Author Response

The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review):

This work provides a new dataset of 71,688 images of different ape species across a variety of environmental and behavioral conditions, along with pose annotations per image. The authors demonstrate the value of their dataset by training pose estimation networks (HRNet-W48) on both their own dataset and other primate datasets (OpenMonkeyPose for monkeys, COCO for humans), ultimately showing that the model trained on their dataset had the best performance (performance measured by PCK and AUC). In addition to their ablation studies where they train pose estimation models with either specific species removed or a certain percentage of the images removed, they provide solid evidence that their large, specialized dataset is uniquely positioned to aid in the task of pose estimation for ape species.

The diversity and size of the dataset make it particularly useful, as it covers a wide range of ape species and poses, making it particularly suitable for training off-the-shelf pose estimation networks or for contributing to the training of a large foundational pose estimation model. In conjunction with new tools focused on extracting behavioral dynamics from pose, this dataset can be especially useful in understanding the basis of ape behaviors using pose.

We thank the reviewer for the kind comments.

Since the dataset provided is the first large, public dataset of its kind exclusively for ape species, more details should be provided on how the data were annotated, as well as summaries of the dataset statistics. In addition, the authors should provide the full list of hyperparameters for each model that was used for evaluation (e.g., mmpose config files, textual descriptions of augmentation/optimization parameters).

We have added more details on the annotation process and have included the list of instructions sent to the annotators. We have also included mmpose configs with the code provided. The following files include the relevant details:

File including the list of instructions sent to the annotators: OpenMonkeyWild Photograph Rubric.pdf

Mmpose configs:

i) TopDownOAPDataset.py

ii) animal_oap_dataset.py

iii) init.py

iv) hrnet_w48_oap_256x192_full.py

Anaconda environment files:

i) OpenApePose.yml

ii) requirements.txt

Overall this work is a terrific contribution to the field and is likely to have a significant impact on both computer vision and animal behavior.

Strengths:

• Open source dataset with excellent annotations on the format, as well as example code provided for working with it.

• Properties of the dataset are mostly well described.

• Comparison to pose estimation models trained on humans vs monkeys, finding that models trained on human data generalized better to apes than the ones trained on monkeys, in accordance with phylogenetic similarity. This provides evidence for an important consideration in the field: how well can we expect pose estimation models to generalize to new species when using data from closely or distantly related ones? - Sample efficiency experiments reflect an important property of pose estimation systems, which indicates how much data would be necessary to generate similar datasets in other species, as well as how much data may be required for fine-tuning these types of models (also characterized via ablation experiments where some species are left out).

• The sample efficiency experiments also reveal important insights about scaling properties of different model architectures, finding that HRNet saturates in performance improvements as a function of dataset size sooner than other architectures like CPMs (even though HRNets still perform better overall).

We thank the reviewer for the kind comments.

Weaknesses:

• More details on training hyperparameters used (preferably full config if trained via mmpose).

We have now included mmpose configs and anaconda environment files that allow researchers to use the dataset with specific versions of mmpose and other packages we trained our models with. The list of files is provided above.

• Should include dataset datasheet, as described in Gebru et al 2021 (arXiv:1803.09010).

We have included a datasheet for our dataset in the appendix lines 621-764.

• Should include crowdsourced annotation datasheet, as described in Diaz et al 2022 (arXiv:2206.08931). Alternatively, the specific instructions that were provided to Hive/annotators would be highly relevant to convey what annotation protocols were employed here.

We have included the list of instructions sent to the Hive annotators in the supplementary materials. File: OpenMonkeyWild Photograph Rubric.pdf

• Should include model cards, as described in Mitchell et al (arXiv:1810.03993).

We have included a model card for the included model in the results section line 359. See Author response image 1.

Author response image 1.  

• It would be useful to include more information on the source of the data as they are collected from many different sites and from many different individuals, some of which may introduce structural biases such as lighting conditions due to geography and time of year.

We agree that the source could introduce structural biases. This is why we included images from so many different sources and captured images at different times from the same source—in hopes that a large variety of background and lighting conditions are represented. However, doing so limits our ability to document each source background and lighting condition separately.

• Is there a reason not to use OKS? This incorporates several factors such as landmark visibility, scale, and landmark type-specific annotation variability as in Ronchi & Perona 2017 (arXiv:1707.05388). The latter (variability) could use the human pose values (for landmarks types that are shared), the least variable keypoint class in humans (eyes) as a conservative estimate of accuracy, or leverage a unique aspect of this work (crowdsourced annotations) which affords the ability to estimate these values empirically.

The focus of this work is on overall keypoint localization accuracy and hence we wanted a metric that is easy to interpret and implement, in this case we made use of PCK (Percentage of Correct Keypoints). PCK is a simple and widely used metric that measures the percentage of correctly localized keypoints within a certain distance threshold from their corresponding groundtruth keypoints.

• A reporting of the scales present in the dataset would be useful (e.g., histogram of unnormalized bounding boxes) and would align well with existing pose dataset papers such as MS-COCO (arXiv:1405.0312) which reports the distribution of instance sizes and instance density per image.

RESPONSE: We have now included a histogram of unnormalized bounding boxes in the manuscript, Author response image 2.

Author response image 2.

Reviewer #2 (Public Review):

The authors present the OpenApePose database constituting a collection of over 70000 ape images which will be important for many applications within primatology and the behavioural sciences. The authors have also rigorously tested the utility of this database in comparison to available Pose image databases for monkeys and humans to clearly demonstrate its solid potential.

We thank the reviewer for the kind comments.

However, the variation in the database with regards to individuals, background, source/setting is not clearly articulated and would be beneficial information for those wishing to make use of this resource in the future. At present, there is also a lack of clarity as to how this image database can be extrapolated to aid video data analyses which would be highly beneficial as well.

I have two major concerns with regard to the manuscript as it currently stands which I think if addressed would aid the clarity and utility of this database for readers.

1) Human annotators are mentioned as doing the 16 landmarks manually for all images but there is no assessment of inter-observer reliability or the such. I think something to this end is currently missing, along with how many annotators there were. This will be essential for others to know who may want to use this database in the future.

We thank the reviewer for pointing this out. Inter-observer reliability is important for ensuring the quality of the annotations. We first used Amazon MTurk to crowd source annotations and found that the inter-observer reliability and the annotation quality was poor. This was the reason for choosing a commercial service such as Hive AI. As the crowd sourcing and quality control are managed by Hive through their internal procedures, we do not have access to data that can allow us to assess inter-observer reliability. However, the annotation quality was assessed by first author ND through manual inspections of the annotations visualized on all of the images the database. Additionally, our ablation experiments with high out of sample performances further vaildate the quality of the annotations.

Relevant to this comment, in your description of the database, a table or such could be included, providing the number of images from each source/setting per species and/or number of individuals. Something to give a brief overview of the variation beyond species. (subspecies would also be of benefit for example).

Our goal was to obtain as many images as possible from the most commonly studied ape species. In order to ensure a large enough database, we focused only on the species and combined images from as many sources as possible to reach our goal of ~10,000 images per species. With the wide range of people involved in obtaining the images, we could not ensure that all the photographers had the necessary expertise to differentiate individuals and subspecies of the subjects they were photographing. We could only ensure that the right species was being photographed. Hence, we cannot include more detailed information.

2) You mention around line 195 that you used a specific function for splitting up the dataset into training, validation, and test but there is no information given as to whether this was simply random or if an attempt to balance across species, individuals, background/source was made. I would actually think that a balanced approach would be more appropriate/useful here so whether or not this was done, and the reasoning behind that must be justified.

This is especially relevant given that in one test you report balancing across species (for the sample size subsampling procedure).

We created the training set to reflect the species composition of the whole dataset, but used test sets balanced by species. This was done to give a sense of the performance of a model that could be trained with the entire dataset, that does not have the species fully balanced. We believe that researchers interested in training models using this dataset for behavior tracking applications would use the entire dataset to fully leverage the variation in the dataset. However, for those interested in training models with balanced species, we provide an annotation file with all the images included, which would allow researchers to create their own training and test sets that meet their specific needs. We have added this justification in the manuscript to guide the other users with different needs. Lines 530-534: “We did not balance our training set for the species as we wanted to utilize the full variation in the dataset and assess models trained with the proportion of species as reflected in the dataset. We provide annotations including the entire dataset to allow others to make create their own training/validation/test sets that suit their needs.”

And another perhaps major concern that I think should also be addressed somewhere is the fact that this is an image database tested on images while the abstract and manuscript mention the importance of pose estimation for video datasets, yet the current manuscript does not provide any clear test of video datasets nor engage with the practicalities associated with using this image-based database for applications to video datasets. Somewhere this needs to be added to clarify its practical utility.

We thank the reviewer for this important suggestion. Since we can separate a video into its constituent frames, one can indeed use the provided model or other models trained using this dataset for inference on the frames, thus allowing video tracking applications. We now include a short video clip of a chimpanzee with inferences from the provided model visualized in the supplementary materials.

Reviewer #1 (Recommendations For The Authors):

• Please provide a more thorough description of the annotation procedure (i.e., the instructions given to crowd workers)! See public review for reference on dataset annotation reporting cards.

We have included the list of instructions for Hive annotators in the supplementary materials.

• An estimate of the crowd worker accuracy and variability would be super valuable!

While we agree that this is useful, we do not have access to Hive internal data on crowd worker IDs that could allow us to estimate these metrics. Furthermore, we assessed each image manually to ensure good annotation quality.

• In the methods section it is reported that images were discarded because they were either too blurry, small, or highly occluded. Further quantification could be provided. How many images were discarded per species?

It’s not really clear to us why this is interesting or important. We used a large number of photographers and annotators, some of whom gave a high ratio of great images; some of whom gave a poor ratio. But it’s not clear what those ratios tell us.

• Placing the numerical values at the end of the bars would make the graphs more readable in Figures 4 and 5.

We thank the reviewer for this suggestion. While we agree that this can help, we do not have space to include the number in a font size that would be readable. Smaller font sizes that are likely to fit may not be readable for all readers. We have included the numerical values in the main text in the results section for those interested and hope that the figures provide a qualitative sense of the results to the readers.

Author Response

eLife assessment

Building on their own prior work, the authors present valuable findings that add to our understanding of cortical astrocytes, which respond to synaptic activity with calcium release in subcellular domains that can proceed to larger calcium waves. The proposed concept of a spatial "threshold" is based on solid evidence from in vivo and ex vivo imaging data and the use of mutant mice. However, details of the specific threshold should be taken with caution and appear incomplete unless supported by additional experiments with higher resolution in space and time.

We thank the reviewers and editors for the positive assessment of our work as containing valuable findings that add to our understanding of cortical astrocytes. We also appreciate their positive appraisal of the proposed concept of a spatial threshold supported by solid evidence.

Regarding their specific comments, we truly appreciate them because they have helped to clarify issues and to improve the study. Provisional point-by-point responses to these comments are provided below. Regarding the general comment on the spatial and temporal resolution of our study, we would like to clarify that the spatial and temporal resolution used in the current study (i.e., 2 - 5 Hz framerate using a 25x objective with 1.7x digital zoom with pixels on the order of 1 µm2) is within the norm in the field, does not compromise the results, nor diminish the main conceptual advancement of the study, namely the existence of a spatial threshold for astrocyte calcium surge.

We respect the thoughtfulness of the reviewers and editors and look forward to improving the paper to fully answer both public and private comments with a revised manuscript.

Reviewer #1 (Public Review):

Lines et al., provide evidence for a sequence of events in vivo in adult anesthetized mice that begin with a footshock driving activation of neural projections into layer 2/3 somatosensory cortex, which in turn triggers a rise in calcium in astrocytes within "domains" of their "arbor". The authors segment the astrocyte morphology based on SR101 signal and show that the timing of "arbor" Ca2+ activation precedes somatic activation and that somatic activation only occurs if at least {greater than or equal to}22.6% of the total segmented astrocyte "arbor" area is active. Thus, the authors frame this {greater than or equal to}22.6% activation as a spatial property (spatial threshold) with certain temporal characteristics - i.e., must occur before soma and global activation. The authors then elaborate on this spatial threshold by providing evidence for its intrinsic nature - is not set by the level of neuronal stimulus and is dependent on whether IP3R2, which drives Ca2+ release from the endoplasmic reticulum (ER) in astrocytes, is expressed. Lastly, the authors suggest a potential physiologic role for this spatial threshold by showing ex vivo how exogenous activation of layer 2/3 astrocytes by ATP application can gate glutamate gliotransmission to layer 2/3 cortical neurons - with a strong correlation between the number of active astrocyte Ca2+ domains and the slow inward current (SIC) frequency recorded from nearby neurons as a readout of glutamatergic gliotransmission. This is interesting and would potentially be of great interest to readers within and outside the glia research community, especially in how the authors have tried to systematically deconstruct some of the steps underlying signal integration and propagation in astrocytes. Many of the conclusions posited by the authors are potentially important but we think their approach needs experimental/analytical refinement and elaboration.

We thank the reviewer for her/his positive appraisal and comments that has helped us to improve the study. In response to their insights, we aim to address the key points raised below:

1. Sequence of Events: We acknowledge the reviewer's interest in our findings regarding the sequence of events. We will provide a more detailed description of the methods and results to clarify the temporal relationships between neural activation, astrocyte calcium dynamics, and astrocyte morphology segmentation.

2. Spatial Threshold: The reviewer accurately identifies our characterization of a spatial threshold (≥22.6% activation) with temporal characteristics as a crucial aspect of our study. We will expand upon this concept by offering a clearer illustration of how this threshold relates to somatic and global activation.

3. Intrinsic Nature of Spatial Threshold: The reviewer's insightful observation regarding the inherent quality of the spatial threshold, regardless of its dependence on neuronal stimuli is noteworthy. We will provide additional details to substantiate this claim, shedding more light on the fundamental nature of this phenomenon.

4. Physiological Implications: The reviewer rightly highlights the potential physiological significance of our findings, particularly in relation to gliotransmission in cortical neurons. We will enhance our discussion by elaborating on the implications of these observations.

The primary issue for us, and which we would encourage the authors to address, relates to the low spatialtemporal resolution of their approach. This issue does not necessarily compromise the concept of a spatial threshold, but more refined observations and analyses are likely to provide more reliable quantitative parameters and a more comprehensive view of the mode of Ca2+ signal integration in astrocytes.

We agree with the reviewer that our spatial-temporal resolution (2 – 5 Hz framerate using a 25x objective and 1.7x digital zoom with pixels on the order of 1 µm) does not compromise the proposed concept of the existence of a spatial threshold for the intracellular calcium expansion.

For this reason, and because their observations might be perceived as both a conceptual and numerical standard in the field, we believe that the authors should proceed with both experimental and analytical refinement. Notably, we have difficulty with the reported mean delays of astrocyte Ca2+ elevations upon sensory stimulation. The 11s delay for response onset in "arbor" and 13s in the soma are extremely long, and we do not think they represent a true physiologic latency for astrocyte responses to the sensory activity. Indeed, such delays appear to be slower even than those reported in the initial studies of sensory stimulation in anesthetized mice with limited spatial-temporal resolution (Wang et al. Nat Neurosci., 2006) - not to say of more recent and refined ones in awake mice (Stobart et al. Neuron, 2018) that identified even sub-second astrocyte Ca2+ responses, largely preserved in IP3R2KO mice. Thus, we are inclined to believe that the slowness of responses reported here is an indicator of experimental/analytical issues. There can be several explanations of such slowness that the authors may want to consider for improving their approach: (a) The authors apparently use low zoom imaging for acquiring signals from several astrocytes present in the FOV: do all of these astrocytes respond homogeneously in terms of delay from sensory stimulus? Perhaps some are faster responders than others and only this population is directly activated by the stimulus. Others could be slower in activation because they respond secondarily to stimuli. In this case, the authors could focus their analysis specifically on the "fast-responding population". (b) By focusing on individual astrocytes and using higher zoom, the authors could unmask more subtle Ca2+ elevations that precede those reported in the current manuscript. These signals have been reported to occur mainly in regions of the astrocyte that are GCaMP6-positive but SR101-negative and constitute a large percentage of its volume (Bindocci et al., 2017). By restricting analysis to the SR101-positive part of the astrocyte, the authors might miss the fastest components of the astrocyte Ca2+ response likely representing the primary signals triggered by synaptic activity. It would be important if they could identify such signals in their records, and establish if none/few/many of them propagate to the SR-101-positive part of the astrocyte. In other words, if there is only a single spatial threshold, the one the authors reported, or two or more of them along the path of signal propagation towards the cell soma that leads eventually to the transformation of the signal into a global astrocyte Ca2+ surge.

We thank the reviewer for these excellent and important comments. The qualm with the mean delays of astrocyte activation is indeed a result of averaging together astrocyte responses to a 20 second stimulus. Indeed, astrocyte responses are heterogeneous and many astrocytes respond much quicker, as can be seen in example traces in Figs. 1D, 1G, and 3C. Indeed, with any biological system variability exists, however here we take the averaged responses in order to identify a general property of astrocyte calcium dynamics: the existence of the concept of a spatial threshold for astrocyte calcium surge.

Further, we used a lower stimulus frequency (2Hz) than Stobart et al. (90 Hz) to assess subthreshold activities. We found that stronger stimuli decreased response delays and will include this result in the revised manuscript. Interestingly, from Fig 4F, higher stimulus did not significantly alter the spatial threshold. In the revised version of the manuscript, we will provide a more detailed analysis and the consequent discussion of this analysis.

In this context, there is another concept that we encourage the authors to better clarify: whether the spatial threshold that they describe is constituted by the enlargement of a continuous wavefront of Ca2+ elevation, e.g. in a single process, that eventually reaches 22.6% of the segmented astrocyte, or can it also be constituted by several distinct Ca2+ elevations occurring in separate domains of the arbor, but overall totaling 22.6% of the segmented surface? Mechanistically, the latter would suggest the presence of a general excitability threshold of the astrocyte, whereas the former would identify a driving force threshold for the centripetal wavefront. In light of the above points, we think the authors should use caution in presenting and interpreting the experiments in which they use SIC as a readout. Their results might lead some readers to bluntly interpret the 22.6% spatial threshold as the threshold required for the astrocyte to evoke gliotransmitter release. Indeed, SIC are robust signals recorded somatically from a single neuron and likely integrate activation of many synapses all belonging to that neuron. On the other hand, an astrocyte impinges in a myriad of synapses belonging to several distinct neurons. In our opinion, it is quite possible that more local gliotransmission occurs at lower Ca2+ signal thresholds (see above) that may not be efficiently detected by using SIC as a readout; a more sensitive approach, such as the use of a gliotransmitter sensor expressed all along the astrocyte plasma-membrane could be tested to this aim.

The reviewer raised an excellent point. Whether the spatial threshold of 22.6% occur in the segmented astrocyte or may be reached occurring in separate domains of the arbor, is an important question and we aim to address this by novel analysis that will be provided in the revised version of the manuscript.

Regarding comments on SIC, we fully agree with the reviewer. In the revised version of the manuscript, we will include text in the discussion to ensure the correct interpretation of the results, i.e., the observed 22.6% spatial threshold for the SIC does not necessarily indicates an intrinsic property of gliotransmitter release; rather, since SICs have been shown to be calcium-dependent, it is not surprising that their presence, monitored at the whole-cell soma, matches the threshold for the intracellular calcium extension.

Additional considerations are that the authors propose an event sequence as follows: stimulus - synaptic drive to L2/3 - arbor activation - spatial threshold - soma activation - post soma activation - gliotransmission. This seems reminiscent of the sequence underlying neuronal spike propagation - from dendrite to soma to axon, and the resulting vesicular release. However, there is no consensus within the glial field about an analogous framework for astrocytes. Thus, "arbor activation", "soma activation", and "post soma activation" are not established `terms-of-art´. Similarly, the way the authors use the term "domain" contrasts with how others have (Agarwal et al., 2017; Shigetomi et al., 2013; Di Castro et al., 2011; Grosche et al., 1999) and may produce some confusion. The authors could adopt a more flexible nomenclature or clarify that their terms do not have a defined structural-functional basis, being just constructs that they justifiably adapted to deal with the spatial complexity of astrocytes in line with their past studies (Lines et al., 2020; Lines et al., 2021).

We agree there is no consensus within the glial field about this event sequence. One major difference between this sequence of events and neuronal spike propagation is directionality from dendrite to soma to axon. It is unknown whether directionality of the calcium signal exists in astrocytes. The term “microdomain” is used in the references above to define distal subcellular domains in contact with synapses, and in order to dissociate from this term we adopt the nomenclature “domain” to define all subcellular domains in the astrocyte arborization. These items will be discussed and clarified in the revised version of the manuscript.

Our previous points suggest that the paper would be significantly strengthened by new experimental observations focusing on single astrocytes and using acquisitions at higher spatial and temporal resolution. If the authors will not pursue this option, we encourage them to at least improve their analysis, and at the same time recognize in the text some limitations of their experimental approach as discussed above. We indicate here several levels of possible analytical refinement.

We believe our spatial (25x objective and 1.7x digital zoom with pixels on the order of 1µm) and temporal (2 – 5 Hz framerate) resolution is within the range used in the glial field. In any case the existence of a spatial threshold for astrocyte calcium surge is not compromised with the use of this imaging resolution.

The first relates to the selection of astrocytes being analyzed, and the need to focus on a much narrower subpopulation than (for example) 987 astrocytes used for the core data. This selection would take into greater consideration the aspects of structure and latency. With the structural and latency-based criteria for selection, the number of astrocytes to analyze might be reduced by 10-fold or more, making our second analytical recommendation much more feasible.

We agree that individual differences exist, however, establishing a general concept requires the sampling of many astrocytes. Nevertheless, we aim to further address this issue in the revised version of the manuscript by analyzing the calcium dynamics in individual domains.

For structure-based selection - Genetically-encoded Ca2+ indicators such as GCaMP6 are in principle expressed throughout an astrocyte, even in regions that are not labelled by SR101. Moreover, astrocytes form independent 3D territories, so one can safely assume that the GCaMP6 signal within an astrocyte volume belongs to that specific astrocyte (this is particularly evident if the neighboring astrocytes are GCaMP6negative). Therefore, authors could extend their analysis of Ca2+ signals in individual astrocytes to the regions that are SR101-negative and try to better integrate fast signals in their spatial threshold concept. Even if they decided to be conservative on their methods, and stick to the astrocyte segmentation based on the SR-101 signal, they should acknowledge that SR101 dye staining quality can vary considerably between individual astrocytes within a FOV - some astrocytes will have much greater structural visibility in the distal processes than others. This means that some astrocytes may have segmented domains extending more distally than others and we think that authors should privilege such astrocytes for analysis. However, cases like the representative astrocytes shown in Figure 4A or Figure S1B, have segmented domains localized only to proximal processes near the soma. Accordingly, given the reported timing differences between "arbor" and "soma" activation, one might expect there to be comparable timing differences between domains that are distal vs proximal to the soma as well. Fast signals in peripheral regions of astrocytes in contact with synapses are largely IP3R2-independent (Stobart et al., 2018). However, the quality of SR101 staining has implications for interpreting the IP3R2 KO data. There is evidence IP3R2 KO may preferentially impact activity near the soma (Srinivasan et al., 2015). Thus, astrocytes with insufficient staining - visible only in the soma and proximal domains - might show a biased effect for IP3R2 KO. While not necessarily disrupting the core conclusions made by the authors based on their analysis of SR101-segmented astrocytes, we think results would be strengthened if astrocytes with sufficient SR101 staining - i.e. more consistent with previous reports of L2/3 astrocyte area (Lanjakornsiripan et al., 2018) - were only included. This could be achieved by using max or cumulative projections of individual astrocytes in combination with SR101 staining to construct more holistic structural maps (Bindocci et al., 2017).

We agree with the ideas concerning SR101, and indeed there could be variability in the origins of the astrocyte calcium signal. Astrocyte territory boundaries can be difficult to discern when both astrocytes express GCaMP6. Here we take a conservative approach to constrain ROIs to SR101-positive astrocyte territory outlines without invading neighboring cells in order to reduce error in the estimate of a spatial threshold. The effect of IP3R2 KO preferentially impacting activity near the soma is interesting, and in line with our conclusions. We agree that the findings from SR101-negative pixels would not necessarily disrupt the core conclusions of the study, and the additional analysis suggested would further strengthen results.

For latency-based selection - The authors record calcium activity within a FOV containing at least 20+ astrocytes over a period of 60s, during which a 2Hz hindpaw stimulation at 2mA is applied for 20s. As discussed above, presumably some astrocytes in a FOV are the first to respond to the stimulus series, while others likely respond with longer latency to the stimulus. For the shorter-latency responders <3s, it is easier to attribute their calcium increases as "following the sensory information" projecting to L2/3. In other cases, when "arbor" responses occur at 10s or later, only after 20 stimulus events (at 2Hz), it is likely they are being activated by a more complex and recurrent circuit containing several rounds of neuron-glia crosstalk etc., which would be mechanistically distinct from astrocytes responding earlier. We suggest that authors focus more on the shorter latency response astrocytes, as they are more likely to have activity corresponding to the stimulus itself.

We agree that different times of astrocyte calcium increases may be due to different mechanisms outside of the astrocyte. We believe the spatial threshold will be intrinsic to these external variables; yet we believe that longer latency responses are physiological and may carry important information to determining the astrocyte calcium responses.

The second level of analysis refinement we suggest relates specifically to the issue of propagation and timing for the activity within "arbor", "soma" and "post-soma". Currently, the authors use an ROI-based approach that segments the "arbor" into domains. We suggest that this approach could be supplemented by a more robust temporal analysis. This could for example involve starting with temporal maps that take pixels above a certain amplitude and plot their timing relative to the stimulus-onset, or (better) the first active pixel of the astrocyte. This type of approach has become increasingly used (Bindocci et al., 2017; Wang et al., 2019; Ruprecht et al., 2022) and we think its use can greatly help clarify both the proposed sequence and better characterize the spatial threshold. We think this analysis should specifically address several important points:

We agree that the creation of temporal maps from our own data will be interesting. We will provide the results of the suggested analysis in the revised version of the manuscript.

1) Where/when does the astrocyte activation begin? Understanding the beginning is very important, particularly because another potential spatial threshold - preceding the one the authors describe in the paper - could gate the initial activation of more distal processes, as discussed above. This sequentially earlier spatial threshold could (for example) rely on microdomain interaction with synaptic elements and (in contrast) be IP3R2 independent (Srinivasan et al., 2015, Stobart et al., 2018). We would be interested to know whether, in a subset of astrocytes that meet the structure and latency criteria proposed above and can produce global activation, there is an initial local GCaMP6f response of a minimal size that must occur before propagation towards the soma begins. The data associated with varying stimulus parameters could potentially be useful here and reveal stimulus intensity/duration-dependent differences.

This is a very important point. It is difficult to pinpoint the beginning of the signal, which is why we rely on the average of responses.

2) Whether the propagation in the authors' experimental model is centripetal? This is implied throughout the manuscript but never shown. We think establishing whether (or not) the calcium dynamics are centripetal is important because it would clarify whether spatially adjacent domains within the "arbor" need to be sequentially active before reaching the threshold and then reaching the soma. More broadly, visualizing propagation will help to better visualize summation, which is presumably how the threshold is first reached (and overcome). The alternative hypothesis of a general excitability threshold, as discussed above, would be challenged here and possibly rejected, thereby clarifying the nature of the Ca2+ process that needs to reach a threshold for further expansion to the soma and other parts of the astrocyte.

We agree that our view is centripetal. Indeed, we have found arborization activity precedes soma activity. However, whether this is intrinsic or due to the fact that synapses are more likely to occur in the periphery requires further studies.

3) In complement to the previous point: we understand that the spatial threshold does not per se have a location, but is there some spatial logic underlying the organization of active domains before the soma response occurs? One can easily imagine multiple scenarios of sparse heterogeneous GCaMP6f signal distributions that correspond to {greater than or equal to}22.6% of the arborization, but that would not be expected to trigger soma activation. For example, the diagram in Figure 4C showing the astrocyte response to 2Hz stim (which lacks a soma response) underscores this point. It looks like it has {greater than or equal to}22.6% activation that is sparsely localized throughout the arborization. If an alternative spatial distribution for this activity occurred, such that it localized primarily to a specific process within the arbor, would it be more likely to trigger a soma response?

This is an interesting point and an analysis of spatial clustering on pre-soma domain activation may be useful to answer it.

4) Does "pre-soma" activation predict the location and onset time of "post-soma" activation? For example, are arbor domains that were part of the "pre-soma" response the first to exhibit GCaMP6f signal in the "post-soma" response?

This is another interesting analysis that can be done with a spatial clustering analysis.

Reviewer #2 (Public Review):

Lines et al investigated the integration of calcium signals in astrocytes of the primary somatosensory cortex. Their goal was to better characterize the mechanisms that govern the spatial characteristics of calcium signals in astrocytes. In line with previous reports in the field, they found that most events originated and stayed localized within microdomains in distal astrocyte processes, occasionally coinciding with larger events in the soma, referred to as calcium surges. As a single astrocyte communicates with hundreds of thousands of synapses simultaneously, understanding the spatial integration of calcium signals in astrocytes and the mechanisms governing the latter is of tremendous importance to deepen our understanding of signal processing in the central nervous system. The authors thus aimed to unveil the properties governing the emergence of calcium surges. The main claim of this manuscript is that there would be a spatial threshold of ~23% of microdomain activation above which a calcium surge, i.e. a calcium signal that spreads to the soma, is observed. Although the study provides data that is highly valuable for the community, the conclusions of the current version of the manuscript seem a little too assertive and general compared with what can be deduced from the data and methods used.

The major strength of this study is the experimental approach that allowed the authors to obtain numerous and informative calcium recordings in vivo in the somatosensory cortex in mice in response to sensory stimuli as well as in situ. Notably, they developed an interesting approach to modulating the number of active domains in peripheral astrocyte processes by varying the intensity of peripheral stimulation (its amplitude, frequency, or duration).

We thank the reviewer for their kind and thoughtful review of our study.

The major weakness of the manuscript is the method used to analyze and quantify calcium activity, which mostly relies on the analysis of averaged data and overlooks the variability of the signals measured. As a result, the main claims from the manuscript seem to be incompletely supported by the data. The choice of the use of a custom-made semi-automatic ROI-based calcium event detection algorithm rather than established state-of-the-art software, such as the event-based calcium event detection software AQuA (DOI: 10.1038/s41593-019-0492-2), is insufficiently discussed and may bias the analysis. Some references on this matter include: Semyanov et al, Nature Rev Neuro, 2020 (DOI: 10.1038/s41583-020-0361-8); Covelo et al 2022, J Mol Neurosci (DOI: 10.1007/s12031-022-02006-w) & Wang et al, 2019, Nat Neuroscience (DOI: 10.1038/s41593-019-0492-2). Moreover, the ROIs used to quantify calcium activity are based on structural imaging of astrocytes, which may not be functionally relevant.

Unfortunately, there is no general consensus for calcium analysis in the astrocyte or neuronal field, and many groups use custom made software made in lab or custom software such as GECIquant or AQuA. While AQuA is an event-based calcium event detection software, it may be that not including inactive domains that are SR101 positive could underestimate the spatial threshold for calcium surge. Our data is not based on the functional events but is based on calcium with structural constraints within a single astrocyte. This is crucial to properly determine the ratio of active vs inactive pixels within a single astrocyte.

For the reasons listed above, the manuscript would probably benefit from some rephrasing of the conclusions and a discussion highlighting the advantages and limitations of the methodological approach. The question investigated by this study is of great importance in the field of neuroscience as the mechanisms dictating the spatio-temporal properties of calcium signals in astrocytes are poorly characterized, yet are essential to understand their involvement in the modulation of signal integration within neural circuits.

We thank the reviewer for their suggestions to benefit the conclusions and discussion.

Reviewer #3 (Public Review):

Summary:

The study aims to elucidate the spatial dynamics of subcellular astrocytic calcium signaling. Specifically, they elucidate how subdomain activity above a certain spatial threshold (~23% of domains being active) heralds a calcium surge that also affects the astrocytic soma. Moreover, they demonstrate that processes on average are included earlier than the soma and that IP3R2 is necessary for calcium surges to occur. Finally, they associate calcium surges with slow inward currents.

Strengths:

The study addresses an interesting topic that is only partially understood. The study uses multiple methods including in vivo two-photon microscopy, acute brain slices, electrophysiology, pharmacology, and knockout models. The conclusions are strengthened by the same findings in both in vivo anesthetized mice and in brain slices.

We thank the reviewer for the positive assessment of the study and his/her comments.

Weaknesses:

The method that has been used to quantify astrocytic calcium signals only analyzes what seems to be a small proportion of the total astrocytic domain on the example micrographs, where a structure is visible in the SR101 channel (see for instance Reeves et al. J. Neurosci. 2011, demonstrating to what extent SR101 outlines an astrocyte). This would potentially heavily bias the results: from the example illustrations presented it is clear that the calcium increases in what is putatively the same astrocyte goes well beyond what is outlined with automatically placed small ROIs. The smallest astrocytic processes are an order of magnitude smaller than the resolution of optical imaging and would not be outlined by either SR101 or with the segmentation method judged by the ROIs presented in the figures. Completely ignoring these very large parts of the spatial domain of an astrocyte, in particular when making claims about a spatial threshold, seems inappropriate. Several recent methods published use pixel-by-pixel event-based approaches to define calcium signals. The data should have been analyzed using such a method within a complete astrocyte spatial domain in addition to the analyses presented. Also, the authors do not discuss how two-dimensional sampling of calcium signals from an astrocyte that has processes in three dimensions (see Bindocci et al, Science 2017) may affect the results: if subdomain activation is not homogeneously distributed in the three-dimensional space within the astrocyte territory, the assumptions and findings between a correlation between subdomain activation and somatic activation may be affected.

In order to reduce noise from individual pixels, we chose to segment astrocyte arborizations into domains of several pixels. As pointed out previously, including pixels outside of the SR101-positive territory runs the risk of including a pixel that may be from a neighboring cell, and we chose to avoid this source of error. We agree that the results have limitations from being acquired in 2D instead of 3D, but it is likely to assume the 3D astrocyte is homogeneously distributed and that the 2D plane is representative of the whole astrocyte. Indeed, no dimensional effects were reported in Bindocci et al, Science 2017. We plan to include a paragraph in the discussion to address this limitation in our study.

The experiments are performed either in anesthetized mice, or in slices. The study would have come across as much more solid and interesting if at least a small set of experiments were performed also in awake mice (for instance during spontaneous behavior), given the profound effect of anesthesia on astrocytic calcium signaling and the highly invasive nature of preparing acute brain slices. The authors mention the caveat of studying anesthetized mice but claim that the intracellular machinery should remain the same. This explanation appears a bit dismissive as the response of an astrocyte not only depends on the internal machinery of the astrocyte, but also on how the astrocyte is stimulated: for instance synaptic stimulation or sensory input likely would be dependent on brain state and concurrent neuromodulatory signaling which is absent in both experimental paradigms. The discussion would have been more balanced if these aspects were dealt with more thoroughly.

Yes, we agree that this is a limitation, and we will acknowledge this is in the discussion.

The study uses a heaviside step function to define a spatial 'threshold' for somata either being included or not in a calcium signal. However, Fig 4E and 5D showing how the method separates the signal provide little understanding for the reader. The most informative figure that could support the main finding of the study, namely a ~23% spatial threshold for astrocyte calcium surges reaching the soma, is Fig. 4G, showing the relationship between the percentage of arborizations active and the soma calcium signal. A similar plot should have been presented in Fig 5 as well. Looking at this distribution, though, it is not clear why ~23% would be a clear threshold to separate soma involvement, one can only speculate how the threshold for a soma event would influence this number. Even if the analyses in Fig. 4H and the fact that the same threshold appears in two experimental paradigms strengthen the case, the results would have been more convincing if several types of statistical modeling describing the continuous distribution of values presented in Fig. 4E (in addition to the heaviside step function) were presented.

We agree with the reviewer that we should add to the paper a discussion for our justification on the use of the Heaviside step function, and plan to include this. We chose the Heaviside step function to represent the on/off situation that we observed in the data. We agree with the reviewer that Fig. 4G is informative and demonstrates that under 23% most of the soma fluorescence values are clustered at baseline. We agree that a similar graph should be included in Fig. 5 as well. We agree that a different statistical model describing the data would be more convincing and also confirmed the spatial threshold with the use of a confidence interval in the text.

The description of methods should have been considerably more thorough throughout. For instance which temperature the acute slice experiments were performed at, and whether slices were prepared in ice-cold solution, are crucial to know as these parameters heavily influence both astrocyte morphology and signaling. Moreover, no monitoring of physiological parameters (oxygen level, CO2, arterial blood gas analyses, temperature etc) of the in vivo anesthetized mice is mentioned. These aspects are critical to control for when working with acute in vivo two-photon microscopy of mice; the physiological parameters rapidly decay within a few hours with anesthesia and following surgery.

We will increase the thoroughness of our methods section. Especially including that body temperature and respiration were indeed monitored throughout anesthesia.

Author Response

We are grateful to the reviewers for recognizing the importance of our work on transcription-independent early recovery of proteasome activity. We also thank them for their thoughtful criticisms and suggested improvements, which we will address in the revised version as described below.

The reviewers and editors asked for data to support the model that early recovery of proteasome activity is due to accelerated proteasome assembly. This model is backed by published data that proteasome assembly intermediates increase dramatically in cells treated with proteasome inhibitors (Fig. 6 in Ref. 46 of the revised manuscript). We will expand the discussion of this paper in a paragraph that describes our model. Another key experiment to confirm this model would be to determine what fraction of nascent polypeptides is degraded within minutes after synthesis, which is not trivial, and Ibtisam ran out of time to conduct these experiments because she had to graduate in spring before the expiration of her visa. This type of experiment usually uses metabolic labeling by a heavy or radioactive amino acid that always includes a prior depletion of a non-labeled amino acid. However, the fundamental flaw of this approach, which is not recognized by the scientific community, is that depletion of an amino acid stresses cells and reduces the rate of protein synthesis, especially if this amino acid is methionine. Thus, this model is not easily to test, and should be considered a speculation. We will therefore move the description of this model, together with Fig. 4, into a separate "Ideas and Speculation" section and remove this model's description from the abstract.

Reviewer 1 raised the possibility that a background band detected on the western blot of DDI2 KO cells could be a highly homologous protease DDI1. This is highly unlikely because, according to Protein Atlas, DDI1 is selectively expressed in the testis and is not expressed in the cell lines we used. Reviewer 1 also suggested that we should base our conclusion on Nrf1 KD, which we de-facto did because we confirmed that DDI2 KD blocks Nrf1 activation (Fig. 1d).

In response to Reviewer 1 critiques regarding the presentation of proteasome subunits stability data in Fig. 4 (Ref. 45 of the revised manusript), we will remove PSMB8 and replace chaperons with the subunits of the 26S base. We will change color palettes, symbols, and axis scales to improve clarity.

We will acknowledge in the discussion that our work did not exclude DDI2 role in the recovery of proteasome after repeated pulse treatments, as suggested by Reviewer 1.

We agree with Reviewer 2 that using proteasome levels is inaccurate when describing our activity measurement data. However, in the manuscript, we use "levels" only when discussing data in the literature. We believe measuring activity and not the total levels is more important because not all proteasomes are active, e.g., latent 20S proteasome core particles.

Reviewer 3 expressed concern that our conclusions were based on data in HAP1 cells, which are haploid, and appear not very sensitive to proteasome inhibitors. This is why we used DDI2 KD in MDA-MB-231 and SUM149 cells, which are highly sensitive to proteasome inhibitors (Weyburne et al., Ref. 11). In our experience, full extent of proteasome inhibitor cytotoxicity is not revealed until 48hr after treatments, and viability determined at 12hr and 24hr as on Fig. 1c should not be used to determine sesnsitivity (it was used for activity assay normalization). We will add a new supplementary figure showing that HAP1 cells are as sensitive to proteasome inhibitors as MDA-MD-231 cells when cell viability is assayed 48hr after treatment (new Fig. S2). Another panel on this new figure will demonstrate that the baseline proteasome activity is very similar in HAP1, MD-MB-231 and SUM149 cells. We will also add data demonstrating that inactivativion of DDI2 by mutation does not change the recovery of proteasome activity in HCT-116 cells (new Fig. 1g). Recovery in MDA-MB-231, SUM149, and HCT-116 cells was measured at 18hr, which is still within the 12 – 24hr window when other investigators observed partially DDI2-dependent recovery.

We have conducted an experiment in which we followed activity recovery for up to 72hr. We found that activity plateaued at 24hr and opted against the repeat because there were no changes. We feel that the manuscript should not include one biological replicate data. The fact that the recovery is incomplete and that cells seem to survive with lower levels of proteasome activity is interesting; however, investigating the molecular basis for this phenomenon is beyond the scope of the current project.

We were not disputing the conclusions of previous studies that DDI2/Nrf1 is responsible for enhanced expression of proteasomal mRNA in cells continuously treated with proteasome inhibitors. In fact, we confirmed that pulse-treatment causes similar increase (Fig. 2b). As for papers that measured activity recovery after pulse treatment, we objectively discuss our results in the context of these papers.

We will also respond to Reviewers' recommendations and minor points:

• We will review the revised version carefully to eliminate spelling and grammatical errors and typos.

• We will no longer refer to DDI2 as a novel protease, as suggested by Reviewer 1.

• We agree with Reviewer 2 that our CHX results do not necessarily mean that recovery involves translation of proteasomal mRNAs, and we will now conclude that proteasome recovery requires protein synthesis.

• We will revise Fig. 1c, 3a and 4a to improve clarity.

• We have stated in the caption that data in Fig. 4a comes from Table S4 in Ref. 45.

• We will accept an excellent suggestion of Reviewer 3 to change "recovery" to "early recovery" in the title.

• Regarding Reviewer 3 request to assay activity recovery at additional time points before 12hr, this was done in the cycloheximide experiment in Fig. 3A.

• Even if we assume that the differences in the observed recovery activity in MDA-MB-231 cells (Fig. 1f) are statistically significant, which may implicate DDI2 involvement in the activity recovery, the percentage is still small, suggesting that most activity recovery is DDI2-independent.

• We will tone down the statement "the present findings suggest that DDI2 desensitizes cells to PI by a different mechanism," replacing "suggest" with "raise a possibility."

• We will indicate that only Bortezomib is approved for mantle cell lymphoma.

• We will change the description of clinical dosing as suggested by Reviewer 3. We will add a reference on PK of subcutaneous bortezomib (Ref. 9), even though the review we quoted (Ref. 7) discussed subcutaneous dosing.

Author Response

Reviewer #3 (Public Review):

Youssef et al. have used a range of markers to identify cancer stem cells (CSCs) in patients with oral cancers. CSCs were identified in lab conditions and were often linked to the invasiveness of cancers. The authors found a combination of markers convincingly liked to known biology and found cells expressing them in the invading cancers.

The major weakness of the paper is in the technical side. There isn't enough description as to how they discriminated between CSCs inside the tumour and those invading its surroundings. Similarly, the way the information is presented it is not clear why artificial intelligence was needed to enhance the accuracy of the method linking CSCs to cancer invasion (and ultimately deadly metastasis to other organs).

The method for applying tumour mask is displayed in Figure 2E for cohort 1 and Figure 2 figure supplement 3 for cohort 2. Briefly, in the image analysis pipeline, dense areas of EpCAM+ (cohort 1) or Vimentin+ (cohort 2) cells are merged to specify tumour/stroma regions. Thus, CSCs inside tumours (in the EpCAM dense tumour region) can be discriminated from CSCs invading the surroundings (in the Vimentin dense stromal region).

Author Response

Reviewer #1 (Pulic Review):

The authors aimed to understand whether the superficial, retinorecipient layers of the mouse superior colliculus (sSC) participate in figure-ground segregation and object recognition. To address this question, they use a combination of optogenetic perturbations of sSC and recordings. These data are consistent with SC being causally involved in object recognition. This would be useful information for the field and likely to be cited.

Thank you for your positive evaluation.

However, I have several concerns regarding their conclusions.

A significant limitation of this study is methodological. The major novelty is the effect of optogenetic silencing, because the recordings are largely correlative, but the optogenetic silencing approach lacks appropriate controls for the effects of the optogenetic excitation light. The authors acknowledge that the optogenetic light is a potential confound, but attempt to address this by shielding the fiber to eliminate light leak and strobing a blue led in the arena. The former does not account for the effects of excitation light scattering intracerebrally--during optogenetic experiments, intracerebral scattering causes the eyes to light up--and for the latter, there is no way to compare the intensity or qualia of the externally strobed LED and the intracerebral light. The proper control would be a cohort of mice lacking channelrhodopsin expression in sSC. Regardless, it is essential to acknowledge this potential confound.

This is a good point. We have added discussion of this in lines 90-95. The proposed experiment was done in Kirchberger et al. (Sci Adv 2021, Suppl Figure 3). In mice without expression of channelrhodopsin trained on the same task as in our study, blue laser light in the cortex did not affect accuracy. Although the exact location of these fibers is different from ours, the distance from the fiber to the eye is very similar. Furthermore, in answer to this comment, we have done a new set of experiments with 4 wild type mice, in which we recorded neural activity in the sSC while delivering optogenetic light stimulation. The procedure was similar to our previous experimental animals except that they did not receive a virus injection. In these mice, we did not see any response in the superior colliculus to the laser light, but we noticed a 5% reduction in response to the visual stimuli (new Figure 1—figure supplement 3). This small reduction could be a small reduction of contrast of the visual stimulus due to the laser light hitting the retina, but given that we did not see any response to the laser alone, it is more likely to come from the known inhibiting effects of light on neural activity (e.g. through heat, see Owen et al. Nat Neurosci 2019). Because our aim was to silence sSC, this particular effect is not a strong confound for our study.

Relatedly, as the authors note, there are GABAergic projection neurons in sSC that may be driving these effects via gain of function. This is a significant concern that has limited the widespread adoption of this approach in sSC despite its popularity in studies in cortex. Indeed, one recently published study of behavioral functions of deep SC found that activating inhibitory neurons actually caused paradoxical behavioral effects consistent with gain of function in the targeted hemisphere, due to the effects of long-range inhibitory projections on the other SC hemisphere. Given the presence of inhibitory projections in sSC, it would be preferable to use an orthogonal method for silencing and at least to thoroughly acknowledge these concerns and cite these recent studies.

This is a valid point. When we started our study, we had some experience with inhibitory opsin (archaerhodopsin and halorhodopsin) and were not confident that we could widely inhibit the sSC reversibly, repeatedly and consistently for an extended period. Other labs have now shown this is feasible with improved inhibitory opsins, so this would now be our preferred option too. The method of silencing sSC by inhibition of GABAergic neurons, however, is still the most common optogenetic method to silence sSC for an extended period (e.g. Hu et al. Neuron 2019, Brenner et al. Neuron 2023) .

We thank the reviewer pointing us to recently published paradoxical behavioral effects. These effects, that we found in Essig et al. (Comm. Biol. 2021) are very interesting, but are not really a concern for the interpretation of our results, partially because as the reviewer pointed out, the GABAergic neurons activated there were in the deep and intermediate layers of the SC, below the sSC that we targeted. The paradoxical effects in that manuscript were attributed to direct inhibition of the contralateral superior colliculus. In our case, we activated the inhibitory neurons bilaterally, and this interhemispheric GABAergic connectivity, if it extends to sSC, only strengthened the bilateral silencing of the sSC. However, we have now discussed the possibility of our transfection of these deeper GABAergic neurons (lines 272-278). The more general point that activating GABAergic neurons in the sSC may also cause inhibition in other structures is indeed a concern. GABAergic neurons in the sSC project to the PBG and the LGN (in particular the vLGN) (Gale & Murphy, 2014; Whyland et al., 2019; Li et al., 2023). Although the primary effect of our manipulation is silencing of the superior colliculus, including the GABAergic neurons (see our answer further below), we cannot exclude the possibility that activating these extracollicular GABAergic projections has an effect. We have edited our discussion of this and updated the references (lines 268-272). However, our measurements in anesthetized (previous submission) and in awake mice (new Figure 1—figure supplement 2) show that apart from a short period directly after the onset of the laser, also almost all putative GABAergic neurons are reduced in their response (see also our answer to the next comment).

A minor point is that although activation of GABAergic neurons in sSC is expected to cause inhibition of neighboring neurons, I would expect channelrhodopsin-expressing GABAergic cells to show an increase in firing during optogenetic excitation. However, it seems that none of the cells plotted (assuming each point in Supplementary Fig 4D is a cell, which the legend does not specify) had such an increase. Do these extracellular recordings not detect inhibitory neurons well?

This is indeed an intriguing observation. The data in the original figure (Supp Fig 1D) was spiking data from 15 recording sites and not from sorted units. This was mentioned in panel C, but not in the caption. For the purpose of the amount of silencing, there was no need to sort single units. Still, it is surprising to see the reduction on almost all channels. The data of Supp Fig 1D came from experiments in anesthetized mice. Prompted by a question from another reviewer, we have now redone these experiments in head-fixed awake mice. The new Figure 1—figure supplement 2 shows these results, for single- and multi-unit clusters. In response to a short laser pulse (50 ms), we find that many units significantly increase their firing rate (Figure 1—figure supplement 2A-B). However, almost all activated then reduce there firing rate and again, we see an overall reduction of responses to visual stimuli. Only one unit fires significantly more when the laser is on during the period of visual stimulation compared to when the laser is off, and the overall firing rate is strongly reduced (Figure 1—figure supplement 2C-E). It appears that optogenetically activating the inhibitory neurons in the sSC for a longer period also reduces the activity of these neurons. The effect that we are seeing might be similar to the paradoxical effects that may occur in visual cortex, where additional excitation of inhibitory neurons leads also leads to their reduced activity due to network dynamics (see e.g. Sadeh & Clopath, Nat Neurosci Rev 2021). However, the effect may also be due to a few inhibitory neurons having a strong inhibitory effect on other inhibitory neurons. This is an interesting point worthy of more investigation, but it falls out to scope of this manuscript.

Finally, the relationship between these stimuli and objects is not entirely clear. The authors acknowledge this but it would be worthwhile to devote more attention to this point. In effect, as the authors note, the gray screen and sinuisoidal grating do not have any sharp edges on the screen, whereas each of the behaviorally relevant stimuli will create a sharp, step-like edge on the screen. Whether edge detection is truly object detection or simply a variant of more general visual detection is unclear.

Indeed, the task can be solved by detection of texture edges, and it is not necessary to integrate the edge components into an object to successfully perform the task. A linear decoder fed with simple cell-like inputs is able to do the orientation task (Luongo et al., 2023). The same network failed to learn the phase task, but also the image of a phase-defined figure contains features that are not present in the background image, and could be solved by learning only local features. Even the texture-defined figures used in Kirchberger et al. (2021) and in earlier monkey studies (Lamme, 1995) which do not contain any sharp stimulus edges can be detected without integrating the local edges into objects and segregation the figure from the background. Several monkey studies show that late neuronal responses in V1 are enhanced for neurons with receptive fields on what we, humans, perceive as the figure. This effect has also been seen in mouse V1, even in the case where there are no local features distinguishing the figure from the background (Fig 7. in Kirchberger et al. 2021). Interfering with activity in V1 in this late phase reduces the ability to detect the figure in human (by TMS) and mouse (by optogenetics). This is suggestive that this figure-ground modulation is used in solving the task, but not a proof. To understand if mice solve the tasks by detecting a figure or by detecting specific features, we can look at generalization. Mice were previously shown to generalize to some degree for size, position and spatial phase of the figure grating patch (Schnabel et al., 2018), suggesting that the mice did not train to detect specific features at specific locations. Rats trained on a similar task had difficulty generalizing from a luminance-defined object to an orientation-defined object (De Keyser et al., 2015), as do mice (Khastkhodaei et al., 2016), but once the rats were acquainted with one set of oriented figures, they immediately generalized to other texture-orientations above chance. On a slightly different figure-detection task mice also showed generalization for different orientations once the initial task was learned (Luongo et al. 2023). This suggests that at least some generalization to object detection occurs in this task. We have added these observation to the discussion (line 301-305).

Reviewer #2 (Public Review):

The goal of this study is to show that the superficial superior colliculus (sSC) of mouse signals figure-ground differences defined by contrast, orientation, and phase, and that these signals are necessary for the animal to detect such figure-ground differences. By inhibiting sSC while the animals perform a figure-ground detection task, the study shows that detection performance decreases when sSC activity is suppressed during the onset of the visual stimulus. The study then intends to show that sSC neurons exhibit surround suppression based on orientation differences, and that surround suppression is stronger when the animal detects the correct location of the figure on the background.

The major strength of this study is the use of a behavioural paradigm to test detection performance of figure-ground stimuli while manipulating neural activity in the sSC during different times after stimulus onset. This paradigm would show whether activity in the sSC is relevant for performing the task. Secondly, the study collected data to confirm previous findings: sSC neurons exhibit orientation specific surround suppression. Additionally, it is impressive that the authors were able to train mice to generalize their task performance across different stimulus categories (figure-ground differences in orientation and phase). This should be highlighted as it may inform future studies.

Thank you for your positive evaluation. We have extended our discussion on the generalization in object detection tasks in mice.

The study has, however, methodological and analytical weaknesses so that the stated conclusions are not supported by the presented results.

1) Optogenetic inhibition is not limited to sSC (even expression may not be limited) About 30% of inhibitory neurons in the sSC project to other areas, e.g. ventral LGN, parabigeminal nucleus and pretectum (Whyland et al, 2019, see ref in manuscript). This means that these areas receive direct inhibition when inhibitory sSC neurons are optogenetically stimulated. This fact is mentioned in the discussion but the consequences and implications for the results are ignored. This is a major flaw of the optogenetic experiments of this study. Additionally, no evidence is given that opsin expression was limited to the superficial layers (except for one histological slice), which the authors acknowledge in line 285. Deeper layers may have other inhibitory neurons with long-range projections.

The finding that sSC neurons show no figure-ground modulation for phase while the optogenetic manipulation has behavioural effects may be an indication for other areas being affected by the optogenetic manipulation.

This is a valid point, also raised by reviewer 1. Although the primary effect of activating the GABAergic neurons in the sSC is a strong reduction of activity in the sSC (see also new figure S1), we cannot rule out that we also activate GABAergic neurons below the sSC and that there are some effects of activating GABAergic connections to the LGN and PBG. We have extended our discussion of this point in lines 269-277. However, as shown in new Figure 1—figure supplement 2, the effect of optogenetically activating Gad2-positive neurons appears to lead to a counter-intuitive reduction of their activity. This effect has previously been observed in cortex.

2) Could other behavioural variables explain the results?

a) Are there any task events other than the visual stimuli that the mice could use to make their decisions? The authors state the use of a custom made lick spout but it is not clear how this spout works, i.e. how do mechanics of the spout deliver water to the right versus the left output and could the mouse perceive these mechanics?

We believe there were no task events besides the visual stimuli that the mice could use to make their decisions. The lick spout was Y-shaped (see Figure 1B) to facilitate the two-alternative forced choice task. Each side of the lick spout was connected to a separate water tube. The water flow in each tube was controlled using a valve. Also, each side of the lick spout was connected to its own lick detector wire. The two valves and the two detector wires were connected to an Arduino which was controlled by our MATLAB task script. The task script was coded such that, when the lick of the mouse had been on the correct side, the valve controlling the water flow on the correct side would briefly open to deliver the water reward. To summarize, the water would only flow after the mouse had licked and if the first lick had been on the correct side. Hence, the water reward did not produce additional cues. We have edited the description of the lick spout in the Methods section to make the functioning of the lick spout more clear (lines 511-513).

b) Could the different neural responses to figure versus ground shown in Fig 2I-J and Fig 3B be explained by behaviours varying between the trial types, e.g. by early lick movements (which are conceivable even if the spout is not present), eye movements or changes in pupil-linked arousal? A behavioural difference seems even more likely to occur between hit and error/miss trials (Fig 4). If these behaviours were not measured, the possibility of behavioural modulation should be discussed.

In the awake behaving electrophysiology experiments, the lick spout was not present until 500 ms after stimulus onset, so the mouse could not lick the spout. We did not record whisking or other face and jaw movements, hence we cannot say for sure whether the mice performed early ‘licks’ in the absence of the lick spout. We did, however, add a supplementary figure showing the licking behavior of the mice in the optogenetic interference experiments (see Figure 1—figure supplement 5). In this experiment, the lick spout was present at all times so all early licks would be recorded. Any licks before 200 ms after stimulus onset were disregarded as this would be too early for the decision to include knowledge about the stimulus. Figure 1—figure supplement 5B shows that the mice indeed only performed very few early licks as they probably knew this would not yield reward. The mice that performed the awake electrophysiology experiments were trained on the same task as these mice before introducing the lick spout delay of 500 ms. So although we cannot rule out early licks during electrophysiology, we think early licks would be an unlikely explanation for the neural response differences.

We have added a new supplementary figure (Figure 2—figure supplement 2) showing data for eye movements and pupil dilation during the tasks. We had excluded all trials where the mice performed eye movements between 0-450 ms after stimulus onset, and indeed we saw no eye movements during the peak of the visual response (0-250 ms). Furthermore, the pupil dilation of the mice also did not change in this period.

All in all, we view it as unlikely that the differences in neural activity in sSc were caused by either licking, eye movements or pupil-linked arousal.

3) What is the behavioural strategy of the animals? Only licks beyond 200 ms after stimulus onset determine the choice of the animal because "mice made early random licks" from 0 to 200 ms. To better understand the behavioural strategies of the animals we need to see their behavioural data, i.e. left and right licks aligned to stimulus onset. It would be particularly interesting to see how number and latency of licks changes during optogenetic manipulation.

Based on these suggestions, we investigated the licking behavior of the mice during the optogenetic experiments in more detail. Our new Figure 1—figure supplement 5 taught us several things:

1) The fully trained mice hardly perform any early licks; they seem to understand that early licks cannot yield reward.

2) The mice typically only lick one side of the lick spout during one trial. In correct trials the fluid reward is given directly after a correct lick, which causes the mouse to lick the correct side of the spout even more. However, even if the first lick is incorrect (bottom rows), the mouse generally does not lick the other (correct) side afterward. They seem to know that correct licks after an incorrect lick do not yield reward.

3) The maximum licking rates were not significantly affected by laser onset.

4) The latency of the first lick (reaction time) was not significantly affected by laser onset. (Please also see our response to question 2b).

4) Data relating to misses should be included in analyses to provide a complete picture of behaviour and neural responses

a) In the optogenetic manipulations, an increase in misses seems to dominate the decreased accuracy (please, explain when a response was counted as a miss). A separate analysis of miss trials may be more robust than of error trials and also offers a different interpretation of the data, namely that the mouse did not see the stimulus rather than perceiving the figure on the opposite side. However, if the mice reduced their lick rate in general during optogenetic stimulation, this begs the question whether their motor performance was affected by optogenetic manipulation. Can this possibility be excluded?

Trials were counted as follows: A trial was counted as a hit when the first lick after 200 ms after stimulus onset was on the correct side. A trial was counted as an error, when the first lick after 200 ms after stimulus onset was on the incorrect side. A trial was counted as a miss, when the mouse did not lick in the window between 200 and 2000 ms after stimulus onset. We have clarified this in the methods section (line 517-526).

Our previous text may not have been sufficiently clear but the decrease in accuracy during optogenetic trials is not dominated by an increase in missed trials. As we have now indicated explicitly in its caption, in figure 1, missed trials are excluded from the analysis. Hence, the significant effects shown in figure 1 are not driven by an increase in missed trials but rather by an increase in erroneous licks. When comparing figure 1 vs figure S3, where the missed trials are added to the analysis as if they were error trials, we can see an overall downward shift of the performances. Indeed, mice miss more trials when the laser is on. The increase in number of missed trials is lower than the increase in number of wrong choices. Furthermore, the range between the performances at early laser onset and late laser onset is still very similar. This indicates that the mice on average do not have higher miss rates when laser onset is early.

Finally, nor maximum licking rate, nor the reaction time is affected by the laser onset (see the new figure S2)

Related to Fig 4, it would be equally interesting to see how FGM changes during misses. Do the changes support the observations for error trials?

We are not convinced that the neural data from missed trials can be interpreted in a simple way. Mice may have various reasons to miss a trial: they may be tired or not paying attention, they may not have seen the stimulus well, they may not feel thirsty enough, they might be distracted by some sensory input that humans might not be aware of, etc. This is why we specifically opted to not use a go-no/go task but instead opted to use a 2-alternative forced choice task.

5) Statistical tests do not support the conclusions, are missing or inadequate

a) In Fig 1E, accuracy is significantly affected at only 1-2 time points in each task, specifically either the 1st and 3rd or the 2nd time point. How do the authors interpret these results? If inhibition starting at the 2nd time point has no significant effects, why would it be significant when inhibition starts later (at the 3rd time)? Furthermore, given that all other starting points of laser stimulation have no significant effects, there is no reason to trust the latency of inhibition effects based on mostly insignificant data points. This analysis in its current form should be removed, including a comparison of latencies between tasks, which was not tested for significance. It may be more meaningful to analyse accuracy for each animal separately. This may reduce variability.

We can understand that the reviewer may have concerns regarding the post-hoc analysis of Fig 1E, but we feel these concerns stem from a misinterpretation of our goal with this analysis. In Figure 1E, we use a 1-way repeated-measures ANOVA. By using this test, we ask whether the performance of the animals is affected by the laser onset. More specifically “does the performance increase or decrease with increasing laser onset?” The test is significant, so indeed the performance goes up as laser onset goes up. This indicates that the performance of the mice is affected by the inhibition of sSC. For the sake of completeness we had included the post-hoc tests for each latency in the statistics table. Indeed, some individual latencies are not significantly different to the no-laser condition. However, this does not invalidate the conclusion of the main test: a repeated measures ANOVA can only be performed on data with 3 or more groups, so the conclusion of the repeated measures ANOVA could not have been drawn from simply those laser onset(s) that is/are significantly different from the no-laser condition. The main effect of higher performance with higher latencies is significant, even if some individual comparisons are non-significant. The difference in significance of the post-hoc tests does not indicate a significant difference between the groups, but insufficient power to do six individual tests.

We have changed the wording in the reporting of the statistics of Figure 1E to hopefully more precisely indicate the conclusions we drew from the statistics. We do not draw conclusions from the post hoc tests. We have considered removing them from the statistics table 1, but believe that some readers might be interested. We can remove them if the reviewer believes that would be better.

b) Analyses regarding the difference in neural response to figure and ground (Fig 2I-J, Fig 3B, Fig 4B, Fig 5C) would be more convincing and informative if the differences were analysed on the level of single neurons in response to the same orientation within their RF (or at the location where the figure is presented, for edge-RF neurons). A histogram of these differences would show how many neurons are affected and how large the effect is in single neurons.

We fully appreciate this idea, but the way we set up the behavioural task does not quite allow for this type of statistical analysis. This is because we tested all three of the tasks during single sessions (contrast/orientation/phase), and on top of that, we varied the orientations of the stimuli (0/90deg), as well as the phase of the gratings (60 different phases). This all was done with the idea that it would prevent the mice from memorizing the individual stimuli of the task. This also had the effect that only very few trials per session contained the exact same stimulus type, figure-ground condition, orientation and phase. For example, if a mouse would perform around 120 trials in a session. 25% of those were contrast-stimulus-trials, 37.5% of those were orientation-stimulus-trials and 37,5% were phase trials. If we look into 120*0.375 = 45 orientation-stimulus-trials, half of those were figure trials, half were ground trials: 22 trials each. If we split these trials up by their individual orientations, we are left with only about 11 trials per condition to analyse for figure-ground effects, each of which would probably have a different grating phase. Given the firing rate variations that the individual neurons show in awake mice, this amount of trials would not provide enough statistical power to test the significance of modulation in single neurons.

Although we feel the study design would not allow analysis of individual neurons in response to the same orientation within their RF, we did perform an aggregated analysis on orientation selectivity. For this analysis, we included all the trials where the RF of the recorded neurons was on the background-half of the screen. We then computed the responses of each neuron to the trials where the background orientation was 0 and 90, respectively. This analysis showed that most neurons had no preference for either of the two tested orientations of the other. Only 4 out of 64 (6%) neurons showed a significant preference. We therefore believe that splitting the data by orientation preference would not be very informative.

c) All statistical tests performed across neurons should account for dependencies due to simultaneous recordings (dependency on session) and due to recordings in the same animal (dependency on animal). This can be done in most cases by using linear mixed-effects models.

