Swin fMRI Transformer Predicts Early Neurodevelopmental Outcomes from Neonatal fMRI

Dowon Kim; Jiook Cha; Patrick Styll

REVIEW 4 major objections 5 minor 35 references

Swin fMRI Transformer Predicts Early Neurodevelopmental Outcomes from Neonatal fMRI

T0 review · 4 major / 5 minor · reviewed 2026-08-12 · deepseek-v4-flash

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Pith's one-line read SwiFT, a 4D spatiotemporal Transformer, predicts neonatal Bayley-III scores from fMRI better than connectivity-based baselines.

desk verdict The application is plausible, but the central comparison is undermined by a test-cohort mismatch that likely explains the reported ICA gains. read the letter →

arxiv 2412.07783 v3 pith:QS74WP5I submitted 2024-11-25 q-bio.NC cs.CVcs.LG

Patrick Styll , Dowon Kim , Jiook Cha This is my paper · ORCID

classification q-bio.NCcs.CVcs.LG

keywords fMRITransformerneonatalBayley-IIIgroupICAmulti-labelpredictionneurodevelopmentaloutcomesexplainableAI

verification ladder T0 review T1 audit T2 compute T3 formal

The pith

A machine-rendered reading of the paper's core claim, the machinery that carries it, and where it could break.

The reading

The paper argues that a 4D spatiotemporal Transformer called SwiFT can predict Bayley-III cognitive, language, and motor composite scores from neonatal resting-state fMRI. The central result is that combining SwiFT with group-ICA feature reduction and multi-label learning (predicting the three scores together) yields consistently better predictions than baseline models that use static functional connectivity matrices. If the claim holds, early brain scans could flag infants at risk of developmental delay, creating a wider window for intervention. The paper also shows that the model's attributions point to brain regions consistent with known functions for each outcome.

What carries the argument

The central object is SwiFT, a Swin 4D fMRI Transformer that patches 4D fMRI volumes into spatiotemporal tokens and applies shifted-window multi-head self-attention to capture local and global dependencies across space and time. The paper reduces dimensionality with group ICA (25 or 100 components), then uses dual regression to obtain subject-specific spatial maps and functional connectivity maps as input features. A shared classification/regression head predicts the three correlated Bayley-III outcomes simultaneously. Interpretations are generated with Integrated Gradients with Smoothgrad sQuare (IG-SQ), averaged across correctly classified test subjects.

What would settle it

Re-run the full pipeline with ICA components estimated from all subjects, or re-estimated within each cross-validation fold, and check whether Multi-ICA still outperforms the baselines; if the advantage disappears or shrinks to noise, the reported gains are an artifact of the held-out cohort composition.

Watch

Extended reading notes

Core claim

On the paper's own terms, the discovery is that SwiFT with group-ICA features and multi-label learning (Multi-ICA) significantly outperforms the strongest baseline in predicting Bayley-III scores: cognitive MAE p=0.004, motor MAE p=0.002, cognitive regression MSE p=0.036, language regression MSE p=0.008, and language classification accuracy p=0.004. Both single-label and multi-label SwiFT variants exceed the baselines in balanced accuracy and regression error, while pretraining on adult fMRI datasets produced only marginal gains. The authors report that multi-label predictions align with the high correlations among cognitive, language, and motor scores, and that Integrated Gradients attributions identify medial prefrontal, Wernicke's, and motor regions for the respective delay risks.

Load-bearing premise

The evaluation assumes that always keeping the 100 healthy infants used to estimate the ICA components in the training set gives an unbiased performance estimate; the test folds then consist only of the remaining infants, and the ICA features come from an outcome-selected subset.

Editorial extensions

If this is right

Multi-label learning across correlated developmental domains improves prediction for each individual domain.
Group-ICA feature reduction cuts input dimensionality without harming predictive performance, with 25 and 100 components performing similarly.
Balanced accuracy for at-risk classification exceeds guessing levels across all three domains, suggesting the signal is usable for early screening.
Attribution maps align with established neuroscience, giving the predictions a neurobiological interpretation.

