-general features and instead overfit to subject-specific session signatures; this pattern is direct in Khan et al.’s selection of LDA over polynomial-kernel SVM for online prosthetic-leg deployment despite the latter’s higher offline accuracy [11], and in Lu et al.’s linear SVM matching deep alternatives on Parkinson’s disease classification with balloon-model features [50]. Second, tree-based ensembles, particularly LightGBM, occupy a productive middle ground for large point-by-point classification on continuous streams, where the per-sample inference cost O(M · log n) remains tractable and native feature importance supports interpretability without post-hoc explainers, as demonstrated by Li et al.’s ~180,000-sample walking-intention detection [46] and Baradaran et al.’s sensory-condition classification [16]. Third, attention-based architectures earn their place specifically when the temporal structure of the hemodynamic response is the analytical target rather than its average amplitude, but require sample sizes (n ≥ 30 with attention regularization, n ≥ 50 for transformer-style) that the corpus only sometimes provides; IVCAN’s curve-attention module [35] and Ji et al.’s attention-augmented Bi-LSTM [34] illustrate productive uses, while ImageNet-pretrained vision transformers [6] illustrate that transfer learning can substitute for sample size in some imaging-style reformulations. The choice of algorithm family is therefore conditioned on three factors more than on architectural sophistication: the sample size available, whether the analytical target is spatial-channel structure or temporal hemodynamic structure, and the deployment hardware constraint.

The cerebral fNIRS corpus spans the full spectrum of supervised learning, from low-capacity linear classifiers appropriate to small samples, through tree-based ensembles for large point-by-point datasets, to deep architectures with self-attention for high-dimensional spatiotemporal data. We organize the corpus into six algorithm families and provide formal definitions of the dominant variant in each, followed by a comparative analysis (Table 3) summarizing data-regime requirements, computational cost, motion-artifact tolerance, and interpretability tier, and the corpus-specific strengths and weaknesses of each family.

Linear discriminant analysis (LDA) projects the d-dimensional feature vector onto a discriminant axis that maximizes between-class separation relative to within-class scatter. For a two-class problem with class means and pooled within-class covariance, the discriminant function takes the form shown in Equation (1).

(1)\text{δ}\left(x\right)=w^{\mathrm{T}}x+b,\mathrm{w}\mathrm{h}\mathrm{e}\mathrm{r}\mathrm{e}w={\sum }_W^{-1}\left({\mu }_1-{\mu }_2\right)

LDA is the workhorse of online fNIRS-BCI deployment because the inference cost is a single dot product. Khan et al. selected LDA over a polynomial-kernel SVM for prosthetic-leg control on exactly this basis, despite the SVM achieving statistically higher offline accuracy [11]. LDA appears as primary classifier in [15,45,63] and as baseline comparator in most other classification studies.

Support vector machines (SVM) solve the soft-margin dual problem shown in Equation (2).

(2)\begin{array}{rl}& {max}_{\alpha }\sum _{i=1}^N{\alpha }_i-\frac{1}{2}\sum _{i,j}{\alpha }_i{\alpha }_j{y}_i{y}_{j}K\left(x_i,x_j\right),\\ & \text{s.t. 0}⩽{\alpha }_i⩽C,\sum _i{\alpha }_i{y}_i=0\end{array}

The kernel function controls the implicit feature mapping. Linear, polynomial, and radial basis function kernels all appear in the corpus [6,11,34,50]. SVM dominates the early proof-of-concept work and remains a strong baseline; ten-algorithm benchmarks consistently place tuned SVM-RBF in the top tier [8,64]. Inference cost scales with the number of support vectors, which can grow linearly with training-set size and motivates LDA substitution for embedded online deployment.

Tree-based gradient boosting constructs an additive ensemble of weak learners, as shown in Equation (3).

(3)F_M\left(x\right)=\sum _{m=1}^{M}vh\left(x\right)

Each weak learner is a regression tree fit to the negative gradient of the loss at the current iteration, and a learning rate controls the contribution of each tree. LightGBM, the implementation chosen by Li et al. for approximately 180,000-sample point-by-point self-paced walking-intention detection [46] and by Baradaran et al. for sensory-condition classification [16], replaces standard level-wise tree growth with leaf-wise growth using histogram-based split-finding, reducing memory and training time on large samples. Tree ensembles offer native feature-importance estimation, which Li et al. used to map walking-intention discriminative features to channels covering the upper prefrontal cortex [46].

Convolutional neural networks (CNN) apply learnable kernel banks to local input neighborhoods. For a 1D temporal CNN operating on a multichannel hemoglobin time series, the output at each time step in each feature map is computed as shown in Equation (4), with a learnable nonlinearity and a bias term per feature map.

(4)y_f\left(t\right)\text{= σ}\left(\sum _{c=1}^C\sum _{\tau =0}^{k-1}{w}_{f,c\text{,τ}}{x}_{c,t\text{+τ}}+b_f\right)

The corpus contains compact 1D CNNs designed for small samples. Brain-NET applies pointwise kernels along the feature dimension followed by cross-channel convolution [10]. ImageNet-pretrained 2D CNNs and vision transformers were fine-tuned on fNIRS reformulated as 3-channel images for walking-task classification in older adults [6]. Three-dimensional CNNs operating on high-density frequency-domain fNIRS arranged as topographic image stacks grouped by source-detector separation appear in [60]. Convolutional LSTM hybrids [5,33] add temporal recurrence to capture multi-second hemodynamic dynamics that pure CNNs would otherwise lose to receptive-field truncation.

Attention-based architectures weight input elements by learned similarity to a query. The scaled dot-product attention used in IVCAN [35] and the attention-augmented Bi-LSTM of Ji et al. [34] computes a softmax-normalized weighted sum of value vectors, as shown in Equation (5).

(5)\text{Attention}\left(\text{Q,K,V}\right)\text{= softmax}\left(\frac{\text{Q}{\text{K}}^{\mathrm{T}}}{\sqrt{d_k}}\right)\text{V}

Queries, keys, and values are linear projections of the input, and the scaling factor in the denominator stabilizes gradients in high-dimensional embedding spaces. Attention is the dominant innovation in the most recent cerebral fNIRS work because it learns where in the multi-second hemodynamic window the task-relevant signal lives, without requiring fixed assumptions about hemodynamic response function shape or latency. IVCAN’s curve-attention module combines spatial pointwise convolutions with dilated convolutions (kernel size 1 by 24, dilation rate 3) to capture the long-range temporal dependence of the canonical hemodynamic response [35], a physiologically motivated architectural choice rather than an off-the-shelf transformer block.

Hybrid statistical-ML pipelines combine classical neuroimaging analysis with downstream ML classification. Kim et al. fed Statistical Parametric Mapping general-linear-model t-values from ipsilesional primary motor cortex into a K-nearest neighbors (kNN) classifier for FMA-UE severity stratification [62]. Perpetuini et al. fed GLM-derived beta values into Gaussian process regression for GMFM-88 motor-function prediction in pediatric cerebral palsy [7]. Li et al. cascaded random forest for action-onset detection with SVM for four-class motion-state classification [47]. Hozan et al. paired regularized discriminant analysis with common spatial pattern dimensionality reduction [57]. These hybrid designs exploit the interpretability of established neuroimaging frameworks while gaining the discriminative power of supervised ML on engineered features.

3.2.3 Feature engineering and tissue-physiology-respecting choices

Feature engineering across the corpus consistently respected three constraints: the slow hemodynamic response, the differential reliability of HbO versus HbR, and contamination from extracerebral and systemic sources. Modified Beer-Lambert Law conversion was universal, with bandpass filtering targeting the neurovascular coupling band (variants of 0.01–0.5 Hz) to suppress cardiac, respiratory, and Mayer-wave contamination [5,7,8,10,18,54,60,62]. Physiological-noise correction strategies included short-separation channel regression [7], temporal-derivative distribution repair plus PCA [8], wavelet-based motion-artifact correction [7], and component-of-interest retention in the 0.01–0.08 Hz hemodynamic band [18,54]. The choice between HbO, HbR, HbT, and combinations was treated as a substantive design decision rather than a default. Several studies focused on HbO alone citing higher signal-to-noise ratio [11,16,29,34,62], while others found combined HbO + HbR significantly improved both accuracy and detection latency [15] or that HbR slope was the most influential single feature for surgical FLS-score prediction [10]. Ma et al. used HbO, HbR, and HbT, finding HbR most informative for speed and HbO most informative for step length [52].

Statistical features (mean, peak, variance, skewness, kurtosis, slope) of the hemodynamic response formed the most common handcrafted base [5,10,11,63]. Physiologically motivated novel features were the most distinctive contributions, particularly brain-state and transition-geometry features grounded in the balloon model of neurovascular coupling [50], Teager-Kaiser energy across five physiologically meaningful frequency sub-bands (cardiac, respiration, myogenic, neurogenic, endothelial) [46], and curve-attention modules combining spatial and dilated convolution motivated by the convolution between task paradigm and hemodynamic response function [35]. Spatial features included channel groupings respecting Brodmann areas and the 10–20 system [5,7,33], region-of-interest averaging by entropy weight method [47], and source-detector-separation grouping to preserve depth-sensitivity hierarchy [60]. Feature-selection strategies ranged from mutual information localizing over primary motor cortex [29], to multivariate joint mutual information arguing that brain regions compensate dynamically [16], meta-transformer methods using random forest importance [64], and exhaustive feature-combination testing [11,63]. Lee et al. systematically swept window length (0.6–15 s) and hemodynamic delay (0–10 s), exposing an explicit accuracy-latency Pareto frontier governed by hemodynamic physiology [15].

3.2.4 Validation strategies

Cross-validation choices reflected awareness of small-sample, between-subject heterogeneity. Leave-one-subject-out cross-validation was the standard for small clinical samples [7,33,35,50], while studies with large point-by-point datasets argued against it on redundancy grounds and used Group-2-Fold or Group-5-Fold preserving subject grouping [45,46]. Five studies implemented dedicated pseudo-online or simulated-online evaluation alongside cross-validation [11,29,45,46,63], typically reporting higher streaming accuracy than offline metrics. Dale et al. contrasted a mixed-subjects training scheme against a fully subject-independent scheme, with the ~10 percentage-point gap between the two framed as itself an empirical finding about session- and subject-specific overfitting in fNIRS BCI [60].