We agree with the reviewer and have changed the analysis for figure 2I, 3B and 3E to an LME analysis (see also Table 1).

d) There was no significant difference between model weights (Fig 3D), so the statement in line 210 (RF-edge neurons had higher weights) should be removed.

In answer to previous we question changed the analysis for what is now Figure 3E to an LME. This shows that relative weights were significantly higher for the orientation compared to the phase task. We have adapted our conclusion accordingly (line 214-218).

e) Fig 4B compares FGM during correct and error trials. This comparison has to be performed with the same set of neurons in correct and error trials (not the case for orientation). Again, the most compelling and informative comparison would be on the level of single neurons: response difference between figure and ground (same visual features at figure position) during hits versus errors.

As described above, we feel the study design does not allow analysis on the level of individual neurons. The analysis in 4B was actually performed using the same set of neurons, we have removed the typo.

f) There is no evidence that FGM for phase was different between hit and error trials as stated in line 234.

Indeed, we had phrased this incorrectly. Since we recorded all task during single recording sessions, we have data for each task for most neurons. We were therefore able to pool the results from the different tasks, and the main d-prime difference between hit vs. error was significant. Post-hoc tests showed that this is mainly driven by the difference in the orientation task. We have edited the wording to be more accurate (line 239-242).

g) It is not clear why and how the mixed linear effects model was used pooling data across tasks (Fig 4C and Fig 5D). Different neurons were recorded for each task, so the sample points (neurons) are not affected by both task effects (orientation and phase). Each task should be analysed separately.

Since we recorded all three task versions during single behavioral sessions, we have data for multiple tasks from each neuron. This is why the linear mixed effects model pools the data across the tasks. We have added a note in the main text for clarity (line 238-242)

h) Bonferroni correction in Fig 1E should correct multiple comparisons across time points, not across tasks (see Table 1).

The multiple time points all belong to the same one-way repeated measures ANOVA, so there’s no need to correct the post-hoc analysis. We did run the ANOVA for three tasks, which is why we corrected the p-values of each task. We think that this is best way, but can also present uncorrected p-values if needed.

i) What is the reason to perform some tests one-tailed, others two-tailed?

Following the reviewer comments, we changed some analyses to LME models. The remaining tests that require definition of the tails are all two-tailed.

6) The results relating to "multisensory neurons" are ambiguous regarding their interpretation (if significant at all) and seem unrelated to the goal of the study. It is particularly likely that behaviours like licking or other movements cause the response differences between figure and ground.

We agree with the reviewer that finding these neurons was not the aim of the study. We did not include enough type of tests in our paradigm to fully determine the properties of these neurons. Furthermore, we note that we have recorded too few of these neurons to draw strong conclusions. The data shown in new Figure 2—figure supplement 1H suggest that the responses of these neurons or not as strongly time-locked to the first lick as they are to the trial onset. We presented the behavior of these neurons in our manuscript, because, whatever their exact behavior, they are clearly distinct from the visually responsive cells that show a short latency response to the visual stimulus (Figure 2—figure supplement 1). We still feel that it is useful for the reader to know there are cells in the sSC that show such a distinct behavior, but we have moved the figure and the accompanying text to a figure supplement to avoid distraction from the main message of the manuscript.

7) What depth were neurons recorded from (Fig 3 and 4)?

The depths of the recorded visually responsive neurons is now shown in Figure 2—figure supplement 1E.

Reviewer #3 (Public Review):

The authors used optogenetic manipulations and electrophysiology recordings to study a causal role and the coding of superficial part of the mouse Superior Colliculus (SCs) during figure detection tasks.

Authors previously reported that figure-ground perception relies on V1 activity (Kirchberger et al. 2021) and pointed out that silencing of V1 reduced the accuracy of the mice but still the performance was above the chance level. Therefore, visual information necessary in this task, could be processed via alternative pathways. In this study, authors investigated specifically SCs and used similar approach and analysis as in Kirchberger et al. 2021. Optogenetic silencing of the activity of visual neurons in SCs impaired the accuracy in all 3 versions of the figure detection task: contrast, orientation, and phase. Electrophysiology recordings revealed that SCs neurons are figure-ground modulated, but only by contrast- and orientation-based figures. They show SCs visually responsive neurons reflect behavioral performance in orientation-based figure task. The authors conclusion is that SCs is involved in figure detection task.

Overall, this study provides evidence that mouse SCs is involved in a figure detection task, and codes for task-related events. Authors heroically compared results between 3 different versions of the figure-based detection task. The logic of the study flows through the manuscript and authors prepared a detailed description of methods.

Thank you for your positive comments.

However, my main concern is with 1) the amount of data used to make the key arguments, and 2) the interpretation of results. The key findings of this study (figure-ground modulations in SCs) could be a result of the visual cortical feedback in SCs during the task, or pupil diameter changes. Unfortunately, the authors did not rule out these possibilities.

Still, this study can be relevant to a general neuroscience audience, and results could be more convincing if the authors could clarify:

1) Optogenetic inactivation

a) The impact of laser stimulation on neural activity is not satisfactory (Supplementary Figure 1). The method seems to be insufficient to fully salience neurons. Electrophysiology control recordings of inactivation are performed in anesthetized mice, which is not a fair estimation of the effect in awake state. Therefore, it rises a major question how effective the inactivation is during the task?

We have conducted new control experiments for the impact of laser stimulation on neural activity, now in awake animals (see Figure 1—figure supplement 2). The reviewer was right to ask for these experiments. We had not expected much difference in the effect of silencing in the awake and anesthetized state. To minimize the animal discomfort, we had therefore done these control experiments in terminal experiments under anesthesia. However, these new set of experiments showed that the impact of laser stimulation was much stronger in awake mice than anesthetized mice. We see an average spike rate reduction of 90% when the laser is on. Although it is not full silencing, we think this reduction is sufficient to draw some conclusions on the role of sSC in the behavioral tasks.

b) Could authors provide more details if laser stimulation has an effect only on visual, or all sampled units? How many of units were recorded, and how many show positive and negative laser modulation?

We defined visually responsive units as units that have an evoked rate of at least 2 spikes/s. In the new figure 1—figure supplement 2D from the new set of control experiments, we plotted, for every unit, the mean rate in laser ON and OFF trials - also including the non-visually responsive units. It is evident that the spiking activity of most units – including those that were not classified as ‘visual’ – is reduced in the laser ON compared to OFF trials. We observed 1 unit that showed strong positive laser modulation over the entire duration (figure 1—figure supplement 1D). Many units were activated by shorter laser pulses directly after laser onset (Figure 1—figure supplement 2A-B), but these also reduced in activity as the stimulation continued.

c) How local the inactivation effect is? Where was the silicon probe placed in relation to AAV expression and optical fiber position?

The AAV was injected at 0.3 mm anterior and 0.5 mm lateral to the lambda cranial landmark. With this injection location we aimed to focus the expression at low/nasal receptive fields, in front of the mouse, because that is where the visual stimulation would take place. From there, the expression did spread laterally across sSC (see Figure 1C). The silicon probe was placed roughly in the same location as the viral injection. The optical fiber was positioned such that the tip would shine on the surface of the sSC at a slight angle, from a lateral distance of ~200 µm from the silicon probe. We have edited the methods section to make this more clear (line 583-585). This procedure allowed us to record only relatively local effects of the inactivation. Although we did not record neural activity across the entirety of sSC, we did record from multiple electrode penetrations per mouse, each time slightly varying the recording location with up to ~300µm and ~500µm in the anterior and lateral directions, respectively. In these variations of recording location the optogenetic effect was always present (see new Figure 1—figure supplement 2G). Moreover, the suppressive effect of optogenetic stimulation of GAD2+ neurons was observed across the entire depth of the sSC (new Figure 1—figure supplement 2H).

2) Number of sessions and units

a) The inactivation effect on behavior (Figure 1E) during phase-task has a significantly larger effect at 66ms after stimulus onset. How can authors explain this? Could this result be biased by one animal/session, or low number of trials for this condition? There is no information about number of trials, or sessions from individual animals. Adding a single example of animal's performance, and sessions for individual mice could clarify results in Figure 1.

The criterium for each mouse to be included in the analysis for one of the tasks was to have 100 trials where optogenetics were used (aggregated across the latencies). So at minimum, we would have about 100 trials/6 latencies = 17 trials per latency per mouse. For most mice though, the number of trials per latency was closer to about 40. We have added more information about this to the methods section (lines 567-570). Despite these inclusion criteria, the 66 ms effect is present for multiple mice (we have now added data visualizations for the individual mice in Figure 1—figure supplement 4). To address the reviewer’s concerns, we can only speculate as to why this happens. It might be random variation. A more speculative conclusion would be that perhaps this 66ms laser onset is particularly disturbing to the visual processing and/or decision-making of the mouse. But we feel that we do not have enough evidence to conclude this.

b) Figure 2H shows an example of neuron with an effect in the figure detection task based on phase difference, but Figure 2I/J (population response) shows there is no effect. Overall, the conclusion is that SCs neurons are not modulated by a phase-defined object. It seems that number of mice and hence units are smaller in phase-detection task comparing to two other tasks. How many of single units are modulated in each version of the task? How big is the FGM effect on single neuron response (could authors provide values in spikes/s)? One task is dropped from analysis which it is one of the main points of the paper: to compare responses across different versions of the figure detection task in SCs. But Figures 3-5 only focuses on two tasks, because there is not enough of data for figure-based contrast task.

We have updated Figure 2H to show spikes/s of the example single neuron response. For the population responses, we explicitly normalized the individual neurons because they all have different baseline and peak firing rates. This normalization was important for the decoding, so we decided to print the data such that the data from Figures 2I and 3B went into the decoding as printed. If we look at the non-normalized values, the maximum amplitude of the average FGM effect is 22.3, 5.9 and 2.9 sp/s respectively for the three tasks (for neurons with RF on stimulus center).

We have furthermore updated the FGM analysis such that the clustered statistic is now based on linear mixed effects statistics instead of T-test statistics. The results based on this new analysis are largely the same (see statistics table T1). We checked the significance of individual neurons in the time window where the grouped LME analysis was significant. For the phase task (n.s. in grouped analysis), we used the significant window from the orientation task. For this analysis, we want to stress that the number of trials for each version of the task for each individual neurons is quite limited as we recorded all three of the tasks during each recording session. Individually, 7/23 neurons were significant for the contrast task, 1/49 were significant for the orientation task, 0/32 were significant for the phase task (after Bonferroni-holm correction).

To address the final part of this comment on dropping the contrast task: we indeed have recorded too few data points to draw conclusions on decoding (Fig. 3) and discriminability (Fig. 4) for the contrast task. However, we do not see the contrast detection task as the main point of the paper. As earlier work had already shown involvement of the sSC in visually-evoked behaviours based on objects that are clearly isolated from the background, the main focus in this work is to show involvement of sSC in complex object detection, where the visual contrast and luminance is the same across object and background.

3) Figure-ground modulation in SCs

a) How is neural activity correlated with pupil size, movement (eg. whisking, or face), or jaw movement (preparation to lick)? Can activity of FGM neurons in SCs be explained by these behavioral variables?

We did not record whisking or other face and jaw movements. We did record the eye of the mice, so have included a new Figure 2—figure supplement 2 which shows eye position and pupil dilation during the task. For the analysis in the originally submitted paper, trials with substantial eye movement (Z-score of eye speed > 2.5) between 0 and 450 ms had already been removed from the analysis. This way, we could exclude effects of eye movements (but not pupil dilation) on the visual responses in sSC. The additional figures and analyses have been done using the same inclusion criteria. Indeed, in the included trials mice did not move their eyes during the peak of the visual response (0-250 ms). The pupil dilation also did not change in this period.

b) Could authors describe in more detail how they measure a pupil position and diameter, by showing raw data, pupil size aligned to task events?

We have added a new Figure 2—figure supplement 2 to show the pupil position and diameter aligned to task onset.

c) How does pupil diameter change between tasks? Small pupil changes can affect responses of visual neurons, and this could be an explanation of FGM effect in SCs. Can authors rule out this possibility, by for example showing pupil size and changes in position at stimulus onset in different tasks?

Our new Figure 2—figure supplement 2B shows that pupil dilation changes and differences in pupil dilation between figure/ground trials do occur, but only after ~300 ms, so after the peak of the visual response and after the FGM is present in sSC.

d) Authors in discussion mentioned that the modulation of V1 could be transferred to SCs through the direct projection. Moreover, animals perform above chance in both inactivation experiments (V1 and SC), which could be also an effect of geniculate projections to HVAs (eg. Sincich et al. 2004). Could authors discuss different possibilities?

The direct geniculate projection to HVAs is an interesting possibility that we had not considered yet. The dLGN in the mouse projects (apart from V1) mostly to the medial HVAs (Bienkowski et al. 2018). The lateral extrastriate regions receive only very sparse input from the dLGN. The medial HVAs, however, could be silenced without drop in performance in a simple visual detection task (Goldback et al., 2020). Therefore, it does not seem likely that this geniculate to HVAs projections would be important in the figure detection task.

4) Interpretation of multisensory neurons is not clear. In Figure 5B, there is an example of neuron with two peaks of response. Authors speculate about the activity (pre-motor) but there is lack of clear measurement showing "multisensory" response of these neurons. Could these responses be related to the movement of the lick spout towards the mouth of the mouse (500 ms after the presentation of the stimulus)? Moreover, the number of "multisensory" units is very low (5 units, and 8 units).

We have not done definitive test to show what these putative multisensory neurons exactly respond to. Because of their response was after the appearance of the lick and time locking to the trial start, rather than to the licking response, we think that is likely that these neurons responded to the appearance of the spout. There might have been visual, auditory, vibrational or touch clues to which these neurons respond. We believe it is interesting for the reader to know that there is class of neurons in the sSC that did not show a visual stimulus but was time locked to the trial. This was the reason that we had included this figure in the manuscript. However, given the reviewers comments we have decided to move the figure and accompanying text to a figure supplement (Figure 2—figure supplement 1) in order to not distract from the main message of the manuscript.

Author Response

Joint Public Review:

1) For the in vitro work, only one cell line is used in this article: HPAEpiC cells, an immortalized human cell line derived from alveolar epithelial type II cells. This limits the generalizability of the results obtained in this study, as SARS-CoV-2 is known to infect several kinds of cells.

We appreciate the concerns of the reviewing editor. To test whether our findings were applicable to other cells, we performed similar experiments in human hepatoma cells (Huh-7) and renal tubular cells (HK-2), which are highly susceptible to SARS-CoV-2 (Yeung et al., 2021). We found that infection by SARS-CoV-2 upregulated the protein levels of ACE2, while colchicine treatment significantly inhibited the expression of ACE2 in HK-2 cells and Huh-7 cells (Revised Figure 3-figure supplement 2A-D). In addition, we found that colchicine treatment also reduced the viral load of SARS-CoV-2 in HK-2 cells and Huh-7 cells (Revised Figure 3-figure supplement 2E and F).

2) From the results of two separate experiments (colchicine leading to reduced ACE2-expression in HPAEpiC cells & colchicine leading to reduced SARS-CoV-2 replication in HPAEpiC cells), the authors infer that inhibition of ACE2 expression by colchicine suppresses SARS-CoV-2 infection. However, their experiments do not explicitly prove this hypothesis and do not give weight to the importance of this reduced ACE2 expression in the colchicine antiviral effect they observed, as other mechanisms may play a (bigger) role in producing this effect.

It has been well-established that the infection of SARS-CoV-2 and the Spike-RBD binding are dependent on ACE2 expression in different cell lines. ACE2 knockdown dramatically reduces SARS-CoV-2 infection in Caco2 cells (Shen et al., 2022), Spike-RBD binding, and SARS-CoV-2 replication in Calu-3 cells (Samelson et al., 2022). In contrast, overexpression of ACE2 greatly enhances SARS-CoV-2 virus infection in both A549 and H1299 cells (Chen et al., 2021). Meanwhile, two recent studies have demonstrated that androgen receptor positively regulates the expression of ACE2 at a transcriptional level (Qiao et al., 2021; Samuel et al., 2020). Importantly, inhibition of ACE2 expression by reducing the AR signaling attenuates SARS-CoV-2 infectivity (Qiao et al., 2021). A very recent study has demonstrated that ursodeoxycholic acid (UDCA), an inhibitor of the farnesoid X receptor (FXR), reduces ACE2 expression in human lung, intestinal, and liver organoids, thereby inhibiting SARS-CoV-2 infection (Brevini et al., 2022). These results clearly demonstrate that ACE2 expression levels determine the efficiency of SARS-CoV-2 infection to host cells.

3) The authors refer to colchicine as a drug leading to mortality benefit when used as treatment for COVID-19 (line 101-105). However, whether colchicine is beneficial in COVID-19 is unclear. For instance, the randomized controlled trial by the RECOVERY Collaborative Group (Lancet Respir Med 2021), which included more than 11,000 patients, did not find benefit from colchicine in patients admitted to hospital with COVID-19. The authors refer to the review of Drosos et al to infer benefit of colchicine in COVID-19, however this review ignores the numerous trials contradicting this (as also stated in a letter from Finsterer in response to this review). The meta-analysis by Elshafei to which the authors refer was published before the largest RCT by the RECOVERY Group was published.

We agree with the assessment made by the reviewing editor. Our goal is to discover a new mechanism of regulating ACE2 expression. Using colchicine, we have- identified that SP1 is a crucial transcription factor that regulates ACE2 expression. In response to the reviewer’s comments, we added the sentences “This study has several limitations. Firstly, although SP1 was identified as a pivotal transcription factor in modulating ACE2 expression via the action of colchicine and MithA, neither of these compounds currently qualify as a candidate for the treatment of COVID-19.…Additionally, the efficacy of colchicine as a treatment for COVID-19 remains inconclusive. While some studies suggest benefits (Chiu et al., 2021; Drosos et al., 2022; Elshafei et al., 2021), others indicate negligible impact on mortality or disease progression (Group, 2021; Mikolajewska et al., 2021).” in Discussion of revised manuscript (Lines 329-342).

4) The authors did not let a pathologist blinded to the infection/treatment state of the animals score the samples obtained in the animal experiments, which could have introduced bias in these results.

We appreciate the concerns of the reviewing editor. Actually, histological observations were made by one of authors, Dr. Li-Qiong Wang, who is a pathologist, blinded to group identity. In response to the reviewer’s suggestion, we have now added a sentence “Tissue sections were evaluated by a trained pathologist (L.-Q. W.) blinded to group identity” in the section of Material and Methods (Lines 516 and 517).

Author Response

We appreciate the insightful comments from three reviewers on our manuscript. These comments help us improve the clarity of this manuscript. We will revise our manuscript comprehensively in subsequent revision, and enclose a detailed response to each of these comments. In this public reply, we focus on (a) clarifying the theoretical motivation and implication of the present study, and (b) discussing the implications of our LLM study. Besides, we provide a brief justification regarding some methodological concerns shared by the reviewers.

1) Theoretical rationale and implication

As we stated in the manuscript, the present study tested whether body size serves as a reference for locomotion and object manipulation, or alternatively, plays a pivotal role in shaping the representation of objects as suggested by Protagoras. Behind this question is the long-lasting debate regarding the representation versus direct perception of affordance.

One outstanding theme shared by many embodied theories of cognition is the replacement hypothesis (e.g., Van Gelder, 1998). This hypothesis challenges the necessity of representation in the sense of computationalism cognitive theories (e.g., Fodor, 1975), which implies discretizing/categorizing inputs and then subjecting them to certain abstraction or symbolization so as to create discrete stand-ins for the input (e.g., representations/states). In this sense, our theoretical motivation can be restated explicitly as to test the ‘representationalization’ of affordance. That is, we tested whether object affordance would simply covary with its continuous constraints such as object size, in line with the representation-free view, or, whether affordance would be ‘representationalized’, in line with the representation-based view, under the constrain of body size. Such representationalization would generate categorization between the affordable (the objects) and those beyond affordance (the environment).

Debates regarding the replacement hypothesis often turn into wrestles on the definition of representation (Shapiro, 2019). The present study tried to avoid this pitfall but examined where the embodied and computational theories make opposite hypotheses: discontinuity. Specifically, we considered two computationalism propositions about representation: (a) representations entail discretization of continuous input, and (b) the product of such discretization (representations) is supramodally accessible (that is, transcending sensorimotor processes). These claims are opposite to the prediction based on the idea of direct perception and other representation-free embodied theories.

Thus, we tested whether, for continuous action-related physical features (such as object size relative to the agents), affordance perception introduces discontinuity and qualitative dissociation, i.e., to allow the sensorimotor input to be assigned into discrete states/kinds, as representations envisioned by computationalists. Alternatively, does the activity directly mirror the input, free from discretization/categorization/abstraction, as proposed by the replacement hypothesis that organisms do not need to re-present the world as they are always in contact with the world in a continuous way?

All the experiment settings and analyses in the present study were organized around this motivation, following a progressive logic chain.

First, we tested the discretization hypothesis, that is, whether affordance leads to discontinuity in perception. Here, the discontinuity in affordance perception would be in line with the representation-based view instead of the representation-free proposals. Second, to ensure that the observed discontinuity can be attributed to the discretization of sensorimotor input involved in human-object interaction rather than amodal sources, such as the discrete abstract concepts of the objects (independent from agent motor capability), we tested the embodied nature of this discontinuity through the body imagination experiment. If there is discontinuity in representing embodied information, this discontinuity should be locked to the motor capacity (constrained by the physical constitution such as body size) of the agent, rather than reflecting independent categorization of the absolute size of the objects. Finally, we probed the supramodality of this embodied discontinuity: whether this discontinuity is accessible beyond the sensorimotor domain. To do this, we leveraged the recent advance in AI and tested whether the discretization observed in affordance perception is supramodally accessible to disembodied agents which lack access to sensorimotor input but only have access to the linguistic materials built upon discretized representations, such as large language models (LLM).

In this way, the experiments in the present study collectively contributed to the debate on the replacement theme of the embodiment of cognition, which serves as one of the three key themes of embodied theories of cognition (Shapiro, 2019). By addressing this theme, we hope to shed light on the nature of representation in, and resulting from, the vision-for-action processing. Our finding regarding discontinuity suggested that sensorimotor input undergoes discretization implied in the computationalism idea of representation. Further, not contradictory to the claims of the embodied theories, these representations do shape processes out of the sensorimotor domain, but after discretization.

2) Implication in the development of LLM-based agents

The finding that affordance was representationalized may have profound implications for the development of LLM-based agents. Traditional robots and non-LLM-based agents require implementation-level action instruction, acting as a tool for human beings to achieve desired results. In contrast, LLM-based agents (for a review, see Wang et al., 2023), such as Auto-GPT and BabyAGI, are able to autonomously perform tasks and achieve desired results based on LLMs’ planning ability. In this sense, LLM-based agents show a primary ability to interact on their own with the world. Generative agents, for instance, the agents in Smallville (Park et al., 2023), are a particularly applauded recent advantage in the school of LLM-based agents, which show even larger potentials in this aspect. Drawing on generative models to simulate human behaviors, these agents can formulate their own memories and goals, generate new environment-dependent behaviors, and interact convincingly with humans and other agents and their environments in the course. This brings new possibilities in resolving the long-lasting challenge in artificial general intelligence (AGI) development, that is, to bestow AI with human-level ability in agent-environment interactions. However, it is worth noting that the present investigation in LLM-based agents is still largely confined to virtual environments. This leaves an open question as to how to equip these agents with the ability of agent-environment physical interaction. Especially, according to embodied theories of cognition, sensorimotor interactions with the environment provide unique knowledge upon which various cognitive domains are built. From this point of view, building agents with human-level ability in agent-environment physical interactions might provide an unreplaceable missing piece for AGI.

By probing the representation of action possibilities (affordances) provided by the environment to the agent (or the absence of them), the present study provided a clue in achieving such ability by illustrating the representationalization of affordance and the supramodality of these representations. For instance, the finding of supramodality may alleviate the doubts about the physical interaction ability of LLM-based agents comparable to biological agents. Specifically, LLM-based agents can leverage the affordance representation distilled into language to interact with the physical world. Indeed, by clarifying and aligning such representation with the physical constitutes of LLM-based agents, and even by explicitly constructing an agent-specific object space, we may facilitate the sensorimotor interactions of LLM-based agents so as to achieve animal-level interaction ability with the world. This in turn may provide new instances for embodied theories.

3) Clarification on incomplete evidence

In response to the methodological and validity concerns of the reviewers, we will provide a point-by-point detailed response to reviewers enclosed with the revised manuscript. Here, we reply to the most prominent concerns.

Reviewers were concerned about the statistical power of both the body imagination experiment and the fMRI experiment. Regarding the number of participants in the imagination study, we would like to clarify that we did not remove 80% of the participants. Actually, a separate sample of participants was recruited in the body imagination experiment. The sample size for the body imagination experiment (100 participants) was indeed smaller than that recruited for the first experiment (528 participants). This is because the first experiment was set for exploratory purposes, and was designed to be over-powered.

Admittedly, the fMRI experiment recruited a small sample (12 participants), which might lead to low power in estimating the affordance effect. In revision, we will acknowledge this issue explicitly. Having said this, note that the null hypothesis of this fMRI study is the lack of two-way interaction between object size and object-action congruency, which was rejected by the significant interaction. That is, the interpretation of the present study did not rely on accepting any null effect. In addition, the fMRI experiment provided convergent evidence for the affordance discontinuity at the neural level. We showed that behind the behavioral discontinuity in action judgement, neural activity was qualitatively different between objects within the affordance boundary and those beyond, which reinforces our statement that objects were discretized along the continuous size axis into two broad categories.

Reviewers also commented that more objects and actions should be included. We agree, and in revision, we will advocate future studies with more objects and more actions to comprehensively portray discontinuity. The present set of objects was designated to cover a relatively large range of object sizes, ranging from 14 cm to 7,618 cm to cover most size categories studied in Konkle and Oliva's (2011) work. In addition, the actions were selected to cover daily interactions between human and objects or environments from single-point movements (e.g., hand, foot) to whole-body movements (e.g., lying, standing) referencing the kinetics human action video dataset (Kay et al., 2017). Thus, this set of selected objects and actions is sufficient to test the discontinuity.

References

Fodor, J. A. (1975). The Language of Thought (Vol. 5). Harvard University Press.

Park, J. S., O'Brien, J. C., Cai, C. J., Morris, M. R., Liang, P., & Bernstein, M. S. (2023). Generative agents: Interactive simulacra of human behavior. arXiv preprint arXiv:2304.03442.

Shapiro, L. (2019). Embodied Cognition. Routledge.

Van Gelder, T. (1998). The dynamical hypothesis in cognitive science. Behavioral and Brain Sciences, 21(5), 615-628.

Wang, L., Ma, C., Feng, X., Zhang, Z., Yang, H., Zhang, J., ... & Wen, J. R. (2023). A survey on large language model based autonomous agents. arXiv preprint arXiv:2308.11432.

Author Response

eLife assessment

This study presents potentially valuable results on glutamine-rich motifs in relation to protein expression and alternative genetic codes. The author's interpretation of the results is so far only supported by incomplete evidence, due to a lack of acknowledgment of alternative explanations, missing controls and statistical analysis and writing unclear to non experts in the field. These shortcomings could be at least partially overcome by additional experiments, thorough rewriting, or both.

We thank both the Reviewing Editor and Senior Editor for handling this manuscript and will submit our revised manuscript after the reviewed preprint is published by eLife.  

Reviewer #1 (Public Review):

Summary

This work contains 3 sections. The first section describes how protein domains with SQ motifs can increase the abundance of a lacZ reporter in yeast. The authors call this phenomenon autonomous protein expression-enhancing activity, and this finding is well supported. The authors show evidence that this increase in protein abundance and enzymatic activity is not due to changes in plasmid copy number or mRNA abundance, and that this phenomenon is not affected by mutants in translational quality control. It was not completely clear whether the increased protein abundance is due to increased translation or to increased protein stability.

In section 2, the authors performed mutagenesis of three N-terminal domains to study how protein sequence changes protein stability and enzymatic activity of the fusions. These data are very interesting, but this section needs more interpretation. It is not clear if the effect is due to the number of S/T/Q/N amino acids or due to the number of phosphorylation sites.

In section 3, the authors undertake an extensive computational analysis of amino acid runs in 27 species. Many aspects of this section are fascinating to an expert reader. They identify regions with poly-X tracks. These data were not normalized correctly: I think that a null expectation for how often poly-X track occur should be built for each species based on the underlying prevalence of amino acids in that species. As a result, I believe that the claim is not well supported by the data.

Strengths

This work is about an interesting topic and contains stimulating bioinformatics analysis. The first two sections, where the authors investigate how S/T/Q/N abundance modulates protein expression level, is well supported by the data. The bioinformatics analysis of Q abundance in ciliate proteomes is fascinating. There are some ciliates that have repurposed stop codons to code for Q. The authors find that in these proteomes, Q-runs are greatly expanded. They offer interesting speculations on how this expansion might impact protein function.

Weakness

At this time, the manuscript is disorganized and difficult to read. An expert in the field, who will not be distracted by the disorganization, will find some very interesting results included. In particular, the order of the introduction does not match the rest of the paper.

In the first and second sections, where the authors investigate how S/T/Q/N abundance modulates protein expression levels, it is unclear if the effect is due to the number of phosphorylation sites or the number of S/T/Q/N residues.

There are three reasons why the number of phosphorylation sites in the Q-rich motifs is not relevant to their autonomous protein expression-enhancing (PEE) activities:

First, we have reported previously that phosphorylation-defective Rad51-NTD (Rad51-3SA) and wild-type Rad51-NTD exhibit similar autonomous PEE activity. Mec1/Tel1-dependent phosphorylation of Rad51-NTD antagonizes the proteasomal degradation pathway, increasing the half-life of Rad51 from ∼30 min to ≥180 min (Ref 27; Woo, T. T. et al. 2020).

1. T. T. Woo, C. N. Chuang, M. Higashide, A. Shinohara, T. F. Wang, Dual roles of yeast Rad51 N-terminal domain in repairing DNA double-strand breaks. Nucleic Acids Res 48, 8474-8489 (2020).

Second, in our preprint manuscript, we have also shown that phosphorylation-defective Rad53-SCD1 (Rad51-SCD1-5STA) also exhibits autonomous PEE activity similar to that of wild-type Rad53-SCD (Figure 2D, Figure 4A and Figure 4C).

Third, as revealed by the results of our preprint manuscript (Figure 4), it is the percentages, and not the numbers, of S/T/Q/N residues that are correlated with the PEE activities of Q-rich motifs.

The authors also do not discuss if the N-end rule for protein stability applies to the lacZ reporter or the fusion proteins.

The autonomous PEE function of S/T/Q-rich NTDs is unlikely to be relevant to the N-end rule. The N-end rule links the in vivo half-life of a protein to the identity of its N-terminal residues. In S. cerevisiae, the N-end rule operates as part of the ubiquitin system and comprises two pathways. First, the Arg/N-end rule pathway, involving a single N-terminal amidohydrolase Nta1, mediates deamidation of N-terminal asparagine (N) and glutamine (Q) into aspartate (D) and glutamate (E), which in turn are arginylated by a single Ate1 R-transferase, generating the Arg/N degron. N-terminal R and other primary degrons are recognized by a single N-recognin Ubr1 in concert with ubiquitin-conjugating Ubc2/Rad6. Ubr1 can also recognize several other N-terminal residues, including lysine (K), histidine (H), phenylalanine (F), tryptophan (W), leucine (L) and isoleucine (I) (Bachmair, A. et al. 1986; Tasaki, T. et al. 2012; Varshavshy, A. et al. 2019). Second, the Ac/N-end rule pathway targets proteins containing N-terminally acetylated (Ac) residues. Prior to acetylation, the first amino acid methionine (M) is catalytically removed by Met-aminopeptides, unless a residue at position 2 is non-permissive (too large) for MetAPs. If a retained N-terminal M or otherwise a valine (V), cysteine (C), alanine (A), serine (S) or threonine (T) residue is followed by residues that allow N-terminal acetylation, the proteins containing these AcN degrons are targeted for ubiquitylation and proteasome-mediated degradation by the Doa10 E3 ligase (Hwang, C. S., 2019).

A. Bachmair, D. Finley, A. Varshavsky, In vivo half-life of a protein is a function of its amino-terminal residue. Science 234, 179-186 (1986).

T. Tasaki, S. M. Sriram, K. S. Park, Y. T. Kwon, The N-end rule pathway. Annu Rev Biochem 81, 261-289 (2012).

A. Varshavsky, N-degron and C-degron pathways of protein degradation. Proc Natl Acad Sci 116, 358-366 (2019).

C. S. Hwang, A. Shemorry, D. Auerbach, A. Varshavsky, The N-end rule pathway is mediated by a complex of the RING-type Ubr1 and HECT-type Ufd4 ubiquitin ligases. Nat Cell Biol 12, 1177-1185 (2010).

The PEE activities of these S/T/Q-rich domains are unlikely to arise from counteracting the N-end rule for two reasons. First, the first two amino acid residues of Rad51-NTD, Hop1-SCD, Rad53-SCD1, Sup35-PND, Rad51-ΔN, and LacZ-NVH are MS, ME, ME, MS, ME, and MI, respectively, where M is methionine, S is serine, E is glutamic acid and I is isoleucine. Second, Sml1-NTD behaves similarly to these N-terminal fusion tags, despite its methionine and glutamine (MQ) amino acid signature at the N-terminus.

The most interesting part of the paper is an exploration of S/T/Q/N-rich regions and other repetitive AA runs in 27 proteomes, particularly ciliates. However, this analysis is missing a critical control that makes it nearly impossible to evaluate the importance of the findings. The authors find the abundance of different amino acid runs in various proteomes. They also report the background abundance of each amino acid. They do not use this background abundance to normalize the runs of amino acids to create a null expectation from each proteome. For example, it has been clear for some time (Ruff, 2017; Ruff et al., 2016) that Drosophila contains a very high background of Q's in the proteome and it is necessary to control for this background abundance when finding runs of Q's.

We apologize for not explaining sufficiently well the topic eliciting this reviewer’s concern in our preprint manuscript. In the second paragraph of page 14, we cite six references to highlight that SCDs are overrepresented in yeast and human proteins involved in several biological processes (32, 74), and that polyX prevalence differs among species (43, 75-77).

1. Cheung HC, San Lucas FA, Hicks S, Chang K, Bertuch AA, Ribes-Zamora A. An S/T-Q cluster domain census unveils new putative targets under Tel1/Mec1 control. BMC Genomics. 2012;13:664.

2. Mier P, Elena-Real C, Urbanek A, Bernado P, Andrade-Navarro MA. The importance of definitions in the study of polyQ regions: A tale of thresholds, impurities and sequence context. Comput Struct Biotechnol J. 2020;18:306-13.

3. Cara L, Baitemirova M, Follis J, Larios-Sanz M, Ribes-Zamora A. The ATM- and ATR-related SCD domain is over-represented in proteins involved in nervous system development. Sci Rep. 2016;6:19050.

4. Kuspa A, Loomis WF. The genome of Dictyostelium discoideum. Methods Mol Biol. 2006;346:15-30.

5. Davies HM, Nofal SD, McLaughlin EJ, Osborne AR. Repetitive sequences in malaria parasite proteins. FEMS Microbiol Rev. 2017;41(6):923-40.

6. Mier P, Alanis-Lobato G, Andrade-Navarro MA. Context characterization of amino acid homorepeats using evolution, position, and order. Proteins. 2017;85(4):709-19.

We will cite the two references by Kiersten M. Ruff in our revised manuscript.

K. M. Ruff and R. V. Pappu, (2015) Multiscale simulation provides mechanistic insights into the effects of sequence contexts of early-stage polyglutamine-mediated aggregation. Biophysical Journal 108, 495a.

K. M. Ruff, J. B. Warner, A. Posey and P. S. Tan (2017) Polyglutamine length dependent structural properties and phase behavior of huntingtin exon1. Biophysical Journal 112, 511a.

The authors could easily address this problem with the data and analysis they have already collected. However, at this time, without this normalization, I am hesitant to trust the lists of proteins with long runs of amino acid and the ensuing GO enrichment analysis.

Ruff KM. 2017. Washington University in St.

Ruff KM, Holehouse AS, Richardson MGO, Pappu RV. 2016. Proteomic and Biophysical Analysis of Polar Tracts. Biophys J 110:556a.

We thank Reviewer #1 for this helpful suggestion and now address this issue by means of a different approach described below.

Based on a previous study (43; Palo Mier et al. 2020), we applied seven different thresholds to seek both short and long, as well as pure and impure, polyX strings in 20 different representative near-complete proteomes, including 4X (4/4), 5X (4/5-5/5), 6X (4/6-6/6), 7X (4/7-7/7), 8-10X (≥50%X), 11-10X (≥50%X) and ≥21X (≥50%X).

To normalize the runs of amino acids and create a null expectation from each proteome, we determined the ratios of the overall number of X residues for each of the seven polyX motifs relative to those in the entire proteome of each species, respectively. The results of four different polyX motifs are shown below, i.e., polyQ (Author response image 1), polyN (Author response image 2), polyS (Author response image 3) and polyT (Author response image 4).

Author response image 1.

Q contents in 7 different types of polyQ motifs in 20 near-complete proteomes. The five ciliates with reassigned stops codon (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.  

Author response image 2.

N contents in 7 different types of polyN motifs in 20 near-complete proteomes. The five ciliates with reassigned stops codon (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.

Author response image 3.

S contents in 7 different types of polyS motifs in 20 near-complete proteomes. The five ciliates with reassigned stops codon (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.  

Author response image 4.

T contents in 7 different types of polyT motifs in 20 near-complete proteomes. The five ciliates with reassigned stops codon (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.

The results summarized in these four new figures support that polyX prevalence differs among species and that the overall X contents of polyX motifs often but not always correlate with the X usage frequency in entire proteomes (43; Palo Mier et al. 2020).

Most importantly, our results reveal that, compared to Stentor coeruleus or several non-ciliate eukaryotic organisms (e.g., Plasmodium falciparum, Caenorhabditis elegans, Danio rerio, Mus musculus and Homo sapiens), the five ciliates with reassigned TAAQ and TAGQ codons not only have higher Q usage frequencies, but also more polyQ motifs in their proteomes (Figure 1). In contrast, polyQ motifs prevail in Candida albicans, Candida tropicalis, Dictyostelium discoideum, Chlamydomonas reinhardtii, Drosophila melanogaster and Aedes aegypti, though the Q usage frequencies in their entire proteomes are not significantly higher than those of other eukaryotes (Figure 1). Due to their higher N usage frequencies, Dictyostelium discoideum, Plasmodium falciparum and Pseudocohnilembus persalinus have more polyN motifs than the other 23 eukaryotes we examined here (Figure 2). Generally speaking, all 26 eukaryotes we assessed have similar S usage frequencies and percentages of S contents in polyS motifs (Figure 3). Among these 26 eukaryotes, Dictyostelium discoideum possesses many more polyT motifs, though its T usage frequency is similar to that of the other 25 eukaryotes (Figure 4).

In conclusion, these new normalized results confirm that the reassignment of stop codons to Q indeed results in both higher Q usage frequencies and more polyQ motifs in ciliates.  

Reviewer #2 (Public Review):

Summary:

This study seeks to understand the connection between protein sequence and function in disordered regions enriched in polar amino acids (specifically Q, N, S and T). While the authors suggest that specific motifs facilitate protein-enhancing activities, their findings are correlative, and the evidence is incomplete. Similarly, the authors propose that the re-assignment of stop codons to glutamine-encoding codons underlies the greater user of glutamine in a subset of ciliates, but again, the conclusions here are, at best, correlative. The authors perform extensive bioinformatic analysis, with detailed (albeit somewhat ad hoc) discussion on a number of proteins. Overall, the results presented here are interesting, but are unable to exclude competing hypotheses.

Strengths:

Following up on previous work, the authors wish to uncover a mechanism associated with poly-Q and SCD motifs explaining proposed protein expression-enhancing activities. They note that these motifs often occur IDRs and hypothesize that structural plasticity could be capitalized upon as a mechanism of diversification in evolution. To investigate this further, they employ bioinformatics to investigate the sequence features of proteomes of 27 eukaryotes. They deepen their sequence space exploration uncovering sub-phylum-specific features associated with species in which a stop-codon substitution has occurred. The authors propose this stop-codon substitution underlies an expansion of ploy-Q repeats and increased glutamine distribution.

Weaknesses:

The preprint provides extensive, detailed, and entirely unnecessary background information throughout, hampering reading and making it difficult to understand the ideas being proposed. The introduction provides a large amount of detailed background that appears entirely irrelevant for the paper. Many places detailed discussions on specific proteins that are likely of interest to the authors occur, yet without context, this does not enhance the paper for the reader.

The paper uses many unnecessary, new, or redefined acronyms which makes reading difficult. As examples:

(1) Prion forming domains (PFDs). Do the authors mean prion-like domains (PLDs), an established term with an empirical definition from the PLAAC algorithm? If yes, they should say this. If not, they must define what a prion-forming domain is formally.

The N-terminal domain (1-123 amino acids) of S. cerevisiae Sup35 was already referred to as a “prion forming domain (PFD)” in 2006 (Tuite, M. F. 2006). Since then, PFD has also been employed as an acronym in other yeast prion papers (Cox, B.S. et al. 2007; Toombs, T. et al. 2011).

M. F., Tuite, Yeast prions and their prion forming domain. Cell 27, 397-407 (2005).

B. S. Cox, L. Byrne, M. F., Tuite, Protein Stability. Prion 1, 170-178 (2007).

J. A. Toombs, N. M. Liss, K. R. Cobble, Z. Ben-Musa, E. D. Ross, [PSI+] maintenance is dependent on the composition, not primary sequence, of the oligopeptide repeat domain. PLoS One 6, e21953 (2011).

(2) SCD is already an acronym in the IDP field (meaning sequence charge decoration) - the authors should avoid this as their chosen acronym for Serine(S) / threonine (T)-glutamine (Q) cluster domains. Moreover, do we really need another acronym here (we do not).

SCD was first used in 2005 as an acronym for the Serine (S)/threonine (T)-glutamine (Q) cluster domain in the DNA damage checkpoint field (Traven, A. and Heierhorst, J. 2005). Almost a decade later, SCD became an acronym for “sequence charge decoration” (Sawle, L. et al. 2015; Firman, T. et al. 2018).

A. Traven and J, Heierhorst, SQ/TQ cluster domains: concentrated ATM/ATR kinase phosphorylation site regions in DNA-damage-response proteins. Bioessays. 27, 397-407 (2005).

L. Sawle and K, Ghosh, A theoretical method to compute sequence dependent configurational properties in charged polymers and proteins. J. Chem Phys. 143, 085101(2015).

T. Firman and Ghosh, K. Sequence charge decoration dictates coil-globule transition in intrinsically disordered proteins. J. Chem Phys. 148, 123305 (2018).

(3) Protein expression-enhancing (PEE) - just say expression-enhancing, there is no need for an acronym here.

Thank you. Since we have shown that addition of Q-rich motifs to LacZ affects protein expression rather than transcription, we think it is better to use the “PEE” acronym.

The results suggest autonomous protein expression-enhancing activities of regions of multiple proteins containing Q-rich and SCD motifs. Their definition of expression-enhancing activities is vague and the evidence they provide to support the claim is weak. While their previous work may support their claim with more evidence, it should be explained in more detail. The assay they choose is a fusion reporter measuring beta-galactosidase activity and tracking expression levels. Given the presented data they have shown that they can drive the expression of their reporters and that beta gal remains active, in addition to the increase in expression of fusion reporter during the stress response. They have not detailed what their control and mock treatment is, which makes complete understanding of their experimental approach difficult. Furthermore, their nuclear localization signal on the tag could be influencing the degradation kinetics or sequestering the reporter, leading to its accumulation and the appearance of enhanced expression. Their evidence refuting ubiquitin-mediated degradation does not have a convincing control.

Based on the experimental results, the authors then go on to perform bioinformatic analysis of SCD proteins and polyX proteins. Unfortunately, there is no clear hypothesis for what is being tested; there is a vague sense of investigating polyX/SCD regions, but I did not find the connection between the first and section compelling (especially given polar-rich regions have been shown to engage in many different functions). As such, this bioinformatic analysis largely presents as many lists of percentages without any meaningful interpretation. The bioinformatics analysis lacks any kind of rigorous statistical tests, making it difficult to evaluate the conclusions drawn. The methods section is severely lacking. Specifically, many of the methods require the reader to read many other papers. While referencing prior work is of course, important, the authors should ensure the methods in this paper provide the details needed to allow a reader to evaluate the work being presented. As it stands, this is not the case.

Thank you. As described in detail below, we have now performed rigorous statistical testing using the GofuncR package.

Overall, my major concern with this work is that the authors make two central claims in this paper (as per the Discussion). The authors claim that Q-rich motifs enhance protein expression. The implication here is that Q-rich motif IDRs are special, but this is not tested. As such, they cannot exclude the competing hypothesis ("N-terminal disordered regions enhance expression").

In fact, “N-terminal disordered regions enhance expression” exactly summarizes our hypothesis.

On pages 12-13 and Figure 4 of our preprint manuscript, we explained our hypothesis in the paragraph entitled “The relationship between PEE function, amino acid contents, and structural flexibility”.

The authors also do not explore the possibility that this effect is in part/entirely driven by mRNA-level effects (see Verma Na Comms 2019).

As pointed out by the first reviewer, we show evidence that the increase in protein abundance and enzymatic activity is not due to changes in plasmid copy number or mRNA abundance (Figure 2), and that this phenomenon is not affected by translational quality control mutants (Figure 3).

As such, while these observations are interesting, they feel preliminary and, in my opinion, cannot be used to draw hard conclusions on how N-terminal IDR sequence features influence protein expression. This does not mean the authors are necessarily wrong, but from the data presented here, I do not believe strong conclusions can be drawn. That re-assignment of stop codons to Q increases proteome-wide Q usage. I was unable to understand what result led the authors to this conclusion.

My reading of the results is that a subset of ciliates has re-assigned UAA and UAG from the stop codon to Q. Those ciliates have more polyQ-containing proteins. However, they also have more polyN-containing proteins and proteins enriched in S/T-Q clusters. Surely if this were a stop-codon-dependent effect, we'd ONLY see an enhancement in Q-richness, not a corresponding enhancement in all polar-rich IDR frequencies? It seems the better working hypothesis is that free-floating climate proteomes are enriched in polar amino acids compared to sessile ciliates.

Thank you. These comments are not supported by the results in Figure 1.

Regardless, the absence of any kind of statistical analysis makes it hard to draw strong conclusions here.

We apologize for not explaining more clearly the results of Tables 5-7 in our preprint manuscript.

To address the concerns about our GO enrichment analysis by both reviewers, we have now performed rigorous statistical testing for SCD and polyQ protein overrepresentation using the GOfuncR package (https://bioconductor.org/packages/release/bioc/html/GOfuncR.html). GOfuncR is an R package program that conducts standard candidate vs. background enrichment analysis by means of the hypergeometric test. We then adjusted the raw p-values according to the Family-wise error rate (FWER). The same method had been applied to GO enrichment analysis of human genomes (Huttenhower, C., et al. 2009).

Curtis Huttenhower, C., Haley, E. M., Hibbs, M., A., Dumeaux, V., Barrett, D. R., Hilary A. Coller, H. A., and Olga G. Troyanskaya, O., G. Exploring the human genome with functional maps, Genome Research 19, 1093-1106 (2009).

The results presented in Author response image 5 and Author response image 6 support our hypothesis that Q-rich motifs prevail in proteins involved in specialized biological processes, including Saccharomyces cerevisiae RNA-mediated transposition, Candida albicans filamentous growth, peptidyl-glutamic acid modification in ciliates with reassigned stop codons (TAAQ and TAGQ), Tetrahymena thermophila xylan catabolism, Dictyostelium discoideum sexual reproduction, Plasmodium falciparum infection, as well as the nervous systems of Drosophila melanogaster, Mus musculus, and Homo sapiens (74). In contrast, peptidyl-glutamic acid modification and microtubule-based movement are not overrepresented with Q-rich proteins in Stentor coeruleus, a ciliate with standard stop codons.

1. Cara L, Baitemirova M, Follis J, Larios-Sanz M, Ribes-Zamora A. The ATM- and ATR-related SCD domain is over-represented in proteins involved in nervous system development. Sci Rep. 2016;6:19050.

Author response image 5.

Selection of biological processes with overrepresented SCD-containing proteins in different eukaryotes. The percentages and number of SCD-containing proteins in our search that belong to each indicated Gene Ontology (GO) group are shown. GOfuncR (Huttenhower, C., et al. 2009) was applied for GO enrichment and statistical analysis. The p values adjusted according to the Family-wise error rate (FWER) are shown. The five ciliates with reassigned stop codons (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.

Author response image 6.

Selection of biological processes with overrepresented polyQ-containing proteins in different eukaryotes. The percentages and numbers of polyQ-containing proteins in our search that belong to each indicated Gene Ontology (GO) group are shown. GOfuncR (Huttenhower, C., et al. 2009) was applied for GO enrichment and statistical analysis. The p values adjusted according to the Family-wise error rate (FWER) are shown. The five ciliates with reassigned stops codons (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.

Author Response

The following is the authors’ response to the original reviews.

eLife assessment

The study provides valuable insights into allosteric regulation of BTK, a non-receptor protein kinase, challenging previous models. Using a variety of biophysical and functional techniques, the paper presents evidence that the N-terminal PH-TH domain of BTK exists in a conformational ensemble surrounding a compact SH3-SH2-kinase core, that the BTK kinase domain can form partially active dimers, and that the PH domain can form a novel inhibitory interface after SH2/SH3 disengagement. Overall the presented evidence is solid, but the EM results may be over-interpreted and the work would benefit from additional functional validation.

We made every effort in our descriptions of the cryoEM data presented for full-length BTK to not overinterpret the results. In essence this is not an ideal EM target but given the failure by us and others to capture the full-length multi-domain protein crystallographically, we decided that the albeit low resolution cryoEM data are useful to the field.

Reviewer #1 (Public Review):

The manuscript by Lin et al describes a wide biophysical survey of the molecular mechanisms underlying full-length BTK regulation. This is a continuation of this lab's excellent work on deciphering the myriad levels of regulation of BTKs downstream of their activation by plasma membrane localised receptors.

The manuscript uses a synergy of cryo EM, HDX-MS and mutational analysis to delve into the role of how the accessory domains modify the activity of the kinase domain. The manuscript essentially has three main novel insights into BTK regulation.

1) Cryo EM and SAXS show that the PHTH region is dynamic compared to the conserved Src module.

2) A 2nd generation tethered PH-kinase construct crystal of BTK reveals a unique orientation of the PH domain relative to the kinase domain, that is different from previous structures.

3) A new structure of the kinase domain dimer shows how trans-phosphorylation can be achieved.

Excitingly these structural works allow for the generation of a model of how BTK can act as a strict coincidence sensor for both activated BCR complex as well as PIP3 before it obtains full activity. To my eye the most exciting result of this work is describing how the PH domain can inhibit activity once the SH3/SH2 domain is disengaged, allowing for an additional level of regulatory control.

I have very few experimental concerns as the methods and figures are well-described and clear. As the authors are potentially saying that the previously solved PH domain-kinase interface is artefactual, additional evidence strengthening their model would be helpful to resolve any possible controversies.

We do not argue that the previously solved PH domain-kinase interface is artefactual. Instead we point out that the PH/kinase interface identified in the prior structure is incompatible with the contacts between the SH3 and kinase domains in autoinhibited BTK. This then leads us to the suggestion that a PH/kinase inhibitory interaction may instead occur upon dissociation of the SH3-SH2 cassette from the kinase domain. Our data support that model. Moreover, our data suggest the PHTH domain is dynamic, likely not settling in to one particular autoinhibitory state. Thus, it is possible the previously solved PH/kinase structure exists within the conformational ensemble of a range PH/kinase domain interactions. In an effort to clarify our think we added two sentences to the Discussion (pg. 19).

Reviewer #2 (Public Review):

In this study, multiple biophysical techniques were employed to investigate the activation mechanism of BTK, a multi-domain non-receptor protein kinase. Previous studies have elucidated the inhibitory effects of the SH3 and SH2 domains on the kinase and the potential activation mechanism involving the membranebound PIP3 inducing transient dimerization of the PH-TH domain, which binds to lipids.

The primary focus of the present study was on three new constructs: a full-length BTK construct, a construct where the PH-TH domain is connected to the kinase domain, and a construct featuring a kinase domain with a phosphomimetic at the autophosphorylation site Y551. The authors aimed to provide new insights into the autoinhibition and allosteric control of BTK.

The study reports that SAXS analysis of the full-length BTK protein construct, along with cryoEM visualization of the PH-TH domain, supports a model in which the N-terminal PH-TH domain exists in a conformational ensemble surrounding a compact/autoinhibited SH3-SH2-kinase core. This finding is interesting because it contradicts previous models proposing that each globular domain is tightly packed within the core.

Furthermore, the authors present a model for an inhibitory interaction between the N-lobe of the kinase and the PH-TH domain. This model is based on a study using a tethered complex with a longer tether than a previously reported construct where the PH-TH domain was tightly attached to the kinase domain (ref 5). The authors argue that the new structure is relevant. However, this assertion requires further explanation and discussion, particularly considering that the functional assays used to assess the impact of mutating residues within the PH-TH/kinase domain contradict the results of the previous study (ref 5).

In our hands BTK activity is not significantly affected by mutation of just two residues, R133 and Y134. It is somewhat difficult to compare the previously reported activity assay for the same BTK mutant (Wang et al. ref 5, Figure 4D) with the data we report here. For unexplained reasons, the time scale for the quantitative assay in the previous work is truncated to 50 munutes for the R133/Y134 mutant data compared to 120 minutes for all of the other activity data reported in that figure. In our data, if we qualitatively examine the differences in a representative progress curve at 50 minutes between WT and the double R133/Y134 mutant (see Figure 6a, dark blue and pink traces) one might conclude that the R133/Y134 mutation is activating BTK. However, when we calculate the average kinase activity rate ± standard error for three independent experiments we find that the difference between WT and the double R133/Y134 mutant is not significant (see Figure 6b and c). Thus, instead of making any assertions about the previously published data we are trying to be as rigoruous as possible in presentation and interpretation of our own data.

In addition, throughout the manuscript we tried to be very careful in our discussion of our data and that published previously, to avoid conclusive statements about the previously described interface. Afterall, one of our overriding conclusions is that the N-terminal region of BTK is highly dynamic. See response to reviewer 1 above.

Additionally, the study presents the structure of the kinase domain with swapped activation loops in a dimeric form, representing a previously unseen structure along the trans-phosphorylation pathway. This structure holds potential relevance. To better understand its significance, employing a structure/function approach like the one described for the PH-TH/kinase domain interface would be beneficial.

We completely agree with this comment and are pursuing such studies now.

Overall, this study contributes to our understanding of the activation mechanism of BTK and sheds light on the autoinhibition and allosteric control of this protein kinase. It presents new structural insights and proposes novel models that challenge previous understandings. However, further investigation and discussion would significantly strengthen the study.

As indicated we are pursuing further investigation and felt that the body of work presented here is sufficient for a single manuscript.

Reviewer #3 (Public Review):

Yin-wei Lin et al set out to visualize the inactive conformation of full-length Bruton's Tyrosine Kinase (BTK), a molecule that has evaded high-resolution structural studies in its full-length form to this date. An open question in the field is how the Pleckstrin Homology-Tec Homology (PHTH) domain inhibits BTK activity, with multiple competing models in the field. The authors used a complimentary set of biophysical techniques combined with well-thought-out stabilizing mutations to obtain structural insights into BTK regulation in its full-length form. They were able to crystallize the full-length construct of BTK but unfortunately, the PHTH was not resolved yielding a structure similar to that previously obtained in the field. The investigation of the same construct by SAXS yielded an elongated structural model, consistent with previous SAXS studies. Using cryo-EM the authors obtained a low-resolution model for the FL BTK with a loosely connected density assigned to the dynamic PHTH around the compact SH2-SH3-Kinase Domain (KD) core. To gain further molecular insights into PHTH-KD interactions the authors followed a previously reported strategy and generated a fusion of PHTH-KD with a longer linker, yielding a crystal structure with a novel PHTH-KD interface which they tested in biochemical assays. Lastly, Yin-wei Lin et al crystallized the BTK KD in a novel partially active state in a "face-to-face" dimer with kinases exchanging the activation loops, although partially disordered, being theoretically perfectly positioned for transphosphorylation. Overall this presents a valiant effort to gain molecular insights into what clearly is a dynamic regulatory motif on BTK and is a valuable addition to the field.

However, this work can be improved by considering these points:

1) The cryo-EM reconstructions are potentially over-interpreted. The reported resolution for all of the analyzed reconstructions is better than 8Å, at which point helices should be recognized as well-resolved structural elements. In the current view/depiction of the cryo-EM maps/models it is hard to see such structural features and it would be great if the authors could include a panel showing maps at higher thresholds to show correspondence between the helices in the kinase C lobe and the cryo-EM maps. Otherwise, the overall positioning of the models within the cryo-EM maps is hard to evaluate and may very well be wrong. (Fig 4, S2).

First, we fully recognize the model is low-resolution and we are careful in our discussion of the cryo-EM data to use language that acknowledges the limitations of the model. Nevertheless, this is the model we have (specific data processing points are discussed below).

The resolution numbers are from the Fourier Shell Correlation (FSC) curve given by Cryosaprc at the end of refinement. We do acknowledge the reviewer’s comments that the resolution could be over estimated in that calculation, but our main focus is to show that the overall domain arrangement of the autoinhibited BTK core (Src-module) fits into the reconstructions.

We tested visualizing the maps at higher threshold, but the secondary structures of the reconstructions were still not well resolved. We do realize that with the current reconstructions, we do not have the structural details to correctly orientate and fit individual domains; this is why we chose to simply fit the available crystal structure of the autoinhibited BTK SH3-SH2-kinase core into the maps.

2) With the above in mind, if the maps are not at the point where helices are well resolved, it may be beneficial to low-pass filter the maps to a more conservative resolution for fitting, analysis, and representation. (Fig 4, S2).

Using low-pass filtered maps at 10Å or unsharpened maps, the fitting of the BTK model and map do not change significantly.

3) It would be valuable to get a quantitative metric on the model/map fitting for the cryo-EM work. One good package for this is Situs which provides cross-correlation values for the top orthogonal fits, without user input for initial fitting. This would again increase confidence in the correctness of model positioning on the map. (Fig 4, S2).

Thank you for this suggestion. We tested the colores feature (Exhaustive One-At-A-Time 6D Search) in Situs to perform model to map fitting without user input as the reviewer suggested. The highest ranked fitting is identical to what we presented in the manuscript. Following are the cross-corelation numbers calculated from “Fit-in-map” tool in chimera and from “collage” function in Situs. We now indicate this step in the caption to Figure 4.

Author response table 1.

4) It would be great to see 2D class averages from the particles contributing to each of the 3D classes. Theoretically, a clear bright "blob" (hypothesized to be the PHTH domain) should be observable in the 2D class averages. In the current 2D class averages that region is unconvincingly weak. (Fig 4, S2).

We attempted to improve both 2D and 3D reconstructitions by feeding the particles from each 3D class through many cycles of 2D classification and selection to exclude ‘bad’ paritcles, but neither the 2D class averages nor 3D reconstructions could be improved.

We agree the feature that appears in the 2D class averages is weak. The BTK protein is only 77kD in size and is highly dynamic and flexible. Thus, in reality this is not an ideal system for cryo-EM. As well, the PHTH domain itself is quite small and NMR data, acquired in the context of a different project, provides evidence that the isolated PHTH domain is dynamic in solution (NMR linewidths vary throughout the protein suggesting intermediate exchange). Nevertheless, given the inability to capture the PHTH domain in crystal structures of full-llength BTK we reasoned that cryo-EM could provide some insight. In the future we anticipate building on these data to include inhibitory binding partners of BTK; however such an effort is beyond the scope of the current work.

5) It seems like there was quite a large circular mask applied during 2D classification. Are authors confident that the weak density attributed to the PHTH domain is not neighboring particles making their way into the extraction box? It would be great if the authors would trim their particle stack with a very stringent interparticle distance cutoff (or report the cutoff in the manuscript if already done so) to minimize this possibility.

We initially picked particles using a small radius (100 Å), and stringently selected 2D classes with particles that contained only density aligning to the core SH3-SH2-kinase domains. We found, however, that 3D ab initio reconstruction always resulted in an additional density located at different positions around the larger core density. The structure of a single BTK PHTH domain fits into that additional remote density. Given the additional density that consistently appeared in 3D reconstructions, we went back and picked particles using a larger circular mask (200 A). Subsequent 2D classification and 3D reconstruction from this analysis gave similar results and are presented in the manuscript.

Regardless of the mask radius, we used stringent conditions for particle picking and checked for the presence of duplicates. An interparticle distance cutoff of 0.1 to 0.5 times the particle diameter was used and resulted in fewer number of particles, but the presence of the extended density remains. We also made use of template picking (2D class averages) to repick the particles and found no significant difference in the number of particles or quality of 2D classifications.

6) The cryo-EM processing may benefit from more stringent particle picking. The authors picked over 2M particles from 750 micrographs which likely represents very heavy overpicking. I would encourage the authors to re-pick the micrographs with 2D class averages and use more stringent metrics to reduce the overpicking. This may result in higher-resolution reconstructions. (Fig 4, S2).

This was an effort to maximize the number of particles extracted. After multiple rounds of 2D classification and selection to exclude empty and junk particles, the final number of particles selected for 3D ab-initio reconstructions were only 68,788, and only ~20K particles for each 3D reconstruction. Thus, we are not concerned that we overpicked particles. This approach is described in Supp Figure S2.

7) The Dmax from SAXS for the Full Length BTK is at 190Å. It would be great if the authors could make a cartoon of what domain arrangement may satisfy this distance, as it is quite extended for such a small particle. Can the authors rule out dimerization at SAXS concentrations? (Fig 1).

SAXS data for full-length, wild-type BTK has been previously published (Márquez et al, 2003 EMBO J. (2003) 22:4616-4624). Our data for WT BTK are consistent with that published previously (and we have cited this previous work). In that work, the authors attribute the ~200 Å Dmax value to an elongated BTK conformation where the domains of BTK are arranged in a linear fashion (a figure showing this domain arragement is provided by Marquez et al. precluding the need for such a cartoon here).

In the present work we take advantage of targeted mutations to stabilize the autoinhibted SH2-SH2-kinase core and the Dmax value that we report for this more autoinhibited version of full-length BTK (FL 4P1F) is ~150Å. Notwithstanding low resolution in both SAXS and cryoEM, it is notable that superposition of the cryoEM models in Figure 4c & d gives a distance of ~150Å between the PHTH domains from the two models.

Finally, we cannot completely rule out that a small fraction of full length BTK is forming dimers. However, in our experience purifying and working with this protein, we find that purified and concentrated monomeric fulllength Btk proteins (as high as 15mg/ml) are quite stable and remain monomeric and free of aggregation even after sitting at 4°C for more than a week. Here the BTK SAXS data were collected within 24 hours after the samples were thawed.

8) In Figure S1 (C) it seems that the curves are just scattering curves with Guinier plots in the inserts, but are labeled as Guinier plots in the legend. The Guinier plots for some samples (FL 4P1F) show signs of aggregation, which may complicate the analysis, it could be beneficial to redo.

We thank the reviewer for pointing out our mistake in presention of the SAXS data. We have now replaced plots in Figure S1c with the correct scattering profiles for each construct with the Guinier insets shown. We revised the label of this panel to “Scattering profile and Guinier plots (insets)”.

In addition, we re-processed the FL 4P1F data by performing buffer subtraction (using a different buffer alone scattering dataset (also collected during original data acquisition)). The data quality after reprocessing were significantly improved (see new scattering profiles and Guinier plots for full-length BTK in Supplementary Figure S1). Protein stability (see above) and the current data quality therefore suggest that aggregation is not complicating the SAXS analysis.

9) Have the authors verified that the activation loop mutations that they introduce do not disrupt the PHTH binding as they previously reported an activation loop on BTK to interact with PHTH, an interaction they do not see here? If so, a citation would be helpful in the text. If not, testing this would strengthen the paper.

The same activation loop mutations were included in the constructs used in the previous solution studies of the PHTH/kinase domain interaction by NMR and HDX (see ref [11]). We clarify this point in the methods section. As well, all but one of the sequence changes introduced into the activation loop are at positions at the ‘base’ of the activation loop and therefore are not surface exposed. Only one amino acid change is on the exposed part of the activation loop (V555T).