Reading between the lines

Editorial extensions of the paper, not claims the author makes directly.

The evaluation fixed the 100 healthy ICA-estimation subjects into the training set, so test folds contain only the remaining infants; re-estimating ICA inside each fold could change the reported gains.
Adult-data pretraining gave marginal gains, so the paper's evidence suggests cross-age pretraining is not an effective transfer path; neonatal-specific pretraining should be tested.
Significance testing across numerous metrics without correction means some reported p-values would not survive a multiple-comparison adjustment; the robust core is the regression and motor/language improvements.
The interpretation maps are averaged only over correctly classified subjects, which may make attributions look more consistent than they would be across all test cases.

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Editorial analysis

A structured set of objections, weighed in public.

Desk editor's note, referee report, and a circularity audit.

Desk Editor's Note

read the letter

Quick take: the paper’s central comparison is compromised. Multi-ICA’s reported gains over baselines (cognitive MAE p=0.004, motor MAE p=0.002) may be an artifact of different test cohorts. Section 3.4 says the 100 healthy subjects used for Group ICA were always in the training set. That means ICA models are tested only on the remaining, healthier, GA-restricted subjects, while the baseline models in Section 3.2 appear to be evaluated on the full 619-subject cohort. You can’t run a significance test between metrics computed on different test populations and call it a consistent improvement.

What’s new: applying SwiFT to neonatal fMRI for BSID-III prediction, with multi-label learning and ICA features, is a legitimate new application. The paper is transparent: it reports means and SDs over 5-fold CV, admits pretraining didn’t transfer, and notes that ICA dimensionality (25 vs 100) made little difference. That level of honesty is welcome.

The soft spots, in order of severity: (1) the test-cohort mismatch above; (2) the group ICA maps are estimated once from outcome-selected healthy subjects and not re-estimated within each fold, which violates a clean nested-CV design and means test features depend on a non-representative atlas; (3) the statistical test is underspecified – no test name, no multiple-comparison correction, and folds are correlated because the same 100 subjects appear in every training set. These are fixable with a matched-cohort re-analysis and proper nested CV. Effect sizes are modest (AUC ~0.6), and no code is released, but those are secondary for an application paper.

Who this is for: researchers working on early neurodevelopmental prediction from fMRI and on transformer applications to small medical imaging datasets. It’s a worthwhile question and the pipeline is plausible, so I’d send it to review rather than desk-reject. But the authors need to redo the evaluation before the comparative claims can be trusted.

Recommendation: peer review, with major revision expected.

Referee Report

4 major / 5 minor

Summary. The paper introduces SwiFT, a 4D Swin Transformer, to predict Bayley-III cognitive, language, and motor composite scores from neonatal resting-state fMRI in the dHCP cohort. The authors evaluate SwiFT on raw fMRI volumes and on group-ICA-reduced features, under both single-label and multi-label prediction, comparing against ROI-based baselines (BrainNetCNN, VanillaTF, BNT, XGBoost). They report that a multi-label ICA-based variant (Multi-ICA) significantly outperforms the strongest baseline on several metrics, with p-values such as p=0.004 for cognitive MAE and p=0.002 for motor MAE in Section 3.5. They also use Integrated Gradients with Smoothgrad SQuare to identify brain regions associated with each outcome. The central empirical claim is that Multi-ICA provides significant and consistent gains over the best baseline, with the strongest evidence claimed for regression tasks.

