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Under review as a conference paper at ICLR 2027

Representation Over Capacity: Sparse Temporal Access for Functional Connectivity

Abstract

Resting-state fMRI is inherently temporal, yet most brain-network models operate on a static summary of the signal. Standard functional connectivity (FC) compresses an entire BOLD scan into a single matrix, averaging away how interactions between brain regions evolve over time. We argue that this creates a representational bottleneck: once temporal variation is discarded, increasing downstream model capacity cannot recover it. We introduce **TempLasso**, a deliberately low-capacity temporal FC model that selects a small set of discriminative connections, tracks them across local FC windows, and models their trajectories with a lightweight BiGRU. Across three rs-fMRI cohorts and five static FC backbones, TempLasso outperforms 13 of 15 substantially more complex static models. When used as a plug-and-play temporal branch, **X+TempLasso** improves all 15 backbone–dataset combinations, with an average gain of +4.63 AUC points. In contrast, directly applying the full static backbone to every temporal window is markedly less reliable, showing that greater per-window model capacity does not necessarily translate into better temporal modeling. A complementary theoretical analysis formalizes static FC as a many-to-one temporal compression: Bayes-optimal prediction with temporal access cannot be worse than prediction restricted to static FC, and can be strictly better when discarded temporal structure is task-relevant. Together, these results suggest that progress in brain-network learning may depend less on increasingly elaborate models of a static connectome and more on preserving and exploiting the temporal structure already present in the signal.

Primary area:
applications to neuroscience & cognitive science
Keywords:
esting-state fMRI, functional connectivity, dynamic functional connectivity, temporal graph learning, brain network learning, connectomics, representation learning, neuroimaging

Reviews

Among:
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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_KQ2TOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

The paper investigates whether preserving temporal connectivity information can be more valuable than increasing model capacity on static FC. TempLasso selects discriminative connections using ℓ1-regularized logistic regression and models their sliding-window trajectories with a BiGRU. It can also augment existing static backbones through fusion. Experiments cover three cohorts and five backbones, with additional temporal-order and windowing controls.

Critical strengths
  1. The paper asks a clear and relevant question; whether static aggregation limits FC modeling more than architectural capacity. TempLasso provides a simple temporal branch that can augment different static backbones. The writing and introductory primer make the work accessible to an ML audience.

  2. The training and model-selection protocol includes useful safeguards. Models use identical subject splits, normalization and edge selection are fitted on training subjects only, and configurations are selected using validation data. Per-combination paired tests are reported, including non-significant results.

  3. The experiments include informative controls beyond the main static comparison; full-backbone temporalization, shuffled-order and order-invariant aggregators, and window-length sensitivity. Positive mean fusion gains across all 15 backbone–dataset combinations provide encouraging empirical evidence.

Critical weaknesses
  1. The source of the temporal benefit remains insufficiently isolated. Although the order-invariant MLP control is useful, a static classifier on the same selected edges and simple window-summary baselines are missing. The experiments also do not establish whether the gains require time-varying coupling or can be explained by stationary temporal statistics, sampling variability, or acquisition-related effects.

  2. The fusion results do not isolate temporal complementarity from general ensemble benefits. Prediction-level fusion averages independently trained static and temporal models, but no matched static–static fusion control is provided. Reporting positive gains in all 15 combinations therefore supports augmentation empirically without establishing how much benefit specifically requires temporal inputs.

  3. The “representation over capacity” interpretation is not cleanly isolated. TempLasso and TempX differ in supervised edge selection, input dimensionality, and architecture, alongside capacity. Selected-edge counts and parameter counts are not reported, and edge selection itself is not ablated. These omissions make it difficult to distinguish the benefits of temporal access, sparsity, and model size.

  4. Statistical support remains limited by dependence and small cohorts. The aggregate tests treat 15 combinations sharing cohorts and splits as independent, while PPMI test splits contain approximately three participants from each minority class. Reporting inconsistencies also require clarification, particularly standalone PPMI performance in Table 2 versus Tables 8–10 and the GRU performance gap stated in Appendix C.3.