10) Can the authors comment on the surfaces which are accessible and inaccessible to the PHTH in the crystal (Fig 3E)? The fact that PHTH doesn't adopt a stable conformation in the solvent channel to some degree indicates that the accessible interaction surfaces are not suitable for PHTH interactions, as the "effective concentration" of the PHTH would be quite high. Are these surfaces consistent with the cryo-EM analysis?

This is an excellent point and we did state the following in describing the crystallization results:

“the crystallography results are consistent with a flexible N-terminal PHTH domain with the caveat that the domain swapped dimer organization might limit native autoinhibitory contacts between the PHTH and SH3SH2-kinase regions.”

In the domain swapped dimer seen in the crystal, a symmetry related molecule does partially block the Ghelix region of the kinase domain while the activation loop and C-helix in the N-lobe remain accessible. Our previous solution studies (ref [11]) pointed to the G helix as part of the interaction interface in addition to the activation loop and part of the N-lobe. We have now modified the sentence above to more clearly describe which parts of the kinase domain are inaccessible in the crystal and the possible ramifications of the steric environment on PHTH domain mobility in the crystal (see pg. 10). That said, all of our previous HDX data shows little protection in the PHTH domain in full-length BTK (mapping of the PHTH/kinase interaction was only possible in trans using excess PHTH domain) and so our data can be best summarized by concluding that the PHTH domain visits a number of conformational states and makes transient contacts with various regions of the kinase domain (dependent upon whether the SH3-SH2 region is engaged or not). This is similar to the ‘fuzzy’ intramolecular contacts described for the N-terminal region of the SRC family. Like the SRC family, BTK (and other TEC kinases) contain a long disordered linker between the N-terminal region and the compact SH3-SH2-kinase core.

11) For the novel active state dimer of the Kinase Domain it would be great to see some functional validation of the dimerization interface. It is structurally certainly quite suggestive, but without such experiments the functional significance is unclear. If appropriate mutations have been published previously a citation would be helpful.

We completely agree. We scoured the literature and our own facuntional assay results over many years but the appropriate mutations to test the functional significance of the kinase domain dimer have not been reported or previously studied in our lab. We are therefore actively pursuing this line of investigation now.

Reviewer #1 (Recommendations For The Authors):

I have the following proposed experiments/analysis that should help.

1) To better validate the putative PH-kinase interface seen, the authors should try some alphafold multimer / rosettaTTFold modelling of just the PHTH module with the kinase domain. The advantage of this is that it will test how conserved over evolution the potential interface is, and will help to decipher discrepancies between the two structures. This may end up being similar to what is seen in Akt (in this case the alphafold prediction does not match the allosteric inhibitor structure, or the nanobody bound structure), but this could help provide additional insight into how the PH domain interacts.

We have applied alphafold to this system. The PHTH-kinase fusion sequence was fed to Alphafold and the separate PHTH and kinase domains to Aphafold multimer. The results provide a range of ‘complexes’ none of which recapitulate the PHTH/kinase interface reported here or that reported by Wang et al in previous work. Three of five results from Alphafold Multimer place the PHTH domain on the activation loop face of the kinase domain consistent with the previous solution data pointing to a similar regulatory interface. This is interesting but our experience in applying alphafold to dynamic confromationally heterogeneous systems is that the results need to be considered with caution. For that reason we did not include any of the alphafold predictions in the manuscript.

Evolutionary conservation is discussed further in the next section:

2) Could the authors provide a detailed evolutionarily analysis of the binding surface between the PHTH and kinase domains and include this in Fig5, this also would help interpret the likelihood of this interface.

This is an excellent question and we have in fact previously published a detailed evolutionary analysis of the BTK kinase domain in collaboration with Kannan Natarajan (see Amatya et al., PNAS, 2019, [ref 11]). In that work we found that evolutionarily conserved residues on the kinase domain map to the activation loop face, supporting the solution data that the PHTH interacts with the kinase domain across the activation loop face. That work predated alphafold but it is interesting that, to the exent that alphafold predicts anything, it seems to converge on the PHTH domain containg the activation loop face.

In the context of our current work, and this question from the reviewer, we re-examined the evolutionary anlysis carried out previously and find that BTK (or TEC family) specific residues on the kinase domain do not appear at the newly identified PHTH/kinase interface we report here. We could speculate that since the ‘back’ of the kinase domain N-lobe interacts with multiple binding partners (SH3, SH2-linker and PHTH) evolutionary pressures may have resulted in a certain degree of plasticity to allow recognition of multiple binding partners.

Evolutionary analysis of the BTK PH domain was also carried out previously and shows that the conserved sites map to the phospholipid binding pocket of the PH domain. The analysis did not include TH domain residues. Since we find the TH domain contributes to the PHTH/kinase interface in our crystal structure, we do not have the data at this time to do a thourough anaylsis but we appreciate this comment and can address this in furture work with collaborators.

Author Response

First of all, we would like to thank you for the opportunity to get the three valuable sets of comments on our work from the reviewers and the important summary from the Chief Editor. If we understand correctly, at this moment, we are expected to check for any factual errors, and our response at this stage will affect the choice of which reviewer’s comment will be published as a part of the reviewed Preprint. If so, we want to comment on some of the reviewer's points (Part A). These are not factual errors but more misunderstandings that need to be corrected. Furthermore, it depends on your decision whether it will be a part of the response or not. In Part B, we will address the reviewer's comments.

Part A:

1) Reviewers #1 and #3 missed our originally already reported PNAs dynamics based on live-cell imaging (mainly Reviewer #3 stressed that the dynamic we present is extrapolated from fixed imaging). We previously published the detailed dynamics of PNAs as detected by live-cell imaging (Imrichova, Aging 2019, doi: 10.18632/aging.102248. Epub 2019 Sep 7). It seems that we have not sufficiently highlighted this important aspect in the present eLife manuscript, despite in the Introduction part, we have described the dynamic transitions between the individual PNAs types/stages, yet without explicitly emphasizing that such dynamic insights were deduced from our live-cell imaging experiments.

2) Reviewer#2 asked us to reconcile the different phenotypes after RNAi of TOP2A (KD induces PNAs) and TOP2B (KD does not induce PNAs), vis a vis the fact that the TOP2B-targeting drug -doxorubicin is a strong inducer of PNAs formation. We would like to stress that doxorubicin is not a specific poison of TOP2B (e.g., Atwal 2019; DOI: 10.1124/mol.119.117259). It can poison (at low concentration) or inhibit (at high concentration) all subtypes of topoisomerase 2. In other words, doxorubicin targets a wider spectrum of type 2 topoisomerases and hence can limit any potential redundant roles of the individual subtypes, which, on the other hand, can manifest under conditions when only a specific one member is depleted genetically. We have further discussed this interesting issue in the discussion presented in our manuscript, and we believe there is no discrepancy, due to the wider impact of doxorubicin and an apparently more dominant role of TOP2A than TOP2B in preventing PNAs.

3) We are aware that the biological significance of the interaction of PML with nucleolus has not been fully solved yet. At this moment, we can conclude that PNAs recognize and sequester the damaged/aberrant rDNA from active nucleolus. This novel sorting mechanism might be necessary for maintaining the integrity of the repetitive rDNA loci that might otherwise be altered or lost during complex recombinational rDNA repair. Importantly, we also identified substances (mostly chemotherapeutics) that cause rDNA damage. Given that PML is a multifaceted protein involved in diverse processes; PML depletion might affect several stress-related processes. The rDNA quality/quantity analysis is also highly challenging because of the high number of rDNA copies (200-400). As preparing such an experimental model/s is difficult and time-consuming, addressing this issue in more detail will be a part of our follow-up work. Nevertheless, we will perform the bulk of the experiments recommended by the reviewers, to strengthen the conclusions of this manuscript, as follows: A) We will explore whether the PNAs formation is linked to some specific cell cycle phase; B) To strengthen the experiments with inhibition of NHEJ (DNA PKi) and HR (B02i), we will perform the RNA interference or use some other inhibitor/s operating through a distinct mechanism yet targeting the same repair process; C) We will analyze the recovery from I-PpoI treatment and assess cell proliferation, ability to form colonies, and the presence of senescent cells.

Part 2

Reviewer #1 (Public Review):

Summary:

This paper described the dynamics of the nuclear substructure called PML Nucleolar Association (PNA) in response to DNA damage on ribosomal DNA (rDNA) repeats. The authors showed that the PNA with rDNA repeats is induced by the inhibition of topoisomerases and RNA polymerase I and that the PNA formation is modulated by RAD51, thus homologous recombination. Artificially induced DNA double-strand breaks (DSBs) in rDNA repeats stimulate the formation of PNA with DSB markers. This DSB-triggered PNA formation is regulated by DSB repair pathways.

Strengths:

This paper illustrates a unique DNA damage-induced sub-nuclear structure containing the PML body, which is specifically associated with the nucleolus. Moreover, the dynamics of this PML Nucleolar Association (PNA) require topoisomerases and RNA polymerase I and are modulated by RAD51-mediated homologous recombination and non-homologous end-joining. This study provides a unique regulation of DSB repair at rDNA repeats associated with the unique-membrane-less subnuclear structure.

Weaknesses:

Although the PNA formation on rDNA repeat is nicely shown by cytological analysis, the biological significance of PNA in DSB repair is not fully addressed.

At this moment, we cannot mechanistically fully elucidate the biological significance of this peculiar process. However, our data shows that the dynamic interaction of PML with nucleolus can sequester damaged rDNA from reactivating nucleolus. We propose that in this way, the actively transcribed intact rDNA is protected from possible detrimental interaction with the defective, PNAs-sequestered rDNA, most likely to avoid the harmful intra- and inter-chromosomal recombination events that would otherwise likely occur during recombinational repair of the damaged rDNA, as the rDNA repeats present on 5 chromosomes are repetitive. Thus, this novel sorting mechanism might help sustain repetitive rDNA loci integrity.

Reviewer #2 (Public Review):

In this manuscript, the authors aim to study the PML-nucleoli association (PNAs) by different genotoxic stress and to determine the underlying molecular mechanisms.

First, from a diverse set of genotoxic stress conditions (topoisomerases, RNA Pol I, rRNA processing, and DNA replication stress), the authors have found that the inhibition of topoisomerases and RNA Polymerase I has the highest PNA formation associated with p53 stabilization, gamma-H2AX, and PAF49 segregation. It was further demonstrated that Rad51-mediated HR pathway but not NHEJ pathway is associated with the PNA formation. Immuno-FISH assays show that doxorubicin induces DSBs (53BP1 foci) in rDNA and PNA interactions with rDNA/DJ regions. Furthermore, endonuclease I-Ppol induced DSB at a defined location in rDNA and led to PNAs.

Most claims by the authors are supported by the data provided. However, below weaknesses/concerns may need to be addressed to improve the quality of the study.

1) Top2B toxin doxorubicin had the highest degree of elevating PNAs; however, Top2B-knockdown had almost no noticeable effects on PNAs. How to reconcile the different phenotypes targeting Top2B?

1) We thank the reviewer for this comment and below explain why there is no discrepancy in the observed phenotypes. Doxorubicin is not a specific poison of TOP2B (e.g., Atwal 2019; DOI: 10.1124/mol.119.117259). It can poison (stabilize ternary complex at low concentration) or inhibit (e.g., defects in decatenation at high concentration) all subtypes of topoisomerase 2. It intercalates DNA (alteration of DNA torsion; histone eviction) and elevates oxidative stress. Therefore, the observed effect of doxorubicin reflects its broader impact, also beyond inhibition of Top2B: as doxorubicin targets a wider spectrum of type 2 topoisomerases and hence can limit any potential redundant roles of the individual subtypes (which on the other hand can manifest under conditions when only one specific member is depleted genetically), thereby causing a robust induction of PNAs. We have further discussed this issue in the Discussion section of our manuscript, and we believe there is no discrepancy, in the observed phenotypes due to the wider impact of doxorubicin and an apparently more dominant role of TOP2A than TOP2B (both of which are impacted to some extent by doxorubicin) in preventing PNAs.

2) To test the role of Rad51 and DNA-PKcs in the PNA formation, Rad51 inhibitor B02 and DNA-PKcs inhibitor NU-7441 were chosen to use in the study. To further exclude the possible off-target of B02 and NU-7441, siRNA-mediated knockdown of Rad51 and DNA-PKcs would be an appropriate complementary approach to the pharmaceutical inhibitor approach.

We are grateful for this suggestion and will perform the recommended experiments the outcome of which will indeed help to exclude the possible off-target effects of B02 and NU-7441. We are now collecting/testing the necessary tools and will carry out these analyses proposed by the reviewer.

3) Several previous studies have shown the activation of the nucleolar ATM-mediated DNA damage response pathway by I-Ppol-induced DSBs in rDNA. What is the role of nucleolar ATM in the regulation of PNAs?

We are aware of the relevant literature on ATM, and appreciate this question from the reviewer. During the revision of this manuscript, we will therefore address the role of ATM signaling in the phenomena that we report here. As ATM signaling is essential for the repression of pre-rRNA synthesis and the compaction of rDNA into the nucleolar caps in response to rDNA damage, we will complement this knowledge by testing to what extent might ATM inhibition affect the induction of PNAs/PML-NDS in our model and experimental settings.

Reviewer #3 (Public Review):

Summary:

Hornofova et al. examined interactions between the nucleolus and promyelocytic leukemia nuclear bodies (PML-NBs) termed PML-nucleolar associations (PNAs). PNAs are found in a minor subset of cells, exist within distinct morphological subcategories, and are induced by cellular stressors including genotoxic damage. A systematic pharmacological investigation identified that compounds that inhibit RNA Polymerase 1 (RNAPI) and/or topoisomerase 1 or 2A caused the greatest proportion of cells with PNA. A specific RAD51 inhibitor (R02) impacted the number of cells exhibiting PNAs and PNA morphology. Genetic double-strand break (DSB) induction within the rDNA locus also induced PNA structures that were more prevalent when non-homologous end joining (NHEJ) was inhibited.

Strengths:

PNA are morphologically distinct and readily visualized. The imaging data are high quality, and rDNA is amenable to studying nuclear dynamics. Specific induction of rDNA damage is a strong addition to the non-specific pharmacological damage characterized early in the manuscript. These data nicely demonstrate that rDNA double-strand breaks undermine PNA formation. Figure 1 is a comprehensive examination and presents a compelling argument that RNAPI and/or TOP1, TOP2A inhibition promote PNA structures.

Weaknesses:

The data are limited to fixed fluorescent microscopy of structures present in a minority of cells. Data are occasionally qualitative and/or based upon interpretation of dynamic events extrapolated from fixed imaging. This study would benefit from live imaging that captures PNA dynamics.

We believe this comment reflects a misunderstanding, for the following reason: We fully agree with the reviewer that live-cell imaging is critical to properly capture the dynamics of the PNAs formation and evolution, and apologize for not sufficiently highlighting that this was already presented in our previous study in which we described the existence and dynamics of PNAs over time, based on the live cell imaging that the reviewer correctly regards as important. In Imrichova et al. (doi: 10.18632/aging.102248. Epub 2019 Sep 7), we used live-cell imaging to describe the dynamics of forming PNAs and the transition between individual types, and we referred to this work in the Introduction section of our present manuscript. By those experiments, including the live-cell imaging, we showed that after the recovery of RNAPI transcription, which usually follows the washout (removal) of the DNA-damaging agents, the funnel-like PNAs are transformed into PML-NDS. These newly emerging PNAs (PML-NDS) are placed next to the reactivated nucleolus. To document this, we paste below the relevant part of the Introduction text that was included in our submitted manuscript (see below in italics). Nevertheless, we did not emphasize that the transition between individual types of PNAs was obtained using live-cell imaging of cells ectopically expressing PML-EGFP and B23-RFP. In the revised manuscript, we will include this critical information and will complement this by a scheme explaining the dynamics of PNAs transitions.

Copied text from our manuscript, relevant to this issue: Doxorubicin, a topoisomerase inhibitor and one of the PNAs inducers, provokes a dynamic interaction of PML with the nucleolus, where the different phases linked to RNAPI inhibition can be discriminated into four basic structural subtypes of PNAs termed according to the 3D structures obtained by super-resolution microscopy as PML 'bowls', PML 'funnels', PML 'balloons' and PML nucleolus-derived structures (PML-NDS; (36)). The doxorubicin-induced inhibition of RNAPI leads to a nucleolar cap formation around which diffuse PML accumulates to form the PML bowl. Note that this event is rare as a minority of nucleolar caps are enveloped by PML (36). As the RNAPI inhibition continues, PML bowls protrude into PML funnels or transform into PML balloons wrapping the whole nucleolus. When the stress is relieved and RNAPI resumes activity, a PML funnel transforms into distinct compartments placed next to the non-segregated (i.e., reactivated) nucleoli, PML nucleolus-derived structures (PML-NDS). PML-NDSs contain nucleolar material, rDNA, and markers of DNA DSBs (36,37).

Cell cycle and cell division are not considered. Double-strand break repair is cell cycle dependent, and most experiments occur over days of treatment and recovery. It is unclear if the cultures are proliferating, or which cell cycle phase the cells are in at the time of analysis. It is also unclear if PNAs are repeatedly dissociating and reforming each cell division.

We agree this is an important point. In a complementary setting we previously published (Imrichova et al., doi: 10.18632/aging.102248. Epub 2019 Sep 7) that exposure of RPE-1 hTERT cells to doxorubicin caused cell cycle arrest and cellular senescence. Thus, most of such cells will not enter the cell cycle again. Regarding the I-PpoI-based model, we indeed did not show in the present manuscript how I-PpoI activation (rDNA damage) affects the cell cycle. In our preliminary experiments that address this issue, we saw that only about 1–3% of cells can recover from the stress and form colonies in a colony-forming assay. We will further repeat and corroborate these preliminary data and include these results in the revised manuscript, together with β-galactosidase staining to demonstrate the presence of senescent cells.

Furthermore, as suggested by this reviewer, we will assess the cell cycle phase/position of the cells in our experiments, to find out whether the cell cycle phase affects/correlates with the PNAs formation.

The relationship of PNA morphologies (bowl, funnel, balloon, and PML-NDS) also remains unclear. It is possible that PNAs mature/progress through the distinct morphologies, and that morphological presentation is a readout of repair or damage in the rDNA locus. However, this is not formally addressed.

This is partly explained by our response to Reviewer no 1, related to our previous live-cell imaging analyses. The 'bowl' emerges first and can be transformed into a 'funnel' or 'balloon'. All these PML structures are in contact with the nucleolar cap (the RNAPI is inhibited). Upon reactivation of RNAPI, the funnel can transform into the PML-NDS. At this moment, we cannot conclude to which precise process the individual structure is linked. However, we already know (Hornofova et al., DOI: 10.1016/j.dnarep.2022.103319) that the funnels colocalize with the highest portion of rDNA, which may reflect some process of concentration/clustering of rDNA. This observation is supported by results presented in this manuscript, which show that individual acrocentric chromosomes (NORs) also accumulate in one funnel. To summarize, the formation of the bowl reflects the aberration in rDNA. The funnel can accumulate rDNA and NORs in one site. The transition between the funnel and PML-NDS mirrors the changes after the reactivation of RNAPI and facilitates the sequestration of damaged rDNA/NORs outside of the active nucleolus. As the processes linked to the individual PNA are not solved yet, we will at least address this issue in a discussion.

An I-Ppol targeted sequence within the rDNA locus suggests 3D structural rearrangement following damage. An orthogonal approach measuring rDNA 3D architecture would benefit comprehension.

This is a very inspiring idea, although demanding and somewhat outside the focused scope of the present study. Our follow-up work will focus on the localization of individual NORs using immune-FISH after introducing the rDNA damage by I-PpoI. In the context of those studies, we also plan to analyze rDNA 3D architecture.

Following I-Ppol induction, it is possible that cells arrest in a G1 state. This may explain why targeting NHEJ has a greater impact on the number of 53BP1 foci and should be investigated.

We fully agree with this possibility and in response, we will perform a series of cell cycle analysis experiments to address this issue, during the revision phase of this manuscript. We will analyze whether I-Ppol-induced PNAs are linked to some cell cycle phase(s).

Conclusions: PNAs are a phenomenon of biological significance and understanding that significance is of value. More work is required to advance knowledge in this area. The authors may wish to examine the literature on APBs (Alt-associated PML-NBs), which are similar structures where telomeres associate with PML-NBs in a specific subset of cancers. It is possible that APBs and PNAs share similar biology, and prior efforts on APBs may help guide future PNA studies.

We will follow this recommendation by the reviewer. In ALT, PML is essential for clustering several (damaged) telomeres into APB. In PML-deficient cells, there is not only a defect in the formation of APB, but also the ALT telomeric DNA synthesis in G2 cells is blocked. As we already mentioned, funnel-like PNAs can accumulate several NORs. Thus, the recombination process between NORs might be facilitated. We will highlight this link and its relevance for cancer in our revised manuscript, thank you.

Author Response

The following is the authors’ response to the original reviews.

We are grateful to the reviewers for their insightful comments, suggestions, and criticism. In the updated version of the manuscript, all these will be properly reflected. Here we briefly address the main points raised:

Reviewer #1:

1.1) Patient selection and tumor area selection are crucial for this study but not very carefully defined. Why are some core and others not? Figure referral is an issue here (sup figure 6 where all core and non-core samples are supposed to be according to the legend of Fig 4 is likely sup fig 7 but this is then a complete copy paste of Figure 4). In the methods it is stated that the core samples are based on limited contamination of additional morphotypes (<20%) but Fig 4 suggests that all tumours listed have multiple morphotypes.

The tissue samples were obtained from a hospital cohort of patients with stage II-IV colorectal cancer (at diagnostic time), with no particular selection criteria imposed, as this was an exploratory study.

Tumor regions were marked for macro-dissection by an experienced pathologist following the standard practice for whole-tumor transcriptomics studies. The subregions (morphological regions) were marked by the same experienced pathologist for macro-dissection (in an adjacent section) and reassessed later with respect to their “morphological purity”. It is impossible to macro-dissect regions containing a single morphological pattern. Hence, those regions which contained significant amount (>=20%) of other morphologies were considered “non-core”, while the rest were called “core” regions. This distinction applies to morphological regions solely and not to whole-tumor samples. Indeed, the reference in caption to Figure 4, should refer to Supp. Fig. 7 (and has been updated).

1.2) CMS subtype should be performed with single sample predictor rather than CMScaller.

We agree that a single-sample predictor for CMS is needed, however CMScaller is the de facto classifier for CMS (>130 citations) so we used it to illustrate the practical implications.

1.3) A couple of surprising observations need specification. MUC2 is a strong CMS3 reporter gene yet Mucinous tumours appear to end up in CMS4 rather than 3. Can the authors show that indeed stroma cells are very evident in these samples?

We do not have a direct estimation of the amount of stromal cells, but the high scores of the various fibroblast-related signatures in mucinous regions (Fig2 B, D) indicate that, indeed, there is an enrichment in stroma. In the follow-up study we plan to perform specific staining as well as spatial transcriptomics of these regions to further investigate our findings.

1.4) The SE PP and CT are assigned to CMS2, but in Figure 4 this appears a lot more variable than the authors would make the reader believe. The full data are not completely clear (see point 1).

In the paper, we transparently state that PP, SE, and CT were assigned to CMS2 in 62.5%, 41.7% and 41.9% of cases, respectively. These proportions referred to all samples for which CMSCaller made a prediction. In Fig.4, we also show the proportion of cases in which CMSCaller did not predict any subtype.

1.5) The tumor response rates are rather weird as this is likely dependent on the complete tumour and not so much the subareas. It is not very well described what we see in this analysis.

We did not compute any response rates but simple prognostic scores as (weighted, if weights were provided) means of genes in the specific signatures (see Methods). The question addressed was whether these scores were comparable between whole tumor and corresponding tumor regions (within same tumor). Given the observed (relative) variability, the more important follow-up question - which we cannot answer with our limited survival data – is whether a higher score in a region in comparison with whole-tumor is indeed indicative of a higher risk of relapse.

1.6) Serrated adenomas have previously been aligned with CMS4. Is this different from serrated areas in cancers?

We do not have data from adenomas to compare with the serrated carcinoma regions. But a comparison of (regions of) both traditional serrated and sessile serrated adenomas to serrated carcinoma would be interesting.

1.7) The fact that iCMS2 and iCMS3 align rather well with the current analysis of the distinct regions suggests that the analysis that was reported last year is the proper way to view tumor intrinsic signatures. The authors now propose a rather similar outcome to this issue which does take away a lot of the novelty of the findings of this study.

In the manuscript it is clearly stated that our goal was to describe the molecular characteristics associated with several morphological patterns. It was not to propose another stratification paradigm for colorectal cancer. As such, our analyses were not limited to molecular subtypes and the respective observations were but a small part of our findings. Indeed, the intrinsic subtypes (iCMS 2/3) were stable and robust, as they were based on the genes expressed in epithelial cells, and they might well prove to be of clinical importance too. However, they do not cover all aspects (e.g. fibroblasts subtypes) and, as stated in Joanito et al. Nat Gen 54, pages 963–975 (2022), “iCMS, MSI status and CMS jointly inform the molecular classification of CRC”. Last, in our opinion, the molecular classification of CRC, while a useful point of view in tumour classification, is not covering all the necessary perspectives on tumour heterogeneity.

Reviewer #2:

2.1) Overall, the manuscript provides an interesting histological/morphological framework through which we can consider heterogeneity in colorectal carcinoma and an approach by which we might improve the performance of gene expression-based classifiers in predicting clinical behaviour and/or responses to therapy. Exploration of CRC morphotypes and their differences was quite interesting. However, more work is needed to support the claims made by the authors. While I appreciate that the authors themselves identify limitations of their study within the manuscript, I believe awareness of these limitations is not reflected in some of the claims made in the abstract and at points in the main text when discussing the use of expression-based classifiers.

The manuscript was improved to clarify several aspects that Reviewer 2 rightly pointed out:

1. We clarify that for a patient (tumor) there might be one or several corresponding transcriptomics profiles (see Methods).

2. The resulting “molecular portraits” were not derived with the goal to deconvolve the bulk tumor expression profiles and to estimate the proportions of morphotypes. Whether this is possible at all, is an open question and we mention this aspect in “Ideas and Speculation” section.

3. We improved figures captions to be more descriptive.

4. We included the reference for “Isela signature” at its first appearance.

Author Response

eLife assessment

This useful study addresses epilepsy caused by the loss of a molecule called Pten, resulting in hyperactivity of the mTOR pathway. The findings suggest that inhibiting two molecules called mTORC1 and mTORC2 can reduce epilepsy symptoms but there is much less effect when inhibited separately. The evidence supporting the conclusions is currently incomplete, but could be strengthened after additional experiments.

We thank the editors for this assessment and the reviewers for their comments. We will consider each of the recommendations we received and revise the manuscript accordingly.

Reviewer #1 (Public Review):

Hyperactivation of mTOR signaling causes epilepsy. It has long been assumed that this occurs through overactivation of mTORC1, since treatment with the mTORC1 inhibitor rapamycin suppresses seizures in multiple animal models. However, the recent finding that genetic inhibition of mTORC1 via Raptor deletion did not stop seizures while inhibition of mTORC2 did, challenged this view (Chen et al, Nat Med, 2019). In the present study, the authors tested whether mTORC1 or mTORC2 inhibition alone was sufficient to block the disease phenotypes in a model of somatic Pten loss-of-function (a negative regulator of mTOR). They found that inactivation of either mTORC1 or mTORC2 alone normalized brain pathology but did not prevent seizures, whereas dual inactivation of mTORC1 and mTORC2 prevented seizures. As the functions of mTORC1 versus mTORC2 in epilepsy remain unclear, this study provides important insight into the roles of mTORC1 and mTORC2 in epilepsy caused by Pten loss and adds to the emerging body of evidence supporting a role for both complexes in the disease development.

Strengths:

The animal models and the experimental design employed in this study allow for a direct comparison between the effects of mTORC1, mTORC2, and mTORC1/mTORC2 inactivation (i.e., same animal background, same strategy and timing of gene inactivation, same brain region, etc.). Additionally, the conclusions on brain epileptic activity are supported by analysis of multiple EEG parameters, including seizure frequencies, sharp wave discharges, interictal spiking, and total power analyses.

Weaknesses:

1) The sample size of the study is small and does not allow for the assessment of whether mTORC1 or mTORC2 inactivation reduces seizure frequency or incidence. This is a limitation of the study.

We agree that this is a minor limitation of the present study, however, for several reasons we decided not to pursue this question by increasing the number of animals. First, we performed a power analysis of the existing data. This analysis showed that we would need to use 89 animals per group to detect a significant difference (0.8 Power, p= 0.05, Mann-Whitney test) in the frequency of generalized seizures in the Pten-Raptor group and 31 animals per group in the Pten-Rictor group versus Pten alone. It is simply not feasible to perform EEG monitoring on this many animals. Second, even if we did do enough experiments to detect a reduction in seizure frequency, it is clear that neither Raptor nor Rictor deletion provides the kind normalization in brain activity that we seek in a targeted treatment. Both Pten-Raptor and Pten-Rictor animals still have very frequent spike-wave events (Fig. 3D) and highly abnormal interictal EEGs (Fig. 4), suggesting that even if generalized seizures were reduced, epileptic brain activity persists. This is in contrast to the triple KO animals, which have no increase in SWD above control level and very normal interictal EEG.

2) The authors describe that they inactivated mTORC1 and mTORC2 in a new model of somatic Pten loss-of-function in the cortex. This is slightly misleading since Cre expression was found both in the cortex and the underlying hippocampus, as shown in Figure 1. Throughout the manuscript, they provide supporting histological data from the cortex. However, since Pten loss-of-function in the hippocampus can lead to hippocampal overgrowth and seizures, data showing the impact of the genetic rescue in the hippocampus would further strengthen the claim that neither mTORC1 nor mTORC2 inactivation prevents seizures.

Thank you for pointing out this issue. Cre expression was observed in both the cortex and the dorsal hippocampus in most animals, and we agree that differences in cortical versus hippocampal mTOR signaling could have differential contributions to epilepsy. We focused our studies on the cortex because spike-and-wave discharge, the most frequent and fully penetrant EEG phenotype in our model, is associated with cortical dysfunction. We had also performed a preliminary analysis of the hippocampal Cre expression, which suggested that Cre expression in the hippocampus did not affect generalized seizure occurrence. We plan to include data on Cre expression in the hippocampus in the revised version of the manuscript.

3) Some of the methods for the EEG seizure analysis are unclear. The authors describe that for control and Pten-Raptor-Rictor LOF animals, all 10-second epochs in which signal amplitude exceeded 400 μV at two time-points at least 1 second apart were manually reviewed, whereas, for the Pten LOF, Pten-Raptor LOF, and Pten-Rictor LOF animals, at least 100 of the highest-amplitude traces were manually reviewed. Does this mean that not all flagged epochs were reviewed? This could potentially lead to missed seizures.

We reviewed at least 48 hours of data from each animal manually. All seizures that were identified during manual review were also identified by the automated detection program. It is possible but unlikely that there are missed seizures in the remaining data.

4) Additionally, the inclusion of how many consecutive hours were recorded among the ~150 hours of recording per animal would help readers with the interpretation of the data.

Thank you for this recommendation. We plan to include a table with more information about the EEG recordings in the revised version of the manuscript. The number of consecutive hours recorded varied because the wireless system depends on battery life, which was inconsistent, but each animal was recorded for at least 48 consecutive hours on at least two occasions.

5) Finally, it is surprising that mTORC2 inactivation completely rescued cortical thickness since such pathological phenotypes are thought to be conserved down the mTORC1 pathway. Additional comments on these findings in the Discussion would be interesting and useful to the readers.

Soma size was increased 120% by Pten inactivation and partially normalized to a 60% increase from Controls by mTORC2 inactivation (Fig. 2C). We and others have previously shown that mTORC2 inactivation in neurons reduces both soma size and dendritic outgrowth (PMIDs: 36526374, 32125271, 23569215). Thus, we do not find it completely surprising that mTORC2 inactivation reduces the cortical thickness increase caused by Pten loss. There may still be a slight increase in cortical thickness in Pten-Rictor animals, but it is statistically indistinguishable from Controls. We will elaborate on this in our revised submission.

Reviewer #2 (Public Review):

Summary:

The study by Cullen et al presents intriguing data regarding the contribution of mTOR complex 1 (mTORC1) versus mTORC2 or both in Pten-null-induced macrocephaly and epileptiform activity. The role of mTORC2 in mTORopathies, and in particular Pten loss-off-function (LOF)-induced pathology and seizures, is understudied and controversial. In addition, recent data provided evidence against the role of mTORC1 in PtenLOF-induced seizures. To address these controversies and the contribution of these mTOR complexes in PtenLOF-induced pathology and seizures, the authors injected a AAV9-Cre into the cortex of conditional single, double, and triple transgenic mice at postnatal day 0 to remove Pten, Pten+Raptor or Rictor, and Pten+raptor+rictor. Raptor and Rictor are essentially binding partners of mTORC1 and mTORC2, respectively. One major finding is that despite preventing mild macrocephaly and increased cell size, Raptor knockout (KO, decreased mTORC1 activity) did not prevent the occurrence of seizures and the rate of SWD event, and aggravated seizure duration. Similarly, Rictor KO (decreased mTORC2 activity) partially prevented mild macrocephaly and increased cell size but did not prevent the occurrence of seizures and did not affect seizure duration. However, Rictor KO reduced the rate of SWD events. Finally, the pathology and seizure/SWD activity were fully prevented in the double KO. These data suggest the contribution of both increased mTORC1 and mTORC2 in the pathology and epileptic activity of Pten LOF mice, emphasizing the importance of blocking both complexes for seizure treatment. Whether these data apply to other mTORopathies due to Tsc1, Tsc2, mTOR, AKT or other gene variants remains to be examined.

Strengths:

The strengths are as follows: 1) they address an important and controversial question that has clinical application, 2) the study uses a reliable and relatively easy method to KO specific genes in cortical neurons, based on AAV9 injections in pups. 2) they perform careful video-EEG analyses correlated with some aspects of cellular pathology.

Weaknesses:

The study has nevertheless a few weaknesses: 1) the conclusions are perhaps a bit overstated. The data do not show that increased mTORC1 or mTORC2 are sufficient to cause epilepsy. However the data clearly show that both increased mTORC1 and mTORC2 activity contribute to the pathology and seizure activity and as such are necessary for seizures to occur.

We agree that our findings do not directly show that either mTORC1 or mTORC2 hyperactivity are sufficient to cause seizures, as we do not individually hyperactivate each complex in the absence of any other manipulation. We interpreted our findings in this model as suggesting that either is sufficient based on the result that there is no epileptic activity when both are inactivated, and thus assume that there is not a third, mTOR-independent, mechanism that is contributing to epilepsy in Pten, Pten-Raptor, and Pten-Rictor animals. In addition, the histological data show that Raptor and Rictor loss each normalize activity through mTORC1 and mTORC2 respectively, suggesting that one in the absence of the other is sufficient. However, we agree that there could be other potential mTOR-independent pathways downstream of Pten loss that contribute to epilepsy. We will revise the manuscript to reflect this.

2) the data related to the EEG would benefit from having more mice. Adding more mice would have helped determine whether there was a decrease in seizure activity with the Rictor or Raptor KO.

Please see response to Reviewer 1’s first Weakness.

3) it would have been interesting to examine the impact of mTORC2 and mTORC1 overexpression related to point #1 above.

We are not sure that overexpression of individual components of mTORC1 or mTORC2 would result in their hyperactivation or lead to increases in downstream signaling. We believe that cleanly and directly hyperactivating mTORC1 or especially mTORC2 in vivo without affecting the other complex or other potential interacting pathways is a difficult task. Previous studies have used mTOR gain-of-function mutations as a means to selectively activate mTORC1 or pharmacological agents to selectively activate mTORC2, but it not clear to us that the former does not affect mTORC2 activity as well, or that the latter achieves activation of mTORC2 targets other than p-Akt 473, or that it is truly selective. We agree that these would be key experiments to further test the sufficiency hypothesis, but that the amount of work that would be required to perform them is more that what we can do in this Short Report.

Reviewer #3 (Public Review):

Summary: This study investigated the role of mTORC1 and 2 in a mouse model of developmental epilepsy which simulates epilepsy in cortical malformations. Given activation of genes such as PTEN activates TORC1, and this is considered to be excessive in cortical malformations, the authors asked whether inactivating mTORC1 and 2 would ameliorate the seizures and malformation in the mouse model. The work is highly significant because a new mouse model is used where Raptor and Rictor, which regulate mTORC1 and 2 respectively, were inactivated in one hemisphere of the cortex. The work is also significant because the deletion of both Raptor and Rictor improved the epilepsy and malformation. In the mouse model, the seizures were generalized or there were spike-wave discharges (SWD). They also examined the interictal EEG. The malformation was manifested by increased cortical thickness and soma size.

Strengths: The presentation and writing are strong. The quality of data is strong. The data support the conclusions for the most part. The results are significant: Generalized seizures and SWDs were reduced when both Torc1 and 2 were inactivated but not when one was inactivated.

Weaknesses: One of the limitations is that it is not clear whether the area of cortex where Raptor or Rictor were affected was the same in each animal.

We plan to include data further describing the location of knockout in each animal (in both the hippocampus and cortex) in the revised version of the paper. Initial analyses indicated that the affected area did not differ between groups.

Also, it is not clear which cortical cells were measured for soma size.

In the Methods it says “Soma size was measured by dividing Nissl stain images into a 10 mm2 grid. The somas of all GFP-expressing cells fully within three randomly selected grid squares in Layer II/III were manually traced.” Earlier under “Histology and imaging” it says “Three sections per animal at approximately Bregma -1.6, -2,1, and -2.6 were used.”

Another limitation is that the hippocampus was affected as well as the cortex. One does not know the role of cortex vs. hippocampus. Any discussion about that would be good to add.

See response to Reviewer 1’s second Weakness.

It would also be useful to know if Raptor and Rictor are in glia, blood vessels, etc.

Raptor and Rictor are thought to be ubiquitously active in mammalian cells including glia and endothelial cells. Previous studies have shown that mTOR manipulation can affect astrocyte function and blood vessel organization, however, our study induced gene knockout using an AAV that expressed Cre under control of the hSyn promoter, which has previously been shown to be selective for neurons. Manual assessment of Cre expression compared with DAPI, NeuN, and GFAP stains suggested that only neurons were affected.

Author Response

Reviewer #1 (Public Review):

The manuscript investigates how humans store temporal sequences of tones in working memory. The authors mainly focus on a theory named "Language of thought" (LoT). Here the structure of a stimulus sequence can be stored in a tree structure that integrates the dependencies of a stimulus stored in working memory. To investigate the LoT hypothesis, participants listened to multiple stimulus sequences that varied in complexity (e.g., alternating tones vs. nearly random sequence). Simultaneously, the authors collected fMRI or MEG data to investigate the neuronal correlates of LoT complexity in working memory. Critical analysis was based on a deviant tone that violated the stored sequence structure. Deviant detection behavior and a bracketing task allowed a behavioral analysis.

Results showed accurate bracketing and fast/correct responses when LoT complexity is low. fMRI data showed that LoT complexity correlated with the activation of 14 clusters. MEG data showed that LoT complexity correlated mainly with activation from 100-200 ms after stimulus onset. These and other analyses presented in the manuscript lead the authors to conclude that such tone sequences are represented in human memory using LoT in contrast to alternative representations that rely on distinct memory slot representations.

Strengths

The study provides a concise and easily accessible introduction. The task and stimuli are well described and allow a good understanding of what participants experience while their brain activation is recorded. Results are extensive as they include multiple behavioral investigations and brain activation data from two different measurement modalities. The presentation of the behavioral results is intuitive. The analysis provided a direct comparison of the LoT with an alternative model based on estimating a transition-probability measure of surprise.

For the fMRI data, the whole brain analysis was accompanied by detailed region of interest analyses, including time course analysis, for the activation clusters correlated with LoT complexity. In addition, the activation clusters have been set in relation (overlap and region of interest analyses) to a math and a language localizer. For the MEG data, the authors investigated the LoT complexity effect based on linear regression, including an analysis that also included transitional probabilities and multivariate decoding analysis. The discussion of the results focused on comparing the activation patterns of the task with the localizer tasks. Overall, the authors have provided considerable new data in multiple modalities on a well-designed experiment investigating how humans represent sequences in auditory working memory.

Weaknesses

The primary issue of the manuscript is the missing formal description of the LoT model and alternatives, inconsistencies in the model comparisons, and no clear argumentation that would allow the reader to understand the selection of the alternative model. Similar to a recent paper by similar authors (Planton et al., 2021 PLOS Computational Biology), an explicit model comparison analysis would allow a much stronger conclusion. Also, these analyses would provide a more extensive evidence base for the favored LoT model. Needed would be a clear argumentation for why the transitional probabilities were identified as the most optimal alternative model for a critical test. A clear description of the models (e.g., how many free parameters) and a description of the simulation procedure (e.g., are they trained, etc.) Here it would be strongly advised to provide the scripts that allow others to reproduce the simulations.

We thank the reviewer for the requests and critiques. Although this paper follows upon our extensive prior behavioral work (Planton et al.), we agree that it should stand alone and that therefore the models need to be described more fully. We have now added a formal description of the LoT in the subsection The Language of Thought for binary sequences in the Results section and have added a formal and verbal description of the selected sequences in Figure 1-figure supplement 1. Furthermore, we added a model comparison similar to the one done in (Planton et al., 2021 PLOS Computational Biology). This analysis is now included in Figure 2 and in the Behavioral data subsection of the Results section. It replicates previous behavioral results obtained in Planton et al., 2021 PLOS Computational Biology, namely that complexity, as measured by minimal description length in the binary version of the “language of geometry” was the best predictor of participants’ behaviour.

Interestingly, we found that the model that considered both complexity and surprise had even lower AIC suggesting that statistical learning is simultaneously occurring in the brain (Brain signatures of a multiscale process of sequence learning in humans, M Maheu, S Dehaene, F Meyniel - eLife, 2019). In this respect, we do not consider surprise from transition probabilities as an alternative model but rather as a mechanism that is occurring in parallel to sequence compression. The main goal of this work was to determine how sequence processing was affected by sequence structure, captured by the language of thought. In this line, we didn't select the tested sequences in order to investigate statistical learning but, instead, chose them with similar global statistical properties.

The MEG experiment provided us with the opportunity to separate temporally the contributions of statistical mechanisms from the ones of sequence compression according to the language of thought. Indeed, contrary to the fMRI experiment, we could model at the item level the statistical properties of individual sounds. We report the results when accounting jointly for statistical processing and LoT-complexity in Supplementary materials.

The different models considered in previous work didn’t need to be trained. The sequence complexity they provided could be analytically computed based on sequence minimal description length.

Furthermore, the manuscript needs a clear motivation for the type of sequences and some methodological decisions. Central here is the quadratic trend selectively used for the fMRI analysis but not for the other datasets.

To design the MEG, we had to decrease the number of sequences from 10 to 7. We selected them based on the LoT-complexity and the type of sequence information they spanned. As a consequence, the predictors for linear and quadratic complexity are very correlated (82%). Unfortunately, due to low SNR, this doesn’t allow to robustly account for the contributions of quadratic complexity in the MEG-recorded brain signals. Still, in response to the referee, we performed a linear regression as a function of quadratic complexity on the residuals of the regression as function of statistics and complexity that we report here. No significant clusters were found for habituation and standard trials but two were found (corresponding to the same topography) for deviant trials for late time-points.

In Author response image 1 regression coefficients for the quadratic complexity regressor regressed on the residuals of the surprise from transition probabilities and complexity. In Author response image 2, 2 significant clusters were found for the deviant sounds.

We also averaged the decoding scores from Figure7.A over the time-window obtained from the temporal cluster-based permutation test (see Author response image 2). The choice of complexity values didn’t allow any clear assessment of the contribution of the quadratic complexity term.

In summary, in the current design, we do not think that the number of tested sequences allows us to clearly conclude that no quadratic effect can be found for Habituation and Standard trials. We would need to re-design an experiment to test specifically the quadratic complexity contribution to brain signals in MEG.

Author response image 1.

Author response image 2.

Also, the description of the linear mixed models is missing (e.g., the random effect structure, e.g., see Bates, D., Kliegl, R., Vasishth, S., & Baayen, H. (2015). Parsimonious mixed models. arXiv preprint arXiv:1506.04967.). Moreover, sample sizes have not been justified by a power analysis.

The linear mixed model that is considered in this work is very simple, it only uses Subject as a random variable. This is now stated clearly in the corresponding part in the Experimental procedures section:

To test whether subject performance correlated with LoT complexity, we performed linear regressions on group-averaged data, as well linear mixed models including participant as the (only) random factor. The random effect structure of the mixed models was kept minimal, and did not include any random slopes, to avoid the convergence issues often encountered when attempting to fit more complex models.

Author Response

Reviewer #3 (Public Review):

Myelodysplastic syndrome (MDS) is a heterogenous, clonal hematopoietic stem cell disorder characterized by morphological dysplasia in one or more hematopoietic lineages, cytopenias (most frequently anemia), and ineffective hematopoiesis. In patients with MDS, transfusion therapy treatment causes clinical iron overload; however it has been unclear if treatment with iron chelation yields clinical benefits. In the present study, the authors use a transgenic mouse model of MDS, NUP98-HOXD13 (referred to here as "MDS mice") to investigate this area. Starting at 5 months of age (before MDS mice progress to acute leukemia), the authors administered DFP in the drinking water for 4 weeks, and compared parameters to untreated MDS mice and WT controls.

The authors first show that MDS mice exhibit systemic iron overload and macrocytic anemia that is improved by treatment with the iron chelator deferiprone (DFP). They then perform a detailed characterization the effects of DFP treatment on erythroid differentiation and various parameters related to iron transport and trafficking in MDS erythroblasts. Strengths of the work are the use of a well-characterized mouse model of MDS with appropriate animal group sizes and detailed analyses of systemic iron parameters and erythroid subpopulations. A remediable weakness is that in certain areas of the Results and Discussion, the authors overinterpret their findings by inferring causation when they have only shown a correlation. Additionally, when drawing conclusions based on changes in erythroblast mRNA expression levels between groups, the authors should consider that translation efficiency may be altered in MDS and that the NUP98 fusion protein itself, by acting as a chimeric transcription factor, may also impact gene expression profiles. Given that the application of chelators for treatment of MDS remains controversial, this work will be of interest to scientists focused on erythroid maturation and iron dysregulation in MDS, as well as clinicians caring for patients with this disorder.

Major Comments

1) The authors define the stages of erythroblast differentiation using the CD44-FSC method, which assumes that CD44 expression levels during the stages of erythroid differentiation are not altered by MDS itself. Are morphologically abnormal erythroblasts, such as bi-nucleate forms, captured in this analysis, and if so, are they classified in the appropriate subset? The percentage of erythroblasts in the bone marrow of MDS mice in this current study is lower than that reported by Suragani et al (Nat Med 2014), who employed a different strategy to define erythroid precursors. While representative erythroblast gating is presented as Supplemental Figure 17, it would be important to present representative gating from all 3 animal groups: WT, MDS, and MDS+DFP mice.

We appreciate this comment and have added representative gating for all 3 groups to Supplemental Figure 17 (new Figure 3 – figure supplement 6 in the revised manuscript).

2) Methods, "Statistical analysis." The authors state that all comparisons were done with 2-tailed student paired t test, which would not be appropriate for comparisons being made between independent animals groups (i.e. when groups are not "paired").

We appreciate this comment and have reanalyzed all revised mouse data using one-way ANOVA with multiple comparisons and Tukey post-test analyses when more than 2 groups were compared. This has been edited in the Methods section in the revised manuscript.

3) The Results (p.7) indicates that both sexes showed similar responses to DFP; however, the figure legends do not indicate sex. Given that systemic iron metabolism in mice shows sex-related differences, sex should be specified.

We appreciate this comment and present here the gender-specific data for the reviewers’ evaluation (Author respone image 1). Similarly elevated transferrin saturation (a) (n = 3-4 male mice/group and n = 4-6 female mice/group) and hemoglobin (b) (n = 4-6 male mice/group and n = 4-9 female mice/group) are observed in male and female DFP-treated MDS mice. (c) Bone marrow erythroblasts are decreased to a greater degree in male relative to female DFP-treated MDS mice (n = 4-7 male mice/group and n = 8-9 female mice/group). We have added the data on gender-specific measures to new Figure 1 - figure supplement 3, Figure 2 – figure supplement 1, and Figure 3 – figure supplement 1 in the revised manuscript.

Author respone image 1.

Author Response

Reviewer #1 (Public Review):

Erbacher and colleagues provide further evidence for the function of epithelial cells as major contributors to the transduction of sensory stimuli. This technically advanced imaging study of human skin advances support for the anatomical and functional association of nerve fibers and skin keratinocytes. With combined high-resolution imaging and immunolabeling, the authors also advance the idea that gap junctions are at least one means by which direct neurochemical (e.g., ATP) communication from stimulated keratinocytes to nerve fibers can be achieved.

A major strength of the study is the combined use of super-resolution array tomography (srAT), expansion microscopy, structured illumination microscopy and immunolabeling to analyze human skin in situ as well as co-cultures of human neurons and keratinocytes. High resolution static and video imaging of skin clearly supports the ensheathment by keratinocytes of nerve fiber projections as they traverse layers of the epidermis. Another strength of this study is the srAT imaging combined with connexin Cx43 immunolabeling that focus on sites of nerve fiber-keratinocyte contact zones. Imaging of Cx43+ plaques support these sites as regions of direct epithelial-neural contact and as such, of communication.

Although imaging data support Cx43+/connexin plaques and neural ensheathment as regions of direct epithelial-neural communication, e.g., via keratinocyte release of ATP, this relationship remains correlative and lacking in quantification.

The conclusion of this paper regarding the anatomical relationship between nerves and keratinocytes is well supported. Data also support the proposal of connexin plaques as sites of communication, although analyses that validate this relationship, using experimental models and in human samples, remain for future studies.

Please note, comments referring to specific pages within the revised manuscript always refer to the tracked-word file version.

Reviewer #2 (Public Review):

Erbacher et al. have used new techniques to explore the neuro-cutaneous structures of human epidermis, which is a valuable goal given the lack of in-depth studies in human skin. Human skin is less studied than rodent skin because it presents challenges in obtaining samples and finding excellent immunohistological labels. They have employed expansion microscopy and super resolution array tomography for histological studies and have developed a human keratinocyte and human iPSC-derived sensory neuron co-culture. The authors have used these techniques to investigate the relation of intraepidermal nerve fibers (IENF) and keratinocytes, as well as to probe the localization of connexin 43. The data offer some anatomical insights, but as is does not add to our understanding of keratinocyte-neuron coupling.

Strengths:

This paper is applying newer techniques to probe structure in human skin and establishes some useful immunohistochemical labels to do this, which sets up a foundation that will be valuable for future studies. The observation that IENF sometimes tunnel through keratinocytes is interesting, and the manuscript does show that Cx43 hemichannels are localized near IENF. Their data definitely represents a technical achievement, as these studies are challenging.

Weaknesses:

Throughout the paper, the authors imply that they make discoveries that shed light on neuro-cutaneous interactions, but the data in this manuscript do not offer any functional insight into connections between IENF and keratinocytes. For example, the final figure legend indicates they have found evidence of "electrical and chemical synapse-like contacts to nerve fibers" (Figure 9), but no such evidence was shown. Only a single neuron vesicular marker (synaptophysin) was shown to localize to neurons in culture, as expected. They also "...propose a crucial role of nerve fiber ensheathment and Cx43-based keratinocyte-fiber contacts in neuropathic pain and small fiber pathology." but do not show any data regarding the contribution of their anatomical findings to sensory function.

We recognize that our anatomical findings do not provide a complete picture of neuro-cutaneous interactions. Related findings on functional level, namely activation of nerve fibers after keratinocyte stimulation were previously reported (Klusch et al., 2013; Mandadi et al., 2009; Sondersorg et al., 2014). However, these studies otherwise lack morphological and molecular grounding and human biomaterial/cells, which we aimed to decipher in our study. We agree that functional and anatomical findings need to be connected in the future. We rephrased and attenuated our conclusions on Cx43 contacts in the context of IENF-keratinocyte interaction.

Their data do show that IENF are anatomically closely apposed to keratinocytes, but this is inevitable given their location in the epidermis. The expression of Cx43 in human epidermis is also known (PMID: 7518858) and localizing Cx43 plaques near IENF does not add to current knowledge, as wide expression in keratinocytes naturally positions them near the embedded IENF. There is no indication whether IENF also expresses Cx43 to form gap junctions. Moreover, due to the lack of quantification, it is not clear whether Cx43 labeling is enriched at IENF sites as compared to other areas on the keratinocytes.

We appreciate previous work on Cx43 and have integrated respective findings in the revised Introduction of our manuscript (see page 3-4):

“Connexin 43 (Cx43) pores are well established as a major signaling route for keratinocyte-keratinocyte communication (Tsutsumi et al., 2009) and potentially transduce external stimuli likewise towards afferents.”

As the Reviewer highlighted, Cx43 is widely clustered between keratinocytes and serves as an intercellular signaling route. Similar to keratinocyte-keratinocyte contacts, gap junctions (homomeric/heteromeric) or hemichannels towards IENF are possible. We aimed to quantify Cx43 contacts in healthy control and small fiber neuropathy patient-derived skin sections, since alterations in these contacts would affirm their biological relevance. We have generated pilot data for relative quantification of Cx43 contacts in skin samples of healthy controls (n = 5) and patients with small fiber neuropathy (n = 4). We have added respective passages in the Methods (see page 16-18), Results (see page 31-33), and Discussion (see page 41) sections of our revised manuscript. Please also see Figure 5.

The authors' implication that their anatomical data offers insight into neuro-cutaneous functional coupling is a leap that is evident throughout the manuscript.

We have attenuated our tone throughout the manuscript e.g. in:

Abstract (page 2):

“Unraveling human intraepidermal nerve fiber ensheathment and potential interaction sites advances research at the neuro-cutaneous unit.”

Discussion (page 42):

”Our observation of Cx43 plaques along the course of IENF in native skin and a human co-culture model substantiates a morphological basis and suggests keratinocyte hemichannels or gap junctions as one potential signaling pathway towards IENF.”

Conclusion (page 44):

“Epidermal keratinocytes show an astonishing set of interactions with sensory IENF including ensheathment and potential electrical and chemical synapse-like contacts to nerve fibers which may have substantial implications for the pathophysiological understanding of neuropathic pain and neuropathies.”

References

Jiang, N., Rasmussen, J.P., Clanton, J.A., Rosenberg, M.F., Luedke, K.P., Cronan, M.R., Parker, E.D., Kim, H.-J., Vaughan, J.C., Sagasti, A., 2019. A conserved morphogenetic mechanism for epidermal ensheathment of nociceptive sensory neurites. eLife 8, e42455.

Klein, T., Gruener, J., Breyer, M., Schlegel, J., Schottmann, N.M., Hofmann, L., Gauss, K., Mease, R., Erbacher, C., Finke, L., 2023. Small fibre neuropathy in Fabry disease: a human-derived neuronal in vitro disease model. bioRxiv, 2023.2008. 2009.552621.

Klusch, A., Ponce, L., Gorzelanny, C., Schafer, I., Schneider, S.W., Ringkamp, M., Holloschi, A., Schmelz, M., Hafner, M., Petersen, M., 2013. Coculture model of sensory neurites and keratinocytes to investigate functional interaction: chemical stimulation and atomic force microscope-transmitted mechanical stimulation combined with live-cell imaging. J. Invest. Dermatol. 133, 1387-1390.

Kruger, L., Perl, E., Sedivec, M., 1981. Fine structure of myelinated mechanical nociceptor endings in cat hairy skin. J. Comp. Neurol. 198, 137-154.

Mandadi, S., Sokabe, T., Shibasaki, K., Katanosaka, K., Mizuno, A., Moqrich, A., Patapoutian, A., Fukumi-Tominaga, T., Mizumura, K., Tominaga, M., 2009. TRPV3 in keratinocytes transmits temperature information to sensory neurons via ATP. Pflugers. Arch. 458, 1093-1102.

Sondersorg, A.C., Busse, D., Kyereme, J., Rothermel, M., Neufang, G., Gisselmann, G., Hatt, H., Conrad, H., 2014. Chemosensory information processing between keratinocytes and trigeminal neurons. J. Biol. Chem. 289, 17529-17540.

Talagas, M., Lebonvallet, N., Leschiera, R., Sinquin, G., Elies, P., Haftek, M., Pennec, J.P., Ressnikoff, D., La Padula, V., Le Garrec, R., 2020. Keratinocytes Communicate with Sensory Neurons via Synaptic‐like Contacts. Ann. Neurol. 88, 1205-1219.

Tavares-Ferreira, D., Shiers, S., Ray, P.R., Wangzhou, A., Jeevakumar, V., Sankaranarayanan, I., Cervantes, A.M., Reese, J.C., Chamessian, A., Copits, B.A., Dougherty, P.M., Gereau, R.W.t., Burton, M.D., Dussor, G., Price, T.J., 2022. Spatial transcriptomics of dorsal root ganglia identifies molecular signatures of human nociceptors. Sci. Transl. Med. 14, eabj8186.

Tenenbaum, C.M., Misra, M., Alizzi, R.A., Gavis, E.R., 2017. Enclosure of Dendrites by Epidermal Cells Restricts Branching and Permits Coordinated Development of Spatially Overlapping Sensory Neurons. Cell Rep. 20, 3043-3056.

Tobin, D.J., 2006. Biochemistry of human skin--our brain on the outside. Chem. Soc. Rev. 35, 52-67.

Author Response

Reviewer #1 (Public Review):

The authors provide compelling evidence that the activation of distinct populations of NTS neurons provides stronger decreases in eating/body weight when co-activated. Avoidance is not necessarily linked to the extent of the effects but seems to depend on specific neurons which when activated, not only reduce eating but also induce avoidance reactions. The results of this study provide strong data promoting multi-targeted approaches to reduce eating and body weight in obesity. Interestingly, none of the pathways identified is necessary for the weight-reducing effect of vertical sleeve gastrectomy. Future studies will hopefully shed light on the type of neurotransmitters released by these distinct populations of NTS neurons.

We thank the reviewer for these helpful and supportive comments.

Reviewer #2 (Public Review):

Prior results established that Lepr, Calcr, and Cck neurons are non-overlapping neuronal populations in the NTS that individually suppress food intake when activated. This paper examines the consequences of activating or inhibiting two or three of these populations simultaneously. Activating two or three populations inhibits food intake a body weight more than each individually. Activation of Lepr and/or Calcr neurons is not aversive based on the conditioned taste aversion test, whereas activating all three is aversive by this test, indicating that aversion due to Cck neurons activation is dominant. Vertical sleeve gastrectomy (VSG) causes weight loss, but inhibiting each of these neurons individual or all three of them does not prevent weight loss. Overall, this paper provides a solid set of results but does not provide mechanistic insight into any of the phenomena examined.

We have now added data demonstrating differences in the activation of FOS-IR in the downstream targets of our NTS neuron types, alone or in combination (new Figure 6). Our findings reveal that each population (NTSLepr, NTSCalcr, and NTSCck) activates an at least partially distinct set of neurons and that only NTSCck cells activate the known aversive PBN CGRP cells. These data suggest that the cumulative effects mediated by each of these NTS populations stem in part from their ability to activate at least partly distinct populations of downstream neurons.

Unfortunately, it is outside of the scope of this manuscript (and the realm of the currently possible) to define the neurons that mediate the response to VSG, and we have now reorganized the manuscript to clarify that our VSG data (along with the feeding-induced FOS-IR data) serve to reveal that additional populations of neurons (other than NTSLCK cells) must contribute to the restraint of feeding.

Author Response

Reviewer #1 (Public Review):

I believe it is important for the authors to clarify how the time frames to test for group differences of ERP components were defined. Were the components defined based on a grand average across lesions and controls or based or on the maximum range for both groups? As the paper is written currently this is unclear to me. It is also unclear why the group comparisons between controls and lateral PFC group were based only on the control group. To ensure no inadvertent biases towards the larger control group were introduced and ensure the studies findings were reliable, it would be appreciated if the authors could clarify this.

We thank the reviewer for the helpful comment. We recognize the need for a clearer definition of time frames for testing group differences in the ERP components and apologize for any ambiguity in the previous version of the manuscript.

Regarding the time frames to test for group differences of ERP components for the OFC and control groups, they were determined based on the combined maximum range for both groups. The time range for each group and each ERP component was derived from the statistical analysis of the condition contrasts run for each group. For instance, for the Local Deviance MMN, the condition contrast (i.e., Control condition versus Local Deviance condition) for the CTR group revealed a MMN component from 67 to128 ms, while the same condition contrast for the OFC group revealed a MMN from 73 to131 ms. The time frame used for the group comparison on the MMN time window was 50 to 150 ms to capture component activity for both groups. In the same way, for the Local Deviance P3a, the condition contrast (i.e., Control condition versus Local Deviance condition) for the CTR group revealed a P3a component ranging from 141 to 313 ms, while the same condition contrast for the OFC group revealed a P3a from 145 to 344 ms. The time frame used for the group comparison on the P3a time window encompassed 140 to 350 ms to capture component activity for both groups.

In the “Results” section of the main manuscript, together with the results from the cluster-based permutation independent samples t-tests, we provide the time frames in which the latter were computed for each ERP component. These segments have been highlighted with yellow in the revised manuscript. Moreover, in the section “Materials and methods - Statistical analysis of event-related potentials” of the main manuscript [page 37, paragraph 2], we provide a revised description of how the time frames for group differences of ERPs were defined. The revised description states: “In a second step, to check for differences in the ERPs between the two main study groups, we ran the same cluster-based permutation approach contrasting each of the four conditions of interest between the two groups using independent samples t-tests. The cluster-based permutation independent samples t-tests were computed in the latency range of each component, which was determined based on the maximum range for both groups combined. The latency range for each group and component was based on the time frames derived from the statistical analysis of task condition contrasts.”

Regarding the comparisons between the lateral PFC and control groups, they were not based solely on the control group condition contrast. This was miswritten. The approach to define time frames to test for ERP differences between the CTR and the lateral PFC group was the same as the one used to test differences between CTR and OFC groups. We apologize for any confusion this may have caused. We have revised the erroneous statements in the Supplementary File 1 [highlighted text, page 9-10].

An additional potential weakness of the paper, and one that if addressed would increase our confidence that neural differences arise because of the specific lesion effect, is the lack of evidence that the lesion and control groups do not differ on measures that could inadvertently bias the neural data. For example, while the groups did not differ on demographics and a range of broad cognitive functions, were there any differences between the number or distribution of bad/noisy channels in each subject between the two groups? Were there differences in the number of blinks/saccades or distribution of blinks or saccades across the conditions in each subject across the two groups.

We thank the reviewer for this suggestion. We have completed a number of measurements and tests to ensure that the OFC lesion group and the control group did not differ on measures that could affect the neural data. First, we computed the number of bad/noisy channels for each subject and group, and found that the two groups did not differ significantly. Second, we computed the number of trials remaining after removing the noisy segments across conditions for each subject and group, and found no significant differences between the groups. Third, the number of blinks/saccades across conditions for each subject and group showed no significant group differences. Altogether, the results indicate that the neural differences observed in our study arose because of the specific lesion effect.

These additional EEG measures and the statistical test results are included in the Supplementary File 1 [page 15-16] and Supplementary File 1g. We have also added text in the section “Materials and methods - EEG acquisition and pre-processing” of the main manuscript [page 35, paragraph 3], which states: “To ensure the validity of the neural data analysis, potential sources of bias were assessed between the healthy control participants and the OFC lesion patients. Specifically, no significant differences were observed between the two groups in terms of the number of noisy channels, the number of noisy trials, or the number of blinks across the task blocks and the experimental conditions.”

On a similar note, while I appreciate this is a well established task could the authors clarify whether task difficulty is balanced across the different conditions? The authors appear to have used the counting task to ensure equal attention is paid across conditions although presumably the blocks differ in the number of deviant tones and therefore in the task difficulty. Typically, tasks to maintain attention are orthogonal to the main task and equally challenging across the different blocks. Is there a way to reassure readers that this has not affected the neural results?