Significance. If the evaluation were sound, the paper would be of interest to the neurodevelopmental-prediction community: predicting Bayley-III scores from neonatal fMRI is a clinically relevant task, the use of a 4D spatiotemporal Transformer is a reasonable architectural choice, and the inclusion of group-ICA feature extraction and IG-SQ interpretability adds value. The paper also uses a well-known public dataset (dHCP) and reports multiple baselines. However, the current evaluation protocol contains a test-cohort mismatch, outcome-based selection in the ICA feature-extraction step, and underspecified statistical testing. These issues directly affect the validity of the reported p-values and the paper's central claim that Multi-ICA significantly and consistently outperforms the baselines. The interpretability analysis is a strength but does not compensate for the statistical weaknesses in the predictive comparison.

major comments (4)

[Section 3.4 vs. Section 3.1] The evaluation protocol for ICA-based models is not comparable to that for the baselines. Section 3.4 states that 'the 100 healthy subjects used for Group ICA were always included in the training set,' which means the test folds for ICA experiments always exclude those 100 subjects. Section 3.1 states that '5-fold cross-validation ensured consistent and fair splits between experiments,' suggesting that the baseline experiments in Section 3.2 use the full cohort (619 subjects with usable fMRI data). If this is the case, the Multi-ICA results in Table 3 and the baseline results in Table 1 are computed on different test populations, and the p-values in Section 3.5 comparing them are not valid. Please specify the exact subject count and fold assignment for every experiment, and either use identical test-fold compositions for all models or restrict all comparisons to the same subject subset.
[Section 3.4, 'Data Sampling'] The group-ICA maps are estimated from 100 neonates selected because they have all Bayley-III scores above 85, i.e., an outcome-selected healthy subset. Even though ICA itself is unsupervised, the choice of the 100 subjects uses the outcome labels, and the same 100 subjects are always placed in the training set. This has two consequences: (i) the ICA atlas is estimated from a non-representative, healthy-only sample, and (ii) for test subjects, the ICA features are derived from an atlas that was built using label information and the same atlas is reused across all folds. This can bias the feature space and inflate apparent performance of ICA-based models. Please justify this design or re-estimate the ICA within each training fold on training data only, without selecting subjects by outcome.
[Section 3.5] The statistical significance analysis is underspecified. No test name is given, no correction for multiple comparisons is described, and the fold structure (the same 100 subjects appear in every training fold) creates dependence across folds that standard paired tests do not handle. The p-values reported (e.g., cognitive MAE p=0.004, motor MAE p=0.002) are not tied to a specific test procedure, and it is not stated whether they compare the Multi-ICA model to the best baseline for each metric or to raw SwiFT. Given the large number of metrics, tasks, and model variants, a multiple-comparison correction is essential. Please provide the full statistical testing protocol, including the test name, the paired comparison unit, and the correction method.
[Section 3.3] The claim that 'SwiFT yielded significant performance gains for both regression and classification tasks' in the raw-fMRI experiments is not supported by any reported significance test. The only p-values appear in Section 3.5 and concern the Multi-ICA variant. If the paper intends to claim significant gains for raw SwiFT (Table 2) over baselines (Table 1), those comparisons must be statistically tested as well, with the same cohort-matching and multiple-comparison considerations. As written, this statement overstates the evidence.

minor comments (5)

[Section 3.4, 'Training Process'] The sentence 'Due to the specific sequence lengths required for IC-based training (42 and 100)' is confusing: earlier in Section 3.3 the sequence lengths are given as 20, 50, and 100. Please clarify what the values 42 and 100 refer to.
[Figure 4 caption] The caption says 'The strongest baseline was taken to represent baseline performance' but does not specify which baseline was used for each task and metric. Please give the exact baseline model per comparison, as the best baseline varies across metrics in Table 1.
[Section 5] The sentence 'could be implemented into the current pipeline without major changes Finally, pretraining on adult data...' is missing a period or semicolon between 'changes' and 'Finally'. Please fix the punctuation.
[Abstract] The abstract states that 'SwiFT significantly outperforms baseline models' but Section 3.5 reports several non-significant comparisons (e.g., cognitive classification AUC p=0.413). Please temper the abstract to reflect the specific metrics and model variants for which significance was found.
[Tables 1-3] The tables would be more readable if the best result in each column were bolded or marked, and if the number of subjects used in each experiment (e.g., 619 vs. 519) were stated in the table caption. This would also help the reader identify the cohort mismatch discussed above.