Questions for authors
  1. Please compare against a static logistic/MLP classifier on the same selected connections, using matched FC preprocessing, and a simple classifier on per-edge mean/SD of windowed FC. Together with the existing order-invariant MLP, these would help isolate which information accounts for the gains.

  2. How does X+TempLasso compare with X fused with another static predictor under the same validation and fusion protocol? Please also report which fusion strategy, embedding concatenation or probability averaging, was selected for each split and backbone–dataset combination.

  3. Please ablate supervised edge selection using random edges matched in number and, where feasible, all 4,950 edges with the same temporal aggregator. Report selected-edge counts across splits and trainable parameter counts, so that the sparsity and low-capacity claims can be assessed separately.

  4. How is the shuffled-window permutation generated: independently per subject, per epoch, or fixed? Since shuffling overlapping windows also disrupts local smoothness, a matched stationary-surrogate experiment preserving static covariance and ROI power spectra, with corresponding model retraining and evaluation, would help clarify whether changing coupling is necessary for the observed benefit.

  5. Please provide dependence-aware uncertainty estimates for the aggregate gains and clarify the stability of model selection with very small clinical validation sets. Also reconcile PPMI TempLasso performance of 62.12±8.30 in Table 2 versus 62.98±7.42 in Table 8, and the reported GRU gap of 2.18 versus 1.49.

Reviewer_JMgzOpenReview ↗
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2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper studies whether preserving temporal functional-connectivity information is more useful than increasing the capacity of models operating on a single whole-scan paradigm. TempLasso is developed by introducing sliding-window in covariance estimation, selecting a fixed subset of edge with L1-regularized logistic regression, and summarizing their trajectories with a small BiGRU. TempLasso is suitable for combination with existing static FC backbones. Experiments show that TempLasso yields better performance in all 15 configurations of backbones and datasets. Theoretical analysis is performed about how original temporal signal can outperform restriction to static FC.

Critical strengths
  1. The paper evaluates the same lightweight temporal branch with five backbone families on three cohorts. All 15 augmentation comparisons have positive mean gains. This consistency across the evaluated settings is meaningful to support the claim that sparse temporal access serves as an addition to existing FC pipelines.

  2. The authors provide a well-controlled ablation analysis of temporal aggregation by keeping the selected edges fixed while varying temporal aggregation. The ordered BiGRU performs best on the two evaluated ablation cohorts, and TempX offers a comparison with applying a full static encoder to every window. These results support the effectiveness of the representation and aggregation of temporal FC.

Critical weaknesses
  1. The edge selection in L1- regularized logistic regression does not consider the tendency of each edge weight. The edge selection is invariant to window order, which affects the discrimination between two ordered trajectories. As a result, connections that are informative for temporal dynamics can be discarded before the BiGRU step to cause critical information loss.

  2. The stability of edge selection given different seeds is not analyzed. The choice of random seed in model initialization may lead to different coefficients in l1-regression and further result in different set of selected edges. There are no experiments to evaluate the stability under different seeds.

  3. Experimental results are not consistent in the manuscript and appendix. The performance of TempLasso in PPIM is 62.12±8.30 in Table 2 but 62.98±7.42 in Tables 8 and 9.

Questions for authors
  1. With the same local FC windows and temporal encoder, how does L1 selection compare with matched-K random edge subsets and a full-edge or projected-edge input under a comparable parameter budget?

  2. Will the selected edge set dramatically change given different seeds in L1-regularized logistic regression model initialization? How intense does such change influence the performance of TempLasso?

1 comment

Dear Reviewer JMgz,

As the discussion period closes tomorrow, we wanted to check whether our responses and the revised paper address your concerns, and we would be glad to clarify anything before the deadline. Thank you again for your time and constructive review.