Thank you for pointing this out. Indeed, the experimental blocks differ in the number of deviant tones and therefore in the task difficulty. Thus, it is a very good suggestion to look for behavioral performance differences across the different blocks. In the present set of analyses, two block types were used: Regular (xX) and Irregular (xY). In regular blocks, where the repeated sequence is xxxxx, participants were required to count the rare/uncommon sequences, i.e., xxxxy and xxxxo. In irregular blocks, where the repeated sequence is xxxxy, participants were required to count the rare/uncommon sequences, i.e., xxxxx and xxxxo. We have now updated the behavioral analysis. First, by excluding the omission block’s counting performance, and second, by calculating the counting performance separately for the two blocks. The new behavioral analysis revealed that participants from both groups performed better in the irregular block compared to the regular block. However, there was no statistically significant difference between the counting performances of the two groups.

The new results are reported on page 5 of the main manuscript, section “Results - Behavioral performance”, paragraph 1: “Participants from both groups performed the task properly with an average error rate of 9.54% (SD 8.97) for the healthy control participants (CTR) and 10.55% (SD 6.18) for the OFC lesion patients (OFC). There was no statistically significant difference between the counting performance of the two groups [F(24) = 0.11, P = 0.75]. Participants from both groups performed better in the irregular block (CTR: 8.39 ± 8.24%; OFC: 7.50 ± 7.34%) compared to the regular block (CTR: 10.69 ± 11.36%; OFC: 13.60 ± 10.97%) [F(24) = 3.55, P = 0.07]. There was no block X group interaction effect [F(24) = 0.73, P = 0.40].”

As with many patient lesion studies, while the comparison directly against the healthy age matched controls is critical it would have strengthened the authors claims if they could show differences between the brain damaged control group. Given the previous literature that also links lateral PFC with prediction error detection, I understand that this region is potentially not the clearest brain damaged control group and therefore another lesion group might have strengthened claims of specificity. Furthermore, the authors do not offer an explanation for why no differences between lateral PFC and control groups were found when others have previously reported them. Identifying those differences would strengthen our understanding of the involvement of different structures in this task/function.

We thank the reviewer for raising this crucial issue. We recognize the importance of addressing the lack of neurophysiological differences between the lateral PFC lesion group and the control group. First, it is important to clarify that the lateral PFC lesion control group was initially included not as a control for specific lateral PFC lesions but rather a broader control group to account for potentially general effects of frontal brain damage. However, considering that previous studies have implicated specific areas of the lateral PFC (e.g., inferior frontal gyrus; IFG) in predictive processing, we also think that a more thorough justification of these null findings is needed.

Intracranial EEG studies examining local and global level prediction error detection pointed to the role of inferior frontal gyrus (IFG) as a frontal source supporting top-down predictions in MMN generation (Dürschmid et al., 2016; Nourski et al., 2018; Phillips et al., 2016; Rosburg et al., 2005). However, other intracranial studies reported unclear (Bekinschtein et al., 2009) or weak (Dürschmid et al., 2016) frontal MMN effects. El Karoui et al. (2015) observed late ERP responses in the lateral PFC related to global deviants but no MMN to local deviants, and it was not clear where in the PFC these responses occurred, not showing responses in the IFG. Additionally, studies employing dynamic causal modeling of MMN consistently modeled frontal sources in the IFG region (Garrido et al., 2008; Garrido et al., 2009; Phillips et al., 2015). A review by Deouell (2007) highlighted the potential contributions of both IFG and middle frontal gyrus to MMN generation, suggesting that the specific source might vary depending on characteristics of the deviant stimuli, such as pitch or duration.

In Alho et al. (1994) lesion study, diminished MMN to local-level deviants was found after lesion to the lateral PFC, with the lesion cohort exhibiting a hemisphere ratio of 7/3 for left and right hemispheres, respectively, which is different from our cohort's ratio of 4/6. Furthermore, all individuals in that study had infarcts in the middle cerebral artery, resulting in a more uniform lesion location compared to our cohort. Notably, the lesions observed in our lateral PFC group appeared to be situated in more superior brain regions and towards the MFG compared to the predominantly reported involvement of the IFG in previous studies. Another factor that might contribute to the lack of significant effects is the heterogeneity of the lesions in our lateral PFC group (see Supplementary Figures 2, 3 and 4). Especially for the left hemisphere cohort, the individual lesions did not share a consistent anatomical location. The right hemisphere cohort had a greater lesion overlap, but overall, the lesions were not centered in the IFG area with highest overlap being in the MFG area. This distinction in lesion location might contribute to the absence of effects observed in our study.

Regarding the global effect, often reflected in the P300 component, it appears that the neural sources responsible for processing global deviance exhibit a more distributed pattern. This means that the brain regions involved in detecting and processing global deviations may not be as localized or concentrated as those implicated in local deviance processing. Given that the neural mechanisms underlying global deviance detection and processing are likely to involve a wider network of brain regions, they may be less susceptible to disruptions caused by focal lesions in the lateral PFC.

In response to your comment, we have expanded the “Discussion” to address this point by adding a new section titled “Lack of findings in the lateral PFC lesion group” [page 21]. In this section, we first present some of the findings implicating specific areas of the lateral PFC in the generation of MMN and in predictive processing, and then offer an account of the potential reasons behind the lack of neurophysiological differences between the lateral PFC and control groups.

Finally, while the authors have already cited widely across multiple fields, again speaking to the likely large impact the study will make, there does appear to be an unexplored conceptual link between the conclusions here that the OFC supports "the formation of predictions that define the current task by using context and temporal structure to allow old rules to be disregarded so that new ones can be rapidly acquired" and that lesions of the lateral portions of the OFC disrupt the assignment of credit or value to a stimuli that occurred temporally close to the outcome (Walton et al 2010, Noonan et al 2010, PNAS, Rudebeck et al 2017 Neuron, Noonan et al 2017, JON, Wittmann et al 2023 PlosB, note the wider imaging literature in line with this work Jocham et al 2014 Neuron and Wang et al bioRxiv). Without the OFC monkeys and humans appear to rely on an alternative, global learning mechanism that spreads the reinforcing properties of the outcome to stimuli that occurred further back in time. Could the authors speculate on how these two strains of evidence might converge? For example, does the OFC only assign credit in the event of a prediction error or does one mechanism subsume another?

We thank the reviewer for this comment regarding the unexplored conceptual link between our study’s conclusion, which suggests that the OFC facilitates the detection of prediction errors, and the findings of other research that delves into the OFC’s role in assignment of credit to stimuli. We find this comment very interesting and appreciate the opportunity to speculate on the potential functional convergence of these two processes within the OFC.

The OFC is a critical neural hub implicated in learning, decision-making, and adaptive behavior. The detection of prediction errors and the assignment of credit to stimuli are mechanisms linked with the OFC, which play an important role in all these functions (Noonan et al., 2012; Schultz & Dickinson, 2000; Sul et al., 2010; Tobler et al., 2006; Walton et al., 2010; Walton et al., 2011). Prediction errors involve recognizing discrepancies between expected and actual outcomes, which engages the OFC in rapidly updating stimulus valuations to align with newfound information (Holroyd & Coles, 2002; Kakade & Dayan, 2002). Signaling of errors provides a powerful mechanism whereby OFC facilitates adaptive learning and enables the brain to adjust its expectations based on novel experiences (Schultz, 2015; Seymour et al., 2004). Credit assignment, on the other hand, refers to properly identifying the causes of prediction errors. Without proper credit assignment, one might have intact error signaling mechanisms, but lose the ability to learn appropriately. This is especially true when multiple possible antecedents may be related to the error or when past choices have been unpredictable. In such situations, it is important to assign credit to the most recent choice and not get distracted by previous alternatives (Stalnaker et al., 2015).

These mechanisms within the OFC appear interrelated yet distinct. While prediction errors could trigger credit assignment, the OFC's ability to continually assess stimuli's values extends beyond instances of prediction errors. The OFC is involved in continuously evaluating and updating the values of stimuli based on ongoing experiences (Padoa-Schioppa & Assad, 2006; Tremblay & Schultz, 1999). This process enables the brain to learn from both unexpected outcomes and regular, predictable interactions with the environment. In situations where outcomes are not solely determined by prediction errors, the assignment of credit remains important. Complex decision-making involves considering a variety of factors beyond just prediction errors, such as contextual information and long-term consequences. Clarifying the convergence of these mechanisms within the OFC holds profound implications for understanding the intricacies of learning dynamics and the orchestration of adaptive responses to the environment.

While we recognize the value of this discussion, we believe it extends beyond the primary focus of our study. Consequently, we have made the decision not to incorporate it into the current manuscript.

One remaining weakness, which plagues all patient studies, is that of anatomical specificity. The authors have analysed what is, for the field, a large group of patients, and while the lesions appear to be relatively focused on the OFC the individuals vary in the degree to which different subregions within the OFC are damaged. This is increasingly important as evidence over the last 10 years has identified functional roles of these specific structures (Rushworth et al 2011, Neuron, Rudebeck et al 2017 Neuron). It would be important to ultimately know whether the detection of prediction errors was specific to a particular OFC subregion, a general mechanism across this area of cortex, or whether different subregions were more involved during different contexts or types of stimuli/contexts/tasks etc. Some comments on this would be appreciated.

The reviewer raised an important point here. It would have been interesting to explore this aspect. However, one challenge with focal lesion studies is to establish large patient cohorts. The group size of our study, which is relatively large compared to other studies of focal PFC lesions, does not allow us to perform any exploratory lesion-symptom mapping analyses. A larger patient sample will provide a stronger basis for drawing conclusions about the critical role of a particular OFC subregion to the detection of prediction errors and allow statistical approaches to lesion subclassification and brain-behavior analysis (e.g., voxel-based lesion-symptom mapping (Bates et al., 2003; Lorca-Puls et al., 2018)).

Considering the average percentage of damaged tissue in our study, the medial part of OFC or Brodmann area 11 is affected more by the lesion (approx. 33%), followed by the anterior-most region of the prefrontal cortex or Brodmann area 10 (approx. 25%), and the lateral portions of the OFC or Brodmann area 47 (approx. 12%). From our analysis, it is difficult to conclude whether the detection of prediction errors in our study was specific to a certain OFC area, or whether different subregions were involved more than others during different types of stimuli/contexts processing.

To provide a more balanced interpretation of our findings, we incorporated a section in the “Discussion”, titled “Limitations and future directions” [page 24-25], which delves into the limitations of our study and lesion studies generally with respect to anatomical specificity and the challenge to establish large patient cohorts.

Reviewer #2 (Public Review):

The current version of the manuscript is overall very long and verbose, for example, the introduction is 5 pages long and includes up to 102 references. In my view this is way too much. I suppose authors wish to be very detailed, but somehow they get an opposite effect, the main message of the introduction and aims get diluted.

We thank the reviewer for the feedback on our manuscript's length and content. This prompted us to carefully reconsider the balance between providing necessary context and ensuring the clarity of our main message. Our intention was to establish a strong foundation for our research by presenting relevant literature and setting the stage for our aims. In our revised manuscript, we have condensed the Introduction while retaining the key elements necessary to understand the context and motivations behind our research. Specifically, the current version of the “Introduction” is three pages long and includes 83 references.

I wonder if the presentation rate used, SOA; 150 is too fast and the stimuli too short 50 ms. Please prove a rationale for this.

We appreciate the reviewer's thoughtful consideration of the stimulus duration and presentation rate (SOA) used in our study. We understand the importance of providing a rationale for our choices to ensure the validity of our experimental design. The decision to use a SOA of 150 ms and stimuli of 50 ms duration was grounded in established practices and relevant literature in the field. Similar presentation rates and stimulus durations were employed in previous studies using similar auditory oddball paradigms, investigating rapid cognitive processes in combination with event-related potentials (ERPs). For instance, Bekinschtein et al. (2009) first introduced the task by using a SOA of 150 ms and stimulus duration of 50 ms, demonstrating that this combination is sensitive to detecting auditory deviations and eliciting early and late ERP components. Additionally, Wacongne et al. (2011), Chennu et al. (2013), Uhrig et al. (2014), and El Karoui et al. (2015) employed similar task designs with the same SOA and stimulus duration in combination with scalp EEG, fMRI and intracranial recordings, further supporting the validity of this approach. Other studies, employing the same paradigm, such as Chao et al. (2018) and Doricchi et al. (2021), used a SOA of 200 ms but kept the same stimulus duration of 50 ms.

One of the conditions is 'omissions', but results are not reported, so either authors do not mention this at all, or they report these data, which would be probably interesting.

We thank the reviewer for the nice reminder. The “omissions” condition is indeed an integral part of our study, and we acknowledge its potential significance. However, we have decided to publish the detailed analysis of the 'omissions' condition in a separate paper, because we think that such analysis and discussion would make the current paper quite dense and complicated. We apologize for any confusion that might arise from the absence of the 'omissions' results in this manuscript. On page 33 of the main manuscript, we state the reason for not including the “omissions” condition in the current analysis: “In the present set of analyses, the Omission blocks were not further examined, because such analysis and discussion would make the current paper overly dense and complicated.”

The Discussion is very long and in some aspect even too speculative. For example, in the conclusions authors claim that the OFC contributes to a top-down predictive process that modulates the deviance detection system in the primary auditory cortices and may be involved in connecting PEs at lower hierarchical areas with predictions at higher areas. I am not sure the current data support this. This would-be probably more appropriate if they could compare results from OFC and AC etc. so it is a more dynamic study.

We thank the reviewer for this observation. We have made revisions to shorten and refine the discussion, with a primary focus on presenting and interpreting the key results in a more concise and straightforward manner (See tracked changes in the revised manuscript).

However, the overall length of the Discussion has not been reduced significantly because we have introduced two additional sections within the Discussion (i.e., “Lack of findings in the lateral PFC lesion group” and “Limitations and future directions”) in response to reviewers’ request to address the lack of finding in the lateral PFC lesion group and certain limitations associated with the employed lesion method.

We also agree that the claim mentioned by the reviewer is overly too speculative and therefore revised the sentence as follows [page 38, “Conclusion”]: “We suggest that the OFC likely contributes to a top-down predictive process that modulates the deviance detection system in lower sensory areas.”

At the beginning of Discussion, the authors mention that overall, these findings provide novel information about the role of the OFC in detecting violation of auditory prediction at two levels of stimuli abstraction/time scale. I think this needs to be detailed more specifically rather than mention they provide novel results.

We understand the importance of providing readers with precise descriptions about the novelty of our study. Therefore, we have revised the statement to provide more detailed information about the novel contributions offered by our study. The revised text states as follows [“Discussion”, page 18,]: “These findings indicate that the OFC is causally involved in the detection of local and local + global auditory PEs, thus providing a novel perspective on the role of OFC in predictive processing.”

I am not sure I like to have a section as a general discussion within the discussion itself, probably this heading should be reformatted to be more specific to what is discussed.

As suggested by the reviewer, we reformatted the heading to “OFC and hierarchical predictive processing” [page 22-24] to better capture the essence of the content covered in this section of the “Discussion”. Here, we discuss the functional relevance of our EEG findings under the umbrella of the predictive coding framework and the potential role of OFC in predictive processes (See tracked changes in the revised manuscript).

Reviewer #3 (Public Review):

The central claim of the study is that hierarchical predictive processing is altered in OFC patients. However, OFC patients were able to identify global deviants as well as controls. Thus, hierarchical predictive processing itself seems to be unaltered, even though its neural correlates were different. This begs the question of what exactly the functional meaning of the EEG findings is. From the evidence presented this is difficult to determine for three reasons (See comments below).

We thank the reviewer for the detailed observations and valuable comments. The reviewer points out that hierarchical predictive processing is unaltered even though the neural correlates were altered, because OFC patients were able to identify global deviants as accurately as control participants. We respectfully disagree with the reviewer’s claim for two reasons: 1) The primary purpose of the behavioral data in this study was not to measure the participants’ deviant detection performance, but to confirm that they were paying attention to the global rule of each block. However, we agree that an effect of lesion on behavioral performance would strengthen the claim of altered high-level predictive processing. Your point highlights the importance of looking more carefully at our behavioral results. In a follow up study, which we are currently running, we explore the behavioral nuances of our task by measuring reaction times of correct deviant detections. 2) Earlier lesion studies reported typical performance on simple oddball tasks for patients with focal frontal lesions that did not significantly differ from control participants. However, despite normal task execution and neuropsychological profiles, patients with LPFC and OFC lesions present distinct neurophysiological evidence of alterations in novelty processing (Knight, 1984, 1997; Knight & Scabini, 1998; Løvstad et al., 2012; Yamaguchi & Knight, 1991).

Regarding the central claim of our study being that hierarchical predictive processing is altered in OFC patients, we have tried not to make strong claims about our results showing altered hierarchical predictive processing. For example, the conclusion of the abstract states: “the altered magnitudes and time courses of MMN/P3a responses after lesions to the OFC indicate that the neural correlates of detection of auditory regularity violation is impacted at two hierarchical levels of stimuli abstraction.” Thus, we do not claim that detection of regularity violation is directly impaired (e.g., OFC patients were able to identify global deviants as well as healthy controls) but that the neural correlates of deviants’ detection are altered, and therefore impaired.

Finally, we have gone through all the comments/reasons, which the reviewer believes are difficult to determine the functional meaning of our EEG findings, and addressed them one by one (see comments below). We hope that the revised manuscript has been improved accordingly and provides a more critical view on the extent to which the findings support hierarchical predictive coding.

It is possible that the shifts in scalp potentials are due to volume conduction differences linked to post-lesion changes in neural tissue and anatomy rather than differences in information processing per se.

We appreciate your comment regarding the potential influence of volume conduction differences on the observed shifts in scalp potentials in our study. We acknowledge that there are special challenges in interpreting ERP findings in brain lesion populations (Kutas et al., 2012; Rugg, 1995). To reliably interpret changes in the ERPs in lesion patients as reflecting impairments in certain cognitive processes, it is necessary to identify factors that might possibly affect the results and to apply the appropriate control measures. As noted by the reviewer, structural pathology, and the replacement of neural tissue by cerebrospinal fluid following tumor resection, likely causes inhomogeneities in the volume conduction of electrical activity and resulting changes in current flow patterns. Moreover, post-craniotomy skull defects can cause local inhomogeneities in the resistive properties of the skull (Løvstad & Cawley, 2011; Rugg, 1995). Both types of biophysical changes might alter the amplitude levels and/or topography (by altering the configuration of the generators) of surface-recorded ERPs (e.g., Swick (2005)). Consequently, caution is warranted when comparing the ERPs and their scalp distributions of intact and brain-lesioned groups. It is difficult to directly quantify the consequences of brain lesions on tissue conductivity. To conclude that ERP differences between patients and controls reflect functional abnormalities in particular cognitive processes, and not primarily nonspecific effects of structural brain damage, it is helpful to demonstrate that they are specific to certain ERP components/stages of information processing and task conditions. Changes confined to one or a subset of ERP components, that additionally may not manifest across all task conditions, can give some indication concerning the specificity of ERP changes (Kutas et al., 2012; Swaab, 1998). In our study, group differences pertaining to ERP amplitudes were limited to specific task conditions and not across all data. This condition-dependent pattern suggests that the observed shifts are related to the specific cognitive processes engaged during those task conditions rather than being a global artifact of volume conduction. If volume conduction was the main driver, we would expect these group differences to be more uniformly present across task conditions. Another piece of evidence against volume conduction effects is the scalp potentials’ latency differences between the two groups observed for the Local + Global deviance detection. Group differences in the latencies of ERPs, such as the MMN and P3a, cannot be attributed to volume conduction alone (Hämäläinen et al., 1993). These differences in the timing of neural responses strongly indicate genuine variations in cognitive processing.

To provide a more balanced interpretation of our findings, we have incorporated a section in the “Discussion” that delves into the limitations of our study and lesion studies generally with respect to volume conduction and amplitude changes, titled “Limitations and future directions” [page 24-25].

It is unclear from the analyses whether the P3a amplitude differences are true amplitude differences or a byproduct of latency differences. The reason is that the statistical method used (cluster based permutations) might yield significant effects when the latency of a component is shifted, even if peak amplitudes are the same. Complementary analyses on mean or peak amplitudes could resolve this issue.

We thank the reviewer for raising an important concern about the use of cluster-based permutation tests and their potential to yield significant effects when the latency of a component is shifted. We acknowledge this concern and recognize the need for complementary analyses to address this issue. To provide a clearer understanding of the nature of the observed ERP amplitude differences, we conducted complementary analyses on mean amplitudes of the MMN and P3a components on the midline sensors for the conditions where significant group differences were observed. For the MMN component elicited by the Local Deviance, we found group amplitude differences on the electrodes AFz (p = 0.021), Fz (p = 0.008), CPz (p = 0.015), and Pz (p < 0.001). Surprisingly, we also found amplitude differences for the P3a component elicited by the Local Deviance on the electrodes AFz (p < 0.001), Fz (p < 0.001), FCz (p < 0.001), and Cz (p = 0.002) that were not observed previously with the cluster-based permutation analysis. For the MMN component elicited by the Local+Global Deviance, our analysis showed group amplitude differences on the electrodes AFz (p = 0.007), FCz (p = 0.051), Cz (p = 0.004), CPz (p = 0.002), and Pz (p < 0.001). However, as the reviewer rightly pointed out, the group differences for the P3a elicited by the Local + Global Deviance seem to be a byproduct of latency differences, as we did not find amplitude differences on any of the midline electrodes. Overall, this complementary analysis shows that the OFC patients had an attenuated MMN/P3a to local level prediction violation, and an attenuated and delayed MMN followed by a delayed P3a to the combined local and global level prediction violation. The new analysis is added in the Supplementary File 1 [page 5-7] and Supplementary File 1c and 1d.

The MMN, P3a and P3b components are difficult to map to the hierarchical PC theory. Traditionally, the MMN is ascribed to lower level processing while P3a and P3b are ascribed to higher level processing. However, the picture is more complicated. For example, the current results show that the MMN is enhanced in local + global surprise while the P3a is elicited by local surprise. Furthermore, the P3a is classically interpreted as reflecting attention reorientation and the P3b as reflecting the conscious detection of task-relevant targets. How attention and conscious awareness fit in hierarchical PC is not entirely clear.

Indeed, the relationships between MMN, P3a and P3b components and the predictive coding (PC) framework can be intricate. However, numerous studies employed the PC theory to interpret these common electrophysiological signatures as prediction error (PE) signals (Garrido et al., 2007, 2009; Lieder et al., 2013) and dissociations between these ERPs supported that there are successive levels of predictive processing (Chennu et al., 2013; El Karoui et al., 2015; Wacongne et al., 2011).

In terms of hierarchical PC (Friston, 2005), the temporally constrained MMN has been traditionally linked with first-level predictive processing, known as the local effect of short-term stimulus deviance. PE signals at this level feed forward to a temporally extended, attention-dependent system that extracts longer-term patterns. PE signals at the higher level are usually indexed by the P300, identified as the global effect of longer-term stimulus deviance. The P300 reflects a more attention-driven process, emerging in response to novel or low-probability “target” stimuli that violate broader contextual expectations (Polich, 2007), such as those that form over multiple trials. Because the MMN, P3a and P3b also appear to exhibit varying degrees of sensitivity to preconscious and conscious perceptual predictions (Sculthorpe et al., 2009), they could serve as measures for examining the concept of a predictive neural hierarchy.

Indeed, the MMN has been viewed as sensitive to local violation and essentially blind to higher-order regularities. However, this is a simplified view. For example, Wacongne et al. (2011) showed that violating a low-level perceptual expectation triggers the MMN, violating contextual expectations triggers the higher-level P3, and when both expectations are simultaneously violated, a larger response is evoked compared to either one alone. These findings, which are consistent with the results of our study, show that the local and global effects are not fully independent but interact in an early time window, indexed by enhanced and temporally extended MMN responses. They provide support not just for a hierarchical model, but for a predictive rather than a feedforward one. Moreover, the MMN has been found to be relatively insensitive to attention, because it is elicited in situations in which the subjects’ attention is directed away from the stimuli and there are no task demands (Chennu et al., 2013). Given that early MMN is a pre-attentive automatic ERP component (Näätänen et al., 2001; Pegado et al., 2010; Tiitinen et al., 1994), and given that it has been observed in comatose and vegetative state patients (Bekinschtein et al., 2009; Fischer et al., 2004; Naccache et al., 2004), the finding that even early MMN is impaired in OFC patients indicate that patients may suffer from a deficit in sensory predictive processing that is independent of attention and conscious awareness.

The picture is more complicated when it comes to the predictive roles of P3a and P3b components. Following the MMN, a positive polarity P300 complex, sensitive to the detection of unpredicted auditory events, has been reported (Chennu et al., 2013; Doricchi et al., 2021; Kompus et al., 2020; Liaukovich et al., 2022). However, the two types of P300 (P3a and P3b) have not been clearly fitted into the hierarchical PC theory. The P3a is considered to be part of the brain's mechanism for detecting PEs (Wessel et al., 2012; Wessel et al., 2014) and may indicate that the brain is reallocating attentional resources to process and learn from these unexpected events. The P3a is typically interpreted as reflecting an involuntary attentional reorienting process (Escera & Corral, 2007; Ungan et al., 2019), which may relate to the operations of the ventral attention network (Corbetta et al., 2008; Corbetta & Shulman, 2002; Nieuwenhuis et al., 2005). Predictive coding emphasizes the role of contextual information in generating predictions with P3a being influenced by the context in which an unexpected event occurs (Schomaker et al., 2014). In the hierarchy of predictive processing, the P3a may reflect PEs at different hierarchical levels, depending on the complexity of the prediction and the degree to which it deviates from the sensory input. On the other hand, the P3b is linked to higher-level cognitive processes that involve updating long-term predictions based on incoming sensory information. It is highly dependent on attention, conscious awareness and active engagement with the task (Bekinschtein et al., 2009; Del Cul et al., 2007; Sergent et al., 2005; Strauss et al., 2015). It is thought to play a role in integrating the unexpected sensory input into the current context, potentially leading to updates of predictions in working memory (Chao et al., 1995; Donchin & Coles, 1988; Polich, 2007).

Hierarchical PC theory is continually evolving, and the relationship between these ERP components and attention or conscious awareness remains an active area of research. We acknowledge the need for further investigation to better understand how attention and conscious awareness fit within this framework. In light of your comment, we provide a more comprehensive discussion about the functional meaning of the EEG findings in our “Discussion - OFC and hierarchical predictive processing” [page 22-24].

The fact that lateral PFC patients show unaltered neural responses contradicts prominent views from PC identifying this region as a generator of the MMN and a source of predictions sent to temporal auditory areas.

We appreciate the reviewer's comment and want to acknowledge that another reviewer raised this concern previously. We have provided a detailed response to this issue in our previous response (see Response to Reviewer #1 Comment 4). We have expanded the “Discussion” to address this point by adding a new section titled “Lack of findings in the lateral PFC lesion group” [page 21]. In this section, we first present some of the findings implicating specific areas of the lateral PFC in the generation of MMN and in predictive processing, and then offer an account of the potential reasons behind the lack of neurophysiological differences between the lateral PFC and control groups.

For these reasons, a more critical view on the extent to which the findings support hierarchical predictive coding is needed.

By responding to the reviewer’s previous comments (i.e., the reasons why the reviewer thinks it is difficult to determine the functional meaning of the EEG findings), we believe that we have offered a more critical view on this matter.

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Author Response

Reviewer #2 (Public Review):

Major weaknesses:

1) The biggest weakness of the manuscript is the lack of appropriate explanation and interpretation of these observed cyclin D1 ubiquitination and degradation by at least five different combinations of Cullin-E3 ligases. Are all the five cullin-E3 combinations exclusive and/or redundant to each other for cyclin D1 ubiquitination? What are the speculations in terms of the underlying mechanism? At least a working model should be included to better interpret the data.

Cyclin D1 has been recognized as an oncogene, which is upregulated in multiple types of cancers. In different types of cells, different E3 ligase may be involved in the process of cyclin D1 protein degradation. Even in the same cells, multiple E3 ligases may be involved in cyclin D1 degradation to make sure that steady-state protein levels of cyclin D1 are under surveillance and fine-tune regulation.

2) Although a phosphorylation-mutant cyclin D1 (i.e., T286) was included in the manuscript, there is no Lysine residue mutant within cyclin D1 identified and characterized for the critical function of cyclin D1 ubiquitination.

It was reported that Lysine 269 is essential for cyclin D1 ubiquitination (Barbash et al., 2009). WT or mutant cyclin D1 (K269R) expression plasmids were co-transfected with Keap1, DDB2, and AMBRA1 expression plasmids into HEK293 cells. 48 hours after transfection, changes in cyclin D1 protein levels were detected by the Western blot analysis. We found the expression of WT cyclin D1 was decreased in HEK293 cells with Keap1, DDB2, and AMBRA1 co-transfected, while the expression of K269R mutant cyclin D1 showed no significant decrease in rhe cells co-transfected with co-transfected Keap1, DDB2, and AMBRA1, suggesting that Lysine 269 is essential for cyclin D1 ubiquitination.

3) The significance of these different Cullin 1-7 and associated E3 ligases (Keap1-CUL3, DDB2-CUL4A/4B, WSB2-CUL2/5, and RBX1-CUL1-7) in cyclin D1 ubiquitination is mainly determined by siRNA-mediated knockdown or overexpression of target cullin/E3 proteins. However, it is not clear whether the observed phenotypes of cyclin D1 are due to these cullin-E3 ligases directly or indirectly. In vitro ubiquitination assay with E1, E2, and E3 should be performed to demonstrate whether recombinant cyclin D1 is ubiquitinated.

We have performed in vitro ubiquitination assay as the reviewer suggested. The results demonstrated that Keap1, DDB2, and WSB2 can induce cyclin D1 ubiquitination. Especially, Keap1 induced cyclin D1 ubiquitination and formed ubiquitination ladder similar to AMBRA1-induced cyclin D1 ubiquitination ladder. In contrast, no clear ubiquitination ladder was observed in Rbx1 group (Figure S16).

Author Response

Reviewer #1 (Public Review):

This manuscript provides a comprehensive investigation of the effects of the genetic ablation of three different transcription factors (Srf, Mrtfa, and Mrtfb) in the inner ear hair cells. Based on the published data, the authors hypothesized that these transcription factors may be involved in the regulation of the genes essential for building the actin-rich structures at the apex of hair cells, the mechanosensory stereocilia and their mechanical support - the cuticular plate. Indeed, the authors found that two of these transcription factors (Srf and Mrtfb) are essential for the proper formation and/or maintenance of these structures in the auditory hair cells. Surprisingly, Srf- and Mrtfb- deficient hair cells exhibited somewhat similar abnormalities in the stereocilia and in the cuticular plates even though these transcription factors have very different effects on the hair cell transcriptome. Another interesting finding of this study is that the hair cell abnormalities in Srfdeficient mice could be rescued by AAV-mediated delivery of Cnn2, one of the downstream targets of Srf. However, despite a rather comprehensive assessment of the novel mouse models, the authors do not have yet any experimentally testable mechanistic model of how exactly Srf and Mrtfb contribute to the formation of actin cytoskeleton in the hair cells. The lack of any specific working model linking Srf and/or Mrtfb with stereocilia formation decreases the potential impact of this study.

Major comments:

Figures 1 & 3: The conclusion on abnormalities in the actin meshwork of the cuticular plate was based largely on the comparison of the intensities of phalloidin staining in separate samples from different groups. In general, any comparison of the intensity of fluorescence between different samples is unreliable, no matter how carefully one could try matching sample preparation and imaging conditions. In this case, two other techniques would be more convincing: 1) quantification of the volume of the cuticular plates from fluorescent images; and 2) direct examination of the cuticular plates by transmission electron microscopy (TEM).

In fact, the manuscript provides no single TEM image of the F-actin abnormalities either in the cuticular plate or in the stereocilia, even though these abnormalities seem to be the major focus of the study. Overall, it is still unclear what exactly Srf or Mrtfb deficiencies do with F-actin in the hair cells.

Yes, we agree. As suggested by the reviewer, to directly examine the defects in F-actin organization within the cuticular plate of mutant mice, we conducted Transmission Electron Microscopy (TEM) analyses. The results, as presented in the revised Figures 1 and 4 (panels F, G, and E, F, respectively), provide crucial insights into the structural changes in the cuticular plate. Meanwhile, the comparison of the volume of the phalloidin labeled cuticular plate after 3-D reconstruction using Imaris software was conducted and shown in Author response image 1. The results of the cuticular plate (CP) volume were consistent with the relative F-actin intensity change of the cuticular plate in the revised Figures 1B and 4B. For the TEM analysis of the stereocilia, we regret that due to time constraints, we were unable to collect TEM images of stereocilia with sufficient quality for a meaningful comparison. However, we believe that the data we have presented sufficiently addresses the primary concerns, and we appreciate the reviewers’ understanding of these limitations.

Author response image 1.

Figures 2 & 4 represent another example of how deceiving could be a simple comparison of the intensity of fluorescence between the genotypes. It is not clear whether the reduced immunofluorescence of the investigated molecules (ESPN1, EPS8, GNAI3, or FSCN2) results from their mis-localization or represents a simple consequence of the fact that a thinner stereocilium would always have a smaller signal of the protein of interest, even though the ratio of this protein to the number of actin filaments remains unchanged. According to my examination of the representative images of these figures, loss of Srf produces mis-localization of the investigated proteins and irregular labeling in different stereocilia of the same bundle, while loss of Mrtfb does not. Obviously, a simple quantification of the intensity of fluorescence conceals these important differences.

Yes, we agree. In addition to the quantification of tip protein intensity, we have added a few more analyses in the revised Figure 3 and Figure 6, such as the percentage of row 1 tip stereocilia with tip protein staining and the percentage of IHCs with tip protein staining on row 2 tip. Using the results mentioned above, the differences in the expression level, the row-specific distribution and the irregular labeling of tip proteins between the control and the mutants can be analyzed more thoroughly.

Reviewer #2 (Public Review):

The analysis of bundle morphology using both confocal and SEM imaging is a strength of the paper and the authors have some nice images, especially with SEM. Still, the main weakness is that it is unclear how significant their findings are in terms of understanding bundle development; the mouse phenotypes are not distinct enough to make it clear that they serve different functions so the reader is left wondering what the main takeaway is.

Based on the reviewer’s comments, in this revised manuscript, we put more emphasis on describing the effects of SRF and MRTFB on key tip proteins’ localization pattern during stereocilia development, represented by ESPN1, EPS8 and GNAI3, as well as the effects of SRF and MRTFB on the F-actin organization of cuticular plate using TEM. We have made substantial efforts to interpret the mechanistic underpinnings of the roles of SRF and MRTFB in hair cells. This is reflected in the revised Figures 1, 3, 4, 6, and 10, where we provide more comprehensive insights into the mechanisms at play.

We interpret our data in a way that both SRF and MRTF regulate the development and maintenance of the hair cell’s actin cytoskeleton in a complementary manner. Deletion of either gene thus results in somewhat similar phenotypes in hair cell morphology, despite the surprising lack of overlap of SRF and MRTFB downstream targets in the hair cell.

In Figure 1 and 3, changes in bundle morphology clearly don't occur until after P5. Widening still occurs to some extent but lengthening does not and instead the stereocilia appear to shrink in length. EPS8 levels appear to be the most reduced of all the tip proteins (Srf mutants) so I wonder if these mutants are just similar to an EPS8 KO if the loss of EPS8 occurred postnatally (P0-P5).

To address this question, we performed EPS8 staining on the control and Srf cKO hair cells at P4 and P10. We found that the dramatic decrease of the row 1 tip signal for EPS8 started since P4 in Srf cKO IHCs. Although the major hair bundle phenotype of Eps8 KO, including the defects of row 1 stereocilia lengthening and additional rows of short stereocilia also appeared in Srf cKO IHCs, there are still some bundle morphology differences between Eps8 KO and Srf cKO. For example, firstly, both Eps8 KO OHCs and IHCs showed additional rows of short stereocilia, but we only observed additional rows of short stereocilia in Srf cKO IHCs. Secondly, in Valeria Zampini’s study, SEM and TEM images did not show an obvious reduction of row 2 stereocilia widening (P18-P35), while our analysis of SEM images confirmed that the width of row 2 IHC stereocilia was drastically reduced by 40% in Srf cKO (P15). Generally, we think although Srf cKO hair bundles are somewhat similar to Eps8 KO, the Srf cKO hair bundle phenotype might be governed by multiple candidate genes cooperatively.

Reference:

Valeria Zampini, et al. Eps8 regulates hair bundle length and functional maturation of mammalian auditory hair cells. PLoS Biol. 2011 Apr;9(4): e1001048.

A major shortcoming is that there are few details on how the image analyses were done. Were SEM images corrected for shrinkage? How was each of the immunocytochemistry quantitation (e.g., cuticular plates for phalloidin and tip staining for antibodies) done? There are multiple ways of doing this but there are few indications in the manuscript.

We apologize for not making the description of the procedure of images analyses clear enough. As described in Nicolas Grillet group’s study, live and mildly-fixed IHC stereocilia have similar dimensions, while SEM preparation results in a hair bundle at a 2:3 scale compared to the live preparation. In our study, the hair cells selected for SEM imaging and measurements were located in the basal turn (30-32kHz), while the hair cells selected for fluorescence-based imaging and measurements were located in the middle turn (20-24kHz) or the basal turn (32-36kHz). Although our SEM imaging and fluorescence-based imaging of basal turn’s hair bundles were not from the same area exactly, the control hair bundles with SEM imaging have reduced row 1 stereocilia length by 10%-20%, compared to the control hair bundles with fluorescence-based imaging (revised Figure 2 and Figure 5). Generally, our stereocilia dimensions data showed appropriate shrinkage caused by the SEM preparation.

Recognizing the need for clarity, we have provided a detailed description of our image quantification and analysis procedures in the “Materials and Methods” section, specifically under “Immunocytochemistry.” This will aid readers in understanding our methodologies and ensure transparency in our approach.

Reference:

Katharine K Miller, et al. Dimensions of a Living Cochlear Hair Bundle. Front Cell Dev Biol. 2021 Nov 25:9:742529.

The tip protein analysis in Figs 2 and 4 is nice but it would be nice for the authors to show the protein staining separately from the phalloidin so you could see how restricted to the tips it is (each in grayscale). This is especially true for the CNN2 labeling in Fig 7 as it does not look particularly tip specific in the x-y panels. It would be especially important to see the antibody staining in the reslices separate from phalloidin.

Thank you for the suggestions. We have shown tip proteins staining in grayscale separately from the phalloidin in the revised Figure 3 and Figure 6. To clearly show the tip-specific localization of CNN2, we conducted CNN2 staining at different ages during hair bundle development and showed CNN2 labeling in grayscale and in reslices in revised Figure 9-figure supplement 1B.

In Fig 6, why was the transcriptome analysis at P2 given that the phenotype in these mice occurs much later? While redoing the transcriptome analysis is probably not an option, an alternative would be to show more examples of EPS8/GNAI/CNN2 staining in the KO, but at younger ages closer to the time of PCR analysis, such as at P5. Pinpointing when the tip protein intensities start to decrease in the KOs would be useful rather than just showing one age (P10).

We agree with the reviewer. To address this question, we have performed ESPN1, EPS8 and GNAI3 staining on the control and the mutant’s hair cells at P4, P10 and P15 (the revised Figures 3 and 6). According to the new results, we found that the dramatic decreases of the row 1 tip signal for ESPN1 and EPS8 started since P4 in Srf cKO IHCs, is consistent with the appearance of the mild reduction of row 1 stereocilia length in P5 Srf cKO IHCs. For Mrtfb cKO hair cells, the obvious reduction of the row 1 tip signal for ESPN1 was observed until P10. However, a few genes related to cell adhesion and regulation of actin cytoskeleton were significantly down-regulated in P2 Mrtfb deficient hair cell transcriptome. We think that in hair cells the MRTFB may not play a major role in the regulation of stereocilia development, so the morphological defects of stereocilia happened much later in the Mrtfb mutant than in the Srf mutant.

While it is certainly interesting if it turns out CNN2 is indeed at tips in this phase, the experiments do not tell us that much about what role CNN2 may be playing. It is notable that in Fig 7E in the control+GFP panel, CNN2 does not appear to be at the tips. Those images are at P11 whereas the images in panel A are at P6 so perhaps CNN2 decreases after the widening phase. An important missing control is the Anc80L65-Cnn2 AAV in a wild-type cochlea.

We agree with the reviewer. We have conducted more immunostaining experiments to confirm the expression pattern of CNN2 during the stereocilia development, from P0 to P11. The results were included in the revised Figure 9-figure supplement 1B. As the reviewer suggested, CNN2 expression pattern in control cochlea injected with Anc80L65-Cnn2 AAV has also been provided in revised Figure 9E.

Author Response

Reviewer #1 (Public Review):

The work by Yijun Zhang and Zhimin He at al. analyzes the role of HDAC3 within DC subsets. Using an inducible ERT2-cre mouse model they observe the dependency of pDCs but not cDCs on HDAC3. The requirement of this histone modifier appears to be early during development around the CLP stage. Tamoxifen treated mice lack almost all pDCs besides lymphoid progenitors. Through bulk RNA seq experiment the authors identify multiple DC specific target gens within the remaining pDCs and further using Cut and Tag technology they validate some of the identified targets of HDAC3. Collectively the study is well executed and shows the requirement of HDAC3 on pDCs but not cDCs, in line with the recent findings of a lymphoid origin of pDC.

1) While the authors provide extensive data on the requirement of HDAC3 within progenitors, the high expression of HDAC3 in mature pDCs may underly a functional requirement. Have you tested INF production in CD11c cre pDCs? Are there transcriptional differences between pDCs from HDAC CD11c cre and WT mice?

We greatly appreciate the reviewer’s point. We have confirmed that Hdac3 can be efficiently deleted in pDCs of Hdac3fl/fl-CD11c Cre mice (Figure 5-figure supplement 1 in revised manuscript). Furthermore, in those Hdac3fl/fl-CD11c Cre mice, we have observed significantly decreased expression of key cytokines (Ifna, Ifnb, and Ifnl) by pDCs upon activation by CpG ODN (shown in Author response image 1). Therefore, HDAC3 is also required for proper pDC function. However, we have yet to conduct RNA-seq analysis comparing pDCs from HDAC CD11c cre and WT mice.

Author response image 1.

Cytokine expression in Hdac3 deficient pDCs upon activation

2) A more detailed characterization of the progenitor compartment that is compromised following depletion would be important, as also suggested in the specific points.

We thank the reviewer for this constructive suggestion. We have performed thorough analysis of the phenotype of hematopoietic stem cells and progenitor cells at various developmental stages in the bone marrow of Hdac3 deficient mice, based on the gating strategy from the recommended reference. Briefly, we analyzed the subpopulations of progenitors based on the description in the published report by "Pietras et al. 2015", namely MPP2, MPP3 and MPP4, using the same gating strategy for hematopoietic stem/progenitor cells. As shown in Author response image 2 and Author response image 3, we found that the number of LSK cells was increased in Hdac3 deficient mice, especially the subpopulations of MPP2 and MPP3, whereas no significant changes in MPP4. In contrast, the numbers of LT-HSC, ST-HSC and CLP were all dramatically decreased. This result has been optimized and added as Figure 3A in revised manuscript. The relevant description has been added and underlined in the revised manuscript Page 6 Line 164-168.

Author response image 2.

Gating strategy for hematopoietic stem/progenitor cells in bone marrow.

Author response image 3.

Hematopoietic stem/progenitor cells in Hdac3 deficient mice

Reviewer #2 (Public Review):

In this article Zhang et al. report that the Histone Deacetylase-3 (HDAC3) is highly expressed in mouse pDC and that pDC development is severely affected both in vivo and in vitro when using mice harbouring conditional deletion of HDAC3. However, pDC numbers are not affected in Hdac3fl/fl Itgax-Cre mice, indicating that HDCA3 is dispensable in CD11c+ late stages of pDC differentiation. Indeed, the authors provide wide experimental evidence for a role of HDAC3 in early precursors of pDC development, by combining adoptive transfer, gene expression profiling and in vitro differentiation experiments. Mechanistically, the authors have demonstrated that HDAC3 activity represses the expression of several transcription factors promoting cDC1 development, thus allowing the expression of genes involved in pDC development. In conclusion, these findings reveals HDAC3 as a key epigenetic regulator of the expression of the transcription factors required for pDC vs cDC1 developmental fate.

These results are novel and very promising. However, supplementary information and eventual further investigations are required to improve the clarity and the robustness of this article.

Major points

1) The gating strategy adopted to identify pDC in the BM and in the spleen should be entirely described and shown, at least as a Supplementary Figure. For the BM the authors indicate in the M & M section that they negatively selected cells for CD8a and B220, but both markers are actually expressed by differentiated pDC. However, in the Figures 1 and 2 pDC has been shown to be gated on CD19- CD11b- CD11c+. What is the precise protocol followed for pDC gating in the different organs and experiments?

We apologize for not clearly describing the protocols used in this study. Please see the detailed gating strategy for pDC in bone marrow, and for pDC and cDC in spleen (Figure 4 and Figure 5). These information are now added to Figure1−figure supplement 3, The relevant description has been underlined in Page 5 Line 113-116, in revised manuscript.

We would like to clarify that in our study, we used two different panels of antibody cocktails, one for bone marrow Lin- cells, including mAbs to CD2/CD3/TER-119/Ly6G/B220/CD11b/CD8/CD19; the other for DC enrichment, including mAbs to CD3/CD90/TER-119/Ly6G/CD19. We included B220 in the Lineage cocktails to deplete B cells and pDCs, in order to enrich for the progenitor cells from bone marrow. However, when enriching for the pDC and cDC, B220 or CD8a were not included in the cocktail to avoid depletion of pDC and cDC1 subsets . For the flow cytometry analysis of pDCs, we gated pDCs as the CD19−CD11b−CD11c+B220+SiglecH+ population in both bone marrow and spleen. The relevant description has been underlined in the revised manuscript Page 16 Line 431-434.

2) pDC identified in the BM as SiglecH+ B220+ can actually contain DC precursors, that can express these markers, too. This could explain why the impact of HDAC3 deletion appears stronger in the spleen than in the BM (Figures 1A and 2A). Along the same line, I think that it would important to show the phenotype of pDC in control vs HDAC3-deleted mice for the different pDC markers used (SiglecH, B220, Bst2) and I would suggest to include also Ly6D, taking also in account the results obtained in Figures 4 and 7. Finally, as HDCA3 deletion induces downregulation of CD8a in cDC1 and pDC express CD8a, it would important to analyse the expression of this marker on control vs HDAC3-deleted pDC.

We agree with the reviewer’s points. In the revised manuscript, we incorporated major surface markers, including Siglec H, B220, Ly6D, and PDCA-1, all of which consistently demonstrated a substantial decrease in the pDC population in Hdac3 deficient mice. Moreover, we did notice that Ly6D+ pDCs showed higher degree of decrease in Hdac3 deficient mice. Additionally, percentage and number of both CD8+ pDC and CD8- pDC were decreased in Hdac3 deficient mice (Author response image 4). These results are shown in Figure1−figure supplement 4 of the revised manuscript. The relevant description has been added and underlined in the revised manuscript Page 5 Line 121-125.

Author response image 4.

Bone marrow pDCs in Hdac3 deficient mice revealed by multiple surface markers

3) How do the authors explain that in the absence of HDAC3 cDC2 development increased in vivo in chimeric mice, but reduced in vitro (Figures 2B and 2E)?

As shown in the response to the Minor point 5 of Reviewer#1. Briefly, we suggested that the variabilities maybe explained by the timing of anaysis after HDAC3 deletion. In Figure 2C, we analyzed cells from the recipients one week after the final tamoxifen treatment and observed no significant change in the percentage of cDC2 when further pooled all the experiment data. In Figure 2E, where tamoxifen was administered at Day 0 in Flt3L-mediated DC differentiation in vitro, the DC subsets generated were then analyzed at different time points. We observed no significant changes in cDCs and cDC2 at Day 5, but decreases in the percentage of cDC2 were observed at Day 7 and Day 9. This suggested that the cDC subsets at Day 5 might have originated from progenitors at a later stage, while those at Day 7 and Day 9 might originate form the earlier progenitors. Therefore, based on these in vitro and in vivo experiments, we believe that the variation in the cDC2 phenotype might be attributed to the progenitors at different stages that generated these cDCs.

4) More generally, as reported also by authors (line 207), the reconstitution with HDAC3-deleted cells is poorly efficient. Although cDC seem not to be impacted, are other lymphoid or myeloid cells affected? This should be expected as HDAC3 regulates T and B development, as well as macrophage function. This should be important to know, although this does not call into question the results shown, as obtained in a competitive context.

In this study, we found no significant influence on T cells, mature B cells or NK cells, but immature B cells were significantly decreased, in Hdac3-ERT2-Cre mice after tamoxifen treatment (Figure 6). However, in the bone marrow chimera experiments, the numbers of major lymphoid cells were decreased due to the impaired reconstitution capacity of Hdac3 deficient progenitors. Consistent with our finding, it has been reported that HDAC3 was required for T cell and B cell generation, in HDAC3-VavCre mice (Summers et al., 2013), and was necessary for T cell maturation (Hsu et al., 2015). Moreover, HDAC3 is also required for the expression of inflammatory genes in macrophages upon activation (Chen et al., 2012; Nguyen et al., 2020).

5) What are the precise gating strategies used to identify the different hematopoietic precursors in the Figure 4 ? In particular, is there any lineage exclusion performed?

We apologize for not describing the experimental procedures clearly. In this study we enriched the lineage negative (Lin−) cells from the bone marrow using a Lineage-depleting antibody cocktail including mAbs to CD2/CD3/TER-119/Ly6G/B220/CD11b/CD8/CD19. We also provide the gating strategy implemented for sorting LSK and CDP populations from the Lin− cells in the bone marrow (Author response image 5), shown in the Figure 3A and Figure4−figure supplement 1 of revised manuscript.

Author response image 5.

Gating strategy for LSK, CD115+ CDP and CD115− CDP in bone marrow

6) Moreover, what is the SiglecH+ CD11c- population appearing in the spleen of mice reconstituted with HDAC3-deleted CDP, in Fig 4D?

We also noticed the appearance of a SiglecH+CD11c− cell population in the spleen of recipient mice reconstituted with HDAC3-deficient CD115−CDPs, while the presence of this population was not as significant in the HDAC3-Ctrl group, as shown in Figure 4D. We speculate that this SiglecH+CD11c− cell population might represent some cells at a differentiation stage earlier than pre-DCs. Alternatively, the relatively increased percentage of this population derived from HDAC3-deficient CD115−CDP might be due to the substantially decreased total numbers of DCs. This could be clarified by further analysis using additional cell surface markers.

7) Finally, in Fig 4H, how do the authors explain that Hdac3fl/fl express Il7r, while they are supposed to be sorted CD127- cells?

This is indeed an interesting question. In this study, we confirmed that CD115−CDPs were isolated from the surface CD127− cell population for RNA-seq analysis, and the purity of the sorted cells were checked (Author response image 6), as shown in Figure4−figure supplement 1 in revised manuscript.

The possible explanation for the expression of Il7r mRNA in some HDAC3fl/fl CD115−CDPs, as revealed in Figure 4H by RNA-seq analysis, could be due to a very low level of cell surface expression of CD127, these cells therefore could not be efficiently excluded by sorting for surface CD127- cells.

Author response image 6.

CD115−CDPs sorting from Hdac3-Ctrl and Hdac3-KO mice

8) What is known about the expression of HDAC3 in the different hematopoietic precursors analysed in this study? This information is available only for a few of them in Supplementary Figure 1. If not yet studied, they should be addressed.

We conducted additional analysis to address the expression of Hdac3 in various hematopoietic progenitor cells at different stages, based on the RNA-seq analyis. The data revealed a relatively consistent level of Hdac3 expression in progenitor populations, including HSC, MMP4, CLP, CDP and BM pDCs (Author response image 7). That suggests that HDAC3 may play an important role in the regulation of hematopoiesis at multiple stages. This information is now added in Figure1−figure supplement 1B of revised manuscript.

Author response image 7.

Hdac3 expression in hematopoietic progenitor cells

9) It would be highly informative to extend CUT and Tag studies to Irf8 and Tcf4, if this is technically feasible.

We totally agree with the reviewer. We have indeed attempted using CUT and Tag study to compare the binding sites of IRF8 and TCF4 in wild-type and Hdac3-deficient pDCs. However, it proved that this is technically unfeasible to get reliable results due to the limited number of cells we could obtain from the HDAC3 deficient mice. We are committed to explore alternative approaches or technologies in future studies to address this issue.

Author Response

Reviewer #1 (Public Review):

This is a very exciting manuscript from Meng Wang's lab on lysosomal proteomics. They used several different protein tags to identify the lysosomal proteome. The exciting findings include A) specific lysosomal proteins exist in a tissue-specific manner B) lipl-4 overexpression and daf-2 extend life span using different mechanisms C) identification of novel lysosomal proteins D) demonstration of the function of several lysosomal proteins in regulation lysosome abundance and function.

We thank the reviewer for finding our manuscript exciting.

Reviewer #2 (Public Review):

In this manuscript, Yu and colleagues profile the lysosome content in C. elegans. They implement lysosome immunoprecipitation (Lyso-IP) for C. elegans and they convincingly show that this method successfully isolates lysosomes from whole worms. The authors find that the lysosomes of worms overexpressing the lysosomal lipase lipl4 are enriched for AMPK subunits and nucleoporins and that these proteins are required for the longevity of lipl-4 overexpressing worms. The authors also show that this is specific to this longevity pathway given that another long-lived worm strain (daf2) does not exhibit enrichment for nucleoporins nor does it require them for longevity. The authors go on to express the Lyso-IP tag in different tissues of C. elegans (muscle, hypodermis, intestine, neurons) and identify the tissue-specific lysosome proteomes. Finally, the authors use this method to identify lysosome proteins in mature lysosomes and they find new proteins that regulate lysosomal acidification.

The authors present a powerful tool to unbiasedly identify lysosome-associated proteins in C. elegans, and they provide an in-depth assessment of how this method can be used to understand longevity pathways and identify novel proteins. Understanding lysosomal differences in specific tissues or in response to different longevity conditions are exciting as it provides new insight into how organelles could control specific homeostasis responses. This tool and proteomics datasets also represent a great resource for the C. elegans community and should pry open new studies on the regulation and role of the lysosome at the organismal level.

We truly appreciate that the reviewer’s positive comment on our work.

Addressing the following suggestions would help strengthen this already strong manuscript. First, it would be helpful to validate selected candidates from the tissuespecific Lyso-IP to verify that the protocol is still specific with lower sample amounts. Second, it would be helpful to provide more details on the methods, notably for sample preparation and analysis, so that it can serve as a guideline for the community. Third, the manuscript contains a lot of data and conditions, which is great, but they may also feel disconnected in some cases and it could be helpful to focus the study on the main key findings.

We thank the reviewer’s comments. As suggested by the reviewer, we have also generated a CRISPR knock-in line for one hypodermis-specific candidate Y58A7A.1 that encodes a copper transporter and validated its hypodermis-specific lysosomal localization (new Supplementary Figure 2E).

As suggested by the reviewer, we have extended the method section on Lyso-IP to include more details. We believe that the new version should be sufficient for any lab to follow this protocol and conduct their own analyses. We will also take advantage of the eLife “Request a Protocol” feature to share the detailed version of the Lyso-IP method with researchers who are interested.

We have thoroughly reorganized the manuscript to increase the textual clarity and improve the connection between different analyses and results.

Reviewer #3 (Public Review):

The manuscript by Ji et al dissects the important role of lysosomes in cellular metabolism and signaling and their regulation by various associated proteins. The authors utilized deep proteomic profiling in C.Elegans to identify lysosome-associated proteins involved in regulating longevity and discovered the recruitment of AMPK and nucleoporin proteins in response to increased lysosomal lipolysis. Additionally, the authors found lysosomal heterogeneity across different tissues and specific enrichment of the Ragulator complex on Cystinosin-positive lysosomes.

Strengths of this work include the utilization of deep proteomic profiling to identify novel lysosome-associated proteins involved in longevity regulation, as well as the discovery of lysosomal heterogeneity and specific protein enrichments across different worm tissues. These findings point to a complex interplay between lysosomal protein dynamics, signal transduction, organelle crosstalk, and organism longevity.

One weakness of this work may be the limited scope of the study, as it focuses primarily on the identification and characterization of lysosome-associated proteins involved in longevity regulation, with limited mechanistic follow-up and some unsubstantiated claims.

We thank the reviewer for her/his helpful comments and suggestions. The primary goal of this manuscript is to provide new methods and resource to the community. We did have several biological findings from the current study, and mechanistic follow-up with these findings will be interesting future topics but may beyond the scope of the current manuscript. In addition, we have provided new experimental results to further support several claims that the reviewer has commented on.

Author Response

The following is the authors’ response to the original reviews.

We sincerely thank the editor and reviewers for their constructive feedback on our manuscript. Based on their recommendations, we've conducted additional experiments, made revisions to the text and figures, and provide a point-by-point response below.

Reviewer #1 (Recommendations for the authors):

1) The lack of behavioral/physiological measures of the depth of anesthesia (ventilation, heart rate, blood pressure, temperature, O2, pain reflexes, etc...) combined with the lack of dose-response and the use of different routes of administration makes the data difficult to interpret. Sure, there is a clear difference in network activation between KET and ISO, but are those effects due to the depth of the anesthesia, the route of administration, and the dose used? The lack of behavioral/physiological measures prevents the identification of brain regions responsible for some of the physiological effects and different effects of anesthetics.

We greatly appreciate the insightful feedback you have provided.

In response to the concerns about anesthesia depth:

a. We recorded EEG and EMG data both before and after drug administration. Supplementary Figure 1 showcases the changes in EEG and EMG power observed 30 minutes post-drug administration, normalized to a 5-minute baseline taken prior to the drug's administration. Notably, no significant differences were detected in the normalized EEG and EMG power between the ISO and KET groups. Given the marked statistical differences observed between the EEG power in the KET and saline groups, and the EMG power in the home cage and ISO groups, we infer that both anesthetics effectively induced a loss of consciousness.

b. We used standard methods and doses for inducing c-Fos expression with anesthetics, as documented in prior studies (Hua, T, et al., Nat Neurosci, 2020; 23(7): 854-868; Jiang-Xie, L F, et al., Neuron, 2019; 102(5): 1053-1065.e4; Lu, J, et al., J Comp Neurol, 2008; 508(4): 648-62). In future research, it might be more optimal to adopt continuous intraperitoneal or intravenous administration of ketamine.

c. Within the scope of our study, while disparities in anesthesia duration might potentially influence the direct statistical comparison of ISO and KET, such disparities wouldn't compromise the identification of brain regions activated by KET or ISO when assessed as distinct stimuli (ISO vs. home cage; KET vs. saline) or in relation to their individual functional network hub node results.

We hope these additions and clarifications adequately address your concerns and enhance the comprehensibility of our data.

2) Under anesthesia there should be an overall reduction of activity, is that the case? There is no mention of significantly downregulated regions. The authors use multiple transformations of the data to interpret the results (%, PC1 values, logarithm) without much explanation or showing the full raw data in Fig 1. It would be helpful to interpret the data to compare the average fos+ neurons in each region between treatment and control for each drug.

Absence of Significantly Downregulated Regions Under Anesthesia: There are two primary reasons for this observation:

a. Our study's sampling time for the home cage, ISO, saline, and KET groups was during Zeitgeber Time (ZT) 6-7.5. During this period, mice in both the home cage and saline groups typically showed reduced spontaneous activity or were in a sleep state. Our Supplementary Figure 1 EEG and EMG data corroborate this, revealing no significant statistical variations in EEG power between the home cage and ISO groups, nor in EMG power between the saline and KET groups.

b. Our immunohistochemical data showed that the total number of c-Fos positive cells in the two control groups was notably lower than in the experimental groups (Saline group vs KET group: 11808±2386 versus 308705±106131, P = 0.006; Home cage vs ISO group: 3371±840 vs 12326±1879, P = 0.001). This is in line with previous studies, like the one by Cirelli C and team, which found minimal c-Fos expression throughout the mouse brain during physiological sleep (Cirelli, C, and G Tononi, Sleep, 2000; 23(4): 453-69). Thus, in our analysis, we did not detect regions with significant downregulation when comparing anesthetized mice with controls.

Interpreting Raw Data from Figure 1: Regarding the average Fos+ neurons:

In Figures 4 and 5, we utilized raw data (c-Fos cell count) to assess cell expression differences across 201 brain regions within each group. Only brain regions that had significant statistical differences after multiple comparison corrections are shown in the figures.

3) I do not understand their interpretation of the PCA analyses. For instance, in Fig 2 they claim that KET is associated with PC1 while ISO is associated with PC2. Looking at the distribution of points it's clear that the KET animals are all grouped at around +2.5 on PC1 and -2.0 on PC2, this means that KET is associated with both PC1 and PC2 to a similar degree (2 to 2.5). Moreover, I'm confused about why they use PCA to represent the animals/group. PCA is a powerful technique to reduce dimensionality and identify groups of variables that may represent the same underlying construct; however, it is not the best way to identify clusters of individuals or groups.

Clarification on PCA Analyses in Figure 2: Thank you for pointing out the ambiguities in our initial presentation of the PCA analyses. We are grateful for the opportunity to address these concerns.

KET and ISO Associations with PC1 and PC2: You rightly observed that KET samples manifest both a positive value on PC1 (around +2.5) and a negative one on PC2 (around -2.0), suggesting that KET has a substantial influence on both principal components. In PCA, a positive score implies a positive association with that component, whereas a negative score suggests a negative association. Contrarily, ISO samples predominantly exhibit values around +2.5 on PC2, with nearly neutral values for PC1, underlining its stronger association with PC2 and lack of significant correlation with PC1. To ensure transparency and clarity, we've adjusted the corresponding descriptions in our manuscript, which can be found on Line 100.

Rationale Behind Using PCA to Represent Animals/Groups: Our initial step was to conduct PCA clustering analysis on the 201 brain regions within both the ISO and KET groups. In the accompanying chart, varying colors denote different brain regions, while distinct shapes represent separate clusters. There wasn't a pronounced distribution pattern within the ISO and KET groups, which led us to adopt the current computational method presented in the paper. This approach was chosen to directly contrast the relative differential expressions between ISO and KET.

We deeply value your feedback, which has steered us toward a clearer and more accurate presentation of our data. We genuinely appreciate your meticulous review.

Author response image 1.

4) The actual metric used for the first PCA is unclear, is it the FOS density in each of the regions (some of those regions are large and consist of many subregions, how does that affect the analysis) is it the %-fos, or normalized cells? The wording describing this is variable causing some confusion. How would looking at these different metrics influence the analysis?

Thank you for raising concerns about the metrics used in our PCA analysis. We recognize the need for clearer exposition and appreciate the opportunity to clarify.

PCA Metrics: The metric for our PCA is calculated by obtaining the ratio of the Fos density within a specific brain region to the global Fos density across the brain. Briefly, this entails dividing the number of Fos-positive cells in a given region by its volume, and then comparing this to the Fos density of the whole brain. The logarithm of this ratio provides our PCA metric. We've elaborated on this in the Materials and Methods section (Lines 401) and enhanced clarity in our revised manuscript, particularly at Line 96.

In Figure 2A, we employed 53 larger, mutually exclusive brain regions based on the reference from the study by Do et al. (eLife, 2016;5:e13214). However, in Figure 3A, we used a more detailed segmentation, incorporating 201 distinct brain areas that are more granular than those in Figure 2A. Notably, the PCA results from both representations were consistent. The rationale behind selecting either the 53 or 201 brain regions can be found in our response to Question 10.

Rationale for Metric Choice: The log ratio of regional c-Fos densities relative to the global brain density was chosen due to:

a. Notable disparities in c-Fos cell expression across the groups.

b. A significant non-normal distribution of density values across animals within the group. Employing the log ratio effectively mitigates the impact of extreme values and outliers, achieving a more standardized data distribution.

We've added PCA plots based on c-Fos densities, depicted in Author response image 2. However, the data dispersion has resulted in a significantly spread-out horizontal scale for these visuals.

Author response image 2.

5) Based on Fig 3 the authors concludes that ISO activates the hypothalamic regions and inhibits the cortex, however, Fig 1 shows neither an activation of the hypothalamus in the ISO nor an inhibition of the cortex when compared to home cage control. If anything it suggests the opposite.

Thank you for your insightful observations regarding the discrepancies between Figures 2 and 3. We believe that when you refer to Figure 1, you are actually referencing Figure 2C.

ISO activation in Hypothalamus: In Figure 2C, we regret the oversight where we inadvertently interchanged the positions of ISO and Saline. When accurately represented, Figure 2C indeed shows that ISO notably activates the periventricular zone (PVZ) and the lateral zone (LZ) of the hypothalamus compared to the home cage group. Moreover, there's a discernible difference in the hypothalamic response between ISO and KET.