Circularity Check

0 steps flagged · score 0.0 of 10

No significant circularity: the paper's central predictions rest on new empirical evaluations, not on fitted parameters or self-referential definitions.

full rationale

The paper's central claim is that SwiFT, especially the Multi-ICA variant, outperforms baseline models in predicting Bayley-III scores from neonatal fMRI. This claim is supported by new experiments on the dHCP cohort (Tables 1-3), not by a derivation that reduces to its inputs. The SwiFT architecture is cited from the authors' prior work [15], but the paper re-trains and evaluates the model on a different dataset and outcome domain; the self-citation is an implementation reference, not the sole evidence for the performance claim. Group ICA is estimated on 100 healthy subjects who are always assigned to the training set; while this is a label-based sample selection that may bias the evaluation and make comparisons with baselines imperfect, it does not make the predicted scores equal to the ICA fit or to any training label by construction. The IG-SQ maps are post hoc interpretations and do not feed back into the predictive pipeline. Potential concerns about different test cohorts or statistical testing are methodological validity issues, not circular-reasoning steps. Consequently, no circularity is established.

Assumptions & free parameters 5 free parameters · 5 assumptions · 0 invented entities

The paper's central claim rests on standard machine-learning practices (data splitting, hyperparameter tuning) and several domain assumptions about neonatal fMRI preprocessing and ICA generalizability. There are no newly invented physical entities. The free parameters are mainly hyperparameters chosen by search or prior work.

free parameters (5)

Sequence length = 50
Selected by hyperparameter search over 20, 50, 100; yields best performance (Section 3.3).
Number of ICA components = 25 and 100
Evaluated two dimensionalities; performance insensitive (Section 3.4).
MIGP top eigenvectors = 1200
Chosen following UKB pipeline (Section 3.4).
Input padding = 64 for scratch, 96 for pretrained
Adopted to align with SwiFT architecture and pretraining (Section 3.1, 3.3).
Maximum training epochs = 100
Increased due to small dataset and transformer data demands (Section 3.4).

assumptions (5)

domain assumption Bayley-III composite score threshold of 85 separates average development from risk of delay.
Taken from Johnson et al. [5], used to define binary classification labels (Section 2).
domain assumption The dHCP preprocessing pipeline and 40-week template registration produce fMRI data suitable for model input without further artifact screening.
Invoked in Section 2 when describing preprocessing; the paper states 'Since FIX denoising was performed, we did not identify artifactual components' (Section 3.4).
domain assumption Group ICA computed on 100 normally developing neonates provides features that generalize to all test subjects.
The ICA maps are used to generate features for all subjects, including those with delays (Section 3.4).
domain assumption Keeping the 100 ICA subjects always in the training set yields unbiased performance estimates.
Stated in Section 3.4 as minimizing bias, but it changes test distribution.
domain assumption The adjusted metrics (MAEadj, MSEadj) reflect meaningful rescaled values.
Used in tables but the rescaling is not defined (Section 3.1).

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Cite this review

Pith. "Pith review of Swin fMRI Transformer Predicts Early Neurodevelopmental Outcomes from Neonatal fMRI." pith.science (2026). https://pith.science/paper/QS74WP5I

