Originality: The tasks or methods are not new exactly, as they have been applied in electrophysiology (reference 8 in the manuscript), but they are new as applied to fMRI. This is therefore important. Quality: Experiments and application of methods are entirely sound, gpfa method is compared to other PCA methods and is applied to large datasets. Authors acknowledge prospective work needs to be done to draw conclusions in their AD results. Clarity: The submission is well written and organized. Significance: The significance is perhaps the weakest area judged because authors take a known method from a different modality (GPFA has been used extensively in electrophysiology which the authors acknowledge) and apply it to fMRI. To my knowledge the authors have been able to reach conclusions not previously reachable with other dimensionality reduction methods in fMRI datasets. It is important to apply methods from other complementary fields to reach broader conclusions about brain dynamics even if not inventing an entirely new algorithm to do so.

The authors provide a new integrated analysis approach (allowing for simultaneous dimensionality reduction and the possibility of de-noising/artifact correction) to assess slow and infra-slow fluctuations of functional MRI data. They evaluate their approach in a very representative sample and show its potential utility by decoding the task that participants were asked to perform, while being scanned, as well as by predicting behavioral scores from the newly derived latent components as well as clinically-relevant outcomes in a clinical sample. In the following sections, I provide specific feedback with respect to originality, quality, clarity and significance. I hope you will find my comments helpful and constructive. Originality To my knowledge the proposed approach is a novel and innovative way of assessing (task-related or task-free) functional connectivity in the brain in a data-driven manner. Due to its inherent flexibility (e.g. the possibility of incorporating different sources of noise and other covariates of interest, as well as explicitly specifying different kernels), I believe it constitutes a very promising approach that can be extended to address a wide range of questions in the future. While reading the introduction I had the impression that the authors slightly miss-represent the current level of understanding with respect to slow fluctuations or the BOLD response in the brain. While it is true that there are open questions, also with respect to neurovascular coupling, there are studies that have shed light on the nature of the BOLD response (most notably: Logothetis et al., 2001, Neurophysiological investigation of the basis of the fMRI signal, Nature; or Lee et al., 2010, Global and local fMRI signals driven by neurons defined optogenetically by type and wiring, Nature). Claims like ‘For the aforementioned reasons, however, it is unclear whether slow and infra-slow brain dynamics, as measured with fMRI, are relevant for cognitive function.’ (L. 30) seem to be a bit of an overstatement. Especially since I believe that BOLD responses have been related to cognitive function in thousands of studies and these bold responses also fall into the category of what the authors term slow fluctuations (since a canonical HRF has a duration of ~25s-30s corresponds to 0.04-0.033 Hz). I fail to see how these dynamics are qualitatively different from the dynamics the authors study. I also fail to see how one would be able to interpret any dynamics faster than 1Hz given that a typical sampling rate is about 2s (0.5Hz) and the corresponding Nyquist frequency is 0.25 Hz. Can one expect any meaningful sampling of higher frequencies at all in an fMRI study? Despite these issues, I believe the study to make a very original and useful contribution, but I would recommend framing it rather as a new method to study functional connectivity in the brain, with less emphasis on ‘slow dynamics’, which suggests to readers that this is something fundamentally different than what has been done before. Clarity & Quality The paper is written clearly and concisely. I especially appreciate the effort the authors made to show robustness with respect to a different parcellation, comparisons with known strategies, as well as the prediction applications. In the following, I have a few open questions and suggestions for further improvement: One aspect that could be improved is the section about predicting MCIc, it requires a more detailed description of the procedure (at least in the supplementary material). It is unclear to me how the authors accounted for the class-imbalance. Has there been class-weighing, over- or under-sampling? As I understood the supplementary material it seems to me that the MCIs group was over-sampled, however, the MCIc group constitutes the less frequent class. Would you care to elaborate on that? It is also unclear to me why LSO-CV was chosen, as it is prone to overfit. Would a different CV strategy (5-fold for example) not be more appropriate? It would also be helpful to assess ‘potential artifact’ maps and show them to the reader. Do they present known artefactual spatial pattern (close to the boundaries of the brain or ventricles)? Also is the assumption ‘For example, artifacts, such as scanner noise or physiological noise, are unlikely to be synchronized across subjects, whereas dimensions strongly locked to salient aspects of the task would be highly synchronized.’ (L. 154 ff.) indeed correct, since for example behavioral responses that cause motion artifacts may be synchronized across subjects and occur on a slow time scale (e.g. one motion in each trial of the task)? In Figure 2D and 2E it seems as if PCA series-based task classification worked as well as GPFA-series-based classification, secondly, the same seems to be true for GPFA-spectra vs. ROI-spectra. Would it be more accurate to state the GPFA method was at-least as good as conventional methods (rather than stating that it outperformed the conventional methods (L184)? How did you assess significance here? L.186 paragraph on predicting behavioral measures: It would be good to inform the reader on the selection criteria of the behavioral measures you chose to predict. Were they randomly selected or based on previous literature? Also you write ‘that a majority of scores were consistently well predicted’ (L195). Arguably, a correlation of ~.2 is not a very good prediction, it may be a significant prediction, but it certainly does not explain a lot of variance in the target. Maybe this could be rephrased a bit more cautiously. Significance As I already alluded to, I believe that this work constitutes a significant methodological contribution as this approach is a novel and innovative way of assessing (task-related or task-free) functional connectivity in the brain in a data-driven manner. Additionally, the authors undergo a lot of effort to make comparisons to existing methods and validate the predictive utility. Applying this method to a clinical sample constitutes a very valuable empirical contribution in and of itself. COMMENTS TO THE AUTHORS' RESPONSE: First of all, I wanted to thank the authors for a very carefully drafted response. I appreciated that you addressed my concerns in detail. I feel that you adequately address most of my concerns. I would only like to suggest that you include your rationale for selecting behavioral measures in the supplement of the revised manuscript and I would like to clarify one comment I made regarding the implications of your work with respect to how the brain works. I agree that your methods may allow some insights into connectivity pattern that drive task-specific behavior or preceed disease. I just wanted to point out that a data-driven method of the sort that you use comes at a cost of reduced interpretability. If one explicitly models the hemodynamic response function one can make inferences on local vasculature more readily and it is somewhat simpler to relate the BOLD response to neuronal activity. Of course, assumptions that are made to model this can be wrong and this is were I see and aknowledge the added value of your approach. I also want to reiterate that for a potential clinical application (as you have shown) interpretability plays a secondary role. I just felt that this potential short coming should be aknowledged (you also run into this, when it comes to interpreting the high-frequency latents) and would like to encourage you to focus on applications such as the MCI prediction in the future, which I believe is much more valuable than classifying task (however, I understand your motivation for using this as a first toy example). I thank you very much for your great work and hope it will receive the credit it deserves.

One of the primary challenges in fMRI datasets is the slow hemodynamic response. This paper proposes to employ a Gaussian Process Factor Analysis (GPFA) approach for dealing with the mentioned problem. In practice, GPFA is applied to slowly sampled fMRI features provided by the Human Connectome Project for mapping the neural activities to a lower-dimensional space and then extracting smooth latent dynamics. This topic is interesting, and the experiments show some improved accuracy. However, the machine learning novelties and the contributions of this paper is ambiguous. The primary concerns and the minor comments are listed in the following: 1. Although extracting a new lower-dimensional feature space from neural activities (by using GPFA) can increase the accuracy of analysis, there is no causal effect to demonstrate that this improvement is related to fixing the slow hemodynamic issue! 2. Another concern here is the number of data resources. Although the number of samples is acceptable, these data are provided from the same resource. How will the performance of the proposed method be changed if we have batch effects such that fMRI datasets are collected from different machines or locations? 3. The proposed method must be clearly formulated. While this paper in the current format provided a long story (in both the original article and the supplementary material), it is hard to follow the main idea. 4. The limitations and applications of the proposed method must be discussed in details. 5. While noisy features are mentioned repetition through the paper, there is no empirical study to demonstrate what the effect of noise on the performance of the proposed method is? 6. Table S1 in the current format is not informative-rich. === Update after reading rebuttle === Currently, the author(s) address the main concerns in the rebuttal letters, including comment 1 and 2. That is the reason that I have updated the score. However, they must present the revised version of Sections 1 and 2 (answer to comment 3). The presented answers to comments 4 to 6 also must be added to the final version of the paper.