ISO's Effect on the Cortex: The main aim of Figure 3 was to highlight the differing responses between ISO and KET in the cortex. Notably, KET demonstrates a positive correlation with PC1 (+7 on PC1), whereas ISO shows a negative association (-3 on PC1). Given that the coefficient of PC1 for the cortical region is positive, it suggests that the cortical areas activated by KET are inhibited by ISO (with KET's distribution around 0 on PC2). However, the divergence between ISO and the home cage is most apparent in PC2, with ISO clusters at +4 and the home cage approximately at -2, suggesting that ISO activates a different set of cortical nuclei. In alignment with this, Figure 2C also illustrates that ISO activates specific cortical areas, such as ILA and PIR, in contrast to the home cage.

Thus, Figure 3 primarily employs PCA to delineate the contrasts between ISO and KET, whereas Figure 2C emphasizes the comparison of each against their respective controls.

6) Control for isoflurane should be air in the induction chamber rather than home cage. It is possible that Fos activation reflects handling/stress pre-anesthesia in the animals, which would increase Fos expression in the stress-related regions such as the BST, striatum (CeA), hypothalamus (PVH) and potentially the LC.

Thank you for emphasizing the importance of an appropriate control for Isoflurane.

In our efforts to minimize the potential impact of stress-induced c-Fos expression, we implemented several precautionary measures. Prior to the experiment, both groups of mice were subjected to handling and acclimatization within the induction chamber over four days. By the day of the experiment, for the mice in the experimental group, we ensured they were comfortable and exhibited no signs of distress or fear—such as cowering or evading. With care, we slowly relocated them to the nearby anesthesia induction chamber. Using 5% ISO, anesthesia was induced promptly, following a meticulously devised protocol to reduce stress impacts on c-Fos expression.

Moreover, existing studies have shown Isoflurane's activation of BST/CeA (Hua, T, et al., Nat Neurosci, 2020, 23: 854-868), PVH (Xu, Z, et al., British Journal of Anaesthesia, 2023, 130: 446-458), and LC (Lu, J, et al., J Comp Neurol, 2008, 508: 648-62), even when using oxygen controls. Such literature supports our findings, indicating that the activation we observed was indeed due to Isoflurane and not purely stress-related.

7) In the Ket network there are a few anticorrelated regions, most of which are amongst the list of the most activated regions, does this mean that the strong correlation results from an overall decreased activation? And if so, is it possible that the ketamine anesthesia was stronger than the isoflurane, causing a more general reduction in activity?

The pronounced correlations observed within the ketamine (KET) network do not signify a generalized decrease in activation. Instead, these correlations reflect significantly enhanced activity in specific regions under KET anesthesia. This amplified correlation is an indication of a more widespread increase in activity, rather than a decrease. These findings are consistent with previous research, which showed that anesthetic doses of ketamine produce patterns of Fos expression in the CNS similar to wakefulness (Lu, J, et al., J Comp Neurol, 2008; 508(4): 648-62).

Regarding the comparative strength of KET versus ISO anesthesia, our electroencephalographic evidence confirms that both agents induce a loss of consciousness. No significant differences were observed in EEG and EMG readings within the first 30 minutes post-administration. In future research, a continuous intravenous or intraperitoneal administration of KET might be a preferable method.

8) Since they have established networks it would be easy and useful to look at how the different regions identified (sleep, pain, neuroendocrine, motor-related, ...) work together to maintain analgesia, are they within the same module? Do they become functionally connected and is this core network of functional connections similar for KET and ISO?

Thank you for your suggestion. In response to your inquiry, we undertook analysis of the core functional networks for KET and ISO, using a set threshold at r>0.82 and P<0.05. For evaluating the modularity of each network, we utilized Newman's spectral community detection algorithm.

(A) The ISO’s core functional network (56 nodes, 372 edges) predominantly divides into two modules with a modularity quotient of 0.345. ISO-active regions include arousal-associated regions (PL, ILA, PVT), analgesia-related (CeA, LC, PB), neuroendocrine function nuclei (TU, PVi, ARH, PVH, SON) as detailed in Figure 5. Notably, ARH and SON weren't incorporated into the core network. Analgesia-associated regions, such as CeA, LC, and PB, reside within module 1, while neuroendocrine nuclei are spread between modules 1 and 2.

(B) In contrast, KET's core functional network (61 nodes, 1820 edges) splits into three distinct modules, but its low modularity quotient (0.06) indicates a lack of clear functional modularization, suggesting denser interconnections among brain regions. Furthermore, functionally-related regions such as arousal (PL, ILA, PVT, DR), analgesia-related (ACA, APN, PAG, LC), and neuroendocrine regulation (PVH, SON),etc., as seen in Figure 4, are distributed across different modules. This distribution may implies that functions like analgesia and neuroendocrine regulation are not governed by simple, linear processes, but arise from complex, overlapping pathways spanning various modules and functional zones.

In summary, the core functional networks of ISO and KET differ, with functionally-related regions spanning multiple modules, reflecting their diverse roles in varied physiological regulations.

Author response image 3.

9) The naming of the function of some of the regions is very much debatable. For instance, PL/ILA are named "sleep-wakefulness regulation" regions in the paper. I can think of many more important functions of the PL/IL including executive functions, behavioral flexibility, and emotional control. It is unclear how the functions of all the regions were attributed. I am not sure that this biased labeling of structure-function is useful to the reports, it may instead suggest wrong conclusions.

Thank you for your thoughtful feedback regarding our classification of the functions of the PL/ILA regions in our manuscript.

We recognize the challenge in accurately defining the functions of brain regions. While there is evidence highlighting the role of PL/ILA in arousal pathways, we also acknowledge their documented roles in executive functions, behavioral flexibility, and emotional control. In response to your comments, we have refined our description, changing "sleep-wakefulness regulation" to "wake-promoting pathways" (see Line: 159, 164).

It's worth noting that many brain regions, including the PL/ILA, have multiple functions. We agree that a single label might not capture the entirety of their roles. To provide a broader perspective, we will add a section in our manuscript that sheds light on the varied functions of these regions (Line: 181).

10) A point of concern and confusion is the number of brain regions analyzed. In the introduction, it is mentioned that 987 brain regions are considered, but this is reduced to 53 selected brain regions in Figure 2, then 201 brain regions in Figure 3, and reduced again to 63 for the network analysis. The rationale for selecting different brain regions is not clear.

For the 987 brain regions: Using the standard mouse atlas available at http://atlas.brain-map.org/, the mouse brain is organized into nine levels. The broadest category is the grey matter, which then progresses to more specific subdivisions, totaling 987 unique regions.

For the 53 brain regions: To effectively understand the activation patterns of ISO and KET, we started with a broad approach, looking at larger brain areas like the thalamus and hypothalamus. This broad view, presented in Figure 2, focuses on the 5th-level brain regions, encompassing 53 primary areas. This methodology is also employed in the study by Do et al. (Elife, 2016; 5: e13214). We have added the rationale for selecting these brain regions in the main text (Line: 92).

Regarding the 201 brain regions in Figures 3, 4, and 5: We delved deeper, examining the 6th-level brain regions, a common granularity in neuroscience research. This detailed view allowed us to highlight specific areas, like the CeA and PVH (Line:129).

Finally, for Figures 6 and 7, we selected 63 regions that were activated by both ISO and KET, as well as regions previously reported to be related to the mechanism of general anesthesia(Leung, L, et al., Progress in neurobiology, 2014; 122: 24-44) (Line: 220). Using these regions, we analyzed the correlation of c-Fos expression, aiming to construct a functional brain network with strong positive connections.

We hope this clarifies our approach and the rationale behind our region selection at each stage of the study. Thank you for your attention to this detail.

11) The statistical analysis does not seem appropriate considering the high number of comparisons. They use simple t-tests without correction for multiple comparisons.

Thank you for pointing out the concern regarding our statistical analysis. In the revised manuscript, we addressed the issue of multiple comparisons correction in our t-tests. We adopted the statistical methods detailed in the papers by Renier, N, et al., Cell, 2016; and Benjamini, Y, and Y Hochberg, 1995. P-values were adjusted for multiple comparisons using the two-stage linear step-up procedure of Benjamini, Krieger, and Yekutieli, with a false discovery rate (FDR) threshold (Q) of 0.05. This approach is now explained in the Materials and Methods section (Line: 434). After this adjustment, the brain regions we initially identified remained statistically significant. Furthermore, we revisited the original immunohistochemical images to confirm the differences in c-Fos cell expression between the experimental and control groups, reinforcing our conclusions.

12) There is no statistical analysis in Fig 2C。

Thank you for bringing to our attention the lack of statistical analysis in Fig 2C. We have now added the relevant statistical data in Supplementary Table 1 and provided annotations in Fig 2C to reflect this.

Reviewer #2

1) The authors report 987 brain regions in the introduction, but I cannot find any analysis that incorporates these or even which regions they are. Very little rationale is provided for the regions included in any of the analyses and numbers range from 53 in Figure 1, to 201 in Figure 3, to 63 in Figure 6. It would help if the authors could first survey Fos+ counts across all regions to identify a subset that is of interest (significantly changed by either condition compared to control) for follow up analysis.

Thank you for your insightful comments on the number of brain regions analyzed in our study.

987 Brain Regions: The reference to 987 brain regions from the standard mouse atlas (http://atlas.brain-map.org/) represents the entire categorization of the mouse brain across nine levels. We recognize that a comprehensive analysis of all these regions would be valuable, but to ensure clarity and depth, we took a focused approach.

Region Selection Rationale:

Figure 2: Concentrated on 5th-level brain regions (53 areas), inspired by methods from Do et al. (eLife, 2016;5:e13214). This provided a broad overview of c-Fos expression differences. Figures 4 and 5: Delved into 6th-level brain regions (201 areas), a common practice in neuroscience for more detailed study. Figure 6: We focused on 63 regions, which encompass not only the regions activated by both ISO and KET but also those previously reported to be associated with the mechanisms of general anesthesia. Methodological Approach: Our region selection was rooted in identifying areas with significant changes under anesthetic conditions compared to controls. This staged approach allowed a targeted analysis of the most affected regions, ensuring robust conclusions.

Enhancements: We've incorporated comparative analyses of activated brain regions at different hierarchical levels in Figures 4 and 5. For clearer comprehension, we’ve added clarifications in the manuscript at Lines: 92, 130, and 220.

2) Different data transformations are used for each analysis. One that is especially confusing is the 'normalization' of brain regions by % of total brain activation for each animal prior to PCA analysis in Figures 2 and 3. This would obscure any global differences in activation and make it unlikely to observe decreases in activation (which I think is likely here) that could be identified using the Fos+ counts after normalizing for region size (ie. Fos+ count / mm3) which is standard practice in such Fos-based activity mapping studies. While PCA can be powerful approach to identify global patterns, the purpose of the analysis in its current form is unclear. It would be more meaningful to show that regional activation patterns (measured as counts/mm3) are on separate PCs by group.

Thank you for your thoughtful comments. We regret any confusion caused by our initial presentation. For the PCA analysis in Figures 2A and 3A, we calculated the ratio of cell density in each brain region to the overall brain density, and then applied a logarithmic transformation to this ratio. Our approach in Figure 2C was to use the proportion of c-Fos cell counts in individual brain regions to the total cell counts throughout the brain. This methodology considers variations in overall c-Fos cell counts across animals, effectively mitigating potential biases due to differential global activation levels across subjects.

Furthermore, our direct comparison of differences in c-Fos cell counts between ISO, KET, and their respective control groups in Figures 4 and 5 addresses your concerns about potential decreases in activation. Notably, we did not identify any brain regions with significant suppression in these figures, which is consistent with the trends observed post-normalization in Figure 2C.

Given your feedback, we conducted another PCA using cell densities for each region (counts/mm3). However, we found significant variability and non-normal distribution of c-Fos density across the groups, leading to extensive data dispersion. Consequently, normalizing the cell counts across regions and then applying a logarithmic transformation before PCA might be more appropriate.

Author response image 4.

Additionally, our exploration of regional activation patterns using PCA analysis for ISO and KET separately, based on the logarithm ratio of the c-Fos density, revealed that there was no distinct clustering feature among the different brain regions (as illustrated in Author response image 5: colors represented distinct brain regions, while the shapes were indicative of different clusters). This observation further suggests that our original statistical approach might be more suitable.

Author response image 5.

3) Critical problem: The authors include a control group for each anesthetic (ketamine vs. saline, isofluorane vs. homecage) but most analyses do not make use of the control groups or directly compare Fos+ counts across the groups. Strictly speaking, they should have compared relative levels of induction by ketamine versus induction by isoflurane using ANOVAs. Instead, each type of induction was separate from the other. This does not account for increased variability in the ketamine versus isoflurane groups. There is no mention in the Statistics section or in Results section that any multiple comparison corrections were used. It appears that the authors only used Students t-test for each region and did not perform any corrections.

We appreciate the reviewer's insights and have addressed your concerns:

Given the pronounced difference in c-Fos cell count expression between the KET and ISO groups, a direct comparison of Fos+ counts may not effectively capture their inherent disparities. To better highlight these distinctions, we used the logarithm ratio of c-Fos density in our PCA analysis (Figure 3), mitigating potential disparities in overall cell counts between samples and emphasizing relative variations. However, in response to your feedback, we've included additional analyses. Author response image 6 depicts the c-Fos density (cells/mm^3) across different brain regions for the home cage, ISO, saline, and KET groups, with regions like the cerebral cortex, cerebral nuclei, thalamus, and others differentiated by shaded backgrounds. Data are represented as mean ± SEM. We performed a one-way ANOVA followed by Tukey’s post hoc test, marking significant differences between ISO and KET with asterisks: P < 0.001, P < 0.01, P < 0.05.

Regarding multiple comparison corrections, we've conducted thorough analyses on the data in Figure 2C and Figures 4, 5, and 6, implementing multiple comparison corrections. The detailed methodology is provided in the “Statistical analysis” section.

Author response image 6.

4) Figures 4 and 5 show brain regions 'significantly activated' following KET or ISO respectively, but again a subset of regions are shown and the stats seem to be t-tests with no multiple comparisons correction. It would help to show these two figures side by side, include the same regions, and keep the y axis ranges similar so the reader can easily compare the 'activation patterns' across the two treatments. Indeed, it looks like KET/Saline induced activation is an order or magnitude or two higher than ISO/Homecage. I would also recommend that this be the first data figure before any other analyses and maybe further analysis could be restricted to regions that are significantly changed in following KET or ISO here.

Thank you for your constructive feedback regarding Figures 4 and 5.

Comparison and Presentation of Figures 4 and 5: We acknowledge your suggestion to present these figures side by side for easier comparison. In the supplementary figure provided in the previous question, we've placed Figures 4 and 5 adjacent to each other, with consistent y-axis ranges, ensuring that readers can make direct comparisons between the activation patterns elicited by KET and ISO.

Statistical Concerns and Region Selection: As mentioned in our previous response, we have conducted multiple comparison corrections on the data presented in Figures 4 and 5. Detailed procedures are elaborated in the “Statistical analysis” section. We believe this approach addresses your concerns regarding the use of t-tests without corrections for multiple comparisons.

Difference in Activation Levels: We observed that the c-Fos activation due to KET is significantly higher than that from ISO. When presented side-by-side using the same scale, ISO activations appear less prominent, potentially mask subtle differences in the activation patterns of ISO, particularly if both KET and ISO showed changes in the same direction in certain brain regions but differed in magnitude. To address this, we used the proportion of c-Fos cell counts in Figure 2C, the logarithm ratio of c-Fos density in Figure 2A and Figure 3. This method emphasizes the relative changes, rather than absolute values, giving a more balanced view of the effects of each treatment.

5) Analyses in Figure 6 and 7 are interesting but again the choice of regions to include is unclear and makes interpreting the results impossible. For example, in Figure 7 it is unclear why the list of regions in bar graphs showing Degree and Betweenness Centrality are not the same even within a single row?

Thank you for your pertinent observation. The choice of brain regions in Figures 6 and 7 was carefully determined based on two main criteria: regions that were significantly activated by ISO or KET within the scope of our study, and those previously reported to be associated with anesthesia mechanisms and sleep-wake regulation.

Regarding your second concern on Figure 7, the discrepancies observed in the x-axes of the bar graphs arise from our methodological approach. We prioritized presenting the top 20% of regions based on their Degree or Betweenness Centrality values. By separately ranking these regions from highest to lowest, the regions presented for each metric inherently differ. This approach was taken to elucidate nodes that consistently emerge as significant across both metrics, thereby highlighting core nodes in the functional network. Were we to use a consistent x-axis without this ranking, it would not only necessitate a more extensive presentation but might also dilute the emphasis on key information. To clarify this methodology and its rationale for our readers, we have expanded upon this in the manuscript at Line 243.

We hope these clarifications address your concerns and facilitate a clearer understanding of our findings.

Reviewer #1 (Recommendations For The Authors):

Minor points

1) In Table 1: the separation of which substructures belong to which brain structure is not clear

2) Line 132 on page 3 seems to repeat the sentence earlier in the paragraph "KET predominantly affects brain regions within the cerebral cortex (CTX), while significantly inhibiting the hypothalamus, midbrain, and hindbrain."

3) Typos

a) Line 99/100 and 130 Central nucleus (CNU) should be cerebral nucleus

b) Comma on line 166

c) Fig. 4D: KET instead of Keta

d) Line 263 "ep"

e) Line 332: 35" "ml (add space)

4) Will data and code be made available?

Thank you for your detailed feedback.

1. We have revised Table 1 to clarify which substructures belong to which brain structures.

2. We acknowledge the redundancy and have now edited line 139 on page 3 to remove the repeated sentence regarding the effects of KET on brain regions.

3. We have addressed the typos you pointed out:

a. The terms "Central nucleus (CNU)" have been corrected to "cerebral nucleus."

b. The comma issue on line 166 has been rectified.

c. In Fig. 4D, we have corrected "Keta" to "KET."

d. We have corrected the typo "ep" on line 263.

e. A space has been added between "35" and "ml" on line 332 as you indicated.

1. Regarding the availability of data and code, we are currently conducting additional analyses related to this study. Once these analyses are completed, we will be more than happy to make the data and code available.

Thank you for assisting us in improving our manuscript.

Reviewer #2 (Recommendations For The Authors):

Minor comments:

6) The term 'whole-brain mapping' in the title suggests that the mapping was performed on 'intact brains' where in fact serial sections were used here. Maybe the authors could change to 'brain-wide mapping' to align better with the study.

Thank you for your insightful comments.

We have revised the title as suggested, changing "whole-brain mapping" to "brain-wide mapping".

7) It is unclear if the mice were kept under anesthesia for the 90-min duration and how the authors monitored the level of sedation. Additionally, if the KET mice were already sedated why were they further sedated with ISO before perfusions and tissue extraction? The methods should be clarified and any potential confounds discussed.

To maintain consistency in the experimental protocol and to reduce stress reactions in the mice, ISO was used before perfusion in all cases. However, this does not affect c-Fos expression as the expression of c-Fos protein starts 20-30 minutes after stimulation (Lara Aparicio, S Y, et al., NeuroSci, 2022; 3(4): 687-702).

We appreciate your guidance in enhancing the clarity of our manuscript.

Reviewer #3 (Recommendations For The Authors):

Recommendation: Minor corrections.

1) The authors should delve deeper into the molecular mechanisms underlying the observed effects, particularly the changes associated with NMDA and GABA receptors. Exploring these mechanisms would provide a more comprehensive understanding of how Ketamine and Isoflurane modulate neural activity and induce anesthesia.

2) The clinical relevance of these findings has not been sufficiently addressed. It would be valuable to elaborate on how the current research outcomes could potentially lead to changes in current anesthesia practices. For instance, identifying the distinct pathways of action for Ketamine and Isoflurane could aid anesthesiologists in selecting the most appropriate anesthetic based on the specific needs of individual patients or surgical procedures.

3) Both Ketamine and Isoflurane have been associated with neurotoxicity. It is important to discuss how the c-Fos activation induced by these anesthetics could contribute, at least partially, to anesthesia-related neurotoxicity. Examining the potential neurotoxic effects would provide a more comprehensive understanding of the risks associated with these anesthetics and aid in the development of safer anesthesia protocols.

Thank you for your valuable suggestions.

Regarding the three points (1, 2, and 3) you've raised, we fully recognize their significance. In the current study, our primary focus was on the differential impacts of Isoflurane and Ketamine on widespread c-Fos expression in the brain. However, we indeed acknowledge the importance of delving deeper into these mechanisms and their clinical relevance. Therefore, we intend to explore these critical issues in greater detail in our future research endeavors.

We appreciate your feedback, which provides constructive guidance for our subsequent research directions.

Author Response

We thank the three reviewers and the reviewing editor for their positive evaluation of our manuscript. We particularly appreciate that they unanimously consider our work as “important contributions to the understanding of how the CAF-1 complex works”, “The large amounts of data provided in the paper support the authors' conclusion very well” and “The paper effectively addresses its primary objective and is strong”.

We also thank them for a careful reading and useful comments to improve the manuscript. We will build on this input to provide an improved version of the manuscript that will hope to submit soon to eLife along with our point by point answer.

Author Response

eLife assessment

This study uses a multi-pronged empirical and theoretical approach to advance our understanding of how differences in learning relate to differences in the ways that male versus female animals cope with urban environments, and more generally how reversal learning may benefit animals in urban habitats. The work makes an important contribution and parts of the data and analyses are solid, although several of the main claims are only partially supported or overstated and require additional support.

We thank the Editor and both Reviewers for their time and for their constructive evaluation of our manuscript. We will work to address each comment and suggestion offered by the Reviewers in a revision.

Reviewer #1 (Public Review):

Summary:

In this highly ambitious paper, Breen and Deffner used a multi-pronged approach to generate novel insights on how differences between male and female birds in their learning strategies might relate to patterns of invasion and spread into new geographic and urban areas.

The empirical results, drawn from data available in online archives, showed that while males and females are similar in their initial efficiency of learning a standard color-food association (e.g., color X = food; color Y = no food) scenario when the associations are switched (now, color Y = food, X= no food), males are more efficient than females at adjusting to the new situation (i.e., faster at 'reversal learning'). Clearly, if animals live in an unstable world, where associations between cues (e.g., color) and what is good versus bad might change unpredictably, it is important to be good at reversal learning. In these grackles, males tend to disperse into new areas before females. It is thus fascinating that males appear to be better than females at reversal learning. Importantly, to gain a better understanding of underlying learning mechanisms, the authors use a Bayesian learning model to assess the relative role of two mechanisms (each governed by a single parameter) that might contribute to differences in learning. They find that what they term 'risk sensitive' learning is the key to explaining the differences in reversal learning. Males tend to exhibit higher risk sensitivity which explains their faster reversal learning. The authors then tested the validity of their empirical results by running agent-based simulations where 10,000 computer-simulated 'birds' were asked to make feeding choices using the learning parameters estimated from real birds. Perhaps not surprisingly, the computer birds exhibited learning patterns that were strikingly similar to the real birds. Finally, the authors ran evolutionary algorithms that simulate evolution by natural selection where the key traits that can evolve are the two learning parameters. They find that under conditions that might be common in urban environments, high-risk sensitivity is indeed favored.

Strengths:

The paper addresses a critically important issue in the modern world. Clearly, some organisms (some species, some individuals) are adjusting well and thriving in the modern, human-altered world, while others are doing poorly. Understanding how organisms cope with human-induced environmental change, and why some are particularly good at adjusting to change is thus an important question.

The comparison of male versus female reversal learning across three populations that differ in years since they were first invaded by grackles is one of few, perhaps the first in any species, to address this important issue experimentally.

Using a combination of experimental results, statistical simulations, and evolutionary modeling is a powerful method for elucidating novel insights.

Thank you—we are delighted to receive this positive feedback, especially regarding the inferential power of our analytical approach.

Weaknesses:

The match between the broader conceptual background involving range expansion, urbanization, and sex-biased dispersal and learning, and the actual comparison of three urban populations along a range expansion gradient was somewhat confusing. The fact that three populations were compared along a range expansion gradient implies an expectation that they might differ because they are at very different points in a range expansion. Indeed, the predicted differences between males and females are largely couched in terms of population differences based on their 'location' along the range-expansion gradient. However, the fact that they are all urban areas suggests that one might not expect the populations to differ. In addition, the evolutionary model suggests that all animals, male or female, living in urban environments (that the authors suggest are stable but unpredictable) should exhibit high-risk sensitivity. Given that all grackles, male and female, in all populations, are both living in urban environments and likely come from an urban background, should males and females differ in their learning behavior? Clarification would be useful.

Thank you for highlighting a gap in clarity in our conceptual framework. To answer the Reviewer’s question—yes, even with this shared urban ‘history’, it seems plausible that males and females could differ in their learning. For example, irrespective of population membership, such sex differences could come about via differential reliance on learning strategies mediated by an interaction between grackles’ polygynous mating system and male-biased dispersal system, as we discuss in L254–265. Population membership might, in turn, differentially moderate the magnitude of any such sex-effect since an edge population, even though urban, could still pose novel challenges—for example, by requiring grackles to learn novel daily temporal foraging patterns such as when and where garbage is collected (grackles appear to track this food resource: Rodrigo et al. 2021 [DOI: 10.1101/2021.06.14.448443]). We will make sure to better introduce this important conceptual information in our revision.

Reinforcement learning mechanisms:

Although the authors' title, abstract, and conclusions emphasize the importance of variation in 'risk sensitivity', most readers in this field will very possibly misunderstand what this means biologically. Both the authors' use of the term 'risk sensitivity' and their statistical methods for measuring this concept have potential problems.

Please see our below responses concerning our risk-sensitivity term

First, most behavioral ecologists think of risk as predation risk which is not considered in this paper. Secondarily, some might think of risk as uncertainty. Here, as discussed in more detail below, the 'risk sensitivity' parameter basically influences how strongly an option's attractiveness affects the animal's choice of that option. They say that this is in line with foraging theory (Stephens and Krebs 2019) where sensitivity means seeking higher expected payoffs based on prior experience. To me, this sounds like 'reward sensitivity', but not what most think of as 'risk sensitivity'. This problem can be easily fixed by changing the name of the term.

We apologise for not clearly introducing the field of risk-sensitive foraging, which focuses on how animals evaluate and choose between distinct food options, and how such foraging decisions are influenced by pay-off variance i.e., risk associated with alternative foraging options (seminal reviews: Bateson 2002 [DOI: 10.1079/PNS2002181]; Kacelnik & Bateson 1996 [DOI: 10.1093/ICB/36.4.402]). We further apologise for not clearly explaining how our lambda parameter estimates such risk-sensitive foraging. To do so here, we need to consider our Bayesian reinforcement learning model in full. This model uses observed choice-behaviour during reinforcement learning to infer our phi (informationupdating) and lambda (risk-sensitivity) learning parameters. Thus, payoffs incurred through choice simultaneously influence estimation of each learning parameter—that is, in a sense, they are both sensitive to rewards. But phi and lambda differentially direct any reward sensitivity back on choicebehaviour due to their distinct definitions (we note this does not imply that the two cannot influence one another i.e., co-vary on the latent scale). Glossing over the mathematics, for phi, stronger reward sensitivity (bigger phi values) means faster internal updating about stimulus-reward pairings, which translates behaviourally into faster learning about ‘what to choose’. For lambda, stronger reward sensitivity (bigger lambda values) means stronger internal determinism about seeking the non-risk foraging option (i.e., the one with the higher expected payoffs based on prior experience), which translates behaviourally into less choice-option switching i.e., ‘playing it safe’. We hope this information, which we will incorporate into our revision, clarifies the rationale and mechanics of our reinforcement learning model, and why lamba measures risk-sensitivity.

In addition, however, the parameter does not measure sensitivity to rewards per se - rewards are not in equation 2. As noted above, instead, equation 2 addresses the sensitivity of choice to the attraction score which can be sensitive to rewards, though in complex ways depending on the updating parameter. Second, equations 1 and 2 involve one specific assumption about how sensitivity to rewards vs. to attraction influences the probability of choosing an option. In essence, the authors split the translation from rewards to behavioral choices into 2 steps. Step 1 is how strongly rewards influence an option's attractiveness and step 2 is how strongly attractiveness influences the actual choice to use that option. The equation for step 1 is linear whereas the equation for step 2 has an exponential component. Whether a relationship is linear or exponential can clearly have a major effect on how parameter values influence outcomes. Is there a justification for the form of these equations? The analyses suggest that the exponential component provides a better explanation than the linear component for the difference between males and females in the sequence of choices made by birds, but translating that to the concepts of information updating versus reward sensitivity is unclear. As noted above, the authors' equation for reward sensitivity does not actually include rewards explicitly, but instead only responds to rewards if the rewards influence attraction scores. The more strongly recent rewards drive an update of attraction scores, the more strongly they also influence food choices. While this is intuitively reasonable, I am skeptical about the authors' biological/cognitive conclusions that are couched in terms of words (updating rate and risk sensitivity) that readers will likely interpret as concepts that, in my view, do not actually concur with what the models and analyses address.

To answer the Reviewer’s question—yes, these equations are very much standard and the canonical way of analysing individual reinforcement learning (see: Ch. 15.2 in Computational Modeling of Cognition and Behavior by Farrell & Lewandowsky 2018 [DOI: 10.1017/CBO9781316272503]; McElreath et al. 2008 [DOI: 10.1098/rstb/2008/0131]; Reinforcement Learning by Sutton & Barto 2018). To provide a “justification for the form of these equations'', equation 1 describes a convex combination of previous values and recent payoffs. Latent values are updated as a linear combination of both factors, there is no simple linear mapping between payoffs and behaviour as suggested by the reviewer. Equation 2 describes the standard softmax link function. It converts a vector of real numbers (here latent values) into a simplex vector (i.e., a vector summing to 1) which represents the probabilities of different outcomes. Similar to the logit link in logistic regression, the softmax simply maps the model space of latent values onto the outcome space of choice probabilities which enter the categorial likelihood distribution. We can appreciate how we did not make this clear in our manuscript by not highlighting the standard nature of our analytical approach. We will do better in our revision. As far as what our reinforcement learning model measures, and how it relates cognition and behaviour, please see our previous response.

To emphasize, while the authors imply that their analyses separate the updating rate from 'risk sensitivity', both the 'updating parameter' and the 'risk sensitivity' parameter influence both the strength of updating and the sensitivity to reward payoffs in the sense of altering the tendency to prefer an option based on recent experience with payoffs. As noted in the previous paragraph, the main difference between the two parameters is whether they relate to behaviour linearly versus with an exponential component.

Please see our two earlier responses on the mechanics of our reinforcement learning model.

Overall, while the statistical analyses based on equations (1) and (2) seem to have identified something interesting about two steps underlying learning patterns, to maximize the valuable conceptual impact that these analyses have for the field, more thinking is required to better understand the biological meaning of how these two parameters relate to observed behaviours, and the 'risk sensitivity' parameter needs to be re-named.

Please see our earlier response to these suggestions.

Agent-based simulations:

The authors estimated two learning parameters based on the behaviour of real birds, and then ran simulations to see whether computer 'birds' that base their choices on those learning parameters return behaviours that, on average, mirror the behaviour of the real birds. This exercise is clearly circular. In old-style, statistical terms, I suppose this means that the R-square of the statistical model is good. A more insightful use of the simulations would be to identify situations where the simulation does not do as well in mirroring behaviour that it is designed to mirror.

Based on the Reviewer’s summary of agent-based forward simulation, we can see we did a poor job explaining the inferential value of this method—we apologise. Agent-based forward simulations are posterior predictions, and they provide insight into the implied model dynamics and overall usefulness of our reinforcement learning model. R-squared calculations are retrodictive, and they say nothing about the causal dynamics of a model. Specifically, agent-based forward simulation allows us to ask—what would a ‘new’ grackle ‘do’, given our reinforcement learning model parameter estimates? It is important to ask this question because, in parameterising our model, we may have overlooked a critical contributing mechanism to grackles’ reinforcement learning. Such an omission is invisible in the raw parameter estimates; it is only betrayed by the parameters in actu. Agent-based forward simulation is ‘designed’ to facilitate this call to action—not to mirror behavioural results. The simulation has no apriori ‘opinion’ about computer ‘birds’ behavioural outcomes; rather, it simply assigns these agents random phi and lambda draws (whilst maintaining their correlation structure), and tracks their reinforcement learning. The exercise only appears circular if no critical contributing mechanism(s) went overlooked—in this case computer ‘birds’ should behave similar to real birds. A disparate mapping between computer ‘birds’ and real birds, however, would mean more work is needed with respect to model parameterisation that captures the causal, mechanistic dynamics behind real birds’ reinforcement learning (for an example of this happening in the human reinforcement learning literature, see Deffner et al. 2020 [DOI: 10.1098/rsos.200734]). In sum, agent-based forward simulation does not access goodness-of-fit—we assessed the fit of our model apriori in our preregistration (https://osf.io/v3wxb)—but it does assess whether one did a comprehensive job of uncovering the mechanistic basis of target behaviour(s). We will work to make the above points on the insight afforded by agent-based forward simulation explicitly clear in our revision.

Reviewer #2 (Public Review):

Summary:

The study is titled "Leading an urban invasion: risk-sensitive learning is a winning strategy", and consists of three different parts. First, the authors analyse data on initial and reversal learning in Grackles confronted with a foraging task, derived from three populations labeled as "core", "middle" and "edge" in relation to the invasion front. The suggested difference between study populations does not surface, but the authors do find moderate support for a difference between male and female individuals. Secondly, the authors confirm that the proposed mechanism can actually generate patterns such as those observed in the Grackle data. In the third part, the authors present an evolutionary model, in which they show that learning strategies as observed in male Grackles do evolve in what they regard as conditions present in urban environments.

Strengths:

The manuscript's strength is that it combines real learning data collected across different populations of the Great-tailed grackle (Quiscalus mexicanus) with theoretical approaches to better understand the processes with which grackles learn and how such learning processes might be advantageous during range expansion. Furthermore, the authors also take sex into account revealing that males, the dispersing sex, show moderately better reversal learning through higher reward-payoff sensitivity. I also find it refreshing to see that the authors took the time to preregister their study to improve transparency, especially regarding data analysis.

Thank you—we are pleased to receive this positive evaluation, particularly concerning our efforts to improve scientific transparency via our study’s preregistration (https://osf.io/v3wxb).

Weaknesses:

One major weakness of this manuscript is the fact that the authors are working with quite low sample sizes when we look at the different populations of edge (11 males & 8 females), middle (4 males & 4 females), and core (17 males & 5 females) expansion range. Although I think that when all populations are pooled together, the sample size is sufficient to answer the questions regarding sex differences in learning performance and which learning processes might be used by grackles but insufficient when taking the different populations into account.

In Bayesian statistics, there is no strict lower limit of required sample size as the inferences do not rely on asymptotic assumptions. With inferences remaining valid in principle, low sample size will of course be reflected in rather uncertain posterior estimates. We note all of our multilevel models use partial pooling on individuals (the random-effects structure), which is a regularisation technique that generally reduces the inference constraint imposed by a low sample size (see Ch. 13 in Statistical Rethinking by Richard McElreath [PDF: https://bit.ly/3RXCy8c]). We further note that, in our study preregistration (https://osf.io/v3wxb), we formally tested our reinforcement learning model for different effect sizes of sex on learning for both target parameters (phi and lambda) across populations, using a similarly modest N (edge: 10 M, 5 F; middle: 22 M, 5 F ; core: 3 M, 4 F) to our actual final N, that we anticipated to be our final N at that time. This apriori analysis shows our reinforcement learning model: (i) detects sex differences in phi values >= 0.03 and lambda values >= 1; and (ii) infers a null effect for phi values < 0.03 and lambda values < 1 i.e., very weak simulated sex differences (see Figure 4 in https://osf.io/v3wxb). Thus, both of these points together highlight how our reinforcement learning model allows us to say that across-population null results are not just due to small sample size. Nevertheless the Reviewer is not wrong to wonder whether a bigger N might change our population-level results (it might; so might much-needed population replicates—see L270), but our Bayesian models still allow us to learn a lot from our current data.

Another weakness of this manuscript is that it does not set up the background well in the introduction. Firstly, are grackles urban dwellers in their natural range and expand by colonising urban habitats because they are adapted to it? The introduction also fails to mention why urban habitats are special and why we expect them to be more challenging for animals to inhabit. If we consider that one of their main questions is related to how learning processes might help individuals deal with a challenging urban habitat, then this should be properly introduced.

In L53–56 we introduce that the estimated historical niche of grackles is urban environments, and that shifts in habitat breadth—e.g., moving into more arid, agricultural environments—is the estimated driver of their rapid North American colonisation. We will work towards flushing out how urban-imposed challenges faced by grackles, such as the wildlife management efforts introduced in L64–65, may apply to animals inhabiting urban environments more broadly.

Also, the authors provide a single example of how learning can differ between populations from more urban and more natural habitats. The authors also label the urban dwellers as the invaders, which might be the case for grackles but is not necessarily true for other species, such as the Indian rock agama in the example which are native to the area of study. Also, the authors need to be aware that only male lizards were tested in this study. I suggest being a bit more clear about what has been found across different studies looking at: (1) differences across individuals from invasive and native populations of invasive species and (2) differences across individuals from natural and urban populations.

We apologise for not specifying that the review we cite in L42 by Lee & Thornton (2021) covers additional studies on cognition in both urban invasive species as well as urban-dwellers versus nonurban counterparts—we will remedy this omission in our revision. We will also revise our labelling of the lizard species. We are aware only male lizards were tested but this information is not relevant to substantiating our use of this study; that is, to highlight that learning can differ between urban-dwelling and non-urban counterparts. Finally, the Reviewer’s general suggestion is a good one—we will work to add this biological clarity to our revision.

Finally, the introduction is very much written with regard to the interaction between learning and dispersal, i.e. the 'invasion front' theme. The authors lay out four predictions, the most important of which is No. 4: "Such sex-mediated differences in learning to be more pronounced in grackles living at the edge, rather than the intermediate and/or core region of their range." The authors, however, never return to this prediction, at least not in a transparent way that clearly pronounces this pattern not being found. The model looking at the evolution of risk-sensitive learning in urban environments is based on the assumption that urban and natural environments "differ along two key ecological axes: environmental stability 𝑢 (How often does optimal behaviour change?) and environmental stochasticity 𝑠 (How often does optimal behaviour fail to pay off?). Urban environments are generally characterised as both stable (lower 𝑢) and stochastic (higher 𝑠)". Even though it is generally assumed that urban environments differ from natural environments the authors' assumption is just one way of looking at the differences which have generally not been confirmed and are highly debated. Additionally, it is not clear how this result relates to the rest of the paper: The three populations are distinguished according to their relation to the invasion front, not with respect to a gradient of urbanization, and further do not show a meaningful difference in learning behaviour possibly due to low sample sizes as mentioned above.

Thank you for highlighting a gap in our reporting clarity. We will take care in our revision to transparently report our null result regarding our fourth prediction; more specifically, that we did not detect meaningful behavioural or mechanistic population-level differences in grackles’ learning. Regarding our evolutionary model, we agree with the Reviewer that this analysis is only one way of looking at the interaction between learning phenotype and apparent urban environmental characteristics. Indeed, in L282–288 we state: “Admittedly, our evolutionary model is not a complete representation of urban ecology dynamics. Relevant factors—e.g., spatial dynamics and realistic life histories—are missed out. These omissions are tactical ones. Our evolutionary model solely focuses on the response of reinforcement learning parameters to two core urban-like (or not) environmental statistics, providing a baseline for future study to build on”. But we can see now that ‘core’ is too strong a word, and instead ‘supposed’, ‘purported’ or ‘theorised’ would be more accurate—we will revise our wording. As far as how our evolutionary results relate to the rest of the paper, these results suggest successful urban living should favour risk-sensitive learning, and our other analyses in our paper reveal male grackles—the dispersing sex in this historically urban-dwelling and currently urban-invading species—show pronounced risk-sensitive learning, so it appears risk-sensitive learning is a winning strategy for urban-invading male grackles and urban-invasion leaders more generally (we note, of course, other factors undoubtedly contribute to grackles’ urban invasion success, as discussed in ‘Ideas and speculation’; see also our first response to R1). We will work to make these links clearer in our revision. Finally, please see our above response on the inferential sufficiency of our sample size.

In conclusion, the manuscript was well written and for the most part easy to follow. The format of eLife having the results before the methods makes it a bit harder to follow because the reader is not fully aware of the methods at the time the results are presented. It would, therefore, be important to more clearly delineate the different parts and purposes. Is this article about the interaction between urban invasion, dispersal, and learning? Or about the correct identification of learning mechanisms? Or about how learning mechanisms evolve in urban and natural environments? Maybe this article can harbor all three, but the borders need to be clear. The authors need to be transparent about what has and especially what has not been found, and be careful to not overstate their case.

Thank you, we are pleased to read that the Reviewer found our manuscript to be generally digestible. In our revision, we will work to add further clarity, and to temper our tone.

Author Response

The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review):

This manuscript tried to answer a long-standing question in an important research topic. I read it with great interest. The quality of the science is high, and the text is clearly written. The conclusion is exciting. However, I feel that the phenotype of the transgenic line may be explained by an alternative idea. At least, the results should be more carefully discussed.

We thank the reviewer #1 for his/her comments that helped to improve the manuscript. We have incorporated changes to reflect the suggestions provided by the reviewer. Here is a point-by-point response to the reviewer's specific and other minor comments.

Specific comments:

1) Stability or activity (Fv/Fm) was not affected in PSII with the W14F mutation in D1. If W14F really represents the status of PSII with oxidized D1, what is the reason for the degradation of almost normal D1?

In this study, we used W14F mutation to mimic Trp-14 oxidation. The W14F mutant did not affect the stability and photosynthetic activity under normal growth conditions. However, the W14F mutant showed increased D1 degradation and reduced Fv/Fm values under high light. These results suggested that the W14F mutant has almost normal D1 protein stability under growth light conditions, as pointed out by the reviewer.

However, it should be noted that D1 protein in the W14F strain rapidly degraded under high light. In the discussion part, we mentioned the possibility that other OPTMs may have additive effects on D1 degradation. Synergistic effects such as different amino acid oxidations may cause D1 degradation, and among those oxidative damages, W14 oxidation would be a key signal for D1 degradation by FtsH.

2) To focus on the PSII in which W14 is oxidized, this research depends on the W14F mutant lines. It is critical how exactly the W-to-F substitution mimics the oxidized W. The authors tried to show it in Figure 5. Because of the technical difficulty, it may be unfair to request more evidence. But the paper would be more convincing with the results directly monitoring the oxidized D1 to be recognized by FtsH.

We agree that confirming the direct interaction of oxidized D1 protein with FtsH provides more robust evidence. However, since FtsH progressively degrades the trapped substrate, it would be quite a challenging attempt to capture that moment. There are also technical limitations to obtaining sufficient substrate using Co-IP to compare its oxidation state. We included your suggested point in the discussion part. Thank you for your valuable suggestion.

3) Figure 3. If the F14 mimics the oxidized W14 and is sensed by FtsH, I would expect the degradation of D1 even under the growth light. The actual result suggests that W14F mutation partially modifies the structure of D1 under high light and this structural modification of D1 is sensed by FtsH. Namely, high light may induce another event which is recognized by FtsH. The W14F is just an enhancer.

Our results indicated that W14 oxidation is one of the keys to D1 degradation. On the other hand, we agree with the possibility that the reviewer points out. There is the possibility that factors other than W14 may act synergistically to promote D1 degradation. High light triggered more D1 degradation in W14F, suggesting that unknown factor(s) may be required for D1 degradation, e.g., oxidative modification at other sites and/or conformational changes of PSII under the high light. However, the current data that we have cannot reveal. We have incorporated the reviewer's comment and discussed it in the discussion part.

Reviewer #2 (Public Review):

In their manuscript, Kato et al investigate a key aspect of membrane protein quality control in plant photosynthesis. They study the turnover of plant photosystem II (PSII), a hetero-oligomeric membrane protein complex that undertakes the crucial light-driven water oxidation reaction in photosynthesis. The formidable water oxidation reaction makes PSII prone to photooxidative damage. PSII repair cycle is a protein repair pathway that replaces the photodamaged reaction center protein D1 with a new copy. The manuscript addresses an important question in PSII repair cycle - how is the damaged D1 protein recognized and selectively degraded by the membrane-bound ATP-dependent zinc metalloprotease FtsH in a processive manner? The authors show that oxidative post-translational modification (OPTM) of the D1 N-terminus is likely critical for the proper recognition and degradation of the damaged D1 by FtsH. Authors use a wide range of approaches and techniques to test their hypothesis that the singlet oxygen (1O2)-mediated oxidation of tryptophan 14 (W14) residue of D1 to N-formylkynurenine (NFK) facilitates the selective degradation of damaged D1. Overall, the authors propose an interesting new hypothesis for D1 degradation and their hypothesis is supported by most of the experimental data provided. The study certainly addresses an elusive aspect of PSII turnover and the data provided go some way in explaining the light-induced D1 turnover. However, some of the data are correlative and do not provide mechanistic insight. A rigorous demonstration of OPTM as a marker for D1 degradation is yet to be made in my opinion. Some strengths and weaknesses of the study are summarized below:

We thank reviewer #2 for his/her comments that helped to improve the manuscript. We have incorporated changes to reflect the suggestions pointed out as weaknesses by reviewer #2. Other minor comments were also answered in a point-by-point response.

Strengths:

1) In support of their hypothesis, the authors find that FtsH mutants of Arabidopsis have increased OPTM, especially the formation of NFK at multiple Trp residues of D1 including the W14; a site-directed mutation of W14 to phenylalanine (W14F), mimicking NFK, results in accelerated D1 degradation in Chlamydomonas; accelerated D1 degradation of W14F mutant is mitigated in an ftsH1 mutant background of Chlamydomonas; and that the W14F mutation augmented the interaction between FtsH and the D1 substrate.

2) Authors raise an intriguing possibility that the OPTM disrupts the hydrogen bonding between W14 residue of D1 and the serine 25 (S25) of PsbI. According to the authors, this leads to an increased fluctuation of the D1 N-terminal tail, and as a consequence, recognition and binding of the photodamaged D1 by the protease. This is an interesting hypothesis and the authors provide some molecular dynamics simulation data in support of this. If this hypothesis is further supported, it represents a significant advancement.

3) The interdisciplinary experimental approach is certainly a strength of the study. The authors have successfully combined mass spectrometric analysis with several biochemical assays and molecular dynamics simulation. These, together with the generation of transplastomic algal cell lines, have enabled a clear test of the role of Trp oxidation in selective D1 degradation.

4) Trp oxidative modification as a degradation signal has precedent in chloroplasts. The authors cite the case of 1O2 sensor protein EXECUTER 1 (EX1), whose degradation by FtsH2, the same protease that degrades D1, requires prior oxidation of a Trp residue. The earlier observation of an attenuated degradation of a truncated D1 protein lacking the N-terminal tail is also consistent with authors' suggestion of the importance of the D1 N-terminus recognition by FtsH. It is also noteworthy that in light of the current study, D1 phosphorylation is unlikely to be a marker for degradation as posited by earlier studies.

Weaknesses:

1) The study lacks some data that would have made the conclusions more rigorous and convincing. It is unclear why the level of Trp oxidation was not analyzed in the Chlamydomonas ftsH 1-1 mutant as done for the var 2 mutant. Increased oxidation of W14 OPTM in Chlamydomonas ftsH 1-1 is a key prediction of the hypothesis.

We thank the reviewer for this valuable comment. We agree with the reviewer that the analysis of oxidized Trp level will reinforce the importance of Trp oxidation in the N-terminal of D1. In our preliminary experiment, we observed a trend toward increase of the kynurenine in Trp-14 in Chlamydomonas ftsH1-1 strain. However, we found large errors, and we could not conclude that this trend is significant. A possible reason for the large error was that the signal intensity of oxidized Trp was insufficient for quantification in a series of Chlamydomonas experiment. In addition, the fact that the amount of D1 in each culture was not stable also might be one reason. On the other hand, we keep note of a previous result that more fragmentation of D1 protein was observed in the Chlamydomonas ftsH1-1 mutant compared to that in Arabidopsis (Malnoë et al., Plant Cell 2014). This result suggests that an alternative D1 degradation pathway involving other proteases is more active in the Chlamydomonas ftsH1-1 mutant than in Arabidopsis var2 mutant. Furthermore, the Chlamydomonas ftsH1-1 mutant, caused by an amino acid substitution, still has a significant FtsH1/FtsH2 heterohexamer, and the level of FtsH1 and FtsH2 proteins increases significantly under high light irradiation. This is a significant difference from the Arabidopsis var2 mutant lacking FtsH2 subunit and showed reduced protein accumulation. These factors may explain to the lower detection levels of oxidized Trp in Chlamydomonas. We believe that improved sensitivity for detection of oxidized Trp peptides and more sophisticated experimental systems could solve this issue in the future.

It is also unclear to me what is the rationale for showing D1-FtsH interaction data only for the double mutant but not for the single mutant (W14F).

We thank the reviewer for the comment. As suggested by the reviewer, the analysis of the mutant crossing ftsH and W14F single mutation will provide more convincing evidence. Fig.3 showed that the photosensitivity in both W14F and W14FW317F was caused by the enhanced D1 degradation observed, which was due to the W14F mutation. Therefore, we crossed the ftsH mutant with W14FW317F, which has a more severe phenotype, to confirm whether FtsH is involved in this D1 degradation.

Why is the FtsH pulldown of D2 not statistically significant (p value = {less than or equal to}0.1). Wouldn't one expect FtsH pulls down the RC47 complex containing D1, D2, and RC47. Probing the RC47 level would have been useful in settling this.

For the immunoblot result of D2 and its statistical analysis, we answered in the following comment; No.2 in the reviewer's comment in Recommendations For The Authors.

We agree with the reviewer's suggestion that further immunoblot analysis for CP47 protein would help our understanding of FtsH and RC47 interaction. Indeed, we attempted the immunoblot analysis of CP47 after the FtsH Co-IP experiment. However, the detection of CP43 protein was not sensitive enough. This reason may be due to the lower titer of the CP47 antibody compared to the D1 and D2 antibodies.

A key proposition of the authors' is that the hydrogen bonding between D1 W14 and S25 of PsbI is disrupted by the oxidative modification of W14. Can this hypothesis be further tested by replacing the S25 of PsbI with Ala, for example?

It is an interesting question whether amino acid substitution in PsbI-S25 affects the stability of D1-N-term and its degradation by FtsH. We would like to analyze the possibility in the future. We thank the reviewer for this helpful suggestion.

2) Although most of the work described is in vivo analysis, which is desirable, some in vitro degradation assays would have strengthened the conclusions. An in vitro degradation assay using the recombinant FtsH and a synthetic peptide encompassing D1 N-terminus with and without OPTM will test the enhanced D1 degradation that the authors predict. This will also help to discern the possibility that whether CP43 detachment alone is sufficient for D1 degradation as suggested for cyanobacteria.

In vitro experimental systems are interesting. However, FtsH is known to function as a hexamer, which has not yet been successfully reconstituted in vitro. Therefore, it would not be easy to perform an in vitro experimental system using the N-terminal synthetic peptide of D1 as a substrate. Thank you for your valuable suggestions.

3) The rationale for analyzing a single oxidative modification (W14) as a D1 degradation signal is unclear. D1 N-terminus is modified at multiple sites. Please see Mckenzie and Puthiyaveetil, bioRxiv May 04 2023. Also, why is modification by only 1O2 considered while superoxide and hydroxide radicals can equally damage D1?

We agree with the possibility that oxidative modifications in other amino acids are also involved in the D1 degradation, as pointed out by the reviewer. We also thank the reviewer for pointing us to the interesting article of Mckenzie and Puthiyaveetil et al. that showed additional oxidations occurred in the D1-Nterminus, which we had yet to be aware of when we submitted our manuscript. It will be interesting to see how these amino acid oxidations work with W14 oxidation on D1 degradation in the future. The oxidation of Trp by 1O2 can serve as a substrate for FtsH, as in the case of EX1, so we focused on the analysis of Trp oxidation. Single oxygen is believed to be the potential reactive species of Trp oxidation. However, the detected oxidative modifications in this study were not exactly sure depended on singlet oxygen. Thus, we changed several sentences that mention tryptophan oxidation by single oxygen.

4) The D1 degradation assay seems not repeatable for the W14F mutant. High light minus CAM results in Fig. 3 shows a statistically significant decrease in D1 levels for W14F at multiple time points but the same assay in Fig. 4a does not produce a statistically significant decrease at 90 min of incubation. Why is this? Accelerated D1 degradation in the Phe mutant under high light is key evidence that the authors cite in support of their hypothesis.

In Fig. 4a, the p-value comparing the D1 level at 90 min between control and W14F was 0.1075. This value is slightly larger than 0.1. The result that one of the control experiments showed a decrease in D1 level relative to 0 h might cause this value. Given that the D1 level of the remaining three of the four replicates was unchanged in the control experiments, it can be considered an outlier. We believe the results do not affect our hypothesis that the earlier D1 degradation is occurred in W14F.

5) The description of results at times is not nuanced enough, for e.g. lines 116-117 state "The oxidation levels in Trp-14 and Trp-314 increased 1.8-fold and 1.4-fold in var2 compared to the wild type, respectively (Fig. 1c)" while an inspection of the figure reveals that modification at W314 is significant only for NFK and not for KYN and OIA.

In this sentence, we described the result that is compared with the oxidized peptide levels calculated from all Trp-oxidized derivatives. However, as pointed out by the reviewer, it was not correct to explain the result of Fig.1C. We corrected the sentence following the reviewer's suggestion as below;“The levels of Trp-oxidized derivatives, OIA, NFK, and KYN in Trp-14 and the level of KYN in Trp-314 were significantly increased in var2 compared to the wild type, respectively (Fig. 1c). "

Likewise, the authors write that CP43 mutant W353F has no growth phenotype under high light but Figure S6 reveals otherwise. The slow growth of this mutant is in line with the earlier observation made by Anderson et al., 2002.

As pointed out by the reviewer, the growth of W353F seems to be a little slow under HL. We have changed our description of the result part. However, we still conclude that CP43 had little impact on the PSII repair, because the impaired growth in W353F is not as severe as those in W14F and W14F/W317F under HL

In lines 162-163, the authors talk about unchanged electron transport in some site-directed mutants and cite Fig. 2c but this figure only shows chl fluorescence trace and nothing else.

We agreed with the reviewer's suggestion and changed the sentence. In this study, we did not perform detailed photosynthetic analysis. Based on the analysis of phototrophic growth, oxygen-evolving activity, and Chl fluorescence, we concluded that overall photosynthetic activity was not a significant difference in the mutants.

6) The authors rightly discuss an alternate hypothesis that the simple disassembly of the monomeric core into RC47 and CP43 alone may be sufficient for selective D1 degradation as in cyanobacteria. This hypothesis cannot yet be ruled out completely given the lack of some in vitro degradation data as mentioned in point 2. Oxidative protein modification indeed drives the disassembly of the monomeric core (Mckenzie and Puthiyaveetil, bioRxiv May 04 2023).

Thanks for your suggestion. We added a discussion of PSII disassembly by ROS-induced oxidation to the discussion part, and the reference is added.

Reviewer #3 (Public Review):

Light energy drives photosynthesis. However, excessive light can damage (i.e., photo-damage) and thus inactivate the photosynthetic process. A major target site of photo-damage is photosystem II (PSII). In particular, one component of PSII, the reaction center protein, D1, is very suspectable to photo-damage, however, this protein is maintained efficiently by an elaborate multi-step PSII-D1 turnover/repair cycle. Two proteases, FtsH and Deg, are known to contribute to this process, respectively, by efficient degradation of photo-damaged D1 protein processively and endoproteolytically. In this manuscript, Kato et al., propose an additional step (an early step) in the D1 degradation/repair pathway. They propose that "Tryptophan oxidation" at the N-terminus of D1 may be one of the key oxidations in the PSII repair, leading to processive degradation of D1 by FtsH. Both, their data and arguments are very compelling.

The D1 protein repair/degradation pathway in its simplest form can be defined essentially by five steps: (1) migration of damaged PSII core complex to the stroma thylakoid, (2) partial PSII disassembly of the PSII core monomer, (3) access of protease degrading damaged D1, (4) concomitant D1 synthesis, and (5) reassembly of PSII into grana thylakoid. An enormous amount of work has already been done to define and characterize these various steps. Kato et al., in this manuscript, are proposing a very early yet novel critical step in D1 protein turnover in which Tryptophan(Trp) oxidation in PSII core proteins influences D1 degradation mediated by FtsH.

Using a variety of approaches, such as mass-spectrometry (Table 1), site-directed mutagenesis (Figures 2-4), D1 degradation assays (Figures 3, and 4), and simulation modeling (Figure 5), Kato et al., provide both strong evidence and reasonable arguments that an N-terminal Trp oxidation may be likely to be a 'key' oxidative post-translational modification (OPTM) that is involved in triggering D1 degradation and thus activating the PSII repair pathway. Consequently, from their accumulated data, the authors propose a scenario in which the unraveling of the N-terminal of the D1 protein facilitated by Trp oxidation plays a critical 'recognition' role in alerting the plant that the D1 protein is photo-damaged and thus to kick start the processive degradation pathway initiated possibly by FtsH. Coincidently, Forsman and Eaton-Rye (Biochemistry 2021, 60, 1, 53-63), while working with the thermophilic cyanobacterium, Thermosynechococcus vulcanus, showed that when the N-terminal DE-loop of the D1 protein is photo-damaged that occurs which may serve as a signal for PSII to undergo repair following photodamage. While the activation of the processive degradation pathways in Chlamydomonas versus Thermosynechococcus vulcanus have significant mechanistic differences, it's interesting to note and speculate that the stability of the N-terminal of their respective D1 proteins seems to play a critical role in 'signaling' the PSII repair system to be activated and initiate repair. But it's complicated. For instance, significant Trp oxidation also occurs on the lumen side of other PSII subunits which may also play a significant role in activating the repair processes as well. Indeed, Kato et al.,( Photosynthesis Research volume 126, pages 409-416 (2015)) proposed a two-step model whereby the primary event is disruption of a Mn-cluster in PSII on the lumen side.

A secondary event is damage to D1 caused by energy that is absorbed by chlorophyll. But models adapt, change, and get updated. And the data provided by Kato et al., in this manuscript, gives us a unique glimpse/snapshot into the importance of the stability of the N-terminal during photo-damage and its role in D1-turnover. For instance, the author's use site-directed mutagenesis of Trp residues undergoing OPTM in the D1 protein coupled with their D1 degradation assays (Figure 3 and 4), provides evidence that Trp oxidation (in particular the oxidation of Trp14) in coordination with FtsH results in the degradation of D1 protein. Indeed, their D1 degradation assays coupled with the use of a ftsh mutant provide further significant support that Trp14 oxidation and FtsH activity are strongly linked. But for FstH to degrade D1 protein it needs to gain access to photo-damaged D1. FtsH access to D1 is achieved by having CP43 partially dissociate from the PSII complex. Hence, the authors also addressed the possibility that Trp oxidation may also play a role in CP43 disassembly from the PSII complex thereby giving FtsH access to D1. Using a site-directed mutagenesis approach, they showed that Trp oxidation in CP43 appeared to have little impact on the PSII repair (Supplemental Figure S6). This result shows that D1-Trp14 oxidation appears to be playing a role in D1 turnover that occurs after CP43 disassembly from the PSII complex. Alternatively, the authors cannot exclude the possibility that D1-Trp14 oxidation in some way facilitates CP43 dissociation. Further investigation is needed on this point. However, D1-Trp14 oxidation is causing an internal disruption of the D1 protein possibly at the N-terminus of the protein. Consequently, the role of Trp14 oxidation in disrupting the stability of the N-terminal domain of the D1 protein was analyzed computationally. Using a molecular dynamics approach (Figure 5), the authors attempted to create a mechanistic model to explain why when D1 protein Trp14 undergoes oxidation the N-terminal domain of D1protein becomes unraveled. Specifically, the authors propose that the interaction between D1 protein Trp14 with PsbI Ser25 becomes disrupted upon oxidation of Trp14. Consequently, the authors concluded from their molecular dynamics simulation analysis that " the increased fluctuation of the first α-helix of D1 would give a chance to recognize the photo-damaged D1 by FtsH protease". Hence, the author's experimental and computational approaches employed here develop a compelling early-stage repair model that integrates 1) Trp14 oxidation, 2) FtsH activation and 3) D1- turnover being initiated at its N-terminal domain. However, a word of caution should be emphasized here. This model is just a snapshot of the very early stages of the D1 protein turnover process. The data presented here gives us just a small glimpse into the unique relationship between Trp oxidation of the D1 protein which may trigger significant N-terminal structural changes of the D1 protein that both signals and provides an opportunity for FstH to begin protease digestion of the D1 protein.

However, the authors go to great lengths in their discussion section to not overstate solely the role of Trp14 oxidation in the complicated process of D1 turnover. The authors certainly recognize that there are a lot of moving parts involved in D1 turnover. And while Trp14 oxidation is the major focus of this paper, the authors show in Supplemental Fig S4 the structural positions of various additional oxidized Trp residues in the Thermosynecoccocus vulcans PSII core proteins. Indeed, this figure shows that the majority of oxidized Trps are located on the luminal side of PSII complex clustered around the oxygen-evolving complex. So, while oxidized Trp14 may be involved in the early stages of D1 turnover certainly oxidized Trps on the lumen side are also more than likely playing a role in D1 turnover as well. To untangle this complex process will require additional research.

Nevertheless, identifying and characterizing the role of oxidative modification of tryptophan (Trp) residues, in particular, Trp14, in the PSII core provides another critical step in an already intricate multi-step process of D1 protein turnover during photo-damage.

We thank reviewer #3 for all the helpful comments and their supportive review of the manuscript.

We thank the reviewer for raising this interesting study that ROS might disrupt the interaction between the PsbT and D1 in Thermosynechococcus vulcanus. The stroma-exposed DE-loop of D1 is one of the possible cleavage sites by Deg protease. Because the D1 cleavage by Deg facilitates the effective D1 degradation by FtsH under high-light conditions, it is interesting to elucidate Deg and FtsH cooperative D1 degradation further. We added this discussion in the manuscript. Other minor comments were also answered in a point-by-point response.

Reviewer #1 (Recommendations For The Authors):

Other minor points

4) L227. How do you eliminate the possibility of reduced stability under high light?

D1 synthesis under HL as pointed out by the reviewer was not tested in this study. Therefore, we can not rule out the possibility of a reduced D1 synthesis rate under HL in the mutant. However, the rate of D1 turnover(coordinated degradation and synthesis) is increased under HL. Since the pulse-labeling experiment is affected D1 degradation as well as D1 synthesis, even if there is a difference in the rate of D1 synthesis under HL, we can not clearly distinguish whether the cause of reduced labeling is the increased D1 degradation seen in the W14F mutant or the delay in D1 synthesis. We thank the reviewer for this valuable comment.

5) Ls25-26. It would be quite rare that P680 directly absorbs light energy.

We changed the sentence.

6) L28. intrinsic antenna? Is this commonly used? core antenna?

Corrected to “core antenna”

7) Ls4143. Because the process is described as step iii), it is curious to mention it again as other critical steps.

We removed the sentence.

8) L75. Is it correct? Do you mean damage is caused by inhibition?

We changed the sentence to “…the disorder of photosynthesis…”

9) Figure 1c. +4, +16 and +32 should be explained in the legend.

We added the explanation in the legend.

10) Supplementary Figures S1 and S2. Title. Is it true that oxidation depends on singlet oxygen? This is a question. If it is not experimentally proved, modify the expression.

In general, singlet oxygen (1O2) is believed to contribute in vivo oxidation of Trp. However, as suggested, these detected oxidative modifications were not exactly sure depends on singlet oxygen. Thus, we changed the title of Fig S1 and S2.

11) Figure 3. Correct errors in + or - in the Figure.

Corrected

12) L328. Cyc > Cys.

Corrected

Reviewer #2 (Recommendations For The Authors):

1) A few suggestions on typos and style:

• Lines 2-3, please rephrase the sentence. The meaning is unclear.

rephased the sentence to “Photosynthesis is one of the most …”

• Lines 28-29, "Despite its orchestrated coordination...". Tautology.

We changed the sentence.

• Line 31, "...one, known as the PSII repair...". Please rewrite.

We followed the reviewer suggestion and changed the sentence to “…synthesized one in the PSII repair.”

• Line 49, "Their family proteins...". Rephrase.