3.2.5 Interpretability and explainable AI

Formal post-hoc explainable AI methods (SHAP, LIME, integrated gradients) were largely absent from the cerebral fNIRS corpus. Interpretability was instead approached through three strategies. The first was post-hoc feature- and channel-importance analysis tied to neuroanatomy, with Robinson et al. demonstrating mutual-information channel selection localizing over primary motor cortex [29], Li et al. mapping selected channels to functional brain areas [47], and Gao et al. identifying HbR slope as the dominant feature for FLS-score prediction [10]. The second was architectural inductive bias as a substitute for post-hoc explanation, with Dale et al. arguing that 3D CNN positional invariance generalizes across subjects and using mixed-subjects-versus-subject-independent comparison as itself an interpretability test [60], and Li et al.’s C-Att ablation quantifying the contribution of spatial versus dilated convolution [35]. The third was neuroanatomically grounded statistical interpretation, with Kim et al. providing the most extensive treatment by combining group-level Statistical Parametric Mapping activation maps with FMA-UE correlations and tying findings to the broader neuroplasticity literature [62], and Lu et al.’s brain-state-transition features themselves designed as interpretable proxies grounded in neurovascular coupling [50].

3.2.6 Performance landscape

Reported performance varied systematically with task complexity, sample size, and validation rigor. Binary motor-state classification on healthy adults clustered around 70%–90% [5,11,15,29,57,64], with pseudo-online and simulated-online configurations consistently yielding the highest reported accuracies (Minhas et al., (88.19 ± 2.55)% offline rising to 97.5% in simulated online [63]; Li et al., AUC 0.944 with pseudo-online TPR 100%, FPR 2.91%, latency 0.39 ± 1.06 s [46]). Multi-class performance dropped as expected, ranging from ~51%–55% for tri-classifiers against 33% chance [57] up to (90.67 ± 7.07)% for five-class fine-motor complexity with attention-augmented Bi-LSTM [34], with Li et al.’s IVCAN illustrating that motor imagery is uniformly harder than motor execution (61.73% vs. 85.52% on otherwise comparable datasets) [35]. Multi-label and four-class formulations reached 0.81–0.86 accuracy [6,16,33], and Dale et al. reported a ~10 percentage-point drop from mixed-subjects to subject-independent training (F1 0.69 to 0.583), itself an empirical finding about session- and subject-specific overfitting in fNIRS BCI [60]. Continuous regression yielded R² = 0.73 for surgical FLS-score regression [10], R² = 71%–72% for gait speed and step length [52], r = 0.78 for GMFM-88 estimation under leave-one-subject-out cross-validation [7], and r = 0.860 ± 0.069 for FMA-UE prediction with combined SVM models [18]. Clinical-population classification reached 0.82 accuracy for PD-versus-control discrimination [50], 92%–99% for predictable-versus-non-predictable obstacle avoidance in healthy and multiple-sclerosis groups [8], AUC 0.955 for combined ANN prediction of modified Barthel Index at discharge [54], and an 11–39 percentage-point gain from adding ipsilesional primary-motor-cortex t-values to behavioral scores in FMA-UE severity stratification [62].

Several cross-study patterns emerged. Deep learning outperformed the specific traditional ML algorithms tested in the same study by 10 to 25 percentage points, but only where sample sizes permitted transfer learning or attention mechanisms [6,34]; no general advantage of deep learning over traditional ML was observed across the corpus, and classical methods with carefully engineered physiologically grounded features matched or approached deep-learning performance [46,50]. HbO-based features tended to dominate when systemic confounds were controlled [6,16,34], while combined HbO + HbR features remained competitive when motor execution introduced sufficient HbR dynamic range [15,50]. A consistent gap emerged between motor execution and motor imagery, attributed to weaker and more diffuse activation during imagery [29], motivating the attention mechanisms, frequency-band decomposition, and incremental adaptation seen in the most recent papers [34,35,52]. Cross-subject performance remained the harder benchmark, lying 1–5 percentage points below within-subject accuracy in well-designed models [35] but dropping more substantially in others, motivating adaptive enhancement strategies [52] and subject-independent classifier frameworks [29] as paths toward generalizable fNIRS-BCI deployment.

3.3 ML applications to mNIRS

Seven studies applied ML to mNIRS as a single modality [9,21,31,48,51,55,59]; one further study combined mNIRS with sEMG [26] and is addressed in Section 3.4. The synthesis below focuses on the single modality mNIRS corpus.

3.3.1 ML task taxonomy

The seven studies covered a narrow but representative slice of supervised and unsupervised ML problem formulations. Binary classification was the most common framing, used by Chen et al. for old-versus-young aging classification on biceps brachii [48], by Rosati et al. for diabetic-versus-control discrimination and pre-versus-post-training classification within diabetic groups [31], and by Huang et al. for healthy-versus-diabetic foot, with an additional repurposing of the classifier output as a continuous rehabilitation index to track recovery from Buerger’s exercise [59]. Multi-class classification appeared in two studies: Chen et al. extended the framing to four-class motion classification (no compensation, lean-forward, trunk rotation, shoulder elevation), trained separately on healthy simulators and stroke survivors [21], and Liang et al. pushed it to five-class severity grading aligned with Brunnstrom stages 3, 4, 5, 6 plus healthy controls, run separately for upper- and lower-limb data and for passive versus active modes [51]. Two studies departed from the classification framing entirely. Chalitsios et al. used unsupervised novelty/outlier detection (one-class SVM trained on each subject’s early-run kinematic baseline) to count strides deviating from typical patterns and correlated those deviations with SmO₂ [9]. Li et al. framed VO₂ estimation as a time-series regression problem, predicting second-by-second pulmonary VO₂ from muscle oxygen and heart rate inputs [55].

3.3.2 Algorithm families

Two regularities about algorithm-method fit emerge from the mNIRS corpus, both of which trace back to the small-sample regime in which the field currently operates. First, the dominance of low-capacity classifiers (SVM-RBF, RBFNN, shallow ANNs) reflects deliberate methodological choice rather than algorithmic conservatism: every corpus study with sample size below 30 explicitly justified its classifier selection on small-sample grounds [21,48,59], and the lone deep-learning entry [66] used the smallest architecture compatible with regression performance and relied on stratified composite-key splitting to prevent data leakage. The implication is that headline accuracy comparisons between low-capacity and high-capacity models in this corpus are confounded by sample-size differences, and the more interpretable comparison is between methods within the same sample-size regime. Second, the most novel algorithmic contributions in mNIRS are not new architectures but new feature transformations that respect tissue physiology, including DBSI common-mode/differential-mode decomposition [21], time-frequency band separation distinguishing metabolic from autonomic-vascular oscillations [31], and bilateral-asymmetry fusion via Dempster-Shafer evidence theory [51]. The choice of algorithm family in mNIRS is therefore conditioned more on the available physiological feature transformations than on the model architecture itself, and Liang et al.’s GB-DD-MLP-Net [51] is the corpus exception that proves the rule, achieving its performance through architectural innovation paired with bilateral-asymmetry feature fusion.

The mNIRS corpus spans a narrower algorithmic range than the cerebral corpus, with a strong skew toward low-capacity classifiers reflecting the small-sample regime in which most studies operate. We organize the eight studies into four algorithm families and provide formal definitions of the dominant variant in each, with a comparative analysis (Table 4) summarizing data-regime requirements, computational cost, motion-artifact tolerance, and interpretability tier, and the corpus-specific strengths and weaknesses of each family.

SVM were the dominant classifier in the mNIRS corpus, used by three of the eight studies. Chen et al. used SVM with an RBF kernel and grid-searched regularization for aging classification on biceps brachii (n = 24) [48]. Chen et al. used SVM with an RBF kernel, fixed regularization, and a one-versus-one strategy via LIBSVM for the four-class compensatory-movement task [21]. Chalitsios et al. used the one-class SVM variant for unsupervised novelty detection during exhaustive running, with the regularization parameter fixed at 1% and kernel bandwidth tuned by per-subject grid search [9]. The one-class SVM, formalized in Equation 6, is a quadratic-programming problem distinct from the binary-classification SVM of Equation (6); it identifies a hyperplane separating the bulk of training samples from the origin in feature space, with novelty scored by signed distance.

(6)\begin{array}{rl}& {min}_{w,\xi ,\rho }\frac{1}{2}{\left|\left|w\right|\right|}^2+\frac{1}{\nu N}\sum _{i=1}^N{\xi }_i-\rho ,\\ & \text{s.t.}{w}^{\mathrm{T}}\varphi \left(x_i\right)⩾\rho -{\xi }_i,{\xi }_i⩾0\end{array}

Radial basis function neural networks (RBFNN) appeared in Huang et al. for healthy-versus-diabetic-foot classification (n = 45) [59]. The RBFNN computes hidden-layer activations through Gaussian basis functions centered at prototype points and combines them linearly at the output, as shown in Equation (7). Centers were determined by k-means clustering, output weights by normalized least-mean-squares adaptation, and 16 hidden neurons selected via F-measure tuning. The architecture is a natural choice for small-sample biomedical classification because it has fewer parameters than a multi-layer perceptron of comparable expressiveness and is more interpretable than a deep network.

(7)y\left(x\right)=\sum _{j=1}^H{w}_j\exp \left(-\frac{{\left|\left|x-c_j\right|\right|}^2}{{2\sigma }_j^2}\right)+b

Gradient boosting and ensemble deep learning appeared in two studies. Liang et al. introduced the most architecturally complex model in the corpus, a gradient boosting dense dendrite multi-layer perceptron network (GB-DD-MLP-Net), which stacks dense dendrite networks with multilayer perceptrons in a gradient-boosting ensemble inspired by GrowNet [51]. The architecture combines the additive boosting structure of Equation 3 with weak learners that are themselves small dense networks, fitted via second-order Taylor expansion of the loss with a dynamic learning rate and Gelu activation. The model was benchmarked explicitly against XGBoost, LightGBM, and CatBoost, outperforming all three on five-class Brunnstrom severity grading. Li et al. used a feedforward neural network with two repeated dense-batch-normalization-dropout blocks (128 ELU neurons each, dropout 0.3), Adam optimizer, EarlyStopping, and ReduceLROnPlateau callbacks, trained for up to 300 epochs for second-by-second VO₂ regression from muscle oxygen and heart rate inputs [55].