Authors

Reviewer_AdJGOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
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2
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Paper summary

TempLasso selects functional connections using training-only L1-regularized logistic regression, tracks these connections across local FC windows, and summarizes their trajectories with a small BiGRU. The branch can operate alone or be fused with a static FC backbone. Across three cohorts, the paper compares five static backbones and their temporal variants, reports positive mean fusion gains in all 15 combinations, and uses window-order and aggregation controls to study temporal information.

Critical strengths
  1. The sparse temporal branch is a useful, practically motivated alternative to repeatedly applying a large spatial encoder to short-window connectivity. Its compatibility with different static backbones makes the empirical finding relevant beyond one architecture.

  2. The comparisons use matched subject splits and training-only edge selection, and the shuffled-BiGRU control keeps the architecture fixed while disrupting window order. These are informative controls; the consistent direction of the fusion gains is worth reporting even without treating every comparison as an independent discovery.

Critical weaknesses
  1. The main comparison does not cleanly isolate temporal access from estimation and selection choices. Static inputs come from the source benchmark, whereas the temporal branch adds resampling, shrinkage covariance, Fisher transformation, and supervised edge selection. The absence of a matched sparse-static control and actual parameter counts makes the stronger “representation over capacity” conclusion less secure than the narrower finding that this temporal branch improves the tested backbones.

  2. The aggregate significance analysis overstates the number of independent comparisons. The 15 backbone–dataset means still share subjects, splits, and the temporal branch within each cohort; averaging over seeds does not remove that dependence. Consequently, the sign-test and one-sample t-test in Appendix C.1 do not by themselves establish the reported level of cross-setting statistical evidence.

Questions for authors
  1. Does the advantage remain when a static model uses the same selected connections and a matched whole-scan covariance estimator and transformation? Comparing this with the existing window-level MLP control would separate sparse feature selection from access to within-scan variation.
  2. What are the selected-edge counts and trainable parameter counts for each validation-selected configuration? Since the BiGRU width can reach 128 per direction, these values are needed to substantiate the low-capacity comparison.
  3. How much of the fusion gain survives comparison with an equally tuned two-static-model ensemble, and which runs selected probability averaging rather than representation concatenation? A purpose-built dynamic-FC baseline would also clarify whether TempX is representative of a competitive temporal alternative.
  4. Can the aggregate inference account for dependence among backbones and overlapping subject splits? Please also reconcile the standalone PPMI result of 62.12 ± 8.30 in Table 2 with 62.98 ± 7.42 in Tables 8–10 and identify which configurations produced them.

Comments on the paper

14 comments

Regarding the rebuttal to W1/Q1:

I thank the authors for going through the effort of adding these additional experiments which I believe were definitely essential to support the major claims of the paper. I think the newly added matched static and window-summary controls address my main concerns to a great extent. The addition of the distinction between which part of the improvements come from edge selection and which from temporal sequence modelling is very valuable and I believe makes the manuscript stronger.

Regarding the rebuttal to W2/Q2:

The addition of the static-static fusion control is a very strong result and a satisfactory response to my concerns. The PPMI results are particularly strong support for the benefits of temporal fusion. So this shows that temporal fusion helped on two out of the 3 datasets. I understand this is not a trivial question but could the authors elaborate a bit more on why they think the results weren't very supportive for ADNI? I understand they note the small sample size of this dataset but do they have any ideas on what other more mechansistic difference may exists between the datasets that give rise to the lower benefits of temporal fusion in this dataset?

Regarding the rebuttal to W3/Q3:

I think the findings here are quite meaningful and add value to the revised manuscript. I thank the authors for performing these additional experiments. The fact that random edge selection performs substantially worse is promising. Just one last minor point in terms of terminology and how the authors express the results of matching parameter counts: mentioning "full-edge parameter-matched" control is not exactly accurate; since as also reported in Appendix Table 16, this is only approximate parameter matching where feasible. So maybe the authors could use a more careful terminology where adding these new results.

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

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