Rephrased the words.

• Lines 64-66, please rewrite. I am not sure what the authors imply here. Are they talking about FtsH turnover or regulation of FtsH at the protein or gene level?

FtsH itself is also degraded under high-light stress. To compensate for this, ftsH gene expression is upregulated and contributes to the proper FtsH level in thylakoid membranes. We rewrote the sentence as follows “increased turnover of FtsH is crucial for their function under high-light stress. That is compensated by upregulated FtsH gene expression”.

• Line 68, "...to dislocate their substrates..."

We changed the sentence to “to pull their substrates and push them into the protease chamber by ATPase activity”

• Line 86, N-formylkymurenine => N-formylkynurenine

Corrected

• Lines 111-112, "Consistent with previous results...". Please specify which studies are being referred to and cite them if relevant.

We added references.

• Line 114, "...in extracts Arabidopsis..." => "...in extracts of Arabidopsis...".

Corrected

• Line 171, "influences in high-light sensitivity." Please rephrase.

We rephrased the sentence.

• Line 192, Fv/Fm. "v" and "m" should be subscripts.

Corrected

• Line 210, "...encounters...". Unclear meaning.

We rephrased the sentence.

• Line 358, hyphen usage. "fine-tuned". This sentence should be rewritten to make the role of phosphorylation clear. "Fine-tuning" is vague.

We changed the sentence to “…spatiotemporal regulation of D1 degradation”

• Fig. 6 legend, luminal => lumenal

Changed to luminal

2) The statistical notation used for some results is confusing. In Fig. 6b, "*" stands for p = {less than or equal to}0.1 while in fig. 4 it denotes p = {less than or equal to}0.05. If this is not a typo, this usage deviates from the standard one. How is a D2 change in Fig. 6b significant given its p value of {less than or equal to}0.1? The Fig. 6b key for D2 does not correspond with the histogram pattern.

Thank you for your comments and suggestions. The asterisk in the Figure 6b is not a typo. We revised p value sign for less than 0.05 with a single asterisk to avoid confusion. While the case of p value in less than 0.1, we applied section sign “§” instead of the single asterisk sign to avoid confusion. Generally accepted p value to indicate statistically difference is less than 0.05. We found that D1 was p = 0.03322 and D2 was p = 0.07418. As we suspect these p value differences, the results for D2 protein detection were somewhat fluctuating while not in D1 protein detection as you commented. Still the reason of the fluctuating result of D2 signal intensity is not clear yet, we found the p value was between 0.05 and 0.10. We also rewrite the description in the corresponding result part.

3) There are no error bars in Fig. 5d while the error bars in Fig. 5e show that there are no significant differences between Cβ distances of W14F and W14ox with WT contrary to the authors' assertion in the text (lines 254-255).

The reason that there are no error bars in Fig. 5d. is because the fluctuation value in Fig. 5d was calculated from the entire trajectory (i.e., all snapshots) of the MD simulation. In contrast, the Cβ-Cβ distance value can be obtained at each individual snapshot of the simulation. Thus, Fig. 5e shows the averaged distances with the standard deviations (the error bars) over all these snapshots. To prevent any confusion for the reader, we have explicitly described “averaged Cβ-Cβ distance” and added an explanation of the error bars in the caption of Fig. 5e. It is important to note that our focus in the text (lines 254-255) was not on comparing the Cβ-Cβ distance of W14F with that of W14ox but the distance of W14F or W14ox with that of WT.

4) Figure 3 legends and figure labels do not correspond. Fig. 3b should be labeled as High light - Chloramphenicol and likewise, fig 3c should read growth light + Chloramphenicol to be consistent with the legend.

Corrected

5) How are OPTM levels of D1 Trp residues normalized? Is it against unmodified peptides or total proteins?

Oxidation levels of three oxidative variants of Trp in Trp14 and Trp317 containing peptides were obtained by label-free MS analysis. Fig.1 shows the intensity values of oxidized variants of Trp14 and Trp317. In this analysis, the levels of unoxidized peptides were not significantly changed between var2 and WT.

6) Fig. 1a cartoon might need work. It looks like the oxygen atom in OIA is misplaced.

Corrected

Reviewer #3 (Recommendations For The Authors):

In regard to Table 1, the sequence of the mass spectra fragment listed for Trp14 (i.e., ENSSL(W)AR ) in Table 1 is different from the sequence of the mass spectra fragment of Trp14 shown in Supplemental Figure S1 (i.e., ESESLWGR). Likewise, the sequence of the mass spectra fragment listed for Trp317 (i.e., VLNT(W)ADIINR ) in Table 1 is different from the sequence of the mass spectra fragment of Trp14 shown in Supplemental Figure S2 (i.e., VINTWADIINR). This discrepancy, I think can be simply explained.

Table 1 shows the newly detected peptide of Trp oxidation in PSII core protein in Chlamydomonas. On the other hand, Figures S1 and S2 are the results of MS analysis used for the level of Trp oxidation analysis in Arabidopsis var2 mutant, as shown in Fig. 1C. To avoid confusion, we added in the supplemental figure title that it was detected in Arabidopsis.

Labeling: In Figure 3, the figure legend states that b, high-light in the absence of CAM; but panel b, shows +CAM conditions. I think this labeling is incorrect and needs to be -CAM. Likewise, the figure legend states that c, growth-light in the presence of CAM. I think this labeling is incorrect and needs to be +CAM.

Corrected

This reviewer has a few comments/suggestions on the presentation of the sequence alignments showing the various positions of oxidized Trps within the D1(Figure 1), D2 and CP43 (Supplemental Figure S3) and CP47 (Supplemental Figure S3):

The authors should consider highlighting in red all the various Trps shown in Table 1 with the corresponding alignments shown in Figure 1 for D1 protein and corresponding alignments in Supplemental Figure S3 (for D2 and CP43) and Supplemental Figure S3 continued (For CP47). Highlighting the locations of oxidized Trps across various species is very informative but as presented here the red labeling somewhat is haphazard, confusing and thus these figures lose some of their impact factor. For instance, in Supplementary Fig. S4, the reader can visualize the structural positions of oxidized Trp residues in the Thermosynecoccocus vulcanus PSII core proteins. When one then looks at the various alignments presented by the authors, one can see that other species have a similar arrangement of oxidized Trp residues as well. Consequently, when you now collectively look at the data presented in Table 1, Figure 1, Supplemental Figure S3 and Supplemental Figure S4, a picture emerges that illustrates how common the phenomenon of overall Trp oxidation is and more specifically how oxidized Trp14 across species is playing a similar role in possibly activating D1 turnover. I think these Figures, if presented in a more comprehensive and unified fashion, will really add to the paper.

Thank you for your suggestion. In this study, we tried to show the identified oxidized Trp by the MS-MS analysis, the residue conservation in the sequences, and its position in the structure. Since we have to show a lot of information, combining them into one figure is difficult. We hope you understand the reason for this.

Author Response

The following is the authors’ response to the previous reviews.

We are grateful for the helpful comments of both reviewers and have revised our manuscript with them in mind.

One of the main issues raised was that readers may by default assume that our models are correct. We in fact made it very clear in our discussion that the models are merely hypotheses that will need testing by “wet” experiments and we do not therefore agree that even readers unfamiliar with AF would assume that the models must be correct. It was also suggested that readers could be reassured by including extensive confidence estimates such as PAE plots. As it happens, every single model described in the manuscript had reasonably high PAE scores and more crucially the entire collection of output files, including PAE data, are readily accessible on Figshare at https://doi.org/10.6084/m9.figshare.22567318.v2, a fact that the reviewers appear to have overlooked. The Figshare link is mentioned three times in the manuscript. Embedding these data within the manuscript itself would in our view add even more details and we have therefore not included them in our revised manuscript. Likewise, it is rather simple for any reader to work out which part of a PAE matrix corresponds to an interaction observed in the corresponding pdb prediction. Besides which, it is our view that the biological plausibility and explanatory power of models is just as important as AF metrics in judging whether they may be correct, as is indeed also the case for most experimental work.

Another important point was that the manuscript was too long and not readable. Yes, it is long and it could well be argued that we could have written a different type of manuscript, focusing entirely on what is possibly the simplest and most important finding, namely that our AF models suggest that in animal cells Wapl appears to form a quarternary complex with SA, Pds5, and Scc1 in a manner suggesting that a key function of Wapl’s conserved CTD is to sequester Scc1’s Nterminal domain after it has dissociated from Smc3. For right or for wrong, we decided that this story could not be presented on its own but also required 1) an explanation for how Scc1 is induced to dissociate from Smc3 in the first place and 2) how to explain that the quarternary complex predicted for animal cells was not initially predicted for fungi such as yeast. The yeast situation was an exception that clearly needed explaining if the theory was to have any generality and it turned out that delving into the intricate details of the genetics of releasing activity in yeast was eventually required and yielded valuable new insights. We also believe that our work on the recruitment of Eco/Esco acetyl transferases to cohesin and the finding that sororin binds to the Smc3/Scc1 interface also provided important insight into how releasing activity is regulated. We acknowledge that the paper is indeed long but do not think that it is badly written. It is above all a long and complex story that in our view reveals numerous novel insights into how cohesin’s association with chromosomes is regulated and have endeavoured to eliminate any excessive speculation. We feel it is not our fault that cohesin uses complex mechanisms.

Notwithstanding these considerations, we have in fact simplified a few sections and removed one or two others but acknowledge that we have not made substantial cuts.

It was pointed out that a key feature of our modelling, namely the predicted association of Wapl’s C-terminal domain with SA/Scc3’s CES is inconsistent with published biochemical data. The AF predictions for this interface are universally robust in all eukaryotic lineages and crucially fully consistent with published and unimpeachable genetic data. We note that any model that explains all findings is bound to be wrong for the very simple reason that some of these findings will prove to be incorrect. There is therefore an art in Science of judging which data must be explained and accommodated and which should be ignored. In this particular case, we chose to ignore the biochemistry. Time will tell whether our judgement proves correct.

Last but not least, it was suggested that we might provide some experimental support for our proposed SA/Scc3-Pds5-Scc1-WaplC quaternary complex. We are in fact working on this by introducing cysteine pairs (that can be crosslinked in cells) into the proposed interfaces but decided that such studies should be the topic of a subsequent publication. It would be impossible with the resources available to our labs to follow up all of the potential interactions and we therefore decided to exclude all such experiments.

We are grateful for the detailed comments provided by both reviewers, many of which were very helpful, and in many but not all cases have amended the manuscript accordingly.

With regard to the more specific comments:

Reviewer #1 (Recommendations For The Authors):

1) One concern is that observed interfaces/complexes arise because AF-multimer will aim to pack exposed, conserved and hydrophobic surfaces or regions that contain charge complementarity. The risk is that pairwise interaction screens can result in false positive & non-physiological interactions. It is therefore important to report the level of model confidence obtained for such AF calculations:

A) The authors should color the key models according to pLDDT scores obtained as reported by AF. This would allow the reader to judge the estimated accuracy of the backbone and side chain rotamers obtained. At least for the key models and interactions it would be important to know if the pLDDT score is >90 (Correct backbone and most rotamers) or >70 (only backbone is correct).

B) It would also be important to report the PAE plots to allow estimation of the expected position error for most of the important interactions. pLDDT coloring and PEA plots can be shown side-by-side as shown in other published data (e.g. https://pubmed.ncbi.nlm.nih.gov/35679397/ (Supplementary data)

C) The authors should include a Table showing the confidence of template modeling scores for the predicted protein interfaces as ipTM, ipTM+pTM as reported by AlphaFold-multimer. Ideally, they would also include DockQ scores but this may not be essential. Addition of such scores would help classification into Incorrect, Acceptable or of high quality. For example, line 1073 et seq the authors show a model of a SCC1SA and ESCO1 complex (Fig. 37). Are the modeling scores for these interfaces high? It does not help that the authors show cartoons without side chains? Can the authors provide a close-up view of the two interfaces? Are the amino acids are indeed packed in a manner expected for a protein interface? Can we exclude the possibility that the prediction is obtained merely because the sequence segments (e.g. in ESCO1 & ESCO2) are hydrophobic and conserved?

We do not agree that including this level of detail to the text/figures of the manuscript would be suitable. All the relevant data for those who may be sceptical about the models are readily available at https://doi.org/10.6084/m9.figshare.22567318.v2. In our view, the cartoon versions of the models are easier for a reader to navigate. Anyone interested in the molecular details can look at the models directly.

Importantly, no amount of statistical analysis can completely validate these models. What is required are further experiments, which will be the topic of further work from our and I dare from other laboratories.

D) When they predict an interaction between the SA2:SCC1 complex and Sororin's FGF motif, they find that only 1/5 models show an interaction and that the interaction is dissimilar to that seen of CTCF. Again, it would be helpful to know about modeling scores. Can they show a close-up view of the SORORIN FGF binding interface to see if a realistic binding mode is obtained? Can they indicate the relevant region on the PAE plot?

Given that AF greatly favours other interactions of Sororin’s FGF motif over its interaction with SA2-Scc1, we do not agree that dwelling on the latter would serve any purpose.

2) Line 996: AF predicts with high confidence an interaction between Eco1 & SMC3hd. What are the ipTM (& DockQ if available) scores. Would the interface score High, Medium or Acceptable?

As mentioned, see https://doi.org/10.6084/m9.figshare.22567318.v2.

3) Line 1034 et seq: Eco1/ESCO1/ESCO2 interaction with PDS5. Interface scores need to be shown to determine that the models shown are indeed likely to occur. If these interactions have low model confidence, Fig. 36 and discussion around potential relevance to PDS5-Eco1 orientation relative to the SMC3 head remains highly speculative and could be expunged.

See https://doi.org/10.6084/m9.figshare.22567318.v2. It should be clear that the predictions are very similar in fungi and animals. Crucially, we know that Pds5 is essential for acetylation in vivo, so the models appear plausible from a biological point of view.

4) Considering the relatively large interface between ECO1 and SMC3, would the author consider the possibility that in addition to acetylating SMC3's ATPase domain, ECO1 remains bound to cohesin-DNA complex, as proposed for ESCO1 by Rahman et al (10.1073/pnas.1505323112)?

This is certainly possible but we would not want to indulge in such speculation.

5) E.g. Line 875 but also throughout the text: As there is no labeling of the N- and C-termini in the Figures, is frequently unclear what the authors are referring to when they mention that AF models orient chains in a certain manner.

Good point. This has been amended. However, the positions of N- and C- is all available at https://doi.org/10.6084/m9.figshare.22567318.v2.

6) Fig19B: PAE plots: authors should indicate which chains correspond to A, B, C. Which segment corresponds to the TYxxxR[T/S]L motif? Can they highlight this section on the PAE plot?

Good point and amended in the revised manuscript.

Minor comments:

1) Line 440: the WAPL YSR motif is not shown in Fig. 14A

2) Line 691: Scc3 spelling error.

3) Line 931: Sentence ending '... SCC3 (SCC3N).' requires citation.

4) Line 1008: Figure reference seems wrong. It should read: Fig. 34A left and right. Fig. 34B does not contain SCC1.

Many thanks for spotting these. Hopefully, all corrected.

5) Fig. 41 can be removed as it shows the absence of the interaction of Sororin with SMC1:SCC1. Sufficient to mention in the text that Sororin does not appear to interact with SMC1:SCC1.

This is possible but we decided to leave this as is.

Reviewer #2 (Recommendations For The Authors):

Minor points

(1) Are there any predicted models in which one of the two dimer interfaces of the hinge is open when the coiled coils are folded back, as seen in the cryo-EM structure of human cohesin-NIPBL complex in the clamped state?

No AF runs ever predicted half opened hinges. It is possible that the introduction of mutations in one of the two interfaces might reveal a half-opened state and we ought to try this. However, it would not be appropriate for this manuscript, we believe.

(2) Structures of the SA-Scc1 CES bound to [Y/F]xF motifs from Sgo1 and CTCF have been reported, suggesting that a similar motif could interact with SA/Scc3. Surprisingly, AF did not predict an interaction between Scc3/SA and Wapl FGF motifs, which only bind to the Pds5 WEST region. On the other hand, AF predicted interactions of the Sororin FGF motif with both Pds5 WEST and SA CES. Can the authors comment on this Wapl FGF binding specificity? What will happen if a Wapl fragment lacking the CTD is used in the prediction?

This seems to be an academic point as the CTD is always present.

Author Response

The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review):

The study as a concept is well designed, although there are two issues I see in the methodology (these may be just needing further explanation or if I am correct in my interpretation of what was done, may need reanalysis to take into account). Both issues relate to the data that was extracted from the published literature on zoonotic malaria prevalence in the study area.

1) No limit was set on the temporal range

With no temporal limit on the range of studies, the landscape in many cases will have changes between the study being conducted and the spatial data. This will be particularly marked in areas where there has been clearing since the zoonotic malaria prevalence study. Also, population changes (either through population growth, decline or movement) will have occurred. All research is limited in what it can do with the available data, so I realise that there may not be much the authors can do to correct this. One possible solution would be to look at the land use change at each site between the prevalence study and the remote sensing data. I'm not sure if this is feasible, but if it is I would recommend the authors attempt this as it will make their results stronger.

Thank you for the comments. We agree that matching the date of remote sensing data to samples is particularly important for environmental variables that change rapidly (such as forest loss). To clarify, no limit was set on the date range of the studies identified from the literature to ensure no articles were excluded due to arbitrary date restrictions. We have edited the manuscript to clarify this (line 422). Regarding landscape and environmental features, remote sensing data was extracted annually for every year for the full date range of the data (see Table 1 and S11, annual temporal resolution from 2006 to 2020). Forest was then matched contemporaneously (see lines 467–473) meaning that, insofar as it was possible, forest data was extracted for the same year as the data was collected. Where a date range was given for the primate data, the mean year was used. For human population density, covariate data were extracted for multiple years but were found to be relatively stable over the time period for the sites covered, so median year was used (see Supplementary Information, Appendix E and Table S11). Elevation is stable and typically only one time point is used as reference (in this instance the SRTM 90m Digital Elevation model, 2003).

2) Most studies only gave a geographic area or descriptive location.

The spatial analysis was based on a 5km and 20km radius of the 'study site' location, but for many of the studies the exact site is not known. Therefore the 'study site' was artificially generated using a polygon centroid. Considering that the polygon could be an administrative boundary (i.e., district/state/country), this is an extremely large area for which a 5km radius circle in the middle of the polygon is being taken as representative of the 'study site'. This doesn't make sense as it assumes that the landscape is uniform across the district, which in most cases it will not be (in rural areas it is going to be a mixture of villages, forest, plantation, crops etc which will vary across the landscape). This might just be a case of misunderstanding what was done (in which case the text needs rewording to make it clearer) or if I have interpreted it correctly the selection of the centroid to represent the study area does not make sense. I am not sure how to overcome this as it probably not possible to get exact locations for the study sites. One possibility could be to make the remote sensing data the same scale as the prevalence data ie if the study site is only identifiable at the polygon level, then the remote sensing data (fragmentation, cover and population) is used at the polygon level.

Both these issues could have an impact on the study's findings. I would think that in both cases it might make the relationship between the environmental variables and prevalence even clearer.

We would like to thank the reviewer for their concerns and provide some clarification on the methods used to extract environmental variables:

• Centroid was initially explored, but not pursued for the same concerns raised by the reviewer. Taking the centroid would be arbitrary and the central point of a large polygon is not likely to be representative of habitat across the entire sampling area and introduces error so this was not pursued(Cheng et al., 2021). We have clarified the wording in the manuscript with reference to centroids to avoid confusion on this point (line 491).

• We demonstrate a method to account for the lack of precise geolocation by taking 10 ‘pseudo-sampling’ points instead of a single random location, with environmental variables extracted at 5, 10 and 20km for each site (lines 487-500). By including 10 environmental realisations, surveys conducted in smaller or more uniform landscapes will have more consistent covariates and this will lend more weight to the model. Conversely, samples taken from large administrative polygons are likely to be highly variable, and these associations will have less representation in the final model. This approach was used to demonstrate an alternative to using a single arbitrary site to represent the area.

To further support the validity of this technique:

• Figures illustrating the variance of the environmental variables across the 10 sampling sites at 5, 10 and 15km for GADM administrative classifications at country level (GID0), state (GID1), district (GID2) and exact coordinates (GPS) are now included in the SI (Figure S12).

• Sensitivity analyses were conducted, in which final GLMM models were fit again but using only acceptable levels of variance in environmental variables and/or acceptable size of administrative boundary (Table S15 and S16). In sensitivity analyses, forest cover and fragmentation retained a significant effect on prevalence of P. knowlesi in macaques, suggesting this effect is robust to spatial uncertainty.

We would also like to highlight that the main finding of this research is the novel synthesis of regional prevalence of P. knowlesi in simian reservoirs across Southeast Asia, which was formerly assumed to be ubiquitous high prevalence, and which can now be used to inform regionally specific transmission modelling, better estimate spatial risk and parameterise early warning systems for P. knowlesi malaria in countries approaching elimination of human malarias. The risk factor analysis here is provided to begin to understand what may be driving this geographic heterogeneity in P. knowlesi prevalence at finer scales and demonstrate methods that could be used to accommodate spatial uncertainty in secondary data. We appreciate that this may not have been clear and have edited the manuscript accordingly.

Reviewer #2 (Public Review):

This is the first comprehensive study aimed at assessing the impact of landscape modification on the prevalence of P. knowlesi malaria in non-human primates in Southeast Asia. This is a very important and timely topic both in terms of developing a better understanding of zoonotic disease spillover and the impact of human modification of landscape on disease prevalence.

This study uses the meta-analysis approach to incorporate the existing data sources into a new and completely independent study that answers novel research questions linked to geospatial data analysis. The challenge, however, is that neither the sampling design of previous studies nor their geospatial accuracy are intended for spatially-explicit assessments of landscape impact. On the one hand, the data collection scheme in existing studies was intentionally opportunistic and does not represent a full range of landscape conditions that would allow for inferring the linkages between landscape parameters and P. knowlesi prevalence in NHP across the region as a whole. On the other hand, the absolute majority of existing studies did not have locational precision in reporting results and thus sweeping assumptions about the landscape representation had to be made for the modeling experiment. Finally, the landscape characterization was oversimplified in this study, making it difficult to extract meaningful relationships between the NHP/human intersection on the landscape and the consequences for P. knowlesi malaria transmission and prevalence.

Thank you for the feedback on the manuscript. We agree that the data was not originally intended for spatial assessment of landscape impact nor represents a full range of landscape conditions across the region. However, we would like to highlight the first set of results from the meta-analysis. Here, the synthesis of all available data allows for the detection of regional disparities and geographic heterogeneity of prevalence in host species, which individual small-scale opportunistic studies are not powered to do, and which had not been identified before this investigation.

In this context, the risk factor analysis is an exploratory analysis to understand what may be driving the observed geographic variation at broad scales as well as provide a framework for dealing with spatial uncertainty. Landscape data was extracted at a level deemed appropriate given the limitations of the data. The majority were geolocated to district level and sensitivity analysis showed a reasonable consistency of landscape features at our chosen scales (Table S8, Figure S12A). To address some of these concerns, we conducted further analysis to explore the deviation of environmental covariates in each sampling area and ran sensitivity analysis by removing extremely variable datapoints (Table S15 and Table S16). When removing highly uncertain data and/or countrylevel data, effects of canopy cover on non-human primate malaria prevalence is retained, supporting the original findings.

Despite many study limitations, the authors point to the critical importance of understanding vector dynamics in fragmented forested landscapes as the likely primary driver in enhanced malaria transmission. This is an important conclusion particularly when taken together with the emerging evidence of substantially different mosquito biting behaviors than previously reported across various geographic regions.

Another important component of this study is its recognition and focus on the value of geospatial analysis and the availability of geospatial data for understanding complex human/environment interactions to enable monitoring and forecasting potential for zoonotic disease spillover into human populations. More multi-disciplinary focus on disease modeling is of crucial importance for current and future goals of eliminating existing and preventing novel disease outbreaks.

Reviewer #1 (Recommendations For The Authors):

A couple of minor points

1) Was the human density and forest cover correlated? If so was this taken into account

Human density and forest cover at selected scales were not found to be strongly correlated (Spearman’s rank values -0.38 and -0.45 within 5km and 20km buffer radii for human population density respectively).

In selecting variables for inclusion in the final model, we examined variance inflation factors (VIF) to detect and minimise multicollinearity in the model. VIF measures the correlation and strength of correlation between independent predictors. VIF of each predictor variable was examined starting with a saturated model and sequentially excluding the variable with the highest VIF score from the model. Stepwise selection continued until the entire subset of explanatory variables in the global model satisfied a conservative threshold of VIF ≤6 (Rogerson, 2001), which ensures that the remaining variables included in the final model have minimal correlation. Spearman’s correlation matrices for all variables at all scales and final selected variables (below VIF threshold) are included in the Supplementary Information (Figure S13 and Figure S14).

2) Reference (Speldewinde et al., 2019) is down as Davidson et al. in the reference list

Thank you for the thoroughness in this review. There are two similar but separate references, both published in 2019 with the same co-authors, and the (Speldewinde et al, 2019) was incorrectly referenced. They should be (Davidson et al., 2019a) and Davidson et al., 2019b) respectively. This has now been corrected in the manuscript.

Davidson, G., Chua, T.H., Cook, A. et al. Defining the ecological and evolutionary drivers of Plasmodium knowlesi transmission within a multi-scale framework. Malar J 18, 66 (2019). https://doi.org/10.1186/s12936-019-2693-2

Davidson G, Chua TH, Cook A, Speldewinde P, Weinstein P. The Role of Ecological Linkage Mechanisms in Plasmodium knowlesi Transmission and Spread. Ecohealth. 2019;16(4):594-610. https://doi:10.1007/s10393-019-01395-6

Reviewer #2 (Recommendations For The Authors):

Line 143: "We hypothesise that higher prevalence of P. knowlesi in primate host species is driven by landscape change..." without specifying here the kind of landscape change (e.g. "forest degradation and fragmentation") it is virtually impossible to confirm or reject this hypothesis.

We agree that the wording of the hypotheses needed to be more specific. We have edited lines 142 – 145 to specify forest fragmentation as our landscape variable of interest, and to more explicitly include the regional meta-analysis of P. knowlesi prevalence.

Table 1 vs Table S11 discrepancy regarding spatial resolution of Forest cover and fragmentation variables. The original dataset resolution is 30m but I don't think one can compute a PARA index at 30 m since it really requires a polygon that is larger than the single value pixel. Table S11 indicates a 30 km gridcell with some postprocessing of the original datasets.

We appreciate this being identified. The resolution refers to the input layer (tree canopy cover, 30m). PARA was calculated from the binary forest cover layer (30m resolution) within each buffer radii 5, 10 and 20km. We have edited both Table 1 and Table S11 to help clarify this.

It would be very helpful if you provided justification for selecting specific metrics to represent the key landscape variables. How are these particular landscape variables relevant? Why not other land cover/land use components?

We have now included a paragraph in the Supplementary Information (Appendix D) to explain the choice of environmental covariates. Elevation was chosen as an important proxy for vector distribution (but was not retained in model selection). Human population density was chosen as a measure of proximity to human settlement, rather than relying on qualitative assessment of rural/peri-urban/urban. Tree canopy cover and fragmentation indices are key determinants of primate habitat selection and of vector breeding habitat, and justification for the use of perimeter: area ratio is included in the methods section (section beginning line 462).

I think the other issues present substantial weaknesses that you cannot address without redoing the study. I will list those below just for reference.

1) If the forest is so dominant (which I would agree with based on my understanding of macaque ecology), how does it make sense to select completely random points (especially at the country or even state level) to represent landscape covariates? At a minimum, I would suggest getting random points within the forest or better yet forest edge habitat. But even then, I doubt that these points would be at all representative of the conditions of a specific study. The geospatial uncertainty is just too large. The dataset simply doesn't support the analysis that is attempted here.

On the point of selecting from only within forest: forest is a dominant habitat, but Long-tailed macaques are anthropophilic and not exclusively found in forest (Stark et al., 2019), and a proportion of the more opportunistic and nuisance samples caught were found in areas more associated with human activity (Li et al., 2021). As such, random points only within forested areas is also unlikely to capture the true habitat of the primates sampled and selecting only from forested areas would bias the results.

Whilst fully georeferenced samples would be the ideal scenario, the idea behind selecting random points from the sampling polygon is that for smaller areas (with higher spatial certainty), habitat would be more consistent between random points and lend more weight to the final model, whereas large polygons with high uncertainty are likely to vary and lend less weight to the final model. In response to these comments, we have further supported this by running regression models only on samples within a reasonable administrative boundary size and on samples within reasonable threshold of uncertainty (i.e., data points are removed if the deviation of environmental covariates across the 10 random points is so high that the sample is uninformative, or if datapoints can only be geolocated to country-level). In these sensitivity analyses, forest cover and species are retained as factors associated with higher malarial prevalence in non-human primates (Table S15S16).

2) Hansen et al. dataset reflects "tree cover" - which is not the same as "forest cover" since it would also include plantations that are very widely distributed across Southeast Asia. If the animal use of plantations differs from that of natural forests, it will present a large issue for the study.

In this analysis the feature of interest was habitat configuration (fragmentation) and deforestation (forest loss) rather than specific land class. We have defined forest as >50% canopy cover, which considers canopy density given historical forest loss and has precedence in other work (Fornace et al.,, 2016). In addition to importance to macaque ecology, forest (canopy) cover, forest loss and forest edge are noted to be key determinants of vector breeding and vector habitat (Byrne et al., 2021, Chua et al., 2019). For this reason, these are important variables to include in analyses. More specific landscape variables were explored, but the temporal and spatial range of the data precluded fine-scale land classification data. To investigate preliminary links to landscape configuration and habitat fragmentation at broad scales this is felt to be sufficient. We have also amended the manuscript to be more discerning with the use of ‘forest’ to avoid confusion throughout.

3) Tree regrowth in the ecosystems of monsoonal Asia is very rapid. Based on the study description, tree regrowth was not accounted for in the study which could potentially lead to a very large underestimation of tree cover if only tree loss since 2000 was monitored. Again unless there is a reason to assume that macaques do not use young successional forests or use it at a highly reduced rate. Both of these points are acknowledged as limitations at the end of the discussion section but in my opinion they have a very strong impact on the study, making the results non-significant.

This is an interesting suggestion. Macaques do forage in plantations and cultivated landscapes to supplement food, but preferentially roost and range in forest edges and interior forest, though ranging behaviour will be complex and vary across Southeast Asia. In this study the primary interest was in deforestation (forest loss) and fragmentation of old growth forested landscapes, which are key variables both for macaque ecology and for vector breeding sites. Therefore, it was felt that forest loss (transition from >50% canopy cover to <50% canopy cover since 2000) was sufficient to capture this. Ranging behaviour of individual animals and macaque troops would not be captured at this scale, and higher spatial and temporal resolution would be required to characterise relationships with tree regrowth and young plantations which is outside the scope of this study. In all regions, purposeful fine scale follow-up studies would be required to unpick fine scale relationships across a habitat gradient.

I am not 100% sure I understand the geospatial design fully. The pieces are distributed between different subsections and it was challenging to string together the processing chain between subsections of the manuscript and the supplemental information. I would help to add a figure (a flowchart, perhaps?) to the supplemental section that walks through the entire geospatial covariates assembly. E.g.

• GPS location create 5, 10, and 20 km buffers mean elevation, mean population, %(?) Forest, PARA(?) for each buffer - I still don't understand the 30m or 30 km spatial resolution reference for forest and PARA in this context.

This was an error in the table in the Supplementary Information and has been corrected – the forest cover raster has a resolution of 30m, and the perimeter: area ratio is calculated within 5, 10 and 20km buffers.

• landscape covariates receive the full weight (1) in the model. - This is defensible even though not ideal

This is equivalent, but we felt more intuitive, to sampling GPS points x10 and inputting with equal weights to the areal data.

• No GPS location assign to the best identifiable administrative unit (country, state, or district) generate 10 random points within the administrative unit create 5, 10, and 20 km buffers mean elevation, mean population, %(?) Forest, PARA(?) for each buffer landscape covariates from each point receive the proportional weight (0.1) in the model. I do not believe that this approach is representative of macaque habitat/macaque human interaction characterization.

In other examples dealing with spatial uncertainty, the centroid is taken to be representative of an area. This method generates considerable bias and uncertainty – particularly if the uncertainty is not then accounted for by weighting subsequent models (Cheng, 2021). In this exploratory analysis, pseudo-sampling from 10 random sites generates a more realistic generalised environmental realisation than taking a centroid/random point. This was used as an exploratory analysis to explain broad regional trends in prevalence between, which can be used to guide further investigation on fine scale studies which are required to completely describe disease dynamics in specific macaque habitats.

Thank you for this useful suggestion – we have taken this advise and added a flowchart of data processing to the Supplementary Information (Appendix D, Figure S8).

Discussion:

Based on information in Table S4, sampled NHPs were predominantly from human-dominated (peridomestic, agricultural, and urban) landscapes. In forested landscapes, only macaques that live in forest edge habitats were likely sampled in the first place just simply due to extreme challenges in getting to macaques in remote inaccessible areas. There is a very substantial spatial bias in sampling will undoubtedly reflect that fragmented habitat is a key landscape component impacting the prevalence of Pk in NHP, especially as the authors point out in the later part of the discussion, the critical vectors for transmission are also associated with forest edge habitats. High forest fragmentation is also linked to the presence/ increase in migrant human workers (logging or plantation activities) - a population also strongly associated with higher malaria prevalence for a variety of P spp (although I am not aware of studies that are specific to Pk malaria). However, the living conditions for migrant workers have frequently been implicated in higher rates of malaria transmission and thus those could, hypothetically, also contribute to Pk infection rates in NHP. Ultimately, the discussion appears to suggest that the biggest gap in our understanding is within vector ecology and understanding the NHP-vector-human dynamics within local landscape settings. It is an interesting finding. However, my overall conclusion would be that the sampling strategy (both for NHP and geospatial covariates) renders this study as "exploratory" at maximum and that all findings would need to be tested and verified through independent and more rigorously designed studies.

Thank you to the reviewer for a comprehensive assessment. We would first like to highlight the regional meta-analysis, which was one of the main findings. This is a novel result for P. knowlesi literature; being the first demonstration of regional differences in prevalence that correlate to regional hotspots of human incidence, the force of infection from NHP may drive hotspots of P. knowlesi in human populations.

We include a risk factor analysis that suggests a method for dealing with high spatial uncertainty, and an exploratory analysis that finds landscape complexity may be a contributory factor to broad regional heterogeneity. These associations are robust to sensitivity analysis where data with extreme variability in environmental variables is removed (Table S15-S16).

Habitat descriptions in original studies are qualitative, likely subjective, and whilst there is likely to be an important sampling bias there was also evident differences in prevalence between the NHP sampled in different environments from the available data that we have further characterised. Risk factors for human P. knowlesi do include forest loss (reduction in canopy cover) within 5 years and within 2km, as well as contact with macaques and occupations in plantations (Fornace et al., 2014; Fornace et al., 2016). Reverse spillover from humans to NHP is an interesting suggestion, but outside the scope and scale of the study. Given known links of deforestation (forest loss) with human incidence of P. knowlesi and also with increased vector breeding sites (Byrne et al., 2021), this analysis explores whether deforestation is linked to prevalence in reservoir species thus contributing to the force of infection at broad scales.

Author Response:

We are sorry that both eLife and the Reviewers feel that our submitted studies are currently insufficient to support our hypothesis that loss of H2-O function affects thymic Treg selection. As this is the first study directly evaluating loss of H2-O in the thymus we do not feel that we overstated our finding as suggested by Reviewer 1. We hope that a revised version of the manuscript can satisfy the reviewers’ criticisms.

-Reviewer 1 is asking us to address the presumed discrepancies between our previous work (Welsh et al 2020, https://doi.org/10.1371/journal.pbio.3000590) and data from Lee et al. 2021 (https://doi.org/10.4049/jimmunol.2100650) in this current manuscript, which does not report on the development of EAE in DO-KO and DO-WT mice. All experiments here are on naïve mice. As such, we wish to justify our lack of discussion of Lee et al (2021) findings.

Lee et al (2021) reported the effects of DO on both EAE and SLE development, they used mainly H2-Oβ KO mice. As we have never used these CRISPR generated mice, we cannot have a direct in-house comparison. However, we did note that reported disease curve for female H2-Oβ KO mice had a similar trend indicating increased EAE disease development, similar to what we have reported back in our 2020 paper (Welsh et al PLoS Biology). In the single experiment that utilized H2-Oβ KO mice for EAE development, Lee et al found a different disease trend than ours. However, Lee et al (2021)’s tested only 4-5 mice per group in the single experiment and their measurement of the disease development solely relied on visual assessment of the limbs and tail functionality. Our study verified EAE disease development by multiple approached including analyses of MOG-specific tetramer staining of the CNS CD4 lymphocyte infiltrate, and in vivo NIRF whole-body imaging on diseased DO-WT and DO-KO mice using an antibody probe specific to MBP. We had repeated our experiments on the disease development greater than 15 times using 5-8 mice per group. Below is an excerpt from our Results Section of Welsh et al PLoS Biology, clearly explaining how many experiments were performed and the number of mice per group per experiment:

“From these studies, we found that DO-KO mice had an accelerated onset of disease compared to DO-WT mice (Fig 7A). Disease symptoms (Score 1) appeared around Day 8–10 and quickly progressed to advanced disease (Score 3–4) by Day 14–16 in DO-KO. In contrast, DO-WT mice started showing symptoms around Day 12 and progressed to advanced disease scores by Day 20. Total cell infiltration into the CNS tissue was slightly higher in DO-KO mice, but no change in total brain weight was observed (S5 Fig). To further correlate the state of disease with CD4 infiltration, we performed in vivo NIRF whole-body imaging on diseased DO-WT and DO-KO mice using an antibody (Ab) probe specific to myelin basic protein (MBP). The Ab reacts with MBP only when the myelinated glia cells are damaged during disease development [56]. Thus, by detecting demyelination, whole-body imaging allowed us to fully visualize the co-localization of CD4 T cells at the sites of demyelination occurring in diseased mice. Interestingly, when mice of various disease scores were imaged, we found increased co-localization of infiltrating CD4 T cells with anti-MBP staining in DO-KO mice, but not in DO-WT mice (Fig 7B). These data not only confirmed the flow cytometric findings that diseased DO-KO mice have a greater influx of lymphocytes into their CNS tissue (S5 Fig), it also verified the massive demyelination that occurs during the disease”

And again in the Legend to Figure 7;

“Representative curves showing the time course of disease development in DO-KO (red) and DO-WT mice (white). N = 5 mice per group, representative of >15 repeat experiments. Score system: 0 = no symptoms, 1 = limp tail, 2 = limp tail + partial hind limb paralysis, 3 = limp tail + total hind limb paralysis, 4 = limp tail + total hind limb paralysis + partial forelimb paralysis. Data represented as mean ± SEM.”

Despite clarity of the description of our experiments, Lee et al have publicly slandered us and grossly misrepresented our work by stating the following:

“A recent study (11-Welsh et al) found that B6.Oa−/− mice were more susceptible to EAE than control B6J animals. However, that conclusion was based on a single experiment, in which control B6J mice developed very mild EAE disease with an average score of 1, which is far lower than the disease scores published by other groups (30–32) and also observed in our study. Thus, in this inducible model of autoimmunity, H2-O deficiency does not contribute to either disease development or severity.”

-Another important variable between our studies and Lee et al (Lee et al 2021) was the use of a commercially available disease induction kit versus our immunization solutions that followed the established protocols by Nancy Ruddle et al (J Exp Med. 1997 Oct 20; 186(8): 1233–1240. doi: 10.1084/jem.186.8.1233). Notoriously, EAE disease development could vary widely based upon the quantities and purity of, a) MOG peptide, b) amount of tuberculosis antigen in the CFA, c) quantity of pertussis toxin and injection strategies, as well as many other uncontrollable factors. While a comparison these two results are irrelevant to our current study, we will be more than happy to compare our results from the previously published work with Lee et al. in the discussion.

-We want to emphasize that we did follow Hogquists et al’s gating strategy for detecting auditing vs deleted thymocytes by subdividing total thymocytes into “Non-signaled” (TCR-β-, CD5-/inter) and “Signaled” (TCR-β+ CD5+/hi) populations before further gating on only medulla localized CD4 T cells. The “CCR7+ CD4+” label in Figure 1 was meant to orient the reader without overwhelming the figure with numerous flow plots. To address this concern, we will be including (1) updated Supplemental figures showing the complete gating strategy, (2) updated figure legends and text to emphasize the fact that auditing/deletion gating came from CD4 T cells which passed positive selection (i.e. TCR-β+ CD5+/hi), and (3) including representative flow plots for all Figure 1 panels to the revise manuscript.

-Also, regarding “discrepancies between our data and Liljedahl et al 1998”;

H2-O KO mice used by Liljedahl et al were on a 129/Ola genomic background. The H2-O KO mice used for both of our papers have been completely backcrossed to C57BL/6J. Clearly, non-MHC genes contribute to the impacts of MHC proteins, yet how the 129/Ola genomic background could affect the H2-O genes remains to be discovered. And (B), no data was shown supporting their published statement below:

“The proportions of B cells as well as of CD4+ and CD8+ T cells in the lymph node, spleen, and thymus were similar in H2-Oa–deficient and wild-type mice (data not shown)”. (Liljedahl et al 1998).

Reviewer 2:

scRNA-Seq analysis was performed by the Computational Biology Computing Core at Johns Hopkins School of Medicine. We missed including this acknowledgement as our core facility does not request authorship or acknowledgements. The sentence has been edited for the correct terminology.

-About truncated bar graph, in the entire paper we have only two bar graphs, neither of which is truncated. So, we are puzzled by the reviewer’s comment as to what figure he/she is referring to. -We would like to remind the Reviewer 2 that since DO works together with DM and functions differently on peptide of different sequences, the reported data on cumulative effects of DO in vivo have notoriously been rather minor. Especially, since our current study focuses on the naïve mice, major changes were not expected.

-Regarding leaving out gating strategies, we missed out on providing the gating strategies for all the figure in the original version. However, full FACS gating strategies have now been provided in the new supplemental figures and representative FACS plots have been added to ALL main figures.

Author Response

We would like to express our gratitude to the reviewers for their insightful comments and suggestions on our manuscript. We appreciate the time and effort they have devoted to evaluating our work. In response to their valuable feedback, we will undertake a comprehensive revision of our manuscript to address their concerns and enhance the clarity of our findings.

Reviewer #1 has raised the important point of the need for a more thorough exploration of how ELF3 promotes cell tolerance to DNA damage.

Just as mentioned by the reviewer, we totally agreed that genomic instability is key to cell transformation. In the original manuscript, we proposed that ELF3 might be an important factor for cells to tolerate the lethal genomic instability caused by BRCA1 deficiency, keeping an “appropriate” level of genomic instability, thus fueling cell transformation. And we acknowledge the limitation that the mechanism of how ELF3 promotes cell to tolerate DNA damage remains further exploration. To address this, ELF3 overexpression and knockdown experiments in more BRCA1 wildtype or deficient breast cell lines are planned. In addition, since ELF3 is an inherent transcription factor, we suspect the function of ELF3 to promote cell tolerance to DNA damage is mediated by transcription, and more downstream genes of ELF3 will be explored as well.

Regarding the concerns raised by Reviewer #2, we acknowledge that our manuscript may have contained gaps and limitations of the datasets used.

We appreciate the reviewer's feedback regarding the limitations of our cell models and their representativeness of LP cells. While we have utilized MCF10A cells for the knockdown experiments, we understand that these may not be a perfect representation of LP cells. To address this concern, we will incorporate a discussion on the limitations of our cell models and their relevance to LP cells, along with potential plans in LP cells that may be included in future studies.

We will also clarify the rationale for focusing on ELF3 and discuss the other genes identified in our analysis for completeness. Regarding to ELF3 functions in cells other than LP, in our analysis, ELF3 is highly expressed in LPs compared to other cell populations in mammary gland, making ELF3 a previously undefined LP gene. Thus, we suspect that ELF3 functions may be more significant in LP cells. We are also interested in ELF3 functions in cells other than LP cells and will further explore

We agree that different pathogenic variants of BRCA1 may cause diverse impacts on its function and tumorigenesis. We will add detailed information and discussion about BRCA1 pathogenic variants of patients in our single-cell RNA-seq. Also, to enhance the overall clarity of our manuscript, we will revise the figure legends to include critical details that were previously omitted. This will ensure that readers can better evaluate the presented data.

Author Response

We appreciate the feedback from all the reviewers. We will incorporate their comments into the revised manuscript.

In response to reviewer three's suggestion regarding complementary approaches for identifying rootlet components, we'd like to provide further insight into the strategies we explored.

We performed mass spectrometry on our purified rootlets. This identified the rootlet components rootletin and CCDC102B and various axonemal components, due to the association between the rootlet and axoneme. However, due to the limitations in quantifying components using mass spectrometry, we were unable to confidently identify novel rootlet constituents present in quantities comparable to rootletin.

We further attempted cross-linking mass spectrometry on the rootlets to gain deeper insights to the interactions between rootletin molecules. Unfortunately, this effort resulted in a completely insoluble sample despite extended digestion times, leading to issues with mass spectrometry column clogging and rendering our results inconclusive.

We attempted to express rootlet components recombinantly and were able to purify fibres, but they did not contain the characteristic repeat pattern seen in native rootlets. We also considered purifying native rootlets from cultured cells, but realized the yield would be too low for cryo-ET studies.

We therefore regret that other approaches to validate our model are outside the scope of this current work.

Author Response

1) The analysis of Shh deletion in mossy cells and influences of aging related NSC pool decline is not well connected with the rest of the study on the expression/requirement of Shh in mossy cells to regulate seizure-induced neurogenesis. To promote cohesion, the authors should examine/discuss what happens to mossy cells during aging - it is similar or different to what happens to mossy cell neuronal activity during seizures?

We believe that both are similar mechanisms. Seizure induced neurogenesis increases NSC proliferation, which increases demand of Shh to increase self-renewal. Similarly, we assume that increased NSC decline in Shh cKO mice is due to the increased demand of Shh for self-renewal of NSC with aging. It has been shown that NSCs in young mice generally don’t self-renew and instead are consumed after one or two rounds of cell division. On the other hand, NSCs in old mice are known to undergo more rounds of cell division compared with younger mice. This suggests that NSCs may be more dependent on signals driving self-renewal in aged-mice. Our suggestion is that Shh from mossy cells contributes to minimising the NSC pool decline with aging, and therefore loss of Shh from mossy cells results in increased decline of the NSC pool in aged-Shh cKO mice. This aligns with our hypothesis that Shh from mossy cells contributes to maintenance of the NSC pool.

What is the exact mechanism regulating the shift of proliferation capacity of NSC with aging remains unclear and would be an interesting topic for future studies. In addition, whether mossy cell neuronal activity is decreased with age or Shh release/expression is compromised in aged animals remains to be elucidated. Considering these factors together, the brain region(s) and other factors that regulate neuronal activity of mossy cell thereby controlling Shh release and how these are dysregulated in pathological conditions and in aging will be important studies for future research.

2) Only male mice were analyzed in the seizure induction experiments, leaving open the possibility of sex differences since previous reports suggest sex differences in adult neurogenesis.

Seizure induced neurogenesis was observed in both male and female mice. Considering that, we assumed that mossy cell derived Shh regulates seizure induced neurogenesis also in female mice. However, we agree with the reviewers’ comments. We can not exclude the possibility that female mice reacts to KA or seizures differently from male mice, or that Shh from mossy cells might have distinct effects in female mice in that paradigm. It is also an interesting possibility that female specific behaviors may affect mossy cell activation and also regulate neurogenesis though Shh. Because these are large and unresolved questions, we elected to leave potential sex difference in mossy cell regulated neurogenesis for future research.

3) Several control groups are missing:

-For seizure induction: missing vehicle (instead of no KA treatment).

-For TAM induction: missing corn oil only to check leakiness and specificity of transgene.

-For DREADD experiment: missing vehicle (to control for hM3 non-specific effects)

About missing vehicles in KA treatments, we used saline (0.9% NaCl) as a vehicle for Kainic acid, which is commonly used as a vehicle for water soluable reagents in adult neurogenesis experiments. In addition, the average volume of KA solution that mice received intrapenitorially for seizure induction was less than 500ul, which is less than recommended maximum volume in NIH and UCSF. We have not tested if the saline injection makes a difference in our experiments but based on previous reports using saline, we believe that saline would not affect our experimental results.

About Tamoxifen injections, the Gli1-CreER mice have been widely used for fate tracing analysis including in our previous research where Gli1-CreER mice have shown specific recombination in Gli1-expressing NSCs. Our results in this study have shown consistently that Gli1-CreER;;Ai14 mice label NSCs in the dentate gyrus. Given this, we believe that our result using Gli1-CreER line are not affected by non-specific recombination without tamoxifen.

About Clozapine (CZL) injection, we decided to administer CLZ in both control and DREADD animals considering the possible side-effects of CLZ. We agree with the reviewer that our experiment cannot exclude the possibility that expression of hM3Dq affects neurogenesis without CLZ or CNO. However, although we have not included the analysis using saline as a control in our experiments, we have tested that both transgenic and virus-injected mice DREADD expressing mice respond to CLZ and activate neuronal activity of mossy cells compared with control animals. Therefore, we believe that it does not affect the interpretation of our data that mossy cell neuronal activity controls neurogenesis.

We appreciate reviewers' carefully considered comments and we will apply suggested controls to our future research.

Author Response

The following is the authors’ response to the original reviews.

We thank the reviewers for their positive feedback and very helpful comments. We agree that this manuscript focuses primarily on functional outcomes and phenotypes. The studies were designed to address an important clinical question, i.e., repurposing dantrolene for the treatment of ventricular tachyarrhythmias and the prevention of sudden cardiac arrest. Thus, the current manuscript emphasizes in vivo studies over in vitro studies.

However, we also acknowledge the need for additional mechanistic studies. We are in the final stages of submitting a second manuscript in which we dissect the underlying mechanisms through detailed in vitro studies of mitochondrial antioxidant capacity, reactive oxygen species, phosphorylation of ryanodine receptors, autonomic dysfunction, beta-adrenergic signaling, etc. that are beyond the scope of the current manuscript.

Additionally, a third manuscript in progress focuses on the mechanistic link between ion channels, dispersion of repolarization, and sudden cardiac death. We previously reported the preliminary results in abstract form (Circulation Research. 2019;125:A102). Briefly, current-voltage relationships from patch clamp studies of isolated LV myocytes revealed that pressure-overload stress strongly reduced K currents, including IK1, IKs, and IKr. These changes were driven by downregulation of K channels and their components at the mRNA level. As expected, the reduced K currents destabilized the resting membrane potential, especially in phases II and II of the cardiac action potential, and reduced repolarization reserve. Scavenging mitochondrial ROS stabilized repolarization, suggesting mROS is the upstream driver of K channel downregulation. However, we have not specifically tested whether dantrolene stabilizes repolarization via the same mechanism. As such, we agree that "lability" or "dispersion" are more precise terms than "reserve" for the phenomenon reported in the present manuscript, and we have made these changes. Thank you for pointing this out. We have also changed the title accordingly.

The present study investigates the effect of dantrolene on male animals. We agree that we need to evaluate the effect on females, especially because females have historically been underrepresented in studies of sudden cardiac arrest. Based on our preliminary studies, female animals exhibit increased variability in their phenotypic response to pressure-overloaded stress. Given the importance of this issue, we will examine the sex differences in carefully controlled future experiments, including the effect of dantrolene in females controlled for hormonal effects (e.g., with and without oophorectomy).

Author Response

The following is the authors’ response to the previous reviews.

Reviewer #1 (Public Review):

The manuscript focused on roles of a key fatty-acid synthesis enzyme, acetyl-coA-carboxylase 1 (ACC1), in the metabolism, gene regulation and homeostasis of invariant natural killer T (NKT_ cells and impact on these T cells' roles during asthma pathogenesis. The authors presented data showing that the acetyl-coA-carboxylase 1 enzyme regulates the expression of PPARg then the function of NKT cells including the secretion of Th2-type cytokines to impact on asthma pathogenesis. The results are clearcut and data were logically presented.

Thank you for your input into our work. Your comments have been very helpful in enhancing our work.

Reviewer #2 (Public Review):

In this study the authors sought to investigate how the metabolic state of iNKT cells impacts their potential pathological role in allergic asthma. The authors used two mouse models, OVA and HDM-induced asthma, and assessed genes in glycolysis, TCA, B-oxidation and FAS. They found that acetyl-coA-carboxylase 1 (ACC1) was highly expressed by lung iNKT cells and that ACC1 deficient mice failed to develop OVA-induced and HDM-induced asthma. Importantly, when they performed bone marrow chimera studies, when mice that lacked iNKT cells were given ACC1 deficient iNKT cells, the mice did not develop asthma, in contrast to mice given wildtype NKT cells. In addition, these observed effects were specific to NKT cells, not classic CD4 T cells. Mechanistically, iNKT cell that lack AAC1 had decreased expression of fatty acid-binding proteins (FABPs) and peroxisome proliferator-activated receptor (PPAR)γ, but increased glycolytic capacity and increased cell death. Moreover, the authors were able to reverse the phenotype with the addition of a PPARg agonist. When the authors examined iNKT cells in patient samples, they observed higher levels of ACC1 and PPARG levels, compared to healthy donors and non-allergic-asthma patients.

Thank you for your thorough analysis of our work.

Reviewer #1 (Recommendations For The Authors):

1) I suggest the authors to remove one copy of the sentence "It should be noted that CD4-CreAcc1fl/fl mice lack ACC expression in both conventional CD4+ T cells and iNKT cells." in Lines 421-423.

We have removed the redundant sentence originally shown in LINES 421-423. Thank you for pointing this out.

Reviewer #2 (Recommendations For The Authors):

Overall, this is a very strong study with few concerns.

1) Are there tissue specific differences in the iNKT cell populations? The authors examined lung iNKT cells in the Figs 1-3, and used liver NKT cells for the mechanistic studies in Fig 4-5. The studies shown in Fig S2 suggest that ACC1 deficient iNKT cells have developmental defects and impaired homeostatic proliferative capacity. Does ACC1 impact lung and liver iNKT cells similarly and is the lack of allergic asthma in ACC1 deficient iNKT cells due to defective iNKT cell trafficking to the lungs or a failure to survive after transfer (Fig 3)?

2) Similarly, are chemokine receptor expression patterns similar between WT and ACC1 deficient iNKTs (Fig 4)?

3) The authors data suggest that Tregs are not playing a major role in the regulation of asthma induction in their ACC1 deficient mice, based on FoxP3 expression. Did the authors perform suppressor assays to show that the Tregs function similarly in WT and ACC1 deficient mice?

In the revised manuscript, the authors addressed my major concerns.

Thank you for your previous comments. They were very helpful in upgrading our scientific work here.

Author Response

The following is the authors’ response to the original reviews.

We appreciate very much the comments and suggestions on our manuscript "Cylicins are a structural component of the sperm calyx being indispensable for male fertility in mice and human". According to the comments, we performed a series of further experiments, re-worded and re-wrote several paragraphs and re-structured the manuscript according to the reviewers’ comment. We think that the manuscript is now improved and are looking forward to the further evaluations. We provide a point by point response to all comments and have prepared a version.

Recommendations for the authors:

Editor’s comment:

1) As pointed out by all three reviewers, it is critical to show the specificity of the antibodies used. The authors should clarify how the specificity of antibodies is tested. Western blot analysis to show the absence of the protein in the knockout is essential.

As suggested by all reviewers, we additionally performed Western Blot analysis on cytoskeletal protein fractions to further verify the specificity of generated antibodies and the generation of functional knockout alleles. Results nicely confirm the results of the IF staining, however, both anti-bodies detected the bands lower than the predicted molecular weight. In addition, Mass Spectrometry was performed to search for the presence of peptides in the cytoskeletal protein fractions. The paragraph reads now as follows:

Line 127-134: Additionally, Western Blot analyses confirmed the absence of CYLC1 and CYLC2 in cytoskeletal protein fractions of the respective knockout (Fig. 1 G), thereby demonstrating i) specificity of the antibodies and ii) validating the gene knockout. Of note, the CYLC1 antibody detects a double band at 40-45 KDa. This is smaller than the predicted size of 74 KDa as, but both bands were absent in Cylc1-/y. Similarly, the CYLC2 Antibody detected a double band at 38-40 KDa instead of 66 KDa. Again, both bands were absent in Cylc2-/-. Next, Mass spectrometry analysis of cytoskeletal protein fraction of mature spermatozoa was performed detecting both proteins in WT but not in the respective knockout samples (Figure 1 – supplement 5; Figure 1 – supplement 6).

Specificity of antibodies was additionally proven by immunohistochemical staining, showing a specific staining only in testis sections but not in any other organ tested. The section reads now as follows:

Line 115-117: Specificity of antibodies was proven by immunohistochemical stainings (IHC), showing a specific signal in testis sections only, but not in any other organ tested (Figure 1 – supplement 2)

2) Re-structuring/streamlining of the figures is recommended. Please consider the flow suggested by reviewer #2 and shorten the evolutionary analysis which takes up more space than it adds to the value of the story.

We thank the reviewers and editor for the valuable suggestion. We re-structured the figures as suggested and rewrote the results section accordingly. The evolutionary analysis was significantly shortened.

3) Provide statistics for the imaging analysis such as TEM as only a single representative image is shown.

We agree that the observed morphological defects require a detailed statistical evaluation. TEM analysis was performed to confirm the results from optical microscopy and representative images with high magnification are shown for a detailed visualization of the defects. For additional quantification, we included statistics for IF stainings against calyx proteins CCIN and CapZa (Fig. 2 I-J). For TEM, we added additional images to the supplement (Figure 3 – supplement 1). Furthermore, we quantified the manchette length of step 10-13 spermatids to prove the increased elongation of the manchette in Cylc2-/- and Cylc1-/y Cylc2-/- spermatids (Fig. 5 A-B).

4) Please consider other points raised by the reviewers below to improve the manuscript and provide responses on how the authors have addressed them.

We thank all reviewers for the detailed review of our manuscript and their valuable suggestions, which helped a lot to improve the manuscript. We considered all points raised by the reviewers to the best of our knowledge and hope that the reviewers will approve the manuscript ready for publication. We added a point-by-point discussion of all comments/suggestions hereafter.

Reviewer #1 (Recommendations For The Authors):

Major comments:

(1) Antibody specificity: Fig 1E - there are some unspecific binding in Cylc2-/- for CYLC2 and in Cylc1/y Cylc2+/- for CYLC1 in the testis (and elongating spermatids in Figure 1 – Supplement 4). Could authors elaborate/comment on this? Western blot analysis would be also helpful to further support the antibody specificity.

The very weak unspecific staining in the testis for CYLC2 (in Cylc2-/-) and CYLC1 (in Cylc1-/y Cylc2+/-) is only present in the lumen of the seminiferous tubules and/or the residual bodies of the testicular sperm cells and can be referred to as background signal. Importantly, the signal is entirely lost in the PT region, proving specificity of the generated antibodies. We added the following paragraph to the results section:

Line 124-127: The generated antibodies did not stain testicular tissue and mature sperm of Cylc1- and Cylc2-deficient males, except for a very weak unspecific background staining in the lumen of seminiferous tubules and the residual bodies of testicular sperm (Fig. 1 F).

Specificity of antibodies was additionally proven by immunohistochemical staining, showing a specific staining only in testis sections but not in any other organ tested.

Line 115-117: Specificity of antibodies was proven by immunohistochemical stainings, showing a specific staining in testis sections only, but not in any other organ tested (Figure 1 – supplement 2)

To further verify the specificity of generated antibodies and the generation of functional knockout alleles, we additionally performed Western Blot analysis on cytoskeletal protein fractions, confirming the results of the IF staining. No unspecific bands were detected in the Western Blot, further supporting the notion that the weak unspecific signals in IF resemble staining artifacts.

The paragraph reads now as follows:

Line 127-132: Additionally, Western Blot analyses confirmed the absence of CYLC1 and CYLC2 in cytoskeletal protein fractions of the respective knockout (Fig. 1 G), thereby demonstrating i) specificity of the antibodies and ii) validating the gene knockout. Of note, the CYLC1 antibody detects a double band at 40-45 KDa. This is smaller than the predicted size of 74 KDa as, but both bands were absent in Cylc1-/y. Similarly, the CYLC2 Antibody detected a double band at 38-40 KDa instead of 66 KDa. Again, both bands were absent in Cylc2-/-.

(2) Please provide more interpretation of the gene dosage effect of Cylicin 2. It is not common to see a gene dosage effect in the sperm phenotype as transcripts and proteins can be shared between haploids due to syncytium formation during spermatogenesis.

We agree and we apologize for the misinterpretation. In Cylc2+/- mice expression of Cylc2 was reduced by half but there was no altered phenotype observed. The sentence now reads as follows:

Line 112: In Cylc2+/- animals expression of Cylc2 was reduced by 50 %.

(3) Line 194-196 - the authors say that the sperm are smaller, with shorter hooks and increased circularity of the nuclei, and reduced elongation. Are these statistically significant? There seems to be a high variation in the graph in S2D and the statistical analysis is not given.

We agree, performed statistical analyses, and highlighted significantly altered values for sperm head elongation and circularity in Figure 2 – Supplement 3.

(4) Line 153-164 It is interesting that the absence of Cylc2 affected many parts of sperm structure. I think some ratios of sperm always have a morphological defect in diverse ways, so it is hard to confirm the finding only with a single sperm image. I think that it will be important to do some statistical analysis or at the minimum show more TEM images from TEM.

We agree that the observed morphological defects require a detailed statistical evaluation. TEM analysis was performed to confirm the results from optical microscopy and representative images with high magnification are shown for a detailed visualization of the defects. For additional quantification, we included statistics for IF stainings against calyx proteins CCIN and CapZa (Fig. 2 I-J). For TEM, we added additional images to the supplement (Figure 3 – Supplement 1).

(5) Line 236-242 - I believe that the phenotype described applies to the sperm from Cylc2-/- and Cylc1/y Cylc2-/- animals; however, I think that the Cylc1-/y Cylc2+/- has a more subtle, intermediate phenotype between the WT and the genotypes missing both Cylc-/- alleles.

We agree and we added a quantification of manchette length at step 10-13 to visualize the differences between the genotypes. The section reads now as follows: Line 268-272: Manchette length was measured starting from step 10 until step 13 spermatids and the mean was obtained, showing that the average manchette length was 76-80 nm in wildtype, Cylc1-/Y and Cylc2+/- while for Cylc2-/- and Cylc1-/Y Cylc2-/- spermatids mean manchette length reached 100 nm (Fig. 5 B). Cylc1-/Y Cylc2+/- spermatids displayed an intermediate phenotype with a mean manchette length of 86 nm.

(6) Since CYLC1 staining is absent in Fig 5B, does that mean that the mutation resulted in protein degradation/instability? Is RNA present? Additional biochemical studies of Cyclins demonstrating the deleterious nature of the mutations would strengthen the molecular pathogenesis of the human mutations.

Thank you for raising these important questions. The CYLC1 variant c.1720G>C is predicted to cause the amino acid substitution p.(Glu574Gln). It is, thus, conceivable that the RNA is present but either the protein is degraded or misfolded and, therefore, not detectable by IF. Unfortunately, for personal reasons of the patient, it is currently not possible to receive additional semen samples, preventing additional analyses of the semen, e.g. analysis of Cylicin transcript level.

(7) Strongly suggest shortening the evolutionary analysis - all the corresponding materials are in supplemental while texts are extensive- or even consider entirely omitting. It does not add a lot to the current study.

We agree that the evolutionary analysis was very detailed. However, we think that the results are important to understand the role of Cylicins for male reproduction in general. The results obtained from the mouse model might be transferable to other species, including humans. Further, the results present a possible explanation for the subfertility of Cylc1-deficient mice, in contrast to infertility of Cylc2-deficient males. We shortened the section, the paragraph reads as follows:

Line 287-302: To address why Cylc2 deficiency causes more severe phenotypic alterations than Cylc1deficiency in mice, we performed evolutionary analysis of both genes. Analysis of the selective constrains on Cylc1 and Cylc2 across rodents and primates revealed that both genes’ coding sequences are conserved in general, although conservation is weaker in Cylc1 trending towards a more relaxed constraint (Fig. 6). A model allowing for separate calculation of the evolutionary rate for primates and rodents, did not detect a significant difference between the clades, neither for Cylc1 nor for Cylc2, indicating that the sequences are equally conserved in both clades.