Classical statistical approaches with shallow neural networks appeared in Rosati et al., who applied four feature-selection algorithms (QuickReduct, Genetic Rough-Set Attribute Reduction, Ant Rough-Set Attribute Reduction, and ANOVA) and validated reduced feature sets via shallow ANNs with one hidden layer containing approximately half the input neurons, log-sigmoid hidden activations, linear output, and mean-squared-error loss trained by backpropagation [31]. The pipeline reflects an earlier era of mNIRS analysis in which feature selection on time-frequency representations was the analytical workhorse, with the downstream classifier playing a supporting role.

A common thread across the corpus is the deliberate selection of low-capacity models suited to small samples. Chen et al. (n = 24), Huang et al. (n = 45), and Chen et al. (n = 16 across healthy and stroke) explicitly justified SVM or RBFNN on small-sample-size grounds [21,48,59]. The single deep-learning study [55] used the smallest architecture compatible with regression performance and relied on stratified random sampling on a composite key (exercise type × participant × intensity) to prevent data leakage, indicating that even when deep learning enters the mNIRS literature, sample-size discipline remains the operating constraint.

3.3.3 Feature engineering and tissue-physiology-respecting choices

Feature engineering was the dimension on which the mNIRS studies differed most, with many choices physiologically motivated rather than purely data-driven. Time-domain features formed the baseline, including mean and standard deviation per sliding window justified by the low-frequency concentration of NIRS power [21] and negative slopes from the first 10 s of motor-related ΔHbO₂ and ΔHb responses to capture initial metabolism kinetics [48]. Nonlinear-dynamics features appeared in two studies, with multiscale fuzzy approximate entropy and multiscale transfer entropy collapsed into curve-area complexity and coupling indices [48], and approximate entropy alongside 22 other features [51]. Time-frequency features were central in Rosati et al., who applied Choi-Williams distributions and computed band-limited power in the very-low-frequency band (20–40 mHz, linked to long-term metabolic regulation) and low-frequency band (40–140 mHz, linked to vagal activity and microcirculation), plus squared coherence between ΔHbO₂ and ΔHb [31].

Physiologically informed signal transforms represented the most distinctive contribution. Chen et al. proposed Differential-Based Signal Improvement, decomposing the Hb/HbO₂ pair into a common-mode signal (representing blood flow) and a differential-mode signal (representing oxygen consumption), in contrast to Correlation-Based Signal Improvement which assumes Hb and HbO₂ are perfectly negatively correlated; the common-mode signal proved more discriminative for compensatory-motion detection [21]. Bilateral feature fusion via Dempster-Shafer evidence theory (rather than simple concatenation) was unique to Liang et al., motivated by oxygenation asymmetry and compensation in stroke patients, and improved accuracy across all four tested models [51]. Multimodal fusion appeared in Li et al., combining bilateral muscle oxygen with heart rate; the combination yielded substantially better VO₂ predictions than either alone [55].

3.3.4 Validation strategies

Validation schemes were chosen primarily for sample-size constraints rather than methodological purity. Leave-one-out cross-validation was used by Chen et al. for n = 24 [48]; Huang et al. used a train/test split with a tuning-set F-measure of 86.9% alongside a test F-measure of 80% [59]; Chen et al. used 10-fold cross-validation with averaged accuracy across folds [21]. Holdout splits dominated the deep-learning papers, with Liang et al. using 80/20 train/test [51] and Li et al. using 90/10 with stratified random sampling on a composite key (type × participant × intensity) to prevent data leakage and ensure balanced exposure across exercise intensities [66]. Subject-specific modelling was the explicit validation philosophy in Chalitsios et al., where each runner served as their own baseline (the first 40% of the run trained the OCSVM, with the remaining 60% split into four 15% test windows), and a control test at 75% speed for 10 of 16 subjects confirmed that observed deviations were not artefactual; this is the only paper in the corpus that treats subject-specific modelling as a methodological commitment rather than a data-pooling convenience [9]. Equivalence testing appeared in Li et al., who required the predicted VO₂ 90% CI to fall within ±10% of the measured mean, a stricter criterion than correlation alone [66]. A general weakness across the clinical papers is that patient-level cross-validation (holding entire subjects out) is rarely explicit, and sliding-window feature extraction can leak temporally adjacent samples across train/test splits if not handled carefully [21,51,66].

3.3.5 Interpretability

Interpretability was addressed mostly indirectly through feature selection rather than post-hoc explanation methods. Feature-selection-based interpretability was the dominant approach: Rosati et al. provided the most explicit treatment, using four different selection algorithms on the same 24-feature set and observing that they picked different but discriminative subsets, then interpreting the selected features physiologically (TOI-based features dominated the APA comparison, suggesting tissue oxygenation improvement; squared coherence features dominated the FW comparison, suggesting improved O₂/CO₂ balance; the LF coherence band was selected when comparing controls to diabetics, suggesting microcirculatory autoregulatory differences) and flagging %P_LF-post-HHb as the only feature never selected, consistent with prior literature suggesting Hb is less discriminative than HbO₂ in diabetic muscle [31]. Statistical pre-screening for interpretability was used by Chen et al., who ran ANOVA on candidate features before SVM training to ensure that the selected inputs (negative slope, complexity index, coupling index) had independent physiological significance [48]. Architectural interpretability was claimed by Liang et al. for the dense dendrite net component, described as a white-box structure where output logical expressions reflect AND/OR/NOT relations among inputs, although such expressions were not actually extracted or reported [51]. Mechanistic post-hoc interpretation appeared in Chen et al., who used common-mode signal mean values to identify which trunk muscles were primarily activated in each compensatory movement (external oblique abdominis in forward-bending and lateral motions; deep trunk and erector spinae in upward motions), translating model outputs into clinical guidance [21]. The deep-learning and OCSVM papers made limited interpretability claims, with Chalitsios et al. relying on dynamic-systems-theory framing rather than direct model introspection [9,51,66].

3.3.6 Performance landscape

Reported accuracies were uniformly high, reflecting both genuinely strong group-level signals in mNIRS and the methodological caveats discussed below. Binary classification ranged from ~70% on the harder task of distinguishing diabetic subgroups across training protocols [31] up to 91.6% (passive) and 87.5% (active) for old-versus-young biceps-brachii classification [48] and 80% F-measure for healthy-versus-diabetic-foot classification [59]. Multi-class accuracies were surprisingly high, reaching 97.76%–99.47% for four-class compensatory-motion classification (healthy and stroke survivors, with DBSI preprocessing yielding the upper bound) [21] and 98.69%–99.63% for five-class Brunnstrom severity grading across upper- and lower-limb passive/active conditions, outperforming XGBoost, LightGBM, and CatBoost [51]. Time-series regression in Li et al. achieved MAE = 2.11 mL/kg/min, RMSE = 2.95 mL/kg/min, and r = 0.94 for the full muscle-oxygen + heart-rate model across all intensities (r up to 0.98 for VT₁-VT₂ exercise); HR alone outperformed SmO₂ alone, but the combination beat both [55]. Outlier detection in Chalitsios et al. was reported as outlier-percentage trajectories rising from 2.2% baseline to 43.6% in the final 15% of an 8-minute severe-intensity run, with a moderate negative correlation (r = −0.61) between SmO₂ and outlier strides [9].

Several caveats apply. Sample sizes were small (n = 16–55), class imbalance was rarely addressed explicitly, and the very high multi-class accuracies likely reflect sliding-window feature extraction, which inflates apparent sample size but introduces temporal autocorrelation between train and test samples [21,51]. Liang et al. acknowledged that data on stroke patients are limited and that their high accuracy partly reflects sliding-window-based data augmentation [24]. The clearest cross-study pattern is that physiologically informed feature engineering (DBSI, multiscale entropy, bilateral fusion, SmO₂ + HR combination) consistently improved performance over raw signals, often by larger margins than the choice of classifier [21,31,48,51,66]. Across the 32 classification studies in the corpus, headline performance and sample size are jointly visualized in Fig. 3, illustrating the inverse relationship between sample size and reported accuracy that motivates the methodological cautions discussed in Section 3.5.

3.4 Joint cerebral-mNIRS pipelines and multimodal integration

Eleven studies combined cerebral or mNIRS with at least one additional modality. Of these, seven paired cerebral fNIRS with EEG [12,14,17,32,49,53,58]; one paired cerebral fNIRS with multiple autonomic biosignals (electrocardiography, respiratory flow, continuous blood pressure, skin conductance) [28]; one paired cerebral fNIRS with sEMG of the biceps [61]; one paired mNIRS with high-density sEMG [26]; and one combined cerebral fNIRS, EEG, inertial motion capture, and instrumented glove sensors in a four-modality pipeline [56]. Critically, no included study reported a fully co-located cerebral-fNIRS-plus-muscle-NIRS recording, leaving the joint cerebral-muscle hemodynamic pipeline as an open methodological frontier (Section 3.4.5).