@misc{pith2026241207783,
  author       = {Pith},
  title        = {Pith review of: Swin fMRI Transformer Predicts Early Neurodevelopmental Outcomes from Neonatal fMRI},
  year         = {2026},
  howpublished = {\url{https://pith.science/paper/QS74WP5I}},
  note         = {Machine review of arXiv:2412.07783}
}

read the original abstract

Brain development in the first few months of human life is a critical phase characterized by rapid structural growth and functional organization. Accurately predicting developmental outcomes during this time is crucial for identifying delays and enabling timely interventions. This study introduces the SwiFT (Swin 4D fMRI Transformer) model, designed to predict Bayley-III composite scores using neonatal fMRI from the Developing Human Connectome Project (dHCP). To enhance predictive accuracy, we apply dimensionality reduction via group independent component analysis (ICA) and pretrain SwiFT on large adult fMRI datasets to address the challenges of limited neonatal data. Our analysis shows that SwiFT significantly outperforms baseline models in predicting cognitive, motor, and language outcomes, leveraging both single-label and multi-label prediction strategies. The model's attention-based architecture processes spatiotemporal data end-to-end, delivering superior predictive performance. Additionally, we use Integrated Gradients with Smoothgrad sQuare (IG-SQ) to interpret predictions, identifying neural spatial representations linked to early cognitive and behavioral development. These findings underscore the potential of Transformer models to advance neurodevelopmental research and clinical practice.

Figures

Figures reproduced from arXiv: 2412.07783 by the authors.

**Figure 1.** Distributions of composite scores based on binary classification. Assumptions made in [5] largely hold true. MRI Acquisition and Processing MRI data were acquired on a 3T Philips Achieva system with a neonatal 32-channel head coil. The imaging protocol was tailored to the unique characteristics of the neonatal brain. Resting-state fMRI (rs-fMRI) was captured with a multiband-accelerated echo-planar imaging sequence … view at source ↗

**Figure 2.** Rationale of using large amounts of brain fMRI data across different datasets to make up for the little amount of data available for neonates. We expect that learned features from elderly, adult and child data will generalize to limited neonatal fMRI data and thus improve downstream performance for neonates. Single-Label Prediction The choice of sequence length had a notable impact on the model’s performance. A leng… view at source ↗

**Figure 3.** UML Flowchart depicting the workflow to extract features and connectivity maps by leveraging Group Independent Component Analysis [9], [8] and [21]. Results Training Process For each dimensionality, the model was tuned using a predefined hyperparameter search space, including learning rate, patch size, and data augmentation strategies (see Section 3.3). With ICA reducing the input data to a fraction of its original… view at source ↗

Figures from the paper (3 more)

**Figure 4.** Figure 4: Overview of the models’ predictive power via 5-fold cross-validation for BSIDIII regression (MAEadj ) and classification (ACCbal). The strongest baseline was taken to represent baseline performance. Performance by transfer-learning and 100 ICs was omitted due to no st…

**Figure 5.** Figure 5: A glimpse into network-level interpretations, focusing on IC 5 (left) possibly representing the Executive Control Network (ECN). We can see how this network adds to activation in the medial prefrontal cortex for prediction of cognitive delay (right). The analysis revea…

**Figure 6.** Figure 6: Interpretation maps with thresholded Integrated Gradients (IG) maps averaged across ICs for risk of cognitive (top), language (middle) and motor (bottom) delay. These findings reinforce the model’s ability to capture neurobiologically meaningful spatiotemporal pattern…

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2022 doi

Pith tools

Reviewed August 12, 2026 · model on record in the stance chip above.

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Scientific Reports 11, 9068 (2021)

Tustison, Nicholas J., Cook, Philip A., Holbrook, Andrew J., Johnson, Hans J., Muschelli, John, Devenyi, Gabriel A., Duda, Jeffrey T., Das, Sandhitsu R., Cullen, Nicholas C., Gillen, Daniel L., Yassa, Michael A., Stone, James R., Gee, James C., Avants, Brian B.: The ANTsX ecosystem for quantitative biological and medical imaging. Scientific Reports 11, 90...

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Jeremy Kawahara, Colin J. Brown, Steven P. Miller, Brian G. Booth, Vann Chau, Ruth E. Grunau, Jill G. Zwicker, Ghassan Hamarneh: BrainNetCNN: Convolu- tional neural networks for brain networks; towards predicting neurodevelopment. NeuroImage 146, 1038-1049 (2017)

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