To analyze the selective pressure across the coding sequence in more detail, we calculated the evolutionary rates for each codon site across the whole tree. According to the analysis, 34% of codon sites were conserved, 51% under relaxed selective constraint, and 15% positively selected. For Cylc2, 47% of codon sites conserved, 44% under neutral/relaxed constraint, and 9% positively selected. Interestingly, codon sites encoding lysine residues, which are proposed to be of functional importance for Cylicins, are mostly conserved. For Cylc1, 17% of lysine residues are significantly conserved and 35% of significantly conserved codons encode for lysine. For Cylc2, this pattern is even more pronounced with 27.9% of lysine codons being significantly conserved and 24.3% of all conserved sites encoding for lysine (Fig. 6).

Minor comments:

(1) Line 114, 115, 118 à Figure 1D is already well-described in the previous paragraph and thus redundant. Ref Fig 1D, E; but only figure E shows IF. Maybe supposed to be E and F or just 1E?

We apologize for the mix-up with the subfigures. The mentioned paragraph refers to Fig. 1 E-F, which was corrected accordingly.

Line 117-123: Immunofluorescence staining of wildtype testicular tissue showed presence of both, CYLC1 and CYLC2 from the round spermatid stage onward (Fig. 1 E). The signal was first detectable in the subacrosomal region as a cap-like structure, lining the developing acrosome (Fig. 1 E-F, Figure 1 – supplement 3). As the spermatids elongate, CYLC1 and CYLC2 move across the PT towards the caudal part of the cell (Figure 1 – supplement 4). At later steps of spermiogenesis, the localization in the subacrosomal part of the PT faded, while it intensified in the postacrosomal calyx region (Fig. 1 E-F).

(2) Figure 1F - Arguably, IF images show expression of both CYLC1 and CYLC2 to reach/include the acrosome/hook portion of the sperm head, but the diagram does not reflect that. Why is that?

We agree and apologize for the inconsistency. The illustration was adjusted according to the experimental data showing localization of Cylicins in the whole ventral part of the sperm.

(3) Line 124 - PAS staining mentioned on line 124, is not explained (Periodic acid Schiff staining) until line 605

We agree and introduced the abbreviation accordingly. The PAS staining was moved to Fig. 4. The paragraph reads now as follows:

Line 220-222: To study the origin of observed structural sperm defects, spermiogenesis of Cylicin deficient males was analyzed in detail. PNA lectin staining and Periodic Acid Schiff (PAS) staining of testicular tissue sections were performed to investigate acrosome biogenesis.

(4) Some figures are hard to read due to being very small (S1B, 3F).

We agree and we increased the figure size. For former Figure 3F (now figure 4A), insets with higher magnification of representative sperm were added. Insets are additionally shown in Figure 4 – Supplement 1 in higher resolution.

(5) Line 139 Please specify whether the sperm was capacitated or not.

Analysis of the flagellar beat was performed with non-capacitated sperm. We clarified this in the main text:

Line 203: The SpermQ software was used to analyze the flagellar beat of non-capacitated Cylc2-/- sperm in detail 22.

As described in the Material and Methods section, sperm were only activated in TYH medium, prior to analysis:

Line 732-733: Sperm samples were diluted in TYH buffer shortly before insertion of the suspension into the observation chamber.

(6) Line 142-145; The sentence is interrupted strangely, perhaps the authors meant to write: "Interestingly, we observed that the flagellar beat of Cylc2-/- sperm cells was similar to wildtype cells, however, with interruptions during which midpiece and initial principal piece appeared stiff whereas high-frequency beating occurs at the flagellar tip"

We corrected the sentence accordingly.

Line 206-208: Interestingly, we observed that the flagellar beat of Cylc2-/- sperm cells was similar to wildtype cells, however, with interruptions during which midpiece and initial principal piece appeared stiff whereas high frequency beating occurs at the flagellar tip (Fig. 3 C, Video 1, Video 2).

(7) Line 142 -Wrong Figure number. Figure S4A is a phylogenic analysis.

We regret the mix up and corrected the Figure reference accordingly. Line 204-205: Cylc2-/- sperm showed stiffness in the neck and a reduced amplitude of the initial flagellar beat, as well as reduced average curvature of the flagellum during a single beat (Figure 3 – supplement 2).

(8) L146-147 Better placed in Discussion.

We agree, and we omitted this sentence from the results part.

(9) Line 154-156 - The white arrowheads are present in both WT and KO sperm, thus it appears they denote the basal plate, not necessarily the dislocation/parallel position as the current text seems to suggest. Furthermore, the position of the WT and KO sperm is somewhat different with the tail coiling differently, so it is hard to see whether the two are comparable.

We agree and we removed the white arrowhead in the WT sperm picture, and it now depicts only the dislocation of the basal plate in the Cylc2-/- sperm. Due to the morphological anomalies of Cylc2-/- sperm cells, it’s difficult to determine the exact angle of the depicted cell. However, we added more TEM pictures of the sperm cells (3 for WT and 6 for Cylc2-/-) in Figure 3 – Supplement 1.

(10) Line 164 Please describe in detail what mitochondrial damage the readers expect to see from the TEM image.

We evaluated the observed mitochondrial damage in more detail. Unfortunately, the defects described initially seem to be an artifact of apoptotic sperm cells and could not be identified in vital sperm cells in either of the knockout mouse models. We apologize for this misinterpretation, and we deleted this section in the manuscript.

(12) Figure S2A - no WT comparison, difficult to compare without it (mitochondria in Cylc2-/-)

See (10). We evaluated the observed mitochondrial damage in more detail and in comparison to WT. Unfortunately, the defects described initially seem to be an artifact of apoptotic sperm cells and could not be identified in vital sperm cells in either of the knockout mouse models. We apologize for this misinterpretation and we deleted this section in the manuscript.

(13) Line 172-173 - Fig 3C denotes quantification of abnormal acrosome only, however, the text mentions sperm coiled tail being quantified within this graph - which is it? Is it both of them? Or only one of them?

Figure 3 C (now Figure 2G) showed the percentage of abnormal sperm in general comprising acrosomal as well as flagellar defects. We modified the figure and evaluated acrosomal defects and tail defects separately. The results section was changed accordingly and reads now as follows:

Line 152-159: Loss of Cylc1 alone caused malformations of the acrosome in around 38% of mature sperm, while their flagellum appeared unaltered and properly connected to the head. Cylc2+/- males showed normal sperm tail morphology with around 30% of acrosome malformations. Cylc2-/- mature sperm cells displayed morphological alterations of head and mid-piece (Fig. 2 F-G). 76% of Cylc2-/- sperm cells showed acrosome malformations, bending of the neck region, and/or coiling of the flagellum, occasionally resulting in its wrapping around the sperm head in 80% of sperm (Fig. 2 F). While 70% of Cylc1-/Y Cylc2+/- sperm showed these morphological alterations, around 92% of Cylc1-/YCylc2-/- sperm presented with coiled tail and abnormal acrosome (Fig. 2 F-G).

(14) Fig 3D - CCIN in the text, cylicin in the figure - this should be consistent. Furthermore, since only the head is being shown, is CCIN ever detected in the WT sperm tail?

We apologize for the inconsistency, and we added the abbreviation “CCIN” to the figure. CCIN is solely detectable in the sperm head of wildtype sperm as published previously. Irregular staining patterns showing signals in the tail region are only observed upon Cylicin deficiency.

(15) Line 199-200 - To say that head of Cylc2-deficient sperm appears less concave seems redundant, likely the observed increased circularity is contributed to by sperm head being less concave in this region; unless there is an extra point that the authors are trying to make and if so, this needs to be elaborated on

We agree and we deleted the sentence from the manuscript.

(16) Figure legend of Fig S3 is wrong. Only S3A and S3B are present, and in the figure legend S3C corresponds to figure S3B.

We agree and corrected the Figure legends accordingly. Due to the re-structuring of the manuscript, Figures and Supplementary figures were re-ordered as well.

(17) Figure 4B - figure legend and/or text should specify that lectin is green and HOOK1 is in red

We specified the figure legend as well as the main text accordingly: Line: 279-281: Co-staining of the spermatids with antibodies against PNA lectin (green) and HOOK1 (red) revealed that abnormal manchette elongation and acrosome anomalies simultaneously occurred in elongating spermatids of Cylc2-/- male mice (Fig. 5 C).

Line: 560-562: Co-staining of the manchette with HOOK1 (red) and acrosome with PNA-lectin (green) is shown in round, elongating and elongated spermatids of WT (upper panel) and Cylc2-/- mice (lower panel).

(18) Line 261-263 - It is difficult to see what is going on with microtubules in these images, as the resolution is low

We increased the pictures and improved their quality. Microtubules are also depicted with letter ‘m’

(19) Line 265-266 - It seems that there is a persistence of manchette, rather than elongation. From these images, I cannot see gaps, and I am not sure where to look for them. This needs to be labelled further and higher-resolution images could be included for clarity.

We agree, although we observed both excessive elongation and persistence of the manchette. The average length of the manchette is now shown in figure 5B.

The paragraph now reads as follows:

Line 235-239: Microtubules appeared longer on one side of the nucleus than on the other, displacing the acrosome to the side and creating a gap in the PT (Fig. 4 C). Whereas elongated spermatids at step 14-15 in wildtype sperm already disassembled their manchette and the PT appeared as a unique structure that compactly surrounds nucleus, in Cylc2-/- spermatids, remaining microtubules failed to disassemble.

The gaps in the perinuclear theca are better visible in TEM micrographs and the description is now in the paragraph describing TEM.

(20) Line 269 Please include the information of "White arrowhead".

We added the information accordingly.

Line 240-242: In addition, at step 16, the calyx was absent, and an excess of cytoplasm surrounded the nucleus and flagellum (Fig. 4 C, white arrowhead).

(21) Line 276-280 This should be placed in the Discussion.

We agree, and we deleted this concluding remark from the results section.

(22) Is Cylc1 and/or Cylc2 conserved/expressed amongst species other than rodents and primates?

Yes, Cylc1 and Cylc2 homologs were identified in C. elegans for example. We added a schematic to the introduction showing the protein structure of human, mouse and C. elegans CYLC1 and CYLC2 (Figure 1 – supplement 1).

The section reads now as follows:

Line 73-78: In most species, two Cylicin genes, Cylc1 and Cylc2, have been identified (Figure 1- supplement 1). They are characterized by repetitive lysine-lysine-aspartic acid (KKD) and lysine-lysine-glutamic acid (KKE) peptide motifs, resulting in an isoelectric point (IEP) > pH 10 14, 15. Repeating units of up to 41 amino acids in the central part of the molecules stand out by a predicted tendency to form individual short α-helices 14. Mammalian Cylicins exhibit similar protein and domain characteristics, but CYLC2 has a much shorter amino-terminal portion than CYLC1 (Figure 1-supplement 1).

(23) The whole chapter "Cylc2 coding sequence is slightly more conserved among species than Cylc1" references only supplemental figures/tables. I find this unusual.

We agree, and in order to show the results of the evolutionary analysis more clearly, we moved the panel to main Figure 6.

Line 286-302: To address why Cylc2 deficiency causes more severe phenotypic alterations than Cylc1deficiency in mice, we performed evolutionary analysis of both genes. Analysis of the selective constrains on Cylc1 and Cylc2 across rodents and primates revealed that both genes’ coding sequences are conserved in general, although conservation is weaker in Cylc1 trending towards a more relaxed constraint (Fig. 6 A). A model allowing for separate calculation of the evolutionary rate for primates and rodents, did not detect a significant difference between the clades, neither for Cylc1 nor for Cylc2, indicating that the sequences are equally conserved in both clades.

To analyze the selective pressure across the coding sequence in more detail, we calculated the evolutionary rates for each codon site across the whole tree. According to the analysis, 34% of codon sites were conserved, 51% under relaxed selective constraint, and 15% positively selected. For Cylc2, 47% of codon sites conserved, 44% under neutral/relaxed constraint, and 9% positively selected. Interestingly, codon sites encoding lysine residues, which are proposed to be of functional importance for Cylicins, are mostly conserved. For Cylc1, 17% of lysine residues are significantly conserved and 35% of significantly conserved codons encode for lysine. For Cylc2, this pattern is even more pronounced with 27.9% of lysine codons being significantly conserved and 24.3% of all conserved sites encoding for lysine (Fig. 6 B).

(24) Line 332 - CYCL2 should be CYLC2

We corrected the typo accordingly.

(25) Line 340 The ratio of head defects is different from Table 1 (98% here and 99 % in the table). Please check this information.

We apologize for the inconsistency. We checked the raw data and corrected the table accordingly.

(26) Line 344-345 From figure 5C it is difficult to determine whether the sperm are "headless" or whether the heads are attached to the highly coiled tails next to them

We agree and we quantified the percentage of sperm showing abnormal flagella and a headless phenotype. Furthermore, we added an arrowhead to figure 6C to highlight headless sperm. The paragraph reads now as follows:

Line 335-339: Bright field microscopy demonstrated that M2270’s sperm flagella coiled in a similar manner compared to flagella of sperm from Cylicin deficient mice. Quantification revealed 57% of M2270 sperm displaying abnormal flagella compared to 6% in the healthy donor (Fig. 7 D). Interestingly, DAPI staining revealed that 27% of M2270 flagella carry cytoplasmatic bodies without nuclei and could be defined as headless spermatozoa (Fig. 7 C, white arrowhead; Fig. 7 E).

(27) L367-368 I agree with the authors' logic of this sentence. Although, it is better to show the co-localization of proteins using multi-channel immunocytochemistry. As you mentioned on L369 this will make your finding more obvious. If it is available, please include the colocalization images of the proteins.

We performed the multi-channel staining against Cylicin1 and Calicin, as well as Cylicin2 and Calicin on mouse epipidymal sperm and it’s shown in Figure 2 – supplement 4. Unfortunately, we did not manage to obtain stainings of tissue sections since antibodies against Cylicins and Calicin require different sample processing.

The sentence was added in the section describing calyx integrity:

Line 168-169: In epididymal sperm, CCIN co-localizes with both CYLC1 and CYLC2 in the calyx (Figure 2 – supplement 4).

(28) Line 376 Please keep the abbreviation. "Calicin" "CCIN".

We included the abbreviation accordingly.

Line 377-378: CCIN is shown to be necessary for the IAM-PT-NE complex by establishing bidirectional connections with other PT proteins.

(29) Line 377-378 "Based on ~". The authors did not prove the interaction between CCIN and Cylicins in this article. The mislocalization of CCIN might be resulted in the loss of Cylicins, without any "interaction". To reach this conclusion, a more direct result should be provided.

We agree that we overinterpreted this as we and others did not prove the interaction between CCIN and Cylicins so far. We therefore weakened this statement and formulated it as a hypothesis.

Line 377-381: CCIN is shown to be necessary for the IAM-PT-NE complex by establishing bidirectional connections with other PT proteins. Zhang et al. found CYLC1 to be among proteins enriched in PT fraction 7. Based on their speculation that CCIN is the main organizer of the PT, we hypothesize that both CCIN and Cylicins might interact, either directly or in a complex with other proteins, in order to provide the ‘molecular glue’ necessary for the acrosome anchoring.

(30) Line 499 Please specify which is the target of the immunostaining on the Figure legend. (Tubulin à acetylated α-tubulin)

We specified that α-Tubulin was stained. The figure legend reads now as follow: Line 555-557: Immunofluorescence staining of α-Tubulin to visualize manchette structure in squash testis samples of WT, Cylc1-/y, Cylc2+/-, Cylc2-/-, Cylc1 -/y Cylc2+/- and Cylc1-/y Cylc2-/- mice.

(31) Line 502 Please specify which color indicates which target protein (not only cellular structure).

Line 560-562: Co-staining of the manchette with HOOK1 (red) and acrosome with PNA-lectin (green) is shown in round, elongating and elongated spermatids of WT (upper panel) and Cylc2-/- mice (lower panel).

(32) Line 509 Please include scale bar information in the figure legend like Figure 4 (The magnifications of Figure 5 B, C, and D seem different).

We included the scale bar information accordingly (now Figure 6).

Line 575-588: Figure 6: Cylicins are required for human male fertility

(A) Pedigree of patient M2270. His father (M2270_F) is carrier of the heterozygous CYLC2 variant c.551G>A and his mother (M2270_M) carries the X-linked CYLC1 variant c.1720G>C in a heterozygous state. Asterisks (*) indicate the location of the variants in CYLC1 and CYLC2 within the electropherograms.

(B) Immunofluorescence staining of CYLC1 in spermatozoa from healthy donor and patient M2270. In donor’s sperm cells CYLC1 localizes in the calyx, while patient’s sperm cells are completely missing the signal. Scale bar: 5 µm.

(C) Bright field images of the spermatozoa from healthy donor and M2270 show visible head and tail anomalies, coiling of the flagellum as well as headless spermatozoa who carry cytoplasmatic residues without nuclei. Heads were counterstained with DAPI. Scale bar: 5 µm.

(D-E) Quantification of flagellum integrity (D) and headless sperm (E) in the semen of patient M2270 and a helathy donor.

(F-G) Immunofluorescence staining of CCIN (F) and PLCz (G) in sperm cells of patient M2270 and a healthy donor. Nuclei were counterstained with DAPI. Scale bar: 3 µm.

(33) S2A is not clear. Please describe specifically what the left panel and right panel are about to show with a clear indication of what is PM, mitochondria, etc. On the right, in only one cross-section that shows both mitochondria and the 9+2 axoneme, they look both unaltered whereas on the left, there are unpacked, not aligned mitochondria but the tail boundary is not clear to grasp at first sight.

We apologize for the bad quality of the TEM pictures showing the axonemes and the missing labeling. We recorded and included new images showing an intact 9+2 microtubular structure in Cylc2-/-. Furthermore, we added an image for the wildtype control.

(34) S2D: colors of the last three plots of each graph are too close to tell apart

We agree and changed the color scheme for better visualization.

Reviewer #2 (Recommendations For The Authors):

However, I find the manuscript a bit messy, and I will propose to reorganize the figures: following figure 1, showing the reproductive phenotype, I would continue with a figure showing the morphology of sperm in optical microscopy and showing the morphological defect of the nucleus (Fig 3B and 3E), followed with one figure focusing on the flagellum, with images obtained with optical and electronic microscopies, allowing to present the abnormalities of the flagellum and finally the impact on sperm motility and flagellum beating (mix of figure 2FG/3A); next, one figure focusing on acrosome. After that, I would present all data concerning spermiogenesis, starting with figure 2C.

We thank the reviewer for the valuable suggestion, which helps a lot to improve the structure and comprehensibility of the manuscript. We re-organized the figures and the results section accordingly.

Major remarks

1) Line 111. The specificity of raised Ab is not clear. Please specify if antibodies are specific: what immune-decorates anti-CYLC1: only CYLC1 or CYLC1 and CYLC2. Same question for anti-CYLC2

Both antibodies were raised against specific peptides of the CYLC1 or CYLC2 protein, respectively. The antigen peptides used for immunization are depicted in the Material and Methods section (AESRKSKNDERRKTLKIKFRGK and KDAKKEGKKKGKRESRKKR peptides for CYLC1; KSVGTHKSLASEKTKKEVK and ESGGEKAGSKKEAKDDKKDA for CYLC2). The peptides used for immunization are specific as they do not resemble the highly conserved and repetitive KKD/KKE motives present in both, Cylc1 and Cylc2.

The specificity of raised antibodies was validated by IF staining of wildype and Cylicin-deficient testis sections. The results clearly show, that CYLC1 signal is absent in Cylc1-deficient spermatids and CYLC2 signal being absent in Cylc2 deficient spermatids.

Specificity of antibodies was additionally proven by immunohistochemical stainings, showing a specific staining only in testis sections but not in any other organ tested.

Line 115-117: Specificity of antibodies was proven by immunohistochemical stainings, showing a specific staining only in testis sections but not in any other organ tested (Figure 1 - supplement 2)

To further verify the specificity of generated antibodies and the generation of functional knockout alleles, we additionally performed Western Blot analysis on cytoskeletal protein fractions, confirming the results of the IF staining.

The paragraph reads now as follows:

Line 127-134: Additionally, Western Blot analyses confirmed the absence of CYLC1 and CYLC2 in cytoskeletal protein fractions of the respective knockout (Fig. 1 G), thereby demonstrating i) specificity of the antibodies and ii) validating the gene knockout. Of note, the CYLC1 antibody detects a double band at 40-45 KDa. This is smaller than the predicted size of 74 KDa as, but both bands were absent in Cylc1-/y. Similarly, the CYLC2 Antibody detected a double band at 38-40 KDa instead of 66 KDa. Again, both bands were absent in Cylc2-/-. Next, Mass spectrometry analysis of cytoskeletal protein fraction of mature spermatozoa was performed detecting both proteins in WT but not in the respective knockout samples (Figure 1 – supplement 5; Figure 1 – supplement 6).

2) Line 115 and figure 1D. From the images presented in figure 1D, it is not clear where CYLC1 and CYLC2 are localized in the round and in elongated spermatids. Please make double staining using a second Ab to identify the acrosome such as DPY19L2 (best option) or SP56 and the manchette such as acetylated alpha-tubulin.

We agree, and we added a double staining of CYLC1/CYLC2 and SP56 to the supplement (Figure 1 - supplement 3), showing co-localization of the developing acrosome and Cylicins. Manchette staining was not performed due to antibodies being available in same species as those against Cylicins (anti-rabbit).

Line 117-120: Immunofluorescence staining of wildtype testicular tissue showed presence of both, CYLC1 and CYLC2 from the round spermatid stage onward (Fig. 1 E, Figure 1 – supplement 3). The signal was first detectable in the subacrosomal region as a cap like structure, lining the developing acrosome (Fig. 1 E-F, Figure 1 – supplement 3).

3) Line 118 and figure 1. The drawing showing the localization of Cylicin in mature sperm does not fit with the experimental data. Cylicins are located on the whole ventral face of the sperm.

We agree and apologize for the inconsistency. The illustration was adjusted according to the experimental data showing localization of Cylicins in the whole ventral part of the sperm.

4) Figure 1: Change "expression of Cylicin" to "localization of cylicin" (green)

We changed the legend accordingly.

5) Line 124 and figure 2C. In the figure provided, the PAS staining seems defective. The acrosomes do not seem stained (in pink as expected for a PAS staining). It may be due to the low quality of the pdf file, nevertheless, it is important to provide in supplementary data, an enlargement of the spermatid region showing the staining of the acrosome.

We apologize for the bad quality of the PDF file and the low magnification. We restructured the subfigure showing PAS stained spermatids at different steps of spermiogenesis at higher magnification. According to the initial reviewer’s suggestion, the PAS staining was moved to figure 4. The PAS staining in figure 2 was replaced by HE-stained overview testis sections in Figure 3 – supplement 1 showing intact spermatogenesis in all genotypes.

6) Line 130. Please indicate a reference for the lower limit of 58%. If this lower limit corresponds to human sperm, it should be omitted.

Indeed, the given reference limit of 58% is only valid for human sperm samples. Therefore, we omitted the reference limit. The paragraph reads now as follows: Line 144-146: Eosin-Nigrosin staining revealed that the viability of epididymal sperm from all genotypes was not severely affected (Fig. 2 D, Figure 2 – supplement 2).

7) line 152 Sperm morphology. Before showing the ultrastructure of the sperm, it would be important to show sperm morphology observed by optical microscopy. Therefore, I recommend including figure S2 as a principal figure, with a mix of Figures 3B and 3E.

We thank the reviewer for the suggestion. The results section was re-structured accordingly, first showing results of optical microscopy (Fig. 2), followed by an in-depth ultrastructural investigation of morphological defects and their effects on sperm motility. Brightfield images of epididymal sperm were moved from former Figure S2 to main Figure 2.

8) Line 164. figure S2A, showing that the 9+2 pattern is normal in KO sperm, is not convincing. Enlargement is required to conclude that the axoneme structure is normal; from the pictures, it rather seems that some doublets are missing.

We apologize for the bad quality of the TEM pictures showing the axonemes. We recorded and included new images showing an intact 9+2 microtubular structure.

9) Line 196. I would suggest removing the term "mild globozoospermia". Globozoospermia is rather complete (100% of round sperm heads) or incomplete (<90 % of round sperm heads). The anomalies observed on sperm heads, sperm motility, and the decrease in sperm concentration are rather suggestive of an OAT.

We agree and we omitted the term “mild globozoospermia”. Instead, we added a concluding remark to the section, summarizing the described defects as OAT syndrome. The section reads now as follows:

Line 215-217: Taken together, observed anomalies of sperm heads, impaired sperm motility, and the decrease in epididymal sperm concentration show that Cylc deficiency results in a severe OAT phenotype (Oligo-Astheno-Teratozoospermia-syndrome) described in human.

10) Line 248. It is not clear from the data of figure 4B that "the developing acrosome lost its compact adherence to the nuclear envelope". From this figure, only defective morphologies of the acrosome are observed

We agree and we omitted the sentence. Furthermore, it does not add additional information to the manuscript, since defects in the attachment of the acrosome to the nuclear envelope have been described in detail in Figure 4C.

11) line 260-264. Manchette defects appear at stages 9-10. At this stage, the HTCA is already attached to the nucleus of the spermatid. see for instance figure 2 from Shang Y, Zhu F, Wang L, Ouyang YC, Dong MZ, Liu C, Zhao H, Cui X, Ma D, Zhang Z, Yang X, Guo Y, Liu F, Yuan L, Gao F, Guo X, Sun QY, Cao Y, Li W. Essential role for SUN5 in anchoring sperm head to the tail. Elife. 2017 Sep 25;6:e28199. doi: 10.7554/eLife.28199 . Therefore, the hypothesis that "abnormal attachment of the developing flagellum to the basal plate and consequently flipping of the head and coiling of the tail in mature spermatozoa" is unlikely and I suggest modifying this paragraph. In the HOOK paper, the manchette defects occurred earlier.

We read the suggested literature and we agree to this reviewer’s comment. Manchette defects that we observe appear at later stages and are probably not responsible for the morphological anomalies of the mature sperm. We also re-analyzed all the manchette staining pictures and didn’t find any defects at earlier stages, so we decided to delete the sentence from the manuscript.

12) Line 344. Please indicate a percentage of headless spermatozoa. Many sperm is too vague.

We agree and we quantified the percentage of sperm showing abnormal flagella and a headless phenotype. The paragraph reads now as follows:

Line 335-339: Bright field microscopy demonstrated that M2270’s sperm flagella coiled in a similar manner compared to flagella of sperm from Cylicin deficient mice. Quantification revealed 57% of M2270 sperm displaying abnormal flagella compared to 6% in the healthy donor (Fig. 7 D). Interestingly, DAPI staining revealed that 27% of M2270 flagella carry cytoplasmatic bodies without nuclei and could be defined as headless spermatozoa (Fig. 7 C, white arrowhead; Fig. 7 E).

13) Any data concerning the success of ICSI for this patient?

Yes, the outcome of the ICSI were added to the main text. Line 309-311: The couple underwent one ICSI procedure which resulted in 17 fertilized oocytes out of 18 retrieved. Three cryo-single embryo transfers were performed in spontaneous cycles, but no pregnancy was achieved.

14) Finally, it would be interesting to study the localization of PLCzeta in this model, since its localization in the perinuclear theca has been clearly shown (Escoffier et al, 2015 doi:10.1093/molehr/gau098 )

We thank the reviewer for the valuable suggestion and performed PLCzeta staining on human sperm, clearly showing an irregular PT staining pattern in sperm of patient M2270 compared to healthy control sperm. Of note, staining was not possible in the mouse due to the antibody being reactive only for human samples.

The section reads as follows:

Line 343-349: Testis specific phospholipase C zeta 1 (PLCζ1) is localized in the postacrosomal region of PT in mammalian sperm (Yoon and Fissore, 2007) and has a role in generating calcium (Ca²⁺) oscillations that are necessary for oocyte activation (Yoon, 2008). Staining of healthy donor’s spermatozoa showed a previously described localization of PLCζ1 in the calyx, while sperm from M2270 patient presents signal irregularly through the PT surrounding sperm heads (Fig. 7 G). These results suggest that Cylicin deficiency can cause severe disruption of PT in human sperm as well, causing male infertility.

Reviewer #3 (Recommendations For The Authors):

1) Why the Cylc1-/y Cylc2+/- males were infertile? It would be helpful to show the homologue of the two proteins;

To elaborate more on the homology of CYLC1 and CYLC2, we added a more detailed section about the protein and domain structure to the introduction.

Line 73-78: In most species, two Cylicin genes, Cylc1 and Cylc2, have been identified (Figure 1supplement 1). They are characterized by repetitive lysine-lysine-aspartic acid (KKD) and lysine-lysineglutamic acid (KKE) peptide motifs, resulting in an isoelectric point (IEP) > pH 10 14, 15. Repeating units of up to 41 amino acids in the central part of the molecules stand out by a predicted tendency to form individual short α-helices (Hess et al., 1993). Mammalian Cylicins exhibit similar protein and domain characteristics, but CYLC2 has a much shorter amino-terminal portion than CYLC1 (Figure 1supplement 1).

Speculations about the infertility of Cylc1-/y Cylc2+/- males was added to the discussion:

Line 410-413: Interestingly, Cylc1-/Y Cylc2+/- males displayed an “intermediate” phenotype, showing slightly less damaged sperm than Cylc2-/- and Cylc1-/Y Cylc2-/- animals. This further supports our notion, that loss of the less conserved Cylc1 gene might be at least partially compensated by the remaining Cylc2 allele.

2) Western blot is important to show the absence of the two proteins in the mouse models;

To further verify the specificity of generated antibodies and the generation of functional knockout alleles, we additionally performed Western Blot analysis on cytoskeletal protein fractions, confirming the results of the IF staining.

A paragraph was added to the manuscript and reads as follows:

Line 127-134: Additionally, Western Blot analyses confirmed the absence of CYLC1 and CYLC2 in cytoskeletal protein fractions of the respective knockout (Fig. 1 G), thereby demonstrating i) specificity of the antibodies and ii) validating the gene knockout. Of note, the CYLC1 antibody detects a double band at 40-45 KDa. This is smaller than the predicted size of 74 KDa as, but both bands were absent in Cylc1-/y. Similarly, the CYLC2 Antibody detected a double band at 38-40 KDa instead of 66 KDa. Again, both bands were absent in Cylc2-/-. Next, Mass spectrometry analysis of cytoskeletal protein fraction of mature spermatozoa was performed detecting both proteins in WT but not in the respective knockout samples (Figure 1 – supplement 5; Figure 1 – supplement 6).

3) On Page 7, line 227 and line 243, was the acetylated α-tubulin or α-tubulin antibody used?

For all stainings α-tubulin antibody was used. We corrected this accordingly. Line 257-259: We used immunofluorescence staining of α-tubulin on squash testis samples containing spermatids at different stages of spermiogenesis to investigate whether the altered head shape, calyx structure, and tail-head connection anomalies originate from possible defects of the manchette structure.

4) Fig. 2S: A cartoon showing the elongation and circularity of nuclei for evaluation is helpful; The TEM images from the control and Cylc1 KO mice are needed;

Cylc1-/Y TEM picture was added in Figure 3A.

5) The discussion should be rewritten. The current version is to repeat the experiments/findings. The authors should discuss more about the potential mechanisms.

We discussed the observed defects of Cylc-deficient animals and discussed this in relation to other published mouse models deficient in Calyx components. Furthermore, we speculated about potential interaction partners of Cylicins and the importance of these protein complexes for male fertility. However, to this point, we think that it is too farfetched to speculate about potential mechanisms without any evidence for Cylc interaction partner or their exact molecular function. This requires further research.

Author Response

We are grateful to the editors for considering our manuscript and facilitating the peer review process. Importantly, we would like to express our gratitude to reviewers for their constructive comments. Given eLife’s publishing format, we provide an initial author response now, which will be followed by a revised manuscript in the near future. Please find our responses below.

eLife Assessment

This study presents a valuable insight into a computational mechanism of pain perception. The evidence supporting the authors’ claims is solid, although the inclusion of 1) more diverse candidate computational models, 2) more systematic analysis of the temporal regularity effects on the model fit, and 3) tests on clinical samples would have strengthened the study. The work will be of interest to pain researchers working on computational models and cognitive mechanisms of pain in a Bayesian framework.

Thank you very much again for considering the manuscript and judging it as a valuable contribution to understanding mechanisms of pain perception. We recognise the above-mentioned points of improvement and elaborate on them in the initial response to the reviewers.

Reviewer 1

Reviewer Comment 1.1 — Selection of candidate computational models: While the paper juxtaposes the simple model-free RL model against a Kalman Filter model in the context of pain perception, the rationale behind this choice remains ambiguous. It prompts the question: could other RL-based models, such as model-based RL or hierarchical RL, offer additional insights? A more detailed explanation of their computational model selection would provide greater clarity and depth to the study.

Thank you for this point. Our models were selected a-priori, following the modelling strategy from Jepma et al. (2018) and hence considered the same set of core models for clear extension of the analysis to our non-cue paradigm. The key question for us was whether expectations were used to weight the behavioural estimates, so our main interest was to compare expectation vs non-expectation weighted models.

Model-based and hierarchical RL are very broad terms that can be used to refer to many different models, and we are not clear about which specific models the reviewer is referring to. Our Bayesian models are generative models, i.e. they learn the generative statistics of the environment (which is characterised by inherent stochasticity and volatility) and hence operate model-based analyses of the stimulus dynamics. In our case, this happened hierarchically and it was combined with a simple RL rule.

Reviewer Comment 1.2 — Effects of varying levels of volatility and stochasticity: The study commendably integrates varying levels of volatility and stochasticity into its experimental design. However, the depth of analysis concerning the effects of these variables on model fit appears shallow. A looming concern is whether the superior performance of the expectation-weighted Kalman Filter model might be a natural outcome of the experimental design. While the non-significant difference between eKF and eRL for the high stochasticity condition somewhat alleviates this concern, it raises another query: Would a more granular analysis of volatility and stochasticity effects reveal fine-grained model fit patterns?

We are sorry that the reviewer finds shallow ”the depth of analysis concerning the effects of these variables on model fit”. We are not sure which analysis the reviewer has in mind when suggesting a ”more granular analysis of volatility and stochasticity effects” to ”reveal fine-grained model fit patterns”. Therefore, we find it difficult to improve our manuscript in this regard. We are happy to add analyses to our paper but we would be greatful for some specific pointers. We have already provided:

• Analysis of model-naive performance across different levels of stochasticity and volatility (section 2.3, figure 3, supplementary information section 1.1 and tables S1-2)

• Model fitting for each stochasticity/volatility condition (section 2.4.1, figure 4, supplementary table S5)

• Group-level and individual-level differences of each model parameter across stochasticity/volatility conditions (supplementary information section 7, figures S4-S5).

• Effect of confidence on scaling factor for each stochasticity/volatility condition (figure 5)

Reviewer Comment 1.3 — Rating instruction: According to Fig. 1A, participants were prompted to rate their responses to the question, ”How much pain DID you just feel?” and to specify their confidence level regarding their pain. It is difficult for me to understand the meaning of confidence in this context, given that they were asked to report their subjective feelings. It might have been better to query participants about perceived stimulus intensity levels. This per- spective is seemingly echoed in lines 100-101, ”the primary aim of the experiment was to determine whether the expectations participants hold about the sequence inform their perceptual beliefs about the intensity of the stimuli.”

Thank you for raising this question, which allows us to clarify our paradigm. On half of the trials, participants were asked to report the perceived intensity of the previous stimulus; on the remaining trials, participants were requested to predict the intensity of the next stimulus. Therefore, we did query ”participants about perceived stimulus intensity levels”, as described at lines 49-55, 296-303, and depicted in figure 1.

The confidence refers to the level of confidence that participants have regarding their rating - how sure they are. This is done in addition to their perceived stimulus intensity and it has been used in a large body of previous studies in any sensory modality.

Reviewer Comment 1.4 — Relevance to clinical pain: While the authors underscore the rele- vance of their findings to chronic pain, they did not include data pertaining to clinical pain. Notably, their initial preprint seemed to encompass data from a clinical sample (https://www.medrxiv.org /content/10.1101/2023.03.23.23287656v1), which, for reasons unexplained, has been omitted in the current version. Clarification on this discrepancy would be instrumental in discerning the true relevance of the study’s findings to clinical pain scenarios.

The preprint that the Reviewer is referring to was an older version of the manuscript in which we combined two different experiments, which were initially born as separate studies: the one that we submitted to eLife (done in the lab, with noxious stimuli in healthy participants) and an online study with a different statistical learning paradigm (without noxious stimuli, in chronic back pain participants). Unfortunately, the paradigms were different and not directly comparable. Indeed, following submission to a different journal, the manuscript was criticised for this reason. We therefore split the paper in two, and submitted the first study to eLife. We are now planning to perform the same lab-based experiment with noxious stimuli on chronic back pain participants. Progress on this front has been slowed down by the fact that I (Flavia Mancini) am on maternity leave, but it remains top priority once back to work.

Reviewer Comment 1.5 — Paper organization: The paper’s organization appears a little bit weird, possibly due to the removal of significant content from their initial preprint. Sections 2.1- 2.2 and 2.4 seem more suitable for the Methods section, while 2.3 and 2.4.1 are the only parts that present results. In addition, enhancing clarity through graphical diagrams, especially for the experimental design and computational models, would be quite beneficial. A reference point could be Fig. 1 and Fig. 5 from Jepma et al. (2018), which similarly explored RL and KF models.

Thank you for these suggestions. We will consider restructuring the paper in the revised version.

Reviewer 2

Reviewer Comment 2.1 — This is a highly interesting and novel finding with potential impli- cations for the understanding and treatment of chronic pain where pain regulation is deficient. The paradigm is clear, the analysis is state-of-the-art, the results are convincing, and the interpretation is adequate.

Thank you very much for these positive comments.

Reviewer 3

We are really grateful for reviewer’s insightful comments and for providing useful guidance regarding our methodology. We are also thankful for highlighting the strengths of our manuscript. Below we respond to individual weakness mentioned in the reviews report.

Reviewer Comment 3.1 — In Figure 1, panel C, the authors illustrate the stimulation intensity, perceived intensity, and prediction intensity on the same scale, facilitating a more direct comparison. It appears that the stimulation intensity has been mathematically transformed to fit a scale from 0 to 100, aligning it with the intensity ratings corresponding to either past or future stimuli. Given that the pain threshold is specifically marked at 50 on this scale, one could logically infer that all ratings falling below this value should be deemed non-painful. However, I find myself uncertain about this interpretation, especially in relation to the term ”arbitrary units” used in the figure. I would greatly appreciate clarification on how to accurately interpret these units, as well as an explanation of the relationship between these values and the definition of pain threshold in this experiment.

Indeed, as detailed in the Methods section 4.3, the stimulation intensity was originally trans- formed from the 1-13 scale to 0-100 scale to match the scales in the participant response screens. Following the method used to establish the pain threshold, we set the stimulus intensity of 7 as the threshold on the original 1-13 scale. However, during the rating part of the experiment, several of the participants never or very rarely selected a value above 50 (their individually defined pain threshold), despite previously indicating a moment during pain threshold procedure when a stimulus becomes painful. This then results in the re-scaled intensity values as well the perception rating, both on the same 0-100 scale of arbitrary units, to never go above the pain threshold. Please see all participant ratings and inputs in the Figure below. We see that it would be more illustrative to re-plot Figure 1 with a different exemplary participant, whose ratings go above the pain threshold, perhaps with an input intensity on the 1-13 scale on the additional right-hand-side y-axis. We will add this in the revised version as well as highlight the fact above.

Importantly, while values below 50 are deemed non-painful by participants, the thermal stimulation still activates C-fibres involved in nociception, and we would argue that the modelling framework and analysis still applies in this case.

Reviewer Comment 3.2 — The method of generating fluctuations in stimulation temperatures, along with the handling of perceptual uncertainty in modelling, requires further elucidation. The current models appear to presume that participants perceive each stimulus accurately, introducing noise only at the response stage. This assumption may fail to capture the inherent uncertainty in the perception of each stimulus intensity, especially when differences in consecutive temperatures are as minimal as 1°C.

We agree with the reviewer that there are multiple sources of uncertainty involved in the process of rating the intensity of thermal stimuli - including the perception uncertainty. In order to include an account of inaccurate perception, one would have to consider different sources that contribute to this, which there may be many. In our approach, we consider one, which is captured in the expectation weighted model, more clearly exemplified in the expectation-weighted Kalman-Filter model (eKF). The model assumes participants perception of input as an imperfect indicator of the true level of pain. In this case, it turns out that perception is corrupted as a result of the expectation participants hold about the upcoming stimuli. The extent of this effect is partly governed by a subjective level of noise ϵ, which may also subsume other sources of uncertainty beyond the expectation effect. Moreover, the response noise ξ, could also subsume any other unexplained sources of noise.

Author response image 1.

Stimulis intensity transformation

Reviewer Comment 3.3 — A key conclusion drawn is that eKF is a better model than eRL. However, a closer examination of the results reveals that the two models behave very similarly, and it is not clear that they can be readily distinguished based on model recovery and model comparison results.

While, the eKF appears to rank higher than the eRL in terms of LOOIC and sigma effects, we don’t wish to make make sweeping statements regarding significance of differences between eRL and eKF, but merely point to the trend in the data. We shall make this clearer in the revised version of the manuscript. However, the most important result is that the models involving expectation-weighing are arguably better capturing the data.

Reviewer Comment 3.4 — Regarding model recovery, the distinction between the eKF and eRL models seems blurred. When the simulation is based on the eKF, there is no ability to distinguish whether either eKF or eRL is better. When the simulation is based on the eRL, the eRL appears to be the best model, but the difference with eKF is small. This raises a few more questions. What is the range of the parameters used for the simulations?

We agree that the distinction between eKF and eRL in the model recovery is not that clean-cut, which may in turn point to the similarity between the two models. To simulate the data for the model and parameter recovery analysis, we used the group means and variances estimated on the participant data to sample individual parameter values.

Reviewer Comment 3.5 — Is it possible that either eRL or eKF are best when different parameters are simulated? Additionally, increasing the number of simulations to at least 100 could provide more convincing model recovery results.

It could be a possibility, but would require further investigation and comparison of fits for different bins/ranges of parameters to see if there is any consistent advantage of one model over another is each bin. We will consider adding this analysis, and provide an additional 50 simulations to paint a more convincing picture.

Reviewer Comment 3.6 — Regarding model comparison, the authors reported that ”the expectation-weighted KF model offered a better fit than the eRL, although in conditions of high stochasticity, this difference was short of significance against the eRL model.” This interpretation is based on a significance test that hinges on the ratio between the ELPD and the surrounding standard error (SE). Unfortunately, there’s no agreed-upon threshold of SEs that determines sig- nificance, but a general guideline is to consider ”several SEs,” with a higher number typically viewed as more robust. However, the text lacks clarity regarding the specific number of SEs applied in this test. At a cursory glance, it appears that the authors may have employed 2 SEs in their interpretation, while only depicting 1 SE in Figure 4.

Indeed, we considered 2 sigma effect as a threshold, however we recognise that there is no agreed-upon threshold, and shall make this and our interpretation clearer regarding the trend in the data, in the revision.

Reviewer Comment 3.7 — With respect to parameter recovery, a few additional details could be included for completeness. Specifically, while the range of the learning rate is understandably confined between 0 and 1, the range of other simulated parameters, particularly those without clear boundaries, remains ambiguous. Including scatter plots with the simulated parameters on the x- axis and the recovered parameters on the y-axis would effectively convey this missing information. Furthermore, it would be beneficial for the authors to clarify whether the same priors were used for both the modelling results presented in the main paper and the parameter recovery presented in the supplementary material.

Thank for this comment and for the suggestions. To simulate the data for the model and parameter recovery analysis, we used the group means and variances estimated on the participant data to sample individual parameter values. The priors on the group and individual-level parameters in the recovery analysis where the same as in the fitting procedure. We will include the requested scatter plots in the next iteration of the manuscript.

Reviewer Comment 3.8 — While the reliance on R-hat values for convergence in model fitting is standard, a more comprehensive assessment could include estimates of the effective sample size (bulk ESS and/or tail ESS) and the Estimated Bayesian Fraction of Missing Information (EBFMI), to show efficient sampling across the distribution. Consideration of divergences, if any, would further enhance the reliability of the results.

Thank you very much for this suggestion, we will aim to include these measures in the revised version.

Reviewer Comment 3.9 — The authors write: ”Going beyond conditioning paradigms based in cuing of pain outcomes, our findings offer a more accurate description of endogenous pain regula- tion.” Unfortunately, this statement isn’t substantiated by the results. The authors did not engage in a direct comparison between conditioning and sequence-based paradigms. Moreover, even if such a comparison had been made, it remains unclear what would constitute the gold standard for quantifying ”endogenous pain regulation.”

This is valid point, indeed we do not compare paradigms in our study, and will remove this statement in the future version.

Author Response

We would first like to thank the reviewers for their time and effort in their critical review of our manuscript, and appreciate the opportunity to address these comments. We thank the reviewers for appreciating that our experimental design is well crafted, and contributes to the broader understanding of dietary exercise recommendations for metabolic health and muscle development. We have revised the figures and text in accordance with the reviewer’s recommendations, and hope that they appreciate the revised version.

Reviewer #1:

1) A significant limitation of this study pertains to the absence of a detailed exploration into the mechanistic underpinnings of the interaction between high protein intake and resistance exercise at the molecular level. The authors should provide a comprehensive discussion on potential avenues or prospective research directions to address this gap in understanding.

We agree and have added some theories in the discussion on page 14.

2) Figure 4 and Figure 7 can be moved to supplementary and text in the description can be arranged accordingly to make a better flow of the story.

We agree with this suggestion and have made adjustments.

3) The authors have used a high protein diet (36% calorie from protein) and a low protein diet (7% calorie from protein) for this study. The authors should explain whether this mouse diet is practically comparable to the human's high protein (2% of BW) and low protein diet (less than 0.8% BW) or not.

The high protein diet is comparable to a human diet of 180 grams of protein ((0.36x2000 calories)/4 calories per gram=180 g), which is in a range that some people consume, particularly bodybuilders and athletes. The low protein diet is equivalent to 35 grams of protein per day ((0.07x2000 calories)/4 calories/gram=35g), and a diet of just 7% protein is not recommended for humans per the Acceptable Macronutrient Distribution Range (AMDR) of 10-35% dietary protein set by the Institute of Medicine (IOM). We have addressed this on page 14.

4) The color coding of the error bar and lines does not match with the group description in almost every figure. Maybe the authors could choose more contrasting colors.

Thanks, we have adjusted the coloring of the error bars and lines in all figures.

5) In Figure 3C-E it seems like the number of biological samples is not consistent in the LP+WP group. If the authors have excluded any outlier from the analysis, that should be included in the methodology.

We did list outliers in the methodology in the statistics section (page 19): “Outliers were determined using GraphPad Prism Grubbs’ calculator (https://www.graphpad.com/quickcalcs/grubbs1/).”

Reviewer #2:

Very nice work! I do not have a whole lot to say in terms of experiments, analysis, or data to present other than what is in my public review (and you cannot really provide it as it was not in the experimental design). The manuscript is also very well written. My only question is about the following two sentences in the introduction:

"Both exercise and amino acids activate the mechanistic target of TOR (mTOR) protein kinase, which stimulates the protein synthesis machinery needed to stimulate skeletal muscle hypertrophy (Schiaffino et al., 2021). Therefore, The Academy of Nutrition and Dietetics recommends consuming 1.2-2.0 grams of protein per kg of body weight (BW) per day in physically active individuals (Thomas et al., 2016)." I am not sure how the second sentence follows from the first, so I am not convinced that "therefore" is the right adverb in the right place.

Thanks for pointing this out. We have added a clarifying transition to the text (page 3).

Author Response

The following is the authors’ response to the original reviews.

Reviewer 1

Major concerns.

-The experimental details on the electron microscopy data and more specifically on the processing is too minimal. Because of the missing pieces of information, the data cannot be trusted in its current state. The authors should explain how they processed the data: number of particles, software used, 3D reconstruction algorithms etc...For instance, they do not mention anything about the final resolution and whether they tried to improve it. What is the dimension of the boxes used for 2D classes and 3D reconstruction? Besides, the resulting 3D volumes should be displayed at different orientations or from, at least, a movie so one can see whether the modelled data actually fits into the 3D volume in various orientations. Have the authors tried cryo-EM to improve the resolution of the data? Have they generated 3D classes? Also they should comment on why the resolution if rather low.

Thank you for your valuable feedback on our work. We appreciate your suggestions for improvement and agree that we could provide more detailed information on the experimental details of our electron microscopy data. To address your concerns, we have provided additional information on the processing of the data in the revised manuscript.

Regarding the use of cryo-EM, we attempted to use this technique to determine the structure of autoinhibited kinesin-1. Unfortunately, we encountered challenges in getting the kinesin-1 to behave well on the grids, which prevented us from obtaining meaningful results.

-The report goes back and forth from focusing on KIF5B then KIF5C and back to KIF5B. It is thus confusing for the reader and the rationale for highlighting a specific isoform is not clear. Hence the authors should perform similar analysis for both isoforms. Specifically the alpha fold deed learning modeling should also be performed using KIF5C in parallel with the analysis performed on KIF5B.

Thank you for your feedback on our manuscript. We apologize for any confusion caused by the shifting focus between KIF5B and KIF5C. The KIF5B and KIF5C are both kinesin-1 isoforms, should have high structural similarity and should adopt similar structures.

In our current manuscript, we performed AlphaFold structure prediction on both KIF5B and KIF5C stalks and found that they adopt the same structure. Furthermore, the XL-MS data suggests that KIF5B and KIF5C exhibit similar patterns. We choose to model the KIF5B in this case.

For the kinesin-1 tetramer, we re-performed XL-MS on KIF5B-KLC1 and KIF5C-KLC1 (Author response image 1 and 2) to confirm our analysis in the manuscript. Both data showed that KIF5B-KLC1 and KIF5C-KLC1 have a similar folding pattern. The differences between the two are: (1) The crosslinks within the KIF5B are sparse compared to KIF5C. (2) There are fewer crosslinks between KIF5B and KLC1 compared to KIF5C-KLC1. These differences will need further investigation. Given that there are more crosslinks in KIF5C-KLC1, we choose to model the KIF5C-KLC1 in our manuscript.

Author response image 1.

Crosslinked lysine pairs in KIF5B-KLC1 were mapped onto the domain diagram.

Author response image 2.

Crosslinked lysine pairs in KIF5C-KLC1 were mapped onto the domain diagram.

-The proportion of compact versus extended form for KIF5B and KIF5C differs. It seems that KIF5B has a higher proportion of compact conformations both as homodimers and heterotetramers? Can the authors comment on this and suggest any possible molecular argument which would induce this difference? Can the authors comment on this discrepancy? What would induce any extended form given that the wild type constructs should be compact only? Is there any equilibrium in solution between the two conformations?

Thank you for your comments on our manuscript. We appreciate your observation that the proportion of compact versus extended form for KIF5B and KIF5C appears to differ. We did observe that KIF5B has a higher proportion of compact conformations both as homodimers and heterotetramers. We have updated our main text and commented on this difference. We do not have a definitive explanation for this difference, but one possibility is that the differences in the sequence of the two isoforms may contribute to their differential propensities for compact versus extended conformations. It is possible that there is an equilibrium between the two conformations, but we did not explicitly investigate this in our study.

• In Figure 1.C, lower panel, the "extended" conformation does not appear as extended as stated in the text, looking at the negative stain image. In particular, the one on the bottom right look rather compact, instead. The resulting graph shown in Figure 1.E seems a bit off as compared with the images. How were the measurements performed to generate figure 1.E? Were all the particles selected for measurement or were only some of them picked or were the measurements done using class averages? In the same line, the authors should show class averages of the extended conformation as well.

Thank you for your feedback on our manuscript. We appreciate your comments on the presentation of our data in Figure 1C. We agree that some kinesin may not appear as extended in the negative stain images as we stated in the text. For EM sample preparation, we took the fraction corresponding to the extended conformation, used BS3 to crosslink them and then examined them under EM. The compact kinesin-1 molecule could come from the aggregated molecule during the crosslinking process.

Regarding the measurement, we measured the length of individual molecules which clearly looks like the KIF5B from the raw micrographs. Molecules that show any sign of aggregation were not measured. For the class averages of the extended state, given that the extended molecule is about 80 nm in length and very flexible, it would be hard to get meaningful averages. We have updated the methods section to include this measurement method.

-In figure 2B, the EM envelope does not accommodate the CC1 domain which extends way beyond the contour of the 3D volume and thus suggest that the modeling and/or the 3D EM reconstruction is not correct. Also the authors do not comment at all on this even though this is a striking feature. The CC1 might thereby be less disorganized or more flexible than expected by the model.

Thank you for your feedback on our manuscript, particularly with regard to Figure 2B. We appreciate your observation that the EM envelope does not accommodate the CC1 domain, which extends beyond the contour of the 3D volume. We agree that this is a striking feature that may suggest that the modeling and/or the 3D EM reconstruction is not entirely correct. We have added comments regarding this feature in the main text. However, given the current data, we could not generate a better model to describe the structure of CC1 besides using results from the AlphaFold prediction.

-The so called "C-shaped" feature on the class averages (Fig 3D) does not stand out clearly on all of the class averages. It is visible on the right hand panels but not visible on the left hand side. What is the proportion of classes and thus of the dataset which clearly displayed this peculiar C-shaped feature?? Can the authors analyze this?

Thank you for your feedback on our manuscript, particularly with regard to Figure 3D. We acknowledge your observation that the "C-shaped" feature is not clearly visible on all of the class averages. We believe that it could be due to the different orientations of the class averages. We have revised our main text to comment on this.

-The different mutants were subjected to motility assays. However, mutations/truncations could strongly affect their structural features and conformation. The authors should thus, at least for some of them, check their global ultrastructure using electron microscopy, for instance, and 2D class averaging. In particular, it would be worthwhile testing how different mutations induce any transition from a compact to an extended state. Besides, it is not specified whether the truncated mutants are homo-dimeric or monomeric.

Thank you for your valuable feedback on our manuscript, particularly with regard to the motility assays conducted on the different mutants. All the KIF5B mutants should be homodimers as WT KIF5B. We agree that it would be beneficial to check some of the mutants under EM to examine their conformation. However, due to time constraints, we were unable to perform these analyses.

Minor concerns

• Does AlphaFold generate several possible models? Can a selection of those be displayed at least in the supplementary material so the reader can understand how any given model is selected? A short introduction on the alpha fold methodology and how the different obtained structures compare with one another and ultimately how the best structure is selected.

Yes, AlphaFold generates several possible models during the protein structure prediction process. These models are ranked based on their confidence scores, which reflect the degree of certainty with which AlphaFold has predicted each model. In our study, we chose the model with the highest score, while we noticed that the top 5 models from the AlphaFold prediction generally tend to be very similar in the case of the kinesin-1 structure prediction. We have updated the text in the method section to help the reader appreciate our approach.

-When expressing the hetero-tetramers, do the authors generate homodimers as well? If so, can they estimate the relative proportion of all the possible populations?

We used the multibac expression system to co-express the kinesin heavy chain and light chain in sf9 cells. We believe that the hetero-tetramers should account for the majority of products, though we can not rule out the possibility of formation of homodimers.

-The motility assays should be better described.

We have added more text to describe the assay.

-The report does not discuss whether any combinations of isoforms (for instance KIF2B-KIF2C) could assemble into a complex and whether it has already been observed in cells?

We believe that you are asking about whether KIF5B and KIF5C form heterodimer. We did not see any previous literature report on this and have not tested this possibility.

-The authors should discuss why they do not obtain the same results as Kaan et al (2011). For instance, would the experimental conditions responsible for the discrepancies observed?

In the study done by Kaan et al (2011), their structures showed that kinesin-1 motor domains crystallized with a tail peptide holding the motors in an immotile conformation, which supports the model of kinesin-1 autoinhibition where the C-terminal tail of kinesin-1 drives autoinhibition to block motility. However, there are several limitations regarding this study as we mentioned in our manuscript. First, the authors used truncated kinesin heavy chains that only include the motor domain and the neck coil instead of the full length protein. Second, the crystal structure was obtained by adding the tail peptide in trans. Thus, how kinesin-1 folds into an autoinhibited state remains poorly understood, severely limiting our understanding of kinesin-1 regulation.

Our model confirms the critical role of the tail domain as the study done by Kaan et al (2011). We observe that the tail domain lies very close to the motor heads which are consistent with what has been reported in the study done by Kaan et al (2011). However, due to lack of enough lysine residues and the unstructured nature of the tail domain, we could not resolve the exact conformation of the tail domain.

We have addressed the question in our discussion section regarding the tail domain and IAK motif.

-A final schematic model would be beneficial to support the model and could be inserted within the discussion section.

We have added a final model figure as Figure 7 in the discussion section.

-The authors should discuss why the shortest mutant is the most active in the motility assay and how this compares with the full length protein in vivo? Can full-length kinesin1 reach similar motility?

The shortest mutant KIF5B(1-420) only contains the motor domain and CC1, without any regulatory elements to lock it into the inhibited state. It should reflect the intrinsic biophysical property of the kinesin-1 motor domain on the microtubules. We have revised our main text to include this point. However, kinesins in cells are all full length proteins and are subjected to multiple layers of regulation. It would be hard to make the comparison between full length kinesins in vivo and the shortest mutant KIF5B(1-420).

-Have the authors attempted to obtain the structure of a TRAK-1 kinesisn1 complex, for instance by electron microscopy? Will they consider addressing the structure of such full complexes to see whether the protein-protein interactions they infer are indeed reflected within the complexes?

Yes, we did want to check the TRAK1-KIF5B complex using negative staining EM. However, due to the flexibility of TRAK1-KIF5B complex and the low contrast of TRAK1 protein under the negative staining EM, we could not get meaningful results.

-Can the authors test kinesin-TRAK1 complexes in motility assays?

There are already two studies (Canty et al., 2021, Henrichs et al., 2020) that confirmed that TRAK1 can activate the motility of kinesin-1, which we cited in our manuscript. Therefore, we did not test it in our studies.

Reviewer 2

-The lack of crosslinks seems to be interpreted as the lack of interactions, but that this is not necessarily the case. Also BS3 crosslinks mainly amino groups that are about 25A apart, which gives a read out of proximity rather than interactions. How many times were the crosslinking experiments done? In figure 6, there are not many crosslinks for TRAK and kinesin-1 so it would be good to know if it has been repeated.

The number of XL-MS we have done for each sample are: KIF5B (three times), KIF5C (once), KIF5B-KLC1 (twice), KIF5C-KLC1 (twice), KIF5B(1-562) (once), KIF5B-TRAK1 (once) and KIF5B(IAK/AAA) (once). We have added the above information in the method section for the XL-MS.

For the kinesin-1 heterotetramers, we re-performed XL-MS on KIF5B-KLC1 and KIF5C-KLC1 (Figure 1 and Figure 2) to validate our analysis in the manuscript, which shows consistent results as in our manuscript. For the XL-MS experiment on the KIF5B-TRAK1 complex, due to the time limitation, we only performed it once but would like to explore it in the future.

We summarized identified cross-linked pairs for each kinesin-1 sample as supplementary files.

-Regarding the interaction between TRAP and Kif5b, the authors propose TRAP activate Kif5b by disrupted the autoinhibited conformation from the lack of crosslinks and the position of the cross-links identified. What does Kif5b+TRAP (after or before crosslinking) look like by negative stain EM? The authors have done this experiments for the other samples Kif5b and Kif5b KLC so it would should be easy for the authors to do this for Ki5f5b-TRAP. Also can alphafold mutimer predict the Ki5fb-TRAP interface?

Thanks for bringing this up. We tried to get the EM images for the TRAK1-KIF5B complex. We observed that the KIF5B alone and the TRAK1-KIF5B complex tend to fall apart if not being crosslinked before putting onto the grids. For the crosslinked samples, we are unable to see the TRAK1 clearly on the KIF5B due to the flexibility of the TRAK1-KIF5B complex and the low contrast of TRAK1 protein under the negative staining EM. We would like to explore this further.

As for the AlphaFold prediction on KIF5B-TRAK1 complex, we found that AlphaFold did not perform well in predicting the TRAK1 on kinesin-1 stalk. We tried the combination of various TRAK1 and KIF5B fragments, but could not get any meaningful results.

-Figure 4. Very long crosslinks are not explained by the model, and suggest the model could be partially incorrect. Can the authors state the distance between the crosslinked residues in their model in figures? Generally the authors should report all crosslink distance in their figures with molecular models.

Thanks for bringing this up. For the model building, we used the XL-MS data as guidance to model the autoinhibited kinesin-1 with the input from AlphaFold structure prediction and EM map. We assembled the model by piecing together multiple rigid kinesin-1 fragments generated from AlphaFold structure prediction as described in the method section.

We realize that some crosslinked residues in our model have distances greater than the maximum distance allowed for the BS3 crosslinkers, especially for the crosslinked pairs between the TPR and motor domain. We admit that our current model could be partially incorrect. Since we do not have high resolution structure data on kinesin-1, we are unsure about how to make our model to satisfy all the distance constraints. We have addressed the above limitations in our discussion section.

-Figure 5: motility assays, the amount of data analyzed seems quite low. There are only 2 repeats done for each condition. The number of microtubules is reported rather than number of measurements done-can the authors report number of events/motors measured. It would be useful to have the concentration of motors used in the figure. Landing rate: are authors not differentiating motile vs non motile tracks also? What do the mutants look like in EM class averages?

Thanks for bringing this up. We have revised our method section about the single molecule assay to include this information.

Finally, we agree that it would be beneficial to check the mutants under EM. However, due to time limitations, we were unable to perform this experiment.

-The figure in 6D needs revising. This does not look like a pulldown experiment, controls are missing and the proteins do not seem to be stoichiometric. In particular, the third lane. There are also no protein markers.

Thank you for bringing this up. We revised Figure 6 and added the protocol for the pulldown assay in our method section for protein expression and purification.

Minor points

-Is the data available in PRIDE, etc...? Could the authors provide a table of xlinks?

We have included crosslinked pairs detected in our XL-MS as supplementary files for KIF5B, KIF5C, KIF5B-KLC1, KIF5C-KLC1, KIF5B(1-565), KIF5B(IAK/AAA) and KIF5B-TRAK1. We have added a new section called Data Availability in the main manuscript to fully describe this.

-It would be better to have the mapping of the crosslinks in the same figures as the corresponding crosslink map.

Due to the layout of the figure, we choose to show the model and the mapped crosslinks in the same figure.

-No crosslinks were obtained between the IAK motif and the motor domain. This could be due to the lack of neighbouring groups that can crosslink with the K in the motif, rather than the tail not binding/crosslinking to the motor. The text could be edited to explain this

Thanks for bringing this up. We edited the text to add this point.

-Figure 5. Typo in mutation

We revised the figure5

-No hyphen between c and terminus (as that is a noun)

Author Response

Reviewer #1 (Public Review):

Summary:

Rai1 encodes the transcription factor retinoic acid-induced 1 (RAI1), which regulates expression of factors involved in neuronal development and synaptic transmission. Rai1 haploinsufficiency leads to the monogenic disorder Smith-Magenis syndrome (SMS), which is associated with excessive feeding, obesity and intellectual disability. Consistent with findings in human subjects, Rai1+/- mice and mice with conditional deletion of Rai1 in Sim+ neurons, which are abundant in the paraventricular nucleus (PVN), exhibit hyperphagia, obesity and increased adiposity. Furthermore, RAI1-deficient mice exhibit reduced expression of brain-derived neurotrophic factor (BDNF), a satiety factor essential for the central control of energy balance. Notably, overexpression of BDNF in PVN of RAI1-deficient mice mitigated their obesity, implicating this neurotrophin in the metabolic dysfunction these animals exhibit. In this follow up study, Javed et al. interrogated the necessity of RAI1 in BDNF+ neurons promoting metabolic health.

Consistent with previous reports, the authors observed reduced BDNF expression in the hypothalamus of Rai1+/- mice. Moreover, proteomics analysis indicated impairment in neurotrophin signaling in the mutants. Selective deletion of Rai1 in BDNF+ neurons in the brain during development resulted in increased body weight, fat mass and reduced locomotor activity and energy expenditure without changes in food intake. There was also a robust effect on glycemic control, with mutants exhibiting glucose intolerance. Selective depletion of RAI1 in BDNF+ neurons in PVN in adult mice also resulted in increased body weight, reduced locomotor activity, and glucose intolerance without affecting food intake. Blunting RAI1 activity also leads to increases and decreases in the inhibitory tone and intrinsic excitability, respectively, of BDNF+ neurons in the PVN.