3.4.1 Inventory of joint and bimodal recordings

The hardware and protocol diversity within this small corpus is striking (Table S1). Six studies used integrated single-cap EEG-fNIRS systems with co-located optodes and electrodes over sensorimotor cortex, ranging from 8-channel EEG with 2-channel fNIRS in tetraplegic patients (Blokland et al., with a 35 mm long-distance source-detector pair targeting cortex and a 10 mm reference channel correcting for scalp/skull hemodynamics) [58], to 32-channel EEG with cap-mounted NirSmart fNIRS for myoelectric tracking [53], 36-channel EEG with 37-channel fNIRS over premotor, primary motor, and primary somatosensory cortex [49], and 64-channel EEG with 43-channel fNIRS reconstructed onto the Brodmann atlas with 50 overlapping ROIs in subacute stroke [17]. Sample sizes ranged from 7 healthy adults [28] to 27 stroke patients plus 13 controls across three timepoints [17]. Two studies recorded peripherally rather than cortically: Huang et al. used a custom-built hybrid sEMG-NIRS array (NMEP-HBO SyncACQ) with 60-channel sEMG (2050 Hz) interlaced with 60-channel NIRS (11 Hz, max 20 Hz) on the lumbar erector spinae for fatigue assessment [26], and Syed et al. used a Myo armband for biceps sEMG paired with motor-cortex fNIRS for upper-limb prosthesis control in healthy participants and trans-humeral amputees [61]. Two studies introduced explicit physiological-noise-reference channels: Ortega et al. recorded forehead scalp hemodynamics with a separate NONIN device for verification of cortical (not scalp) origin of fNIRS signals [32], and Blokland et al.’s 10 mm reference channel served the same function [58]. Synchronization strategies spanned MATLAB-based parallel/serial port triggers [14], Psychophysics Toolbox event triggers [49], custom Python trigger boxes [12,17], custom Brain-Body-Monitoring APIs integrating Lab Streaming Layer with motion-capture wrappers [56], and direct trigger inputs to the fNIRS amplifier [28]. Anatomical placement was overwhelmingly cortical, with optodes and electrodes co-aligned over bilateral sensorimotor cortex in seven of eleven studies; peripheral muscle recordings (sEMG, ECG, blood pressure, skin conductance, respiratory flow, IMU, glove flex sensors) were anatomically separated from the cortical channels in every study where both were present.

3.4.2 Convergent methodologies across cerebral and muscle pipelines

Several methodological motifs recurred across both cerebral and muscle pipelines despite the different physiological substrates. Modified Beer-Lambert law conversion and bandpass filtering targeting the neurovascular coupling band (variants of 0.01–0.5 Hz) were universal to all NIRS preprocessing, regardless of tissue site [26,61]. Sliding-window feature extraction with mean, standard deviation, slope, and band-limited spectral power formed the common feature-engineering base [21,26,61]. Task-related component analysis emerged as a shared single-trial spatial-filtering strategy, used by Jiang et al. on EEG μ-band and fNIRS HbO features for bimanual coordination [49] and by Wu et al. on EEG and fNIRS during gait [12]. Per-subject calibration and subject-specific modelling, identified earlier as the methodological commitment of Chalitsios et al. for mNIRS [9], reappeared in the joint corpus through Zimmermann et al.’s per-subject Hidden Markov Model topology tuning [28] and Syed et al.’s per-motion modality-arbitration scheme calibrated to each participant’s signal strength [61]. CNN with attention or LSTM extensions emerged as the dominant deep-learning strategy across both cerebral- and muscle-domain hybrid pipelines, with Ortega et al.’s cnnatt for grip-force decoding [32], Huang et al.’s DCHANet dual-stream architecture for low-back fatigue [26], and Syed et al.’s 3-layer CNN for upper-limb motion classification [61] all sharing the same broad design pattern.

3.4.3 Tissue-specific divergences

Tissue-physiology-respecting choices diverged sharply between cerebral and muscle pipelines. Cerebral fNIRS pipelines emphasized cortical anatomy and topographical mapping, with channels placed by 10-20 or 10-10 system [12,14,17,32,49,56,58], analyses anchored to Brodmann areas [17,21], and source reconstruction onto cortical atlases for ROI-based analysis [17]. mNIRS pipelines instead emphasized depth penetration and tissue-layer specificity, with Huang et al. designing the NIRS array to reach 10–60 mm depth (max 30 mm) to capture core lumbar muscle hemodynamics that surface EMG could not access [26]. Physiological-noise correction strategies also diverged: cerebral pipelines used short-separation channel regression [7], temporal-derivative distribution repair plus PCA [8], and component-of-interest retention in the 0.01–0.08 Hz hemodynamic band [18,54] to suppress superficial scalp signal, while muscle pipelines focused on motion-artifact correction [61] and contraction-induced electrode-skin impedance fluctuations [26]. The interpretation of the HbO/HbR pair followed correspondingly different logics. In cerebral pipelines, HbO and HbR were treated as the two faces of the canonical hemodynamic response function, with HbO favored for its higher signal-to-noise ratio when systemic confounds were controlled [11,16,29,34,62] and HbR retained in select studies for its sensitivity to motor pathology [10,15,52]. In muscle pipelines, the same chromophore pair was reframed through the muscle-physiology lens of blood flow versus oxygen consumption, with Chen et al.’s Differential-Based Signal Improvement decomposing HbO + HbR as a common-mode (blood flow) signal and HbO–HbR as a differential-mode (oxygen consumption) signal [21], a transformation that has no direct cerebral analogue because cortical neurovascular coupling does not separate cleanly into supply and demand components in the same way. The convergent methodologies, tissue-specific divergences, and the resulting open frontier between cerebral fNIRS and mNIRS pipelines are summarized in Fig. 4.

3.4.4 Integration strategies in existing hybrid pipelines

Integration strategies spanned the full early-to-late fusion continuum. Feature-level fusion was the most common, ranging from simple concatenation of modality-specific features fed to a single classifier [12,49,56] to correlation-guided channel selection that retained only EEG and fNIRS channels showing significant alpha-ERD/HbO coupling before concatenation [14]. Hidden Markov Model fusion at the observation level was implemented by Zimmermann et al., concatenating fNIRS and autonomic-biosignal observations into a single 6-dimensional vector and training two parallel HMMs to capture cross-modal correlations [28]. Decision-level fusion appeared in two forms: probabilistic combination of calibrated L1-logistic-regression posteriors equivalent to naïve Bayes fusion [58], and labelled per-motion arbitration assigning each of eight upper-limb motions to whichever modality showed higher per-motion classification accuracy in training [61].

Attention-based fusion appeared in three architecturally sophisticated pipelines: Ortega et al.’s cnnatt with modality-specific 1D convolutional layers feeding into self-attention [32]; Huang et al.’s DCHANet with hierarchical multi-head attention combining a Joint Self-Attention Layer and two cross-attention layers across sEMG and NIRS [26]; and He et al.’s weighted EEG-fNIRS integration, in which EEG-derived classification accuracy served as a dynamic weight vector modulating fNIRS amplitudes through a Guided Attention map, with the optimal 3-second EEG-to-fNIRS delay matching the canonical hemodynamic response latency [53]. The most architecturally elaborate fusion appeared in Lin et al.’s multilayer brain network framework, in which both modalities were source-reconstructed onto the Brodmann atlas, intra-layer edges built from weighted phase lag index (EEG) and Pearson correlation (fNIRS), and inter-layer edges constructed using subject-specific neurovascular coupling strength derived by deconvolving EEG beta-band time-frequency spectra against fNIRS HbO [17].

Across the corpus, ablation comparisons consistently demonstrated additive benefit from fusion, though magnitude varied: bimodal EEG-fNIRS reached 90.1% versus 74.8% (EEG-only) and 82.2% (fNIRS-only) with task-related component analysis (TRCA) features [49], 79% versus 73% for attempted-movement decoding in tetraplegia [58], 93.40% versus 92.79% (EEG-only) and 81.23% (fNIRS-only) in Parkinson’s-disease classification [56], and 20.36% average prediction-error reduction for FMA-UE recovery in subacute stroke [17]. Two negative or qualified findings tempered this picture: Wu et al.’s bimodal TRCA fusion did not significantly exceed unimodal TRCA alone, suggesting redundancy at the feature-concatenation level [12] and Zimmermann et al.’s HMM fusion produced its largest gains in subjects with the worst fNIRS-only performance, interpreted as autonomic biosignals supplying compensatory information when systemic physiological noise contaminated the fNIRS signal [28].

3.4.5 The open frontier

Three observations from this corpus together define the methodological gap that this review’s joint cerebral-muscle pipeline aims to fill. First, no included study recorded cerebral fNIRS and mNIRS simultaneously and in co-location, despite eleven studies adopting other forms of bimodal or multimodal integration. The closest approximations are Syed et al., which paired cerebral fNIRS with biceps sEMG but used electromyography rather than near-infrared spectroscopy at the muscle site [61], and Huang et al., which delivered a sophisticated co-located sEMG-NIRS array but applied it only peripherally to the lumbar erector spinae rather than to the cerebral-muscle axis [26]. Second, where joint recordings did occur, fusion gains were both modest and pathway-dependent: feature-level concatenation often saturated quickly [12], whereas attention-based, hierarchical, and neurovascular-coupling-informed fusion architectures (cnnatt, DCHANet, multilayer brain networks, weighted EEG-fNIRS integration) consistently delivered larger gains by exploiting modality-specific temporal and spatial complementarity [17,26,32,53]. Third, the methodological vocabulary needed to fuse cerebral and mNIRS exists in fragmented form across the corpus, with neurovascular coupling deconvolution [17], canonical HRF latency matching [53], correlation-guided channel selection (AL-Quraishi et al.) [14], and physiologically informed common-mode/differential-mode decomposition [21] all addressing pieces of what a unified cerebral-muscle pipeline would require. A genuinely co-located cerebral-fNIRS-plus-muscle-NIRS recording, paired with an integration architecture that respects the differential time scales (cortical neurovascular coupling at ~3–5 s; peripheral muscle hemodynamics at task-paced second-by-second resolution) and tissue-physiology-specific feature transformations (cortical topography versus muscle depth penetration) is not represented in this corpus. This gap defines an open methodological frontier for adaptive sport, rehabilitation, and BCI applications in which the brain-muscle axis is the substrate of interest. A proposed joint cerebral-mNIRS-ML pipeline that addresses these requirements for adaptive sport, rehabilitation, and BCI applications is outlined in Fig. 5.

3.5 Risk of bias and methodological reporting quality

The 42 included studies were appraised on two complementary dimensions. Risk of bias and applicability were assessed against the PROBAST framework [42] across its four domains (Participants, Predictors, Outcome, Analysis). Methodological reporting quality was assessed against a 10-item TRIPOD + AI-aligned rubric [43] adapted for NIRS-based prediction models, with each study assigned a percentage-of-maximum score and an overall tier (Low ≥ 75%, Some concerns 50%–74%, High < 50%). Per-study PROBAST judgments and TRIPOD + AI scores across the 42 included studies are visualized in Fig. 6, with full per-study TRIPOD + AI item scores and PROBAST domain judgments and rationales provided in Tables S2 and S3, respectively.

3.5.1 PROBAST overall and per-domain judgments

The PROBAST appraisal produced a uniformly concerning overall picture: all 42 studies were rated high overall risk of bias, driven entirely by the analysis domain, in which every included study received a high rating. The remaining domains were judged Low for the majority of studies (Participants: 17 Low/25 High; Predictors: 36 Low/6 High; Outcome: 40 Low/2 High). Elevated participant risk most often reflected recruitment of small healthy convenience cohorts in studies whose stated motivation targeted clinical or athletic populations; the universal High Analysis rating reflected small samples relative to model capacity, sliding-window feature extraction combined with trial-wise rather than subject-wise splitting, hyperparameter and feature-selection circularity on the same data later used for performance reporting, absence of external validation in 41 of 42 studies, and absent or inconsistent calibration assessment. The applicability picture mirrored these patterns for different reasons, with 29 studies receiving High Participant applicability because the studied population fell outside the review’s adaptive-sport, Paralympic, and clinical-rehabilitation focus, and 34 receiving High Predictor applicability because the modality was cortical fNIRS rather than skeletal mNIRS; only 3 of 42 studies received an overall Low applicability rating, all of them muscle-NIRS-based studies sitting closest to the review’s central construct of skeletal-muscle oxygenation impairment [9,21,51].

3.5.2 TRIPOD + AI reporting compliance

The TRIPOD + AI rubric showed a more graded picture, with 10 studies rated Low risk (≥ 75%), 29 Some concerns (50%–74%), and 3 High (< 50%), and a mean total score of 12 of 20 (~ 60% of maximum). Items related to technical model description were the best reported, with feature engineering and comparator-model presence each fully reported in 32 of 42 studies (76.2%), interpretability methods in 24 (57.1%), and train/validation/test splitting in 19 (45.2%). Items related to methodological rigor and uncertainty quantification were the worst reported, with participant flow and sample-size justification fully reported in only 3 studies (7.1%), class balance and chance-level baseline in 3 of 38 applicable studies (7.9%), hyperparameter tuning in 14 (33.3%), missing-data handling in 10 (23.8%), and calibration and uncertainty in 5 (11.9%); the single most poorly reported item was external validation, fully reported in only 1 of 42 studies (2.4%), with 37 reporting only an internal held-out test set and 4 reporting no held-out test set at all. This is the central methodological gap of the corpus and the dominant driver of the universal High Analysis-domain rating in PROBAST.

3.5.3 Cross-cutting reporting weaknesses

Five interrelated weaknesses recurred across the corpus: small convenience samples rarely justified prospectively (only 3 of 42 studies provided any explicit rationale); inconsistent subject-wise versus trial-wise validation, with sliding-window feature extraction paired with trial-wise splitting introducing temporal autocorrelation between training and test samples that almost certainly contributed to the very high accuracies (often > 95%) reported in several deep-learning studies on small clinical samples; hyperparameter tuning, feature selection, and threshold selection performed on the same data later used for performance reporting; near-absence of external validation, with only one study evaluating performance on a fully external dataset; and rare reporting of calibration and uncertainty quantification, with only 5 studies providing calibration assessments and confidence intervals on headline performance metrics. These weaknesses are not specific to NIRS-based ML but reflect the broader immaturity of the prediction-model literature in motor-task and exercise contexts; the Discussion (Section 4) addresses how these reporting standards can be operationalized for joint cerebral-mNIRS pipelines in adaptive sport and rehabilitation.

4 Discussion

4.1 ML applied to cerebral fNIRS in motor rehabilitation and sports training contexts

The cerebral fNIRS corpus catalogued in Sections 3.2.1 and 3.2.2 distributed across binary classification, multi-class classification, and continuous regression tasks, with algorithm choice clustering into three regimes: classical models on small samples; transfer-learning-pretrained CNNs and vision transformers when fNIRS could be reformulated as image-like inputs; and attention-based architectures when the temporal structure of the hemodynamic response was the analytical target. Within this distribution, four patterns relevant to motor rehabilitation and sports training emerge: the dominant role of physiologically grounded feature engineering relative to algorithm class (Section 4.1.1), the task-dependent logic of chromophore selection (Section 4.1.2), the systematic gap between motor-execution and motor-imagery decoding (Section 4.1.3), and the underreporting of subject-independent generalization (Section 4.1.4).

Beyond the taxonomy itself, the cerebral fNIRS literature has long lacked consensus on differential pathlength factor, filter cut-offs, baseline duration, and chromophore selection [13,23]. The corpus assembled here begins to clarify de facto standards: differential pathlength factors of 6.0 for adults with population-adjusted values for pediatric and clinical groups, bandpass filtering between approximately 0.01 and 0.5 Hz, baseline durations of 10 to 30 seconds, and HbO as primary chromophore with HbR or combined comparators reported in motor-execution and motor-recovery paradigms. Against this emerging operational consensus, ML has surfaced patterns that conventional general-linear-model and hand-engineered pipelines have not, including subject-independent decoding of motor intention with sub-second latency, motor-execution-versus-imagery discrimination via attention mechanisms aligned with hemodynamic timescales, and channel-level multivariate inference that conventional region-of-interest averaging would discard [11,15,21,29,35].

4.1.1 Physiologically grounded feature engineering and algorithm choice

The principal leverage point for accuracy in fNIRS-ML at current sample sizes is the feature space rather than the model architecture, with three lines of evidence converging on this finding. First, deep architectures outperformed the specific traditional ML algorithms tested in the same study by 10 to 25 percentage points only when sample sizes supported transfer learning or attention: Ma D et al.’s ImageNet-pretrained vision transformers outperformed SVM, decision tree, and naïve Bayes on walking-task classification [6] and Ji et al.’s attention-augmented Bi-LSTM outperformed traditional CNN, LSTM, and Bi-LSTM baselines on fine-motor complexity decoding [34]. Comparator algorithms differed across studies, so the deep-learning advantage should be read as superiority over the specific comparators tested in each study rather than as a general claim that deep learning surpasses traditional ML in the field. Second, classical models built on physiologically grounded features matched deep architectures on smaller samples: Li et al.’s LightGBM with Teager-Kaiser energy across cardiac, respiratory, myogenic, neurogenic, and endothelial sub-bands reached AUC 0.944 [46], and Lu et al.’s linear SVM on balloon-model-derived features achieved 82% for Parkinson’s disease versus control [50]. Third, Lee et al.’s window-length by hemodynamic-delay sweep within a single classifier produced a 14-percentage-point spread in accuracy from feature configuration alone, governed by hemodynamic physiology rather than model capacity [15]. This asymmetry is documented in the corpus itself. Neither of the two studies establishing the 10 to 25 percentage-point margin reports a hyperparameter search for its traditional comparators: Ma D et al. evaluated Random Forest at a fixed 25 trees and KNN at a fixed k of 5 while sweeping resizing parameters and applying early stopping to the deep models [6], and Ji et al. report an Adam optimizer, L2 weight decay, dropout, and early stopping for the attention-augmented Bi-LSTM but no tuning protocol for the SVM baseline [34]. Where both sides were tuned under a common protocol, the margin narrowed: Dale et al.’s grid search over twelve hyperparameters applied identically to every architecture produced no statistically significant difference between the proposed 3D CNN and its baselines [60]. A reported deep-learning advantage over a default-configured traditional comparator is therefore not, in itself, evidence of architectural advance and may instead reflect under-engineering of the baseline. Future comparisons should report the tuning budget allocated to each model class, and treat any comparison in which only the proposed architecture was tuned as uninformative about architecture.

4.1.2 Chromophore selection: HbO, HbR, and combined approaches

Chromophore selection in cerebral fNIRS-ML should be treated as a task-dependent design decision rather than a default, because every corpus study that examined it directly found chromophore-specific contributions to performance. Lee et al. found that combining HbO and HbR improved accuracy by 3.71% and detection latency by 6.01% over HbO alone for hand opening versus closing in post-stroke patients [15]. Gao et al.’s backward feature selection identified HbR slope as the most influential single feature for predicting Fundamentals of Laparoscopic Surgery scores [10]. Ma H et al. found HbR most informative for gait speed (51.6% feature contribution) while HbO dominated step length (43.3%) [52]. Studies defaulting to HbO did so with explicit physiological justification: Baradaran et al. compared all three configurations for postural-condition classification and grounded the HbO choice in the systemic-confound trade-off appropriate to their minimal-movement standing paradigm [16]. HbO defaults are appropriate for cognitive paradigms with minimal motor activity but inadequate for motor-execution and motor-recovery contexts, in which HbR carries pathology-specific and parameter-specific signal.

A parallel design point applies to spatial aggregation: preserving channel-level structure rather than collapsing to ROI means is the appropriate default for motor-task ML. Lee et al. showed channel-preserving features outperformed channel-averaged features by approximately 15 percentage points [15], and Baradaran et al. argued that brain regions compensate dynamically, so individually weak channels can become informative in combination, a logic captured only by multivariate selection methods such as joint mutual information [16]. Cerebral fNIRS-ML papers targeting motor rehabilitation should therefore report HbR or combined comparators alongside HbO and preserve channel-level structure.

4.1.3 ML strategies for motor execution and motor imagery paradigms

The cerebral corpus reveals a systematic regularity with direct ML-design implications: motor imagery decoding consistently underperforms motor execution decoding on otherwise comparable datasets. Li et al.’s IVCAN reached 85.52% for motor execution against 61.73% for motor imagery on parallel datasets using identical architecture and feature pipeline [35]. Robinson et al. observed that subject-independent classifiers trained on motor-execution data and deployed on motor-imagery test trials reached only 64% to 67% accuracy compared with 80% on parallel motor-execution test trials [29]. The execution-imagery gap is therefore not a property of any one architecture but a property of the imagery signal itself.

The regularity has direct ML-design weight because the two paradigms admit different methodological strategies. Motor execution permits trial-locked feature extraction with relatively stable hemodynamic-response shape, supporting standard supervised decoding pipelines. Motor imagery generates lower signal-to-noise activation that varies across subjects and sessions, motivating attention mechanisms that learn task-relevant time segments rather than assuming fixed timing [34,35], frequency-band decomposition targeting imagery-specific oscillatory signatures [46], and incremental cross-session adaptation [52]. None of these three responses, individually or in combination, has closed the gap.

The regularity also has direct clinical-translation weight, because motor imagery is the operationally relevant paradigm for the populations fNIRS-BCI is designed to serve. Patients with severe paresis or tetraplegia cannot perform overt movement, so any clinical fNIRS-BCI must work on imagery rather than execution. Blokland et al. demonstrated this constraint in a tetraplegia cohort, where bimodal EEG-fNIRS decoding reached 79% for attempted movement but only 70% for imagined movement [58]. Motor-execution-only evaluations should therefore be treated as preliminary methodological characterization, and clinical-translation claims require parallel motor-imagery evaluation on the target population using ML pipelines designed for the imagery paradigm.

4.1.4 Subject-independent generalization

The hardest benchmark in the cerebral corpus, and the one most studies do not report, is subject-independent generalization, with three corpus studies establishing both that the within-to-between subject performance gap is large in default architectures and that the gap is not inherent to fNIRS but tracks model design. Dale et al.’s contrast of mixed-subjects against subject-independent training produced an approximately 10-percentage-point F1 drop (0.69 to 0.58) on the same three-class finger-opposition task with the same 3D CNN [60]. Robinson et al. found subject-independent classifiers in live neurofeedback reached 57 to 80% accuracy across runs, below within-subject performance [29]. By contrast, Li et al.’s IVCAN reached cross-subject performance within 1 to 2 percentage points of within-subject performance (84.20% versus 85.52%; 75.37% versus 75.78%) [35], showing that the gap tracks how aggressively models exploit subject-specific session features rather than reflecting an inherent fNIRS limitation.

The methodological implication is that within-subject accuracy figures, however high, do not characterize the deployment-relevant performance of an fNIRS-BCI intended to operate on new users without per-user retraining. Three reporting practices follow: subject-independent evaluation should be reported as standard rather than as an optional ablation; sliding-window feature extraction paired with trial-wise rather than subject-wise splitting should be avoided because it inflates apparent sample size at the cost of train-test independence; and pseudo-online streaming performance should accompany any model claiming real-time applicability [11,29,45,46,63]. These reporting practices directly address the analysis-domain risk-of-bias concerns common across the corpus.

4.2 ML applied to mNIRS in motor rehabilitation and sports training contexts

The mNIRS corpus is smaller than the cerebral corpus (seven studies versus thirty-three) but methodologically more distinctive, with a higher proportion of papers introducing physiologically novel feature transformations rather than borrowing pipelines from cerebral fNIRS. mNIRS carries information about two simultaneous physiological processes, blood flow and oxygen consumption, that produce opposing correlations between HbO and HbR [21]. Analytical strategies developed for cerebral fNIRS therefore discard physiologically meaningful information when applied to muscle without modification, and three patterns in the muscle corpus are relevant to motor rehabilitation and sports training: tissue-specific feature engineering, the interpretation of reported accuracies in the small-sample regime, and per-subject calibration as a methodological design choice.

4.2.1 Tissue physiology and methodological innovation in mNIRS

The cerebral fNIRS analytical toolbox cannot be transferred wholesale to mNIRS, and four corpus studies illustrate this by introducing muscle-physiology-specific feature transformations with no direct cerebral counterpart. The clearest example is the Differential-Based Signal Improvement (DBSI) introduced by Chen et al. [21]. Cerebral fNIRS commonly uses Correlation-Based Signal Improvement, which assumes HbO and HbR should be perfectly negatively correlated and treats positively correlated components as noise. Chen et al. argued this assumption fails in muscle, where the chromophore changes are driven by two distinct processes: blood flow, which produces a positive correlation, and oxygen consumption, which produces a negative correlation. DBSI accordingly decomposes the chromophore pair into a common-mode signal (HbO + HbR, indexing blood flow) and a differential-mode signal (HbO–HbR, indexing oxygen consumption). The common-mode signal proved more discriminative for compensatory-motion classification than the differential-mode (98.85% vs. 96.14%), inverting the cerebral assumption that common-mode dynamics should be discarded.

Three further studies introduced complementary muscle-specific transformations. Rosati et al. turned to time-frequency analysis using Choi-Williams distributions, computing band-limited power in a very-low-frequency band (20 to 40 mHz, linked to long-term metabolic regulation) and a low-frequency band (40 to 140 mHz, linked to vagal activity and microcirculatory vasomotion), explicitly separating metabolic from autonomic-vascular information [31]. Chen et al. extracted multiscale fuzzy approximate entropy and multiscale transfer entropy to characterize complexity and inter-limb coupling at multiple temporal scales [48]. Liang et al. fused affected- and non-affected-side features via Dempster-Shafer evidence theory, motivated by oxygenation asymmetry in stroke patients, with bilateral fusion improving accuracy across all four ensemble models tested [51]. The cross-cutting lesson is that cerebral fNIRS analytical pipelines imported wholesale into mNIRS discard the physiological information distinguishing blood-flow from oxygen-consumption dynamics, and research groups extending cerebral expertise into muscle work should revisit physiological-noise correction strategies, chromophore-selection logic, and signal-improvement transforms developed for cortical recordings rather than transfer them.

4.2.2 Reported accuracy in mNIRS: sources of inflation and interpretive caveats

Three contextual factors temper the high accuracies reported in the mNIRS corpus, and the principal inflating mechanism is mechanically traceable to validation-strategy choices rather than to model overfitting in the conventional sense. Chen et al. reported 97.76% to 99.47% on a four-class compensatory-motion task [21], and Liang et al. reported 98.69% to 99.63% on five-class Brunnstrom severity grading, outperforming XGBoost, LightGBM, and CatBoost [51]. These values approach the ceiling of what classification metrics can express, in a corpus where sample sizes range from 16 to 55 participants and external validation is reported in only one of eight studies. The inverse relationship between sample size and reported accuracy across the broader corpus, visualized in Fig. 3, locates these results in a regime where performance should be interpreted with explicit attention to validation strategy and sample size: small-sample-size effects, the prevalence of within-subject and trial-wise validation, which was used in five of the eight mNIRS studies [9,21,31,51,66] with the splitting unit left unstated in a further two [48,59], leaving only one study [26] that reported subject-wise splitting alongside its primary scheme, and corpus-wide absence of external validation.

The mechanism is sliding-window feature extraction. This technique multiplies the apparent sample size from tens of participants into thousands of windows but introduces temporal autocorrelation between training and test samples that violates cross-validation independence. When window-level rather than subject-wise splitting is used, adjacent windows sharing physiological state appear in both training and test sets, and the classifier learns to recognize subject-specific signatures rather than the task-general pattern. Liang et al. acknowledged this mechanism in their limitations [51], but the caveat is not propagated to the headline performance figures in the abstract and results tables. Two reporting practices would substantially improve interpretability without requiring new methodological development: subject-wise cross-validation reported alongside any sliding-window cross-validation, with the gap between the two treated as an interpretability finding; and external validation on a modest second-site dataset for any clinically translational claim. A realistic performance ceiling at current sample sizes and validation rigor is closer to 80% to 90% accuracy on multi-class tasks under subject-wise evaluation, consistent with the cleaner-validated binary classification range of 70% to 92% reported across smaller-sample studies [31,48,59].

Achieving figures that transfer to deployment requires a validation framework built on three components. First, subject-wise partitioning, ideally strict leave-one-subject-out cross-validation, in which every window originating from a held-out participant is excluded from training, so that no temporally adjacent window shares physiological state across the train-test boundary. Second, where sliding-window expansion is used to increase sample count, the window-level and subject-level results should both be reported, with the difference between them treated as a quantitative estimate of subject-specific leakage rather than as an inconvenience. Third, external validation on a second-site dataset for any clinically translational claim, since subject-wise partitioning within a single site controls for subject identity but not for device, montage, operator, or population. Under such a framework, the mNIRS corpus would report lower headline figures than it currently does, and those figures would carry substantially more information about deployment performance.

4.2.3 Per-subject calibration in mNIRS analysis

Per-subject calibration appeared as a deliberate methodological design choice in only one corpus study, but it represents the validation paradigm best matched to the populations mNIRS-ML is most likely to serve.

Chalitsios et al. used a one-class SVM for novelty detection during exhaustive running, with each runner’s first 40% of the run training the model and the remaining 60% serving as test windows, so each runner served as their own baseline [9]. A control test at 75% running speed in 10 of 16 subjects confirmed that observed deviations were specifically tied to severe-intensity exercise rather than to artifact.

Adaptive sport, Paralympic training, stroke rehabilitation, and clinical exercise testing all involve cohorts in which between-subject heterogeneity overwhelms group-level signal: residual function, prosthesis configuration, impairment level, training history, and adipose-tissue thickness modulate the mNIRS signal in ways group-pooled training cannot accommodate. A model achieving 99% accuracy on a pooled training set of healthy young controls may not generalize to a Paralympic athlete with asymmetric residual limb innervation. A per-subject baseline approach asks not whether the signal resembles the cohort but whether it has changed relative to itself. The implication is that the dominant corpus validation paradigm, namely group-pooled training with random or k-fold splitting, may be inappropriate at the design level rather than merely under-validated. Subject-specific and subject-conditioned models, in which a brief individual baseline is acquired before deployment and the model adapts to it, warrant more methodological attention than they currently receive in the mNIRS-ML literature.

4.3 Joint cerebral-mNIRS-ML: an open methodological frontier

The five subsections below develop the central argument that joint cerebral-muscle NIRS-ML is methodologically tractable from corpus-validated components but has not been assembled by any included study, with the absence representing a structural gap rather than a technical curiosity. The argument unfolds in five steps: the empirical observation that no included study recorded cerebral fNIRS and mNIRS jointly (Section 4.3.1); the methodological building blocks for such a pipeline already present across the corpus (Section 4.3.2); the integration challenges specific to joining the two compartments (Section 4.3.3); the fusion-architecture lessons from existing bimodal work (Section 4.3.4); and the application domains that most directly motivate the joint pipeline (Section 4.3.5).

4.3.1 The absence of joint cerebral-muscle recordings in the corpus

The defining empirical observation of this review is that no included study recorded cerebral fNIRS and mNIRS jointly and in co-location, despite eleven studies adopting other forms of bimodal or multimodal integration. Seven studies paired cerebral fNIRS with EEG [12,14,17,32,49,53,58], one paired cerebral fNIRS with autonomic biosignals [28], one paired cerebral fNIRS with biceps sEMG [61], one paired mNIRS with high-density sEMG [26], and one assembled a four-modality cerebral pipeline integrating fNIRS, EEG, motion capture, and instrumented gloves [56]. The closest approximations to the joint cerebral-muscle hemodynamic pipeline each substitute one half of the brain-muscle axis with electrophysiology: Syed et al. paired cerebral fNIRS with biceps sEMG but used electromyography rather than near-infrared spectroscopy at the muscle site [61], and Huang et al. delivered a sophisticated co-located sEMG-NIRS array but applied it only peripherally to the lumbar erector spinae rather than across the cerebral-muscle axis [26].

The gap matters because the brain-muscle axis is the substrate of motor rehabilitation, BCI-controlled prosthesis, and adaptive sport, and the same translational question recurs in each domain: is descending neural drive translating into peripheral oxygenation and force production? Neither cerebral fNIRS nor mNIRS alone can answer this question. A cerebral fNIRS recording reveals motor planning, motor execution, and cortical recovery but does not indicate whether the muscle is meeting the metabolic demand the cortex is requesting. A mNIRS recording reveals peripheral oxygen extraction and metabolic balance but does not distinguish whether observed changes reflect altered descending drive, altered muscle physiology, or both. The absence of a joint pipeline in the corpus therefore represents a structural gap in what NIRS-ML can currently deliver.

4.3.2 Methodological building blocks distributed across the corpus

Although no included study assembled a joint cerebral-muscle NIRS-ML pipeline, the methodological building blocks for one are already present across the corpus, distributed across studies that each addressed a single component. Lin et al. demonstrated subject-specific neurovascular coupling deconvolution at the cortical end, deriving NVC strength from EEG beta-band time-frequency spectra deconvolved against fNIRS HbO and using the result as inter-layer edges in a multilayer brain network [17]. He et al. demonstrated canonical-HRF latency matching for cross-modal alignment, with the optimal three-second EEG-to-fNIRS delay matching the canonical hemodynamic response latency [53]. AL-Quraishi et al. demonstrated correlation-guided channel selection for fusion, retaining only EEG and fNIRS channels showing significant alpha-ERD/HbO coupling before concatenation [14]. Chen et al. demonstrated common-mode/differential-mode physiological decomposition at the muscle end, separating the chromophore signal into blood-flow and oxygen-consumption components [21]. Ortega et al. and Huang et al. demonstrated hierarchical attention-based fusion architectures, with cnnatt and DCHANet respectively combining modality-specific convolutional streams via self- and cross-attention layers [26,32]. Chalitsios et al. and Zimmermann et al. demonstrated per-subject calibration as a validation philosophy [9,28].

Fig. 5 integrates these existing pieces into a five-stage research agenda rather than proposing a speculative new architecture: co-located cerebral fNIRS plus mNIRS acquisition, tissue-specific preprocessing, NVC-aware temporal alignment reconciling cortical and muscle hemodynamic time scales, cross-tissue attention-based fusion, and multi-task outputs. The novel contribution is the integration itself, namely the simultaneous co-located cerebral and mNIRS recording paired with a fusion architecture that respects the differential time scales and tissue-physiology-specific feature transformations of the two compartments, which has not been demonstrated in any included study.

4.3.3 Integration challenges specific to joint cerebral-muscle pipelines

Joint cerebral-muscle NIRS-ML inherits the integration challenges of any multimodal hemodynamic pipeline, but three challenges are amplified specifically by the cerebral-muscle combination because the two compartments differ along the dimensions that govern fusion: the temporal dynamics of their hemodynamic responses, the physiological meaning of their chromophore signals, and the noise sources that dominate each recording.

The first challenge is the differential time scales of cortical and peripheral hemodynamics. Cortical neurovascular coupling drives a hemodynamic response that peaks roughly three to five seconds after neural activation, while peripheral muscle hemodynamics respond at task-paced second-by-second resolution, with rapid HbO drops at exercise onset followed by gradual recovery as supply meets demand. Naïve concatenation of cerebral and muscle features at matched timestamps misaligns cause and effect, because the cortical signal at time t reflects neural activity at time t – 4 seconds while the muscle signal at time t reflects metabolic state at time t – 1 second. The corpus contains a directly applicable solution in He et al.’s latency-matched windowing, in which the optimal cross-modal delay was learned empirically rather than assumed [53], and an attention mechanism learning the per-subject delay would generalize this further.

The second challenge is the requirement for tissue-specific feature transformation. HbO and HbR carry different physiological meanings in cerebral and muscle tissue: cerebral HbO/HbR reflect neurovascular coupling on a 3–5 second timescale, whereas muscle HbO/HbR reflect oxygen extraction and reperfusion on a 1-second timescale. Stacking them in a single feature vector without separation discards information. Any joint pipeline must apply tissue-specific preprocessing before fusion: cerebral pipelines emphasizing short-separation regression, NVC-band filtering, and cortical topographical mapping; muscle pipelines emphasizing common-mode/differential-mode decomposition, depth-sensitive channel grouping, and motion-artifact correction tuned to contraction-induced impedance fluctuations. Fig. 5’s stage two reflects this requirement.

The third challenge is the asymmetry of dominant noise sources. Cerebral fNIRS is dominated by superficial scalp confounds, particularly at the prefrontal cortex where systemic physiological noise is heaviest; short-separation channels and component-of-interest filtering in the 0.01–0.08 Hz band are the established mitigations [7,8,18]. mNIRS is dominated by motion artifact, adipose-thickness effects, and skin-pigmentation-modulated optical absorption; per-subject calibration and motion-aware preprocessing are the corresponding mitigations [9,26]. A joint pipeline cannot adopt either set of strategies wholesale; the noise-handling architecture must itself be asymmetric across the two tissues, applying each set of mitigations at its appropriate compartment.

4.3.4 Fusion strategies and their performance differentials

A consistent pattern in the multimodal fusion literature is that simple feature-concatenation fusion saturates quickly, while attention-based, hierarchical, and physiologically informed fusion architectures deliver larger performance gains. Wu et al.’s bimodal TRCA fusion did not significantly exceed unimodal TRCA alone, suggesting redundancy at the feature-concatenation level [12]. Attention-based architectures, by contrast, delivered substantial improvements across diverse tasks: Lin et al.’s multilayer brain network with NVC-defined inter-layer edges achieved a 20.36% NMAE reduction for FMA-UE recovery prediction in subacute stroke [17]; Ortega et al.’s cnnatt produced 54.9% FVAF for grip force decoding versus 48.5% for the linear baseline [32]; Huang et al.’s DCHANet outperformed both feature-extraction-only and decision-level weighted-sum fusion variants [26]; and He et al.’s weighted EEG-fNIRS integration with dynamic per-time-step EEG weights modulating fNIRS amplitudes outperformed constant-weight, NVC, and PSD baselines [53].

Two findings qualify the pattern. First, fusion gains were largest in subjects with the worst unimodal performance, with Zimmermann et al. showing that HMM fusion delivered its largest gains in low-performing subjects, interpreted as autonomic biosignals supplying compensatory information when systemic physiological noise contaminated fNIRS [28]. The implication is that fusion architectures should be evaluated not only by mean improvement but by their performance in the lowest-quartile subjects, where deployment-relevant gains are concentrated. Second, not all fusion strategies deliver value, with the Wu et al. negative result indicating that the discriminating factor is whether the fusion respects modality-specific temporal and spatial complementarity [12]. The default position for new joint cerebral-muscle work should therefore be NVC-aware attention-based fusion rather than feature concatenation, with subject-stratified evaluation reported alongside aggregate metrics.

4.3.5 Application targets for joint cerebral-muscle ML pipelines

Four application domains motivate the joint cerebral-muscle pipeline most directly because they are the domains in which cortical motor signals and peripheral oxygenation must be assessed together rather than separately to answer the question of interest.

In adaptive sport and Paralympic training, the pipeline addresses bilateral asymmetry, mismatch between residual descending drive and peripheral oxygen uptake, and fatigue trajectories under conditions where group-level models trained on able-bodied athletes do not transfer. Per-subject calibration is essential, both because Paralympic populations are small and heterogeneous and because the cerebral-muscle coupling pattern itself is altered by the underlying impairment [66–67]. In stroke and spinal cord injury rehabilitation, the pipeline quantifies the recovery of cortico-muscular coupling, predicting FMA-UE and modified Barthel Index trajectories beyond what unimodal cerebral or muscle models can achieve. Lin et al.’s 20.36% NMAE reduction with multilayer EEG-fNIRS fusion is the closest existing proof-of-concept [17], and the joint cerebral-muscle pipeline extends the same logic by replacing EEG with peripheral muscle hemodynamic measurement, which is more clinically accessible and less artifact-prone during active rehabilitation. In BCI-controlled prosthesis and exoskeleton control, the pipeline closes the control loop with peripheral muscle-oxygenation feedback, complementing cortical motor decoding particularly in populations where surface EMG is unavailable or unreliable, including transhumeral amputees with degraded residual muscle innervation [61] and tetraplegic patients with severed descending pathways [58]. In exercise physiology and wearables, the pipeline addresses the question of whether a peripheral limitation, a central one, or their interaction sets the ceiling on exercise tolerance, which unimodal measurement cannot resolve. The corpus already contains the constituent pieces. Li et al. demonstrated that muscle oxygenation combined with heart rate predicts second-by-second pulmonary VO₂ across the full intensity range from below the first ventilatory threshold to 110% of peak power, establishing mNIRS as a wearable-friendly surrogate for laboratory gas exchange [66]. Chalitsios et al. showed that per-subject baselines rather than group norms are required to detect fatigue-related deviation during running, and that muscle deoxygenation tracks that deviation [9]. On the cerebral side, Ma et al. distinguished lower- from higher-attentional walking states from prefrontal fNIRS in older adults [6], indicating that the cortical cost of locomotion is decodable in the same free-living contexts. Joining these tracks would allow the attentional cost of a movement and its metabolic cost to be estimated concurrently from a single wearable montage, which is the measurement that distinguishes central from peripheral fatigue in the field rather than in the laboratory. This domain also imposes the tightest hardware constraints of the four, since the sensor must survive ambulatory motion artifact and run within a battery budget, linking it directly to the wearable deployment considerations in Section 4.4.3. Across all four domains, the joint cerebral-muscle pipeline is a research agenda assembled from corpus-validated components rather than a deployable method, and concrete validation in the named populations is the natural next step.

4.4 Deployment-relevant computational and hardware considerations

The Timing and Setting fields in Tables 1 and 2 identify which studies support the deployment-relevant observations in this section. Timing was overwhelmingly concurrent: 39 of 42 studies decoded a state present at the time of recording, two predicted a later-measured clinical outcome, and one reported both. Setting was laboratory in 21 studies, clinical in six, sport-specific in one, and mixed in one. Setting was not reported in 13 of 42 studies (31%), meaning that for almost a third of the corpus the physical context in which the model was developed cannot be established from the published text. This is itself a deployment-relevant finding: a model whose recording environment is undocumented cannot be assessed for transfer to a different one, and the reporting gap compounds the external-validation gap discussed above. Three deployment-relevant axes determine whether an fNIRS-ML model intended for rehabilitation or assistive-technology applications is fit for its target hardware: the accuracy-latency Pareto frontier (Section 4.4.1), the algorithm-hardware fit (Section 4.4.2), and wearable and embedded deployment constraints (Section 4.4.3). A model achieving 95% offline accuracy that cannot run in real time on the target hardware, or that depends on acquisition configurations incompatible with wearable deployment, is unfit for the deployment context regardless of its offline metrics, and the corpus contains the empirical evidence to characterize each of the three axes quantitatively.

4.4.1 The accuracy-latency Pareto frontier

The cerebral fNIRS corpus contains direct empirical characterization of the accuracy-latency trade-off, with three studies establishing both the existence of a Pareto frontier governed by hemodynamic physiology and the deployment-relevant choices that follow from it.

Lee et al.’s systematic sweep of feature-window length (0.6 to 15 s) against hemodynamic delay (0 to 10 s) exposed a Pareto frontier governed by hemodynamic physiology rather than model capacity, with a 14-percentage-point spread in accuracy and a four-second spread in detection latency [15]. Two consequences follow. First, any fNIRS-BCI claiming real-time applicability should report accuracy at deployment-relevant window lengths (typically 1 to 3 s for prosthetic control, 3 to 5 s for neurofeedback) rather than at the longest window that maximizes offline accuracy. Second, the gap between offline and streaming accuracy is itself an interpretability finding about the chosen window-delay configuration and should be reported as such.

The corresponding algorithm-class trade-off appeared in two studies. Khan et al. found polynomial-kernel SVM statistically superior to LDA, kNN, QDA, and naïve Bayes in offline evaluation but selected LDA for online prosthetic-leg deployment because of lower computational cost and deterministic inference latency [11]. Li et al. quantified the deployment headroom available to well-engineered classical pipelines: their LightGBM walking-intention detector executed in 2.54 ± 0.29 ms per sample against a 75-ms acquisition sampling period, leaving roughly 30-fold computational margin [46]. These quantified comparisons distinguish a publishable BCI demonstration from a deployable rehabilitation device.

4.4.2 Algorithm-hardware fit

The corpus shows clear stratification in computational requirements across algorithm families (Tables 3 and 4), with five families clustered along the inference-cost axis from microcontroller-feasible to GPU-required.

LDA has constant-time inference O(d) and runs on microcontroller-class hardware. Tuned SVM has inference complexity O(n_SV · d) that scales with training-set size and motivates LDA substitution when support-vector counts grow. Tree-based gradient boosting at deployment cost O(M · log n) per sample remains efficient for ensembles with hundreds of trees, and LightGBM’s leaf-wise growth and histogram-based split-finding are particularly suited to per-sample point-by-point classification on continuous streams [46]. CNNs and attention-based architectures require GPU-class hardware for training and benefit from GPU acceleration at inference; wearable deployment requires model distillation, quantization, or offloading to a paired smartphone. None of the included studies reported on-device inference latency for deep architectures, an omission that engineering-oriented fNIRS-ML work should address routinely in future reporting.

The acquisition-modality constraint operates in the reverse direction: hardware choice determines which downstream model classes are feasible. Continuous-wave fNIRS at 7 to 13 Hz sampling, the dominant configuration in the corpus, supports classical statistical features and shallow networks but constrains attention-based temporal modeling to coarse multi-second resolution. Frequency-domain fNIRS provides absolute oxygenation and superficial-deep separation, enabling 3D CNNs on topographic image stacks grouped by source-detector separation [60]. Time-domain fNIRS, currently absent from the corpus, would in principle support photon-time-of-flight features that no current ML pipeline exploits. Hardware capability advances ahead of analytical innovation in this field, and research design should be deliberate about which acquisition configurations license which downstream model classes.

4.4.3 Wearable and embedded deployment constraints

Three constraints distinctively shape wearable and embedded fNIRS-ML deployment beyond the algorithm-hardware fit considerations of Section 4.4.2: power and memory budgets, motion-artifact and probe-stability drift during ambulatory deployment, and end-to-end latency. Power and memory budgets on battery-operated wearables are typically two to three orders of magnitude tighter than on workstation hardware, favoring quantized fixed-point inference and ruling out large transformer architectures without aggressive distillation. Probe stability and motion-artifact handling face longer-duration drift during ambulatory deployment than during seated laboratory paradigms, and the corpus contains two viable engineering strategies: the per-subject calibration of Chalitsios et al. [9] in running and the windowed approach of Li et al. [46] in walking. End-to-end latency budgets, including acquisition, preprocessing, feature extraction, inference, and downstream actuation, must fit within the application’s control-loop tolerance, typically a few hundred milliseconds for closed-loop neurofeedback and somewhat tighter for direct assistive-device control.

Reporting these end-to-end latencies broken down by pipeline stage would substantially improve the interpretability of fNIRS-ML performance figures for engineering reviewers and deployment teams. Engineering-oriented reporting standards should evolve accordingly, with explicit specification of training-time and inference-time computational cost, hardware target, end-to-end latency, and the accuracy-latency trade-offs that govern the chosen operating point.

4.5 Limitations of this review

Five limitations qualify the conclusions of this review. First, eligibility was restricted to English-language publications, and given that 18 of 42 included studies had first authors based in China, the Chinese-language NIRS-ML literature is likely undersampled and the geographic distribution of methodological practice may be incompletely characterized. Second, the search cutoff was April 2026, and given that 35 of 42 studies appeared from 2020 onward, studies of clear relevance published after the search cutoff will be incorporated during revision. Third, we did not undertake meta-analytic pooling because heterogeneity in target outcomes, performance metrics, validation strategies, and populations renders a common effect estimate uninterpretable; the trade-off is that we report no quantitative effect sizes for the methodological patterns identified across the cerebral fNIRS, mNIRS, and joint-modality syntheses. Fourth, PROBAST [42] and TRIPOD+AI [43] were developed for clinical prediction models, and their fit to BCI-style decoding studies and physiological monitoring tasks is imperfect; we adapted certain items where the original specifications did not map cleanly onto BCI-style decoding studies, and residual judgment calls remain, particularly on the Analysis domain. Fifth, our appraisals were performed in duplicate by independent reviewers with adjudication, but we did not externally validate our PROBAST and TRIPOD+AI judgments against a third assessor team, so the appraisal layer of this review carries a methodological constraint analogous to the one we identify in the corpus itself.

5 Conclusions

This systematic review of 42 studies on ML applications to NIRS-based cerebral and muscle oxygenation in motor rehabilitation and sports training contexts identifies four cerebral fNIRS-ML patterns, three mNIRS-ML patterns, and one open methodological frontier. In cerebral fNIRS, physiologically grounded feature engineering is the principal leverage point for accuracy at current sample sizes; chromophore selection is task-dependent and should not default to HbO without justification; motor imagery decoding consistently underperforms motor execution decoding by 15 to 25 percentage points and requires architecturally different ML pipelines; and subject-independent generalization is underreported, with within-subject accuracy figures systematically misestimating deployment-relevant performance. In mNIRS, muscle-physiology-specific feature transformations such as common-mode/differential-mode signal decomposition and time-frequency band separation are the principal methodological innovations, distinguishing muscle ML pipelines from their cerebral counterparts; the high reported accuracies in the corpus are inflated by sliding-window validation strategies and require subject-wise reporting and external validation to be interpretable; and per-subject calibration represents the validation paradigm best matched to the small heterogeneous cohorts that motivate clinical translation.

The defining gap is structural rather than incremental: no included study recorded cerebral fNIRS and mNIRS jointly in co-location, despite eleven studies adopting other forms of multimodal integration and despite the brain-muscle axis being the substrate of motor rehabilitation, BCI-controlled prosthesis, and adaptive sport. The methodological building blocks for joint cerebral-muscle ML pipelines exist across the corpus, distributed across studies that each addressed a single component, including subject-specific neurovascular coupling deconvolution, canonical-HRF latency matching, common-mode/differential-mode physiological decomposition, hierarchical attention-based fusion, and per-subject calibration. The next step for the field is the integration of these components into co-located joint cerebral-muscle pipelines validated in adaptive sport, stroke and spinal cord injury rehabilitation, and BCI-controlled assistive technology, with engineering-oriented reporting of computational cost, inference latency, and accuracy-latency trade-offs to support real-world deployment.

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