Strengths:

Overall, the experiments are well designed and multidisciplinary approaches are employed to demonstrate that RAI1 deficits in BDNF+ neurons diminish hypothalamic BDNF signaling and produce metabolic dysfunction. The most significant advance relative to previous reports is the finding from electrophysiological studies showing that blunting RAI1 activity leads to increases and decreases the inhibitory tone and intrinsic excitability, respectively, of BDNF+ neurons in the PVN. Furthermore, that intact RAI1 function is required in BDNF+ neurons for the regulation of glucose homeostasis.

Weaknesses:

Some of the data need to be reconciled with previous findings by others. For example, the authors report that more than 50% of BDNF+ neurons in PVN also express pTrkB whereas about 20% of pTrkB+ cells contain BDNF, raising the possibility that autocrine mechanisms might be at play. This is in conflict with a previous study by An et al, (2015) showing that these cell populations are largely non-overlapping in the PVN.

We fully agree with this assessment. Given the difficulty of using immunostaining to characterize the expression of membrane proteins in vivo, and the specificity of the pTrkB antibody in different tissues remains unknown, it is difficult to interpret the signals we observed. We have excluded the data because the histological analysis of p-TRKB and BDNF autocrine/paracrine signalling is not a focus of the present study. Future studies using a more advanced genetic method (i.e., Ntrk2CreER/+; Ai9 mouse line as used by An et al., 2015) is more suitable and should be used in the future to investigate the function of Rai1 in the TRKB+ neurons.

Another issue that deserves more in-depth discussion is that diminished BDNF function appears to play a minor part driving deficits in energy balance regulation. Accordingly, both global central depletion of Rai1 in BDNF+ neurons during development and deletion of Rai1 in BDNF+ neurons in the adult PVN elicited modest effects on body weight (less than 18% increase) and did not affect food intake. This contrasts with mice with selective Bdnf deletion in the adult PVN, which are hyperphagic and dramatically obese (90% heavier than controls). Therefore, the results suggest that deficits in RAI1 in PVN or the whole brain only moderately affect BDNF actions influencing energy homeostasis and that other signaling cascades and neuronal populations play a more prominent role driving the phenotypes observed in Rai1+/- mice, which are hyperphagic and 95% heavier than controls. The results from the proteomic analysis of hypothalamic tissue of Rai1 mutant mice and controls could be useful in generating alternative hypotheses. Depleting RAI1 in BDNF+ neurons had a robust effect compromising glycemic control. However, as the approach does not necessarily impact BDNF exclusively, there should be a larger discussion of alternative mechanisms.

We thank the reviewer for these insightful comments. We want to highlight that global deletion of Rai1 from BDNF neurons did induce food intake increase in male mice (Fig 2figure supplement 4K). We have incorporated the following paragraphs into the discussion section.

Lines 364-384: “Notably, mice lacking one copy of Rai1 in the BDNF-producing cells do not exhibit obesity, whereas SMS patients and SMS mice show pronounced obesity (Burns et al., 2010; Huang et al., 2016; Smith et al., 2005). This indicates that although reduced Bdnf expression and BDNF-producing neurons contribute to regulating body weight, additional molecular changes and other hypothalamic populations also play important roles in regulating body weight homeostasis in SMS. Our RPPA data suggest that mTOR signalling is also misregulated in addition to the reduced activation of the neurotrophin downstream cascades. Hypothalamic mTORC1 is crucial to regulate glucose release from the liver, peripheral lipid metabolism, and insulin sensitivity (Burke et al., 2017; Caron et al., 2016; Smith et al., 2015), while mTORC2 regulates glucose tolerance and fat mass (Kocalis et al., 2014). How the impaired mTOR signalling contributes to energy homeostasis defects in SMS and the therapeutic potential of targeting this pathway to treat SMS-related obesity remains unclear and warrants future investigation.

What additional Rai1-dependent hypothalamic cell types residing in brain regions other than PVH regulate obesity in SMS? Other important cell types such as TRKB neurons within the PVH (An et al., 2020) and several RAI1-expressing hypothalamic nuclei including the arcuate nucleus, ventromedial nucleus of the hypothalamus (VMH), and lateral hypothalamus all play important roles in regulating energy homeostasis. POMC- and AGRP-expressing neurons within the arcuate nucleus are known to regulate food intake and glucose and insulin homeostasis (Quarta et al., 2021; Vohra et al., 2022). Therefore, Rai1 function in these neurons could contribute to obesity in SMS, a topic that awaits future investigation.”

Reviewer #2 (Public Review):

Understanding disease conditions often yields valuable insights into the physiological regulation of biological functions, as well as potential therapeutic approaches. In previous investigations, the author's research group identified abnormal expression of brain-derived neurotrophic factor (BDNF) in the hypothalamus of a mouse model exhibiting Smith-Magenis syndrome (SMS), which is caused by heterozygous mutations of the Rai1 gene. Human SMS is associated with distinct facial characteristics, sleep disturbances, behavioral issues, and intellectual disabilities, often accompanied by obesity. Conditional knockout (cKO) of the Bdnf gene from the paraventricular hypothalamus (PVH) in mice led to hyperphagic obesity, while overexpression of the Bdnf gene in the PVH of Rai1 heterozygous mice restored the SMS-like obese phenotype. Based on these preceding findings, the authors of the present study discovered that homozygous Rai1 cKO restricted to Bdnf-expressing cells, or Rai1 gene knockdown solely in Bdnf-positive neurons in the PVH, induced obesity along with intricate alterations in adipose tissue composition, energy expenditure, locomotion, feeding patterns, and glucose tolerance, some of which varied between sexes. Additionally, the authors demonstrated that a brain-penetrating drug capable of activating the TrkB pathway, a downstream signaling pathway of BDNF, partially alleviated the SMS-like obesity phenotype in female mice with Rai1 heterozygous mutations. Although the specific (neural) cell type responsible for this TrkB signaling remains an open question, the present study unequivocally highlights the importance of Rai1 gene function in PVH Bdnf neurons for the obesity phenotype, providing valuable insights into potential therapeutic strategies for managing obesity associated with SMS.

In the proteomic analysis (Fig. 1), the authors elucidated that multiple phospho-protein signaling pathways, including Akt and mTOR pathways, exhibited significant attenuation in the SMS model mice. Of significance, the manifestation of haploinsufficiency of the Rai1 gene exclusively within the BDNF+ cells demonstrated negligible impact on body weight (Fig. 2supple 3D), despite observing a reduction in BDNF levels in the heterozygous Rai1 mutant (Fig. 1A). Conversely, the homozygous Rai1 cKO in the BDNF+ cells prominently displayed an obesity phenotype, suggesting substantial dissimilarities in the gene expression profiles between Rai1 heterozygous and homozygous conditions within the BDNF+ cell population. It would be advantageous to precisely identify the responsible differentially expressed genes, possibly including Bdnf itself, in the homozygous cKO model. The observed reduction in the excitability of PVH BDNF+ cells (Fig. 3) is presumably attributed to aberrant gene expression other than Bdnf itself, which may serve as a prospective target for gene expression analysis. Notably, the Rai1 homozygous cKO mice in BDNF+ cells exhibited some sexual dimorphisms in feeding and energy expenditures, as evidenced by Fig. 2 and related figures. Exploring the potential relevance of these sexual differences to human SMS cases and investigating the underlying cellular/molecular mechanisms in the future would provide valuable insights.

Although the CRISPR-mediated knockdown of the Rai1 gene (Fig. 4) appears to be highly effective, given the broad transduction of AAV serotype 9, it may be helpful to exclude the possibility of other brain regions adjacent to the PVH, such as the DMH or VMH, being affected by this viral procedure. If the PVH-specificity is established, the majority of Rai1 cKO effects in Bdnf+ cells are primarily attributed to PVH-Bdnf+ cells based on the similarity of phenotypes observed. With regards to the apparent rescue of the body weight phenotype in Rai1 heterozygous mutants using a selective TrkB activator, the specific biological processes, and neurons responsible for this effect remain unclear to this reviewer. Elucidating these aspects would be significant when considering potential applications to human SMS cases.

We appreciate the reviewer's insightful comments. We agree that the logical next step would be to identify the profile of the differentially expressed genes in our homozygous conditional knockout model. We have included the following paragraphs in the discussion.

Lines 364-384: “Notably, mice lacking one copy of Rai1 in the BDNF-producing cells do not exhibit obesity, whereas SMS patients and SMS mice show pronounced obesity (Burns et al., 2010; Huang et al., 2016; Smith et al., 2005). This indicates that although reduced Bdnf expression and BDNF-producing neurons contribute to regulating body weight, additional molecular changes and other hypothalamic populations also play important roles in regulating body weight homeostasis in SMS. Our RPPA data suggest that mTOR signalling is also misregulated in addition to the reduced activation of the neurotrophin downstream cascades. Hypothalamic mTORC1 is crucial to regulate glucose release from the liver, peripheral lipid metabolism, and insulin sensitivity (Burke et al., 2017; Caron et al., 2016; Smith et al., 2015), while mTORC2 regulates glucose tolerance and fat mass (Kocalis et al., 2014). How the impaired mTOR signalling contributes to energy homeostasis defects in SMS and the therapeutic potential of targeting this pathway to treat SMS-related obesity remains unclear and warrants future investigation.

What additional Rai1-dependent non-PVH hypothalamic cell types regulate obesity in SMS? Other important cell types such as TRKB neurons within the PVH (An et al., 2020) and several RAI1expressing hypothalamic nuclei including the arcuate nucleus, ventromedial nucleus of the hypothalamus (VMH), and lateral hypothalamus all play important roles in regulating energy homeostasis. POMC- and AGRP-expressing neurons within the arcuate nucleus are known to regulate food intake and glucose and insulin homeostasis (Quarta et al., 2021; Vohra et al., 2022). Therefore, Rai1 function in these neurons could contribute to obesity in SMS, a topic that awaits future investigation.”

Lines 409-418: “It is plausible that RAI1 regulates the expression of genes encoding inward rectifier K+ channels, which regulate neuronal activity and potentially energy homeostasis. For instance, KIR6 (a family of ATP-sensitive potassium channels, KATP) is widely expressed in the hypothalamus. Deleting the hypothalamic KIR6.2 subunit impairs KATP channel function and glucose tolerance (Miki et al., 2001; Parton et al., 2007). Moreover, reduced expression of hypothalamic GIRK4 (encoding an inwardly rectifying potassium channel) causes obesity (Perry et al., 2008). GABAergic neurotransmission from arcuate AGRP-expressing neurons to the PVH neurons is important to increase appetite by favouring hyperphagia (Atasoy et al., 2012). Disrupting the composition of these ion channels could contribute to reduced PVHBDNF neuronal firing, which awaits further investigations.”

Moreover, to facilitate the future exploration of the potential relevance of sexual differences to human SMS cases, we have incorporated the following explanation in the discussion section.

Lines 419-426: “Female mice with a conditional knockout of Rai1 from BDNF-producing neurons do not display a noteworthy difference in food intake. Conversely, their male counterparts exhibit a significant increase in food intake. Although SMS individuals of both genders tend to overeat, male patients who are obese show significantly higher food consumption than their female counterparts (Gandhi et al., 2022). This observation raises the possibility that Rai1 regulates eating behaviours through multiple cell types in the hypothalamus and that a male-specific involvement of BDNF-producing neurons in regulating food intake, potentially provides a neurobiological basis for the observed pattern in SMS patients (Gandhi et al., 2022).”

To exclude the possibility of other brain regions adjacent to the PVH (such as VMH and arcuate nucleus) being affected by our AAV-CRISPR-mediated Rai1 knockout, we have analyzed other hypothalamic regions including VMH and arcuate nucleus from the same slides used to confirm PVH viral expression and we confirmed that the AAV was not expressed in these regions. We have incorporated a representative image (Figure 4 suppl 1F) depicting limiting AAV expression in these nuclei.

Regarding LM22A-4: It is possible that LM22A-4 functions directly through binding to TRKB or indirectly engages TRKB downstream molecules through activating other receptors such as GPCR. LM22A-4 appears to engage neurotrophin downstream PI3KAKT pathway, which was identified by our RPPA analysis to be downregulated in the hypothalamus of Rai1-deficient mice. Reduced AKT activity is associated with insulin resistance and obesity in mice. Restoration of functional activity of AKT by LM22A-4 could be the primary mode of action for this drug in the brain. However, since we observed that this drug only partially rescued the body weight defect, future research exploring more potent TrkB agonists or utilizing a combination therapy that targets both the neurotrophin and mTOR pathways might yield improved responses to the pharmacological interventions. We have included the following paragraph in the discussion:

Lines 451-461: “ We recognize that while several in vivo studies have demonstrated the potential of LM22A-4 in targeting neurotrophin downstream signalling (Kron et al., 2014; Li et al., 2017), an in vitro analysis failed to demonstrate the ability of LM22A-4 to activate TrkB directly (Boltaev et al., 2017). Therefore, the precise mechanism by which LM22A-4 enhances AKT cascades in the mammalian brain remains unclear and awaits further investigations. In the hypothalamus of SMS mice, LM22A-4 could indirectly engage neurotrophin downstream PI3KAKT pathway through the G protein-coupled receptor-dependent transactivation of the TRKB receptor (Domeniconi & Chao, 2010) or other unknown mechanisms. Moreover, while LM22A4 may have potential side effects, we found that wild-type mice treated with LM22A-4 did not show a further decrease in body weight, suggesting limited side effects regarding body weight regulation.”

Overall, the present study represents a valuable addition to the authors' series of high-quality molecular genetic investigations into the in vivo functions of the Rai1 gene. This reviewer particularly commends their diligent efforts to enhance our comprehension of SMS and contribute to the future development of more effective therapies for this syndrome.

We thank the reviewer for finding our study valuable in advancing the understanding of RAI1 function.

Reviewer #3 (Public Review):

Summary:

Smith-Magenis syndrome (SMS) is associated with obesity and is caused by deletion or mutations in one copy of the Rai1 gene which encodes a transcriptional regulator. Previous studies have shown that Bdnf gene expression is reduced in the hypothalamus of Rai1 heterozygous mice. This manuscript by Javed et al. further links SMS-associated obesity with reduced Bdnf gene expression in the PVH.

Strengths:

The authors show that deletion of the Rai1 gene in all BDNF-expressing cells or just in the PVH BDNF neurons postnatally caused obesity. Interestingly, mutant mice displayed sexual dimorphism in the cause for the obesity phenotype. Overall, the data are well presented and convincing except the data from LM22A-4.

Weaknesses:

1) The most serious concern is about data from LM22A-4 administration experiments (Figure 5 and associated supplemental figures). A rigorous study has demonstrated that LM22A-4 does not activate TrkB (Boltaev et al., Science Signaling, 2017), which is consistent with unpublished results from many labs in the neurotrophin field. It is tricky to interpret body weight data from pharmacological studies because compounds always have some side effects, which can reduce body weight non-specifically.

We thank this reviewer for their valuable comments. Indeed, the precise mechanism by which LM22A-4 exerts its effect is not entirely clear and there has been mixed evidence regarding its identity as a TRKB agonist in vitro. We have refrained from stating LM22A-4 as a partial agonist of TRKB, and instead have focused on highlighting the potential of this drug in activating neurotrophin downstream signalling through increasing AKT phosphorylation in vivo. We have modified the title to remove TRKB, and the following changes have been made in the discussion:

Lines 451-461: “ We recognize that while several in vivo studies have demonstrated the potential of LM22A-4 in targeting neurotrophin downstream signalling (Kron et al., 2014; Li et al., 2017), an in vitro analysis failed to demonstrate the ability of LM22A-4 to activate TrkB directly (Boltaev et al., 2017). Therefore, the precise mechanism by which LM22A-4 enhances AKT cascades in the mammalian brain remains unclear and awaits further investigations. In the hypothalamus of SMS mice, LM22A-4 could indirectly engage neurotrophin downstream PI3KAKT pathway through the G protein-coupled receptor-dependent transactivation of the TRKB receptor (Domeniconi & Chao, 2010) or other unknown mechanisms. Moreover, while LM22A4 may have potential side effects, we found that wild-type mice treated with LM22A-4 did not show a further decrease in body weight, suggesting limited side effects regarding body weight regulation.”

2) The resolution of all figures are poor, and thus I could not judge the quality of the micrographs.

We have updated with higher resolution images.

3) Citation of the literature is not precise. The study by An et al. (2015) shows that deletion of the Bdnf gene in the PVH leads to obesity due to increased food intake and reduced energy expenditure (not just hyperphagic obesity; Line 72). Furthermore, the study by Unger et al. (2017) carried out Bdnf deletion in the VMH and DMH using AAV-Cre and did not discuss SF1 neurons at all (Line 354). The two studies by Yang et al. (Mol Endocrinol, 2016) and Kamitakahara et al. (Mol Metab, 2015) did use SF1-Cre to delete the Bdnf gene and did not observe any obesity phenotype.

We thank the reviewer for bringing this to our attention. We have revised the text to ensure accurate representation of the cited publications. The following changes have been made: Lines 348-350: “ Although BDNF is required in the VMH and DMH to regulate body weight (Unger et al., 2007), embryonic deletion of Bdnf from the SF1-lineage populations including the VMH did not result in obesity (Kamitakahara et al., 2016; Yang et al., 2016).”

4) Animal number is not described in many figure legends.

We thank the reviewer for pointing it out. We have revised the manuscript to incorporate the missing animal numbers.

Reviewer #1 (Recommendations For The Authors):

Additional points:

1) The data provided indicating increased inhibitory tone onto BDNF neurons in PVN of Rai1 mutant mice are not convincing that inhibitory drive is significantly affected.

We have modified the sentences as follows, we have also deleted these conclusions from the abstract and discussion:

Lines 215-220: “We observed a slight rightward shift of the probability of miniature inhibitory postsynaptic current (mIPSC) frequency in cKO PVHBDNF neurons, although the average frequency (Fig 3K) was not significantly different between groups. The probability of mIPSC amplitude also showed a right shift without a significant change (Fig 3L, Figure 3—figure supplement 1D). However, we observes a significant increased area under the curve (Fig 3M).”

2) Fig. 3C - Was outlier analysis performed for these data? One of the data points for the control group looks like an outlier that might be skewing the data.

We performed an outlier analysis and found that indeed one data point was an outlier, after removing this data point, the data remained statistically significant (*p<0.05) and the new manuscript has been updated.

Reviewer #2 (Recommendations For The Authors):

1) The manuscript would benefit from improved usage and precise descriptions of statistics. The authors often provided only general statements such as "one or two-way ANOVA" without specifying the exact statistical tests used. It is important to differentiate between one-way and two-way ANOVA, particularly when using the latter, by clearly indicating the within-group effects and interaction effects. The representation of p-values associated with ANOVA using asterisks requires clarification, specifying which statistics indicate ANOVA results and which ones correspond to post hoc analysis. It is advisable to assess the normality of the distribution before employing t-tests or consider non-parametric comparisons such as Wilcoxon's rank sum test if normality assumptions are not met. Additionally, it is essential to specify whether the tests are one-sided or two-sided and whether they are paired or unpaired. In some figure panels, such as Fig. 2H and K, the statistical tests used were not indicated at all.

We have clarified the exact statistical tests in the figure legend for each figure.

2) Rearranging the figures to facilitate a direct comparison of the sexual phenotypes (Fig. 2 and Fig. 2-supple 4) within the same figures would greatly improve reader comprehension.

We have decided to keep the figure arrangement because of the focus on female mice in the main figures.

3) To improve the comprehension of the figures and text, the following points should be addressed:

• Fig. 1D: The definition of the expression level in the color code is not clear.

Explanation for the color code has been added in the method section.<br /> Lines 652-656: “The vertical axis of the dendrogram represents the dissimilarity (measured as distance) between protein expressions, and the horizontal axis represents the individual test samples. The colour code (ranging from red to yellow to green) specifies the expression levels of different proteins, where red indicates nifies low expression, yellow indicates intermediate expression, and green indicates high expression.”

• Fig. 1F: One parenthesis is missing from the figure label.

Fixed

• Fig. 2C: It is unclear why there are so many dots for just n = 3 animals. It would be better to specify the conditions or use "animals" as a unit of measurement.

The dots represent percentage cells quantified per sliced from 3 animals. It has been clarified in the figures.

• Fig. 2F: There seems to be an unnecessary label "I" in the middle of the panel.

Fixed

• It is not completely clear if the data in Fig. 2E-L were all obtained at 26 weeks of age.

To clarify, following line has been added to the method section:

Lines 517-518: “After the 25th week, mice were subjected to body composition analysis.”

• In Fig. 2-Supple 1, the legend should read "G-J." Additionally, please provide a definition for the arrowheads.

Line 1086: “yellow arrowheads indicate Ai9 marked BDNF cells co-expressing endogenous BDNF.”

• It is not completely clear if the data in Fig. 3 were all obtained from female mice.

It is explained in the legend of Fig 3.

• The description of the number of animals seems to be missing in Fig. 4

The description for the number of animals has been added in the figure legend. Line 1004: “(Ctrl group: n=5, Exp group: n =5)”

• On line 280-281, "Fig 4A." should be corrected to "Fig. 5A."

Corrected.

• In Fig. 5C-E, it is uncertain if multiple pairwise comparisons for three groups are statistically appropriate. At the very least, multiple comparisons should be corrected.

We performed two-way ANOVA where mean body weight of age-matched groups were compared with each other (i.e. between control saline-injected and SMS saline-injected, SMS saline-injected and LM22A-4 -saline injected, and Control saline-injected and SMS LM22A-4 injected). We used Šidák’s multiple comparisons test, where statistical significance was indicated with p<0.05, p < 0.01, p<0.001, **p < 0.0001. We have clarified this in the figure 5 legends.

• The unit of measurement should be standardized across figures, if possible, to facilitate better side-by-side comparisons. For example, most bodyweight figures use "g" (grams), but "mg" (milligrams) is used in Fig. 5.

All measurements are corrected to be consistent (in grams).

• It is unclear if nM (not mM) of glucose was actually measured in the glucose tolerance test (Fig. 2L and Fig. 4L).

Fixed.

Reviewer #3 (Recommendations For The Authors):

1) The authors can remove the LM22A-4 data without much detrimental effects on the conclusion of the manuscript. Otherwise, the authors have to demonstrate that LM22A-4 activates TrkB, does not have any toxicity, and does not cause aversion.

We thank this reviewer the valuable comments and we acknowledge the valid concern. Indeed, the precise mechanism by which LM22A-4 exert its effects is not clear and there has been mixed opinions regarding its function as TRKB agonist in in-vitro assays. To clarify, we have refrained from stating LM22A-4 as a partial agonist of TRKB, and instead have focused on highlighting the potential of this drug in activating neurotrophin downstream signalling through increased AKT phosphorylation, in-vivo.

We have also modified the title of our article to exclude the word “TRKB Signalling”. The new title is as follows:

“Smith-Magenis syndrome protein RAI1 regulates body weight homeostasis through hypothalamic BDNF-producing neurons and neurotrophin downstream signalling”

2) Line 50: "40% > 95th percentile weight, 40% > 85th percentile weight" should be "40% > 95th percentile weight, 80% > 85th percentile weight".

Corrected.

3) Abbreviations for brain-derived neurotrophic factor: Bdnf for gene and BDNF for protein.

Abbreviations have been corrected throughout the manuscript.

4) Need to specify the animal age when viruses were injected into the PVH to inactivate the Bdnf gene.

Line 235: Virus was injected at 3 weeks of age. It has been specified in the main text.

5) Line 832: "3 technical triplicates" can be simplified as "3 technical repeats" because 3 and triplicates are redundant.

Corrected.

6) Figure 2B: The "O" in cKO is misplaced.

Fixed.

7) Figure 3: The black legends in E and F should include Ctrl.

Fixed in the Figure 3.

Author Response

The data we produce are not criticized as such and thus, do not require revision; the criticisms concern our interpretation of them. General themes of the reviews are that i) genetic signatures do not matter for defining neuronal types (here sympathetic versus parasympathetic); ii) that a cholinergic postganglionic autonomic neuron must be parasympathetic; and iii) that some physiology of the pelvic region would deserve the label “parasympathetic”. We answered the latter argument in (Espinosa-Medina et al., 2018) to which we refer the interested reader; and we fully disagree with the first two. Of note, part of the last sentence of the eLife assessment is misleading and does not reflect the referees’ comments. Our paper analyses genetic differences between the cranial and sacral outflow and uses them to argue that they cannot be both parasympathetic. The eLife assessment acknowledges the “genetic differences” but concludes that, somehow, they don’t detract from a common parasympathetic identity. We take issue with this paradox, of course, but it is coherent with the referee’s comments. On the other hand, the eLife assessment alone pushes the paradox one step further by stating that “functional differences” between the cranial and sacral outflows can’t either prevent them from being both parasympathetic. We would also object to this, but the only “functional differences” used by the referees to dismiss our diagnostic of a sympathetic-like character (rather than parasympathetic) for the sacral outflow are between noradrenergic and cholinergic, and between sympathetic and parasympathetic (and we also disagree with those, see above, and below) —not between cranial and sacral.

We will thus use the opportunity offered by eLife to keep the paper as it is (with a few minor stylistic changes). We respond below to the referees’ detailed remarks and hope that the publication, as per eLife new model, of the paper, the referees’ comments and our response will help move the field forward.

Public review by Referee #1

“Consistently, the P3 cluster of neurons is located close to sympathetic neuron clusters on the map, echoing the conventional understanding that the pelvic ganglia are mixed, containing both sympathetic and parasympathetic neurons”.

The greater closeness of P3 than of P1/2/4 to the sympathetic cluster can be used to judge P1/2/4 less sympathetic than P3 (and more… something else), but not more parasympathetic. There is no echo of the “conventional understanding” here.

“A closer look at the expression showed that some genes are expressed at higher levels in sympathetic neurons and in P2 cluster neurons ” [We assume that the referee means “in sympathetic neurons and in P3 cluster neurons”] but much weaker in P1, P2, and P4 neurons such as Islet1 and GATA2, and the opposite is true for SST. Another set of genes is expressed weakly across clusters, like HoxC6, HoxD4, GM30648, SHISA9, and TBX20.

These statements are inaccurate; On the one hand, the classification is not based on impression by visual inspection of the heatmap, but by calculations, using thresholds. Admittedly, the thresholds have an arbitrary aspect, but the referee can verify (by eye inspection of heatmap) that genes which we calculate as being at “higher levels in sympathetic neurons and in P3 cluster neurons, but much weaker in P1, P2, and P4 neurons” or vice versa, i.e. noradrenergic or cholinergic neurons (genes from groups V and VI, respectively), have a much bigger difference than those cited by the referee, indeed are quasi-absent from the weaker clusters or ganglia. In addition, even by subjective eye inspection:

Islet is equally expressed in P4 and sympathetics.

SST is equally expressed in P1 and sympathetics.

Tbx20 is equally expressed in P2 and sympathetics.

HoxC6, HoxD4, GM30648, SHISA9 are equally expressed in all clusters and all sympathetic ganglia.

“Since the pelvic ganglia are in a caudal body part, it is not surprising to have genes expressed in pelvic ganglia, but not in rostral sphenopalatine ganglia, and vice versa (to have genes expressed in sphenopalatine ganglia, but not in pelvic ganglia), according to well recognized rostro-caudal body patterning, such as nested expression of hox genes.”

We do not simply show “genes expressed in pelvic ganglia, but not in rostral sphenopalatine ganglia, and vice versa”, i.e. a genetic distance between pelvic and sphenopalatine, but many genes expressed in all pelvic cells and sympathetic ones, i.e. a genetic proximity between pelvic and sympathetic. This situation can be deemed “unsurprising”, but it can only be used to question the parasympathetic nature of pelvic cells (as we do), or considered irrelevant (as the referee does, because genes would not define cell types, see our response to an equivalent stance by Referee#2). Concerning Hox genes, we do take them into account, and speculate in the discussion that their nested expression is key to the structure of the autonomic nervous system, including its division into sympathetic and parasympathetic outflows.

It is much simpler and easier to divide the autonomic nervous system into sympathetic neurons that release noradrenaline versus parasympathetic neurons that release acetylcholine, and these two systems often act in antagonistic manners, though in some cases, these two systems can work synergistically. It also does not matter whether or not pelvic cholinergic neurons could receive inputs from thoracic-lumbar preganglionic neurons (PGNs), not just sacral PGNs; such occurrence only represents a minor revision of the anatomy. In fact, it makes much more sense to call those cholinergic neurons located in the sympathetic chain ganglia parasympathetic.

This “minor revision of the anatomy” would make spinal preganglionic neurons which are universally considered sympathetic (in the thoraco-lumbar chord), synapse onto large numbers of parasympathetic neurons (in the paravertebral chains for sweat glands and periosteum, and in the pelvic ganglion), robbing these terms of any meaning.

Thus, from the functionality point of view, it is not justified to claim that "pelvic organs receive no parasympathetic innervation".

There never was any general or rigorous functional definition of the sympathetic and parasympathetic nervous systems — it is striking, almost ironic, that Langley, creator of the term parasympathetic and the ultimate physiologist, provides an exclusively anatomic definition in his Autonomic Nervous System, Part I. Hence, our definition cannot clash with any “functionality point of view”. In fact, as we briefly say in the discussion and explore in (Espinosa-Medina et al., 2018), it is the “sacral parasympathetic” paradigm which is unjustified from a functionality point of view, for implying a functional antagonism across the lumbo-sacral gap, which has been disproven repeatedly. It remains to be determined which neurons are antagonistic to which on the blood vessels of the external genitals; antagonism within one division of the autonomic nervous system would not be without precedent (e.g. there exist both vasoconstrictor and vasodilator sympathetic neurons, and both, inhibitor and activator enteric motoneurons). The way to this question is finally open to research, and as referee#2 says “it is early days”.

Public review by Referee #2

This work further documents differences between the cranial and sacral parasympathetic outflows that have been known since the time of Langley - 100 years ago.

We assume that the referee means that it is the “cranial and sacral parasympathetic outflows” which “have been known since the time of Langley”, not their differences (that we would “further document”): the differences were explicitly negated by Langley. As a matter of fact, the sacral and cranial outflows were first likened to each other by Gaskell, 140 years ago (Gaskell, 1886). This anatomic parallel (which is deeply flawed (Espinosa-Medina et al., 2018)) was inherited wholesale by Langley, who added one physiological argument (Langley and Anderson, 1895) (which has been contested many times (Espinosa-Medina et al., 2018) and references within).

In addition, the sphenopalatine and other cranial ganglia develop from placodes and the neural crest, while sympathetic and sacral ganglia develop from the neural crest alone.

Contrary to what the referee says, the sphenopalatine has no placodal contribution. There is no placodal contribution to any autonomic ganglion, sympathetic or parasympathetic (except an isolated claim concerning the ciliary ganglion (Lee et al., 2003)). All autonomic ganglia derive from the neural crest as determined a long time ago in chicken. For the sphenopalatine in mouse, see our own work (Espinosa-Medina et al., 2014).

One feature that seems to set the pelvic ganglion apart is […] the convergence of preganglionic sympathetic and parasympathetic synapses on individual ganglion cells (Figure 3). This unusual organization has been reported before using microelectrode recordings (see Crowcroft and Szurszewski, J Physiol (1971) and Janig and McLachlan, Physiol Rev (1987)). Anatomical evidence of convergence in the pelvic ganglion has been reported by Keast, Neuroscience (1995).

Contrary to what the referee says, we do not provide in Figure 3 any evidence for anatomic convergence, i.e. for individual pelvic ganglion cells receiving dual lumbar and sacral inputs. We simply show that cholinergic neurons figure prominently among targets of the lumbar pathway. This said, the convergence of both pathways on the same pelvic neurons, described in the references cited by the referee, is another major problem in the theory of the “sacral parasympathetic” (as we discussed previously (Espinosa-Medina et al., 2018)).

It should also be noted that the anatomy of the pelvic ganglion in male rodents is unique. Unlike other species where the ganglion forms a distributed plexus of mini-ganglia, in male rodents the ganglion coalesces into one structure that is easier to find and study. Interestingly the image in Figure 3A appears to show a clustering of Chat-positive and Th-positive neurons. Does this result from the developmental fusion of mini ganglia having distinct sympathetic and parasympathetic origins?

The clustering of Chat-positive and Th-positive cells could arise from a number of developmental mechanisms, that we have no idea of at the moment. This has no bearing on sympathetic and parasympathetic.

In addition, Brunet et al dismiss the cholinergic and noradrenergic phenotypes as a basis for defining parasympathetic and parasympathetic neurons. However, see the bottom of Figure S4 and further counterarguments in Horn (Clin Auton Res (2018)).

The bottom of Figure S4 simply indicates which cells are cholinergic and adrenergic. We have already expounded many times that noradrenergic and cholinergic do not coincide with sympathetic and parasympathetic. Henry Dale (Nobel Prize 1936) demonstrated this. Langley himself devoted several pages of his final treatise to this exception to his “Theory on the relation of drugs to nerve system” (Langley, 1921) (p43) (which was actually a bigger problem for him than it is for us, for reason which are too long to recount here; it is as if the theoretical difficulties experienced by Langley had been internalized to this day in the form of a dismissal of the cholinergic sympathetic neurons as a slightly scandalous but altogether forgettable oddity). (Horn, 2018), reviews the evidence that the thoracic cholinergic sympathetic phenotype is brought about by a secondary switch upon interaction with the target and argues that this would be a fundamental difference with the sacral “parasympathetic”. But in fact the secondary switch is preceded by co-expression of ChAT and VAChT with Th in most sympathetic neurons (reviewed in (Ernsberger and Rohrer, 2018)); and we have no idea of the dynamic in the pelvic ganglion. It may also be mentioned in this context that target-dependent specification of neuronal identity has also been demonstrated of other types of sympathetic neurons ((Furlan et al., 2016)

What then about neuropeptides, whose expression pattern is incompatible with the revised nomenclature proposed by Brunet et al.?

There was never any neuropeptide-inspired criterion for a nomenclature of the autonomic nervous system.

Figure 1B indicates that VIP is expressed by sacral and cranial ganglion cells, but not thoracolumbar ganglion cells.

Contrary to what the referee says, there are VIP-positive cells in our sympathetic data set and even strongly positive ones, except they are scattered and few (red bars on the UMAP). They correspond to cholinergic sympathetics, likely sudomotor, which are known to contain VIP (e.g.(Anderson et al., 2006)(Stanke et al., 2006)). In other words, VIP is probably part of what we call the cholinergic synexpression group (but was not placed in it by our calculations, probably because of a low expression level even in sympathetic noradrenergic cells).

The authors do not mention neuropeptide Y (NPY). The immunocytochemistry literature indicates that NPY is expressed by a large subpopulation of sympathetic neurons but never by sacral or cranial parasympathetic neurons.

Contrary to what the referee says, Keast (Keast, 1995) finds 3.7% of pelvic neurons double stained for NPY and VIP in male rats, and says (Keast, 2006) that in females “co-expression of NPY and VIP is common” ( thus in cholinergic neurons that the referee calls “parasympathetic”). Single cell transcriptomics is probably more sensitive than immunochemistry, and in our dichotomized data set (table S1), NPY is expressed in all pelvic clusters and all sympathetic ganglia. In other words, it is one more argument for their kinship. It does not appear in the heatmap because it ranks below the 100 top genes.

References

Anderson, C. R., Bergner, A. and Murphy, S. M. (2006). How many types of cholinergic sympathetic neuron are there in the rat stellate ganglion? Neuroscience 140, 567–576.

Ernsberger, U. and Rohrer, H. (2018). Sympathetic tales: subdivisons of the autonomic nervous system and the impact of developmental studies. Neural Dev 13, 20.

Espinosa-Medina, I., Outin, E., Picard, C. A., Chettouh, Z., Dymecki, S., Consalez, G. G., Coppola, E. and Brunet, J. F. (2014). Neurodevelopment. Parasympathetic ganglia derive from Schwann cell precursors. Science 345, 87–90.

Espinosa-Medina, I., Saha, O., Boismoreau, F. and Brunet, J.-F. (2018). The “sacral parasympathetic”: ontogeny and anatomy of a myth. Clin Auton Res 28, 13–21.

Furlan, A., La Manno, G., Lübke, M., Häring, M., Abdo, H., Hochgerner, H., Kupari, J., Usoskin, D., Airaksinen, M. S., Oliver, G., et al. (2016). Visceral motor neuron diversity delineates a cellular basis for nipple- and pilo-erection muscle control. 19, 1331–1340.

Gaskell, W. H. (1886). On the Structure, Distribution and Function of the Nerves which innervate the Visceral and Vascular Systems. J Physiol 7, 1-80.9.

Horn, J. P. (2018). The sacral autonomic outflow is parasympathetic: Langley got it right. Clin Auton Res 28, 181–185.

Jänig, W. (2006). The Integrative Action of the Autonomic Nervous System: Neurobiology of Homeostasis. Cambridge: Cambridge University Press.

Keast, J. R. (1995). Visualization and immunohistochemical characterization of sympathetic and parasympathetic neurons in the male rat major pelvic ganglion. Neuroscience 66, 655–662.

Keast, J. R. (2006). Plasticity of pelvic autonomic ganglia and urogenital innervation. International Review of Cytology - a Survey of Cell Biology, Vol 248 248, 141-+.

Langley, J. N. (1921). In The autonomic nervous system (Pt. I)., p. Cambridge: Heffer & Sons ltd.

Langley, J. N. and Anderson, H. K. (1895). The Innervation of the Pelvic and adjoining Viscera: Part II. The Bladder. Part III. The External Generative Organs. Part IV. The Internal Generative Organs. Part V. Position of the Nerve Cells on the Course of the Efferent Nerve Fibres. J Physiol 19, 71–139.

Lee, V. M., Sechrist, J. W., Luetolf, S. and Bronner-Fraser, M. (2003). Both neural crest and placode contribute to the ciliary ganglion and oculomotor nerve. Developmental biology 263, 176–190.

Stanke, M., Duong, C. V., Pape, M., Geissen, M., Burbach, G., Deller, T., Gascan, H., Parlato, R., Schütz, G. and Rohrer, H. (2006). Target-dependent specification of the neurotransmitter phenotype:cholinergic differentiation of sympathetic neurons is mediated in vivo by gp130 signaling. Development 133, 141–150.

Zeisel, A., Hochgerner, H., Lönnerberg, P., Johnsson, A., Memic, F., van der Zwan, J., Häring, M., Braun, E., Borm, L. E., La Manno, G., et al. (2018). Molecular Architecture of the Mouse Nervous System. Cell 174, 999-1014.e22.

Author Response

The following is the authors’ response to the original reviews.

eLife assessment

This useful manuscript challenges the utility of current paradigms for estimating brain-age with magnetic resonance imaging measures, but presents inadequate evidence to support the suggestion that an alternative approach focused on predicting cognition is more useful. The paper would benefit from a clearer explication of the methods and a more critical evaluation of the conceptual basis of the different models. This work will be of interest to researchers working on brain-age and related models.

Response: Thank you so much for providing high-quality reviews on our manuscript. We revised the manuscript to address all of the reviewers’ comments and provided full responses to each of the comments below.

Briefly, regarding clearer explanations of the methods, we added additional analyses (e.g., commonality analyses on ridge regression and on multiple regressions with a quadratic term for chronological age) to address some of the concerns and additional details in text and figures to ensure that the reader can fully understand our methodological procedures. Regarding the critical evaluation of the conceptual basis of the different models, we added discussions to help with interpretations and the scope of the generalisability of our findings. For instance, as opposed to treating Brain Cognition and Brain Age as separate biomarkers and comparing them in the ability to explain fluid cognition, we now treated the capability of Brain Cognition in capturing fluid cognition as the upper limit of Brain Age’s capability in capturing fluid cognition. In other words, we now examined the extent to which Brain Age missed the variation in the brain MRI that could explain fluid cognition (for this particular issue, please see our response to Reviewer 3 Public Review #4).

Reviewer 1:

This is a reasonably good paper and the use of a commonality analysis is a nice contribution to understanding variance partitioning across different covariates. I have some comments that I believe the authors ought to address which mostly relate to clarity and interpretation.

Reviewer 1 Public Review #1:

First, from a conceptual point of view, the authors focus exclusively on cognition as a downstream outcome. I would suggest the authors nuance their discussion to provide broader considerations of the utility of their method and on the limits of interpretation of brain-age models more generally. Further, I think that since brain-age models by construction confound relevant biological variation with the accuracy of the regression models used to estimate them, there may be limits to the interpretation of (e.g.) the brain-age gap is as a dimensionless biomarker. This has also been discussed elsewhere (see e.g. https://academic.oup.com/brain/article/143/7/2312/5863667). I would suggest that the authors consider and comment on these issues.

Response: Thank you Reviewer 1 for pointing out these important issues. We addressed them in our response to Reviewer 1 Recommendations For The Authors #1 (see below).

Reviewer 1 Public Review #2

Second, from a methods perspective, there is not a sufficient explanation of the methodological procedures in the current manuscript to fully understand how the stacked regression models were constructed. Stacked models can be prone to overfitting when combined with cross-validation. This is because the predictions from the first-level models (i.e. the features that are provided to the second level 'stacked' models) contain information about the training set and the test set. If cross-validation is not done very carefully (e.g. using multiple hold-out sets), information leakage can easily occur at the second level. Unfortunately, there is not a sufficient explanation of the methodological procedures in the current manuscript to fully understand what was actually done. Please provide more information to enable the reader to better understand the stacked regression models. If the authors are not using an approach that fully preserves training and test separability, they need to do so.

Response: Thank you Reviewer 1. We addressed this issue in our response to Reviewer 1 Recommendations For The Authors #2 (see below). Briefly, we now made it clearer that training models for both non-stacked and stacked models did not involve the test set, ensuring that there was no data leakage between training and test sets.

Reviewer 1 Public Review #3

Please also provide an indication of the different regression strengths that were estimated across the different models and cross-validation splits. Also, how stable were the weights across splits?

Response: Thank you Reviewer 1. We addressed this issue in our response to Reviewer 1 Recommendations For The Authors #3 (see below).

Reviewer 1 Public Review #4:

Please provide more details about the task designs, MRI processing procedures that were employed on this sample in addition to the regression methods, and bias-correction methods used. For example, there are several different parameterisations of the elastic net, please provide equations to describe the method used here so that readers can easily determine how the regularisation parameters should be interpreted.

Response: Thank you Reviewer 1. We addressed this issue in our response to Reviewer 1 Recommendations For The Authors #5-#6. Briefly, we followed your advice and add all of the suggested details.

Reviewer 2 (Public Review):

Reviewer 2 Public Review Overall:

In this study, the authors aimed to evaluate the contribution of brain-age indices in capturing variance in cognitive decline and proposed an alternative index, brain-cognition, for consideration. The study employs suitable data and methods, albeit with some limitations, to address the research questions. A more detailed discussion of methodological limitations in relation to the study's aims is required. For instance, the current commonality analysis may not sufficiently address potential multicollinearity issues, which could confound the findings. Importantly, given that the study did not provide external validation for the indices, it is unclear how well the models would perform and generalize to other samples. This is particularly relevant to their novel index, brain-cognition, given that brain-age has been validated extensively elsewhere. In addition, the paper's rationale for using elastic net, which references previous fMRI studies, seemed somewhat unclear. The discussion could be more nuanced and certain conclusions appear speculative.

Response Thank you for your encouragement. We have now added discussion of methodological limitations (see below). Regarding potential multicollinearity issues, we addressed this comment using Ridge regressions (see our response to Reviewer 2 Recommendations For The Authors #2). Regarding external validation, we now added discussions about how consistency between our results and several recent studies that investigated similar issues with Brain Age in different populations (see Reviewer 2 Recommendations For The Authors #1). Regarding Brain Cognition, we also added previous studies showing similarly high prediction for cognition functioning (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). We added a discussion about Elastic Net (see Reviewer 1 Recommendations For The Authors #6)

Discussion

“There are several potential limitations of this study. First, we conducted an investigation relying only on one dataset, the Human Connectome Project in Aging (HCP-A) (Bookheimer et al., 2019). While HCP-A used state-of-the-art MRI methodologies, covered a wide age range from 36 to 100 years old and used several task-fMRI from different tasks that are harder to find in other bigger databases (e.g., UK Biobank from Sudlow et al., 2015), several characteristics of HCP-A might limit the generalisability of our findings. For instance, the tasks used in task-based fMRI in HCP-A are not used widely in clinical settings (Horien et al., 2020). This might make it challenging to translate the approaches used here. Similarly, HCP-A also excluded participants with neurological conditions, possibly making their participants not representative of the general population. Next, while HCP-A’s sample size is not small (n=725 and 504 people, before and after exclusion, respectively), other datasets provide a much larger sample size (Horien et al., 2020). Similarly, HCP-A does not include younger populations. But as mentioned above, a study with a larger sample in older adults (Cole, 2020) and studies in younger populations (8-22 years old) (Butler et al., 2021; Jirsaraie, Kaufmann, et al., 2023) also found small effects of the adjusted Brain Age Gap in explaining cognitive functioning. And the disagreement between the predictive performance of age-prediction models and the utility of Brain Age found here is largely in line with the findings across different phenotypes seen in a recent systematic review (Jirsaraie, Gorelik, et al., 2023).”

Reviewer 2 Public Review #1:

The authors aimed to evaluate how brain-age and brain-cognition indices capture cognitive decline (as mentioned in their title) but did not employ longitudinal data, essential for calculating 'decline'. As a result, 'cognition-fluid' should not be used interchangeably with 'cognitive decline,' which is inappropriate in this context.

Response Thank you for raising this issue. We now no longer used the word ‘cognitive decline’.

Reviewer 2 Public Review #2:

In their first aim, the authors compared the contributions of brain-age and chronological age in explaining variance in cognition-fluid. Results revealed much smaller effect sizes for brain-age indices compared to the large effects for chronological age. While this comparison is noteworthy, it highlights a well-known fact: chronological age is a strong predictor of disease and mortality. Has the brain-age literature systematically overlooked this effect? If so, please provide relevant examples. They conclude that due to the smaller effect size, brain-age may lack clinical significance, for instance, in associations with neurodegenerative disorders. However, caution is required when speculating on what brain-age may fail to predict in the absence of direct empirical testing. This conclusion also overlooks extant brain-age literature: although effect sizes vary across psychiatric and neurological disorders, brain-age has demonstrated significant effects beyond those driven by chronological age, supporting its utility.

Response For aim 1, we focused our claims on cognitive functioning and not on any clinical significance for neurodegenerative disorders. We now made it clearer that the small effects of the Corrected Brain Age Gap in explaining fluid cognition of aging individuals found here are consistent with a study with a larger sample in older adults (Cole, 2020) and studies in younger populations (8-22 years old) (Butler et al., 2021; Jirsaraie, Kaufmann, et al., 2023).

We believe this issue of the utility of brain age on cognitive functioning vs neurological/psychological disorders requires another consideration, namely the discrepancy in the training and test samples typically used for studies focusing on neurological/psychological disorders. We made this point in the discussion now (see below).

Discussion

“There is a notable difference between studies investigating the utility of Brain Age in explaining cognitive functioning, including ours and others (e.g., Butler et al., 2021; Cole, 2020, 2020; Jirsaraie, Kaufmann, et al., 2023) and those explaining neurological/psychological disorders (e.g., Bashyam et al., 2020; Rokicki et al., 2021). That is, those Brain Age studies focusing on neurological/psychological disorders often build age-prediction models from MRI data of largely healthy participants (e.g., controls in a case-control design or large samples in a population-based design), apply the built age-prediction models to participants without vs. with neurological/psychological disorders and compare Brain Age indices between the two groups. This means that age-prediction models from Brain Age studies focusing on neurological/psychological disorders might be under-fitted when applied to participants with neurological/psychological disorders because they were built from largely healthy participants. And thus the difference in Brain Age indices between participants without vs. with neurological/psychological disorders might be confounded by the under-fitted age-prediction models (i.e., Brain Age may predict chronological age well for the controls, but not for those with a disorder). On the contrary, our study and other Brain Age studies focusing on cognitive functioning often build age-prediction models from MRI data of largely healthy participants and apply the built age-prediction models to participants who are also largely healthy. Accordingly, the age-prediction models for explaining cognitive functioning do not suffer from being under-fitted. We consider this as a strength, not a weakness of our study.”

Reviewer 2 Public Review #3:

The second aim's results reveal a discrepancy between the accuracy of their brain-age models in estimating age and the brain-age's capacity to explain variance in cognition-fluid. The authors suggest that if the ultimate goal is to capture cognitive variance, brain-age predictive models should be optimized to predict this target variable rather than age. While this finding is important and noteworthy, additional analyses are needed to eliminate potential confounding factors, such as correlated noise between the data and cognitive outcome, overfitting, or the inclusion of non-healthy participants in the sample. Optimizing brain-age models to predict the target variable instead of age could ultimately shift the focus away from the brain-age paradigm, as it might optimize for a factor differing from age.

Response We discussed the issue regarding the discrepancy between the accuracy of their brain-age models in estimating age and the brain-age's capacity to explain variance in fluid cognition in our response to Reviewer 3 Public Review #9 (see below). This issue is found to be widespread in a recent systematic review (Jirsaraie, Gorelik, et al., 2023). We now provided several strategies to mitigate this issue to improve the utility of Brain Age in explaining other phenotypes based on our current work and others, using different MRI modalities as well as modelling techniques (Bashyam et al., 2020; Jirsaraie, Kaufmann, et al., 2023; Rokicki et al., 2021).

Regarding potential confounding factors, we are not sure what the reviewer meant by “correlated noise between the data and cognitive outcome”. The current study, for instance, used ICA-FIX (Glasser et al., 2016) to remove noise in functional MRI. It is unclear how much ‘noise’ is still left and might confound our findings. More importantly, we are not sure how to define ‘noise’ as referred to by Reviewer 2 here. As for overfitting, we used nested cross-validation to ensure that training and test sets were separate from each other (see Reviewer 1 Recommendations For The Authors #2). If overfitting happened as suggested, we should see a ‘lower’ predictive performance of age-prediction and cognitive-prediction models since the models would fit well with the training set but would not generalise well to the test set. This is not what we found. The predictive performance of our age-prediction and cognitive-prediction models was high and consistent with the literature. Regarding the inclusion of non-healthy participants in the sample, we discussed this above in our response to Reviewer 2 Public Review #2).

Reviewer 2 Public Review #4:

While a primary goal in biomarker research is to obtain indices that effectively explain variance in the outcome variable of interest, thus favouring models optimized for this purpose, the authors' conclusion overlooks the potential value of 'generic/indirect' models, despite sacrificing some additional explained variance provided by ad-hoc or 'specific/direct' models. In this context, we could consider brain-age as a 'generic' index due to its robust out-of-sample validity and significant associations across various health outcome variables reported in the literature. In contrast, the brain-cognition index proposed in this study is presumed to be 'specific' as, without out-of-sample performance metrics and testing with different outcome variables (e.g., neurodegenerative disease), it remains uncertain whether the reported effect would generalize beyond predicting cognition-fluid, the same variable used to condition the brain-cognition model in this study. A 'generic' index like brain-age enables comparability across different applications based on a common benchmark (rather than numerous specific models) and can support explanatory hypotheses (e.g., "accelerated ageing") since it is grounded in its own biological hypothesis. Generic and specific indices are not mutually exclusive; instead, they may offer complementary information. Their respective utility may depend heavily on the context and research or clinical question.

Response Thank you Reviewer 2 for pointing out this important issue. Reviewer 1 (Recommendations For The Authors #4) and Reviewer 3 (Public Review #4) bought up a similar issue. We agreed with Reviewer 2 that both 'specific/direct' index and Brain Age as a 'generic/indirect' index have merit in their own right. We made a discussion about this issue in our response to Reviewer 3 Public Review #4 (please see this response below).

Briefly, in the revision, as opposed to treating Brain Cognition and Brain Age as separate biomarkers and comparing them, we treated the capability of Brain Cognition in capturing fluid cognition as the upper limit of Brain Age’s capability in capturing fluid cognition. In other words, we now examined the extent to which Brain Age missed the variation in the brain MRI that could explain fluid cognition. We also made a discussion about using our commonality approach to test for this missing variation in future work:

Discussion

“Finally, researchers should test how much Brain Age miss the variation in the brain MRI that could explain fluid cognition or other phenotypes of interest. As demonstrated here, one straightforward method is to build a prediction model using a phenotype of interest as the target (e.g., fluid cognition) and incorporate the predicted value of this model (e.g., Brain Cognition), along with Brain Age and chronological age, into a multiple regression for commonality analyses. The unique effect of this predicted value will inform the missing variation in the brain MRI from Brain Age. If this unique effect is large, then researchers might need to reconsider whether using Brain Age is appropriate for a particular phenotype of interest.”

Reviewer 2 Public Review #5:

The study's third aim was to evaluate the authors' new index, brain-cognition. The results and conclusions drawn appear similar: compared to brain-age, brain-cognition captures more variance in the outcome variable, cognition-fluid. However, greater context and discussion of limitations is required here. Given the nature of the input variables (a large proportion of models in the study were based on fMRI data using cognitive tasks), it is perhaps unsurprising that optimizing these features for cognition-fluid generates an index better at explaining variance in cognition-fluid than the same features used to predict age. In other words, it is expected that brain-cognition would outperform brain-age in explaining variance in cognition-fluid since the former was optimized for the same variable in the same sample, while brain-age was optimized for age. Consequently, it is unclear if potential overfitting issues may inflate the brain-cognition's performance. This may be more evident when the model's input features are the ones closely related to cognition, e.g., fMRI tasks. When features were less directly related to cognitive tasks, e.g., structural MRI, the effect sizes for brain-cognition were notably smaller (see 'Total Brain Volume' and 'Subcortical Volume' models in Figure 6). This observation raises an important feasibility issue that the authors do not consider. Given the low likelihood of having task-based fMRI data available in clinical settings (such as hospitals), estimating a brain-cognition index that yields the large effects discussed in the study may be challenged by data scarcity.

Response Given the use of nested cross-validation, we do not consider the good predictive performance of Brain Cognition found here as overfitting. In fact, we found a similar level of predictive performance of Brain Cognition on another database with younger participants in the past (Tetereva et al., 2022). However, we agreed with Reviewer 2 that the prediction of fluid cognition might be driven by MRI modalities that are different from those that drive the prediction of chronological age. In our own work with other age groups, including young adults (Tetereva et al., 2022) and children (Pat, Wang, Anney, et al., 2022), cognitive functioning seems to be predicted well from task-based functional MRI. And Reviewer 2 is right that task-based fMRI is not commonly used in clinics, making it harder to translate our results. However, given our results, clinicians should be encouraged to use task-based fMRI if their goal is to predict cognitive functioning. Nevertheless, as suggested, we listed data scarcity as one of the limitations of our approach.

Discussion “For instance, the tasks used in task-based fMRI in HCP-A are not used widely in clinical settings (Horien et al., 2020). This might make it challenging to translate the approaches used here.”

Reviewer 2 Public Review #6:

This study is valuable and likely to be useful in two main ways. First, it can spur further research aimed at disentangling the lack of correspondence reported between the accuracy of the brain-age model and the brain-age's capacity to explain variance in fluid cognitive ability. Second, the study may serve, at least in part, as an illustration of the potential pros and cons of using indices that are specific and directly related to the outcome variable versus those that are generic and only indirectly related.

Response We are thankful for the encouragement. For the discrepancy between the predictive performance of age-prediction models and the utility of Brain Age indices as a biomarker for fluid cognition, we made a detailed discussion in our response to Reviewer 3 Public Review #9. More specifically, to ensure that readers can benefit from our findings, we made suggestions on how to ensure the utility of Brain Age indices as a biomarker for other phenotypes by drawing from our own strategy, as well as strategies used by Rokicki and colleagues (2021), Jirsaraie and colleagues (2023) and Bashyam and colleagues (2020).

As for the pros and cons between generic vs specific biomarkers, we made a detailed discussion in our response to Reviewer 3 Public Review #4. We also made some suggestions on how to make use of the difference in the ability between generic vs specific biomarkers (see Reviewer 2 Public Review #4, above).

Reviewer 2 Public Review #7:

Overall, the authors effectively present a clear design and well-structured procedure; however, their work could have been enhanced by providing more context for both the brain-age and brain-cognition indices, including a discussion of key concepts in the brain-age paradigm, which acknowledges that chronological age strongly predicts negative health outcomes, but crucially, recognizes that ageing does not affect everyone uniformly. Capturing this deviation from a healthy norm of ageing is the key brain-age index. This lack of context was mirrored in the presentation of the four brain-age indices provided, as it does not refer to how these indices are used in practice. In fact, there is no mention of a more common way in which brain-age is implemented in statistical analyses, which involves the use of brain-age delta as the variable of interest, along with linear and non-linear terms of age as covariates. The latter is used to account for the regression-to-the-mean effect. The 'corrected brain-age delta' the authors use does not include a non-linear term, which perhaps is an additional reason (besides the one provided by the authors) as to why there may be small, but non-zero, common effects of both age and brain-age in the 'corrected brain-age delta' index commonality analysis. The context for brain-cognition was even more limited, with no reference to any existing literature that has explored direct brain-cognitive markers, such as brain-cognition.

Response Regarding Brain Age and negative health outcomes, we addressed this in our response to Reviewer 1 Recommendations For The Authors #1 (see below). Briefly, we now discussed (1) the consistency between our findings on fluid cognition and other recent works on negative health outcomes, (2) the differences between Brain Age studies focusing on negative health outcomes vs. cognitive functioning and (3) suggested solutions to optimise the utility of brain age for both cognitive functioning and negative health outcomes.

Regarding how Brain Age was used in practice, we addressed this in our response to Reviewer 3 Public Review #2 (see below). Our argument resonates Butler and colleagues’ (2021) suggestion that the common practice for Brain Age analysis should be re-evaluated: “The MBAG and performance on the complex cognition tasks were not associated (r =  .01, p = 0.71). These results indicate that the association between cognition and the BAG are driven by the association between age and cognitive performance. As such, it is critical that readers of past literature note whether or not age was controlled for when testing for effects on the BAG, as this has not always been common practice (e.g., Beheshti et al., 2018; Cole, Underwood, et al., 2017; Franke et al., 2015; Gaser et al., 2013; Liem et al., 2017; Nenadi c et al., 2017; Steffener et al., 2016). (p. 4097).”

Importantly, we also implemented “brain-age delta as the variable of interest, along with linear and non-linear terms of age as covariates” in our additional analyses along with other implementations (see Reviewer 2 Recommendations For The Authors #3). Of particular note, we found that adding a non-linear term (i.e., a quadratic term for chronological age) barely changed the results of commonality analyses.

We now wrote this paragraph to recommend how future research should implement Brain Age:

Discussion

“First, they have to be aware of the overlap in variation between Brain Age and chronological age and should focus on the contribution of Brain Age over and above chronological age. Using Brain Age Gap will not fix this. Butler and colleagues (2021) recently highlighted this point, “These results indicate that the association between cognition and the BAG are driven by the association between age and cognitive performance. As such, it is critical that readers of past literature note whether or not age was controlled for when testing for effects on the BAG, as this has not always been common practice (p. 4097).” Similar to their recommendation (Butler et al., 2021), we suggest future work focus on Corrected Brain Age Gap or, better, unique effects of Brain Age indices after controlling for chronological age in multiple regressions. In the case of fluid cognition, the unique effects might be too small to be clinically meaningful as shown here and previously (Butler et al., 2021; Jirsaraie, Kaufmann, et al., 2023). “

Regarding brain cognition, we now expanded our explanation about Brain Cognition on how it might be relevant to Brain Age and on Brain Cognition’s predictive performance found previously.

Introduction

“Third and finally, certain variation in the brain MRI is related to fluid cognition, but to what extent does Brain Age not capture this variation? To estimate the variation in the brain MRI that is related to fluid cognition, we could build prediction models that directly predict fluid cognition (i.e., as opposed to chronological age) from brain MRI data. Previous studies found reasonable predictive performances of these cognition-prediction models, built from certain MRI modalities (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). Analogous to Brain Age, we called the predicted values from these cognition-prediction models, Brain Cognition. The strength of an out-of-sample relationship between Brain Cognition and fluid cognition reflects variation in the brain MRI that is related to fluid cognition and, therefore, indicates the upper limit of Brain Age’s capability in capturing fluid cognition. Consequently, the unique effects of Brain Cognition that explain fluid cognition beyond Brain Age and chronological age indicate what is missing from Brain Age -- the amount of co-variation between brain MRI and fluid cognition that cannot be captured by Brain Age.”

Discussion

“Third, by introducing Brain Cognition, we showed the extent to which Brain Age indices were not able to capture the variation of brain MRI that is related to fluid cognition. Brain Cognition, from certain cognition-prediction models such as the stacked models, has relatively good predictive performance, consistent with previous studies (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022).”

Reviewer 2 Public Review #8:

While this paper delivers intriguing and thought-provoking results, it would benefit from recognizing the value that both approaches--brain-age indices and more direct, specific markers like brain-cognition--can contribute to the field.

Response Thank you so much for recognising the value of our work. As we mentioned above in our response to Reviewer 2 Public Review #4 and #6, we made some suggestions on how to make use of the difference in the ability between generic vs specific biomarkers.

Reviewer 3 (Public Review):

Reviewer 3 Public Review Overall:

The main question of this article is as follows: "To what extent does having information on brain-age improve our ability to capture declines in fluid cognition beyond knowing a person's chronological age?" While this question is worthwhile, considering that there is considerable confusion in the field about the nature of brain-age, the authors are currently missing an opportunity to convey the inevitability of their results, given how brain-age and the brain-age gap are calculated. They also argue that brain-cognition is somehow superior to brain-age, but insufficient evidence is provided in support of this claim.

Response We addressed the concerns below. The inevitability of our results is not obvious to many researchers who might be interested in Brain Age. We hope our findings might make many issues surrounding Brain Age more obvious, and we now make many suggestions on how to address some of these issues. We no longer argue that Brain Cognition is superior to Brain Age (Reviewer 3 Public Review #4). Rather, we treated the capability of Brain Cognition in capturing fluid cognition as the upper limit of Brain Age’s capability in capturing fluid cognition. We used the unique effects of Brain Cognition that explain fluid cognition beyond Brain Age and chronological age to indicate how much Brain Age misses the variation in the brain MRI that could explain fluid cognition.

Specific comments follow:

Reviewer 3 Public Review #1:

• "There are many adjustments proposed to correct for this estimation bias" (p3). Regression to the mean is not a sign of bias. Any decent loss function will result in over-predicting the age of younger individuals and under-predicting the age of older individuals. This is a direct result of minimizing an error term (e.g., mean squared error). Therefore, it is inappropriate to refer to regression to the mean as a sign of bias. This misconception has led to a great deal of inappropriate analyses, including "correcting" the brain age gap by regressing out age.

Response: Thank you so much for raising this issue. We used the word ‘bias’ following many articles in the field. For instance,

de Lange and Cole (2020) wrote: “brain-age estimation also involves a frequently observed bias: brain age is overestimated in younger subjects and underestimated in older subjects, while brain age for participants with an age closer to the mean age (of the training dataset) are predicted more accurately (Cole, Le, Kuplicki, McKinney, Yeh, Thompson, Paulus, Investigators, et al., 2018, Liang, Zhang, Niu, 2019, Niu, Zhang, Kounios, Liang, 2019, Smith, Vidaurre, Alfaro-Almagro, Nichols, Miller, 2019).”

Cole (2020) wrote: “As recent research has highlighted a proportional bias in brain-age calculation, whereby the difference between chronological age and brain-predicted age is negatively correlated with chronological age (Le et al., 2018, Liang et al., 2019, Smith et al., 2019), an age-bias correction procedure was used. This entailed calculating the regression line between age (predictor) and brain-predicted age (outcome) in the training set, then using the slope (i.e., coefficient) and intercept of that line to adjust brain-predicted age values in the testing set (by subtracting the intercept and then dividing by the slope). After applying the age-bias correction the brain-predicted age difference (brain-PAD) was calculated; chronological age subtracted from brain-predicted age.”

Beheshiti and colleagues (2019) used bias in their title: “Bias-adjustment in neuroimaging-based brain age frameworks: a robust scheme”

More recently, Cumplido-Mayoral and colleagues (2023) wrote: “As recent research has shown that brain-age estimation involves a proportional bias (de Lange et al., 2020a; Le et al., 2018; Liang et al., 2019; Smith et al., 2019), we applied a well-established age-bias correction procedure to our data (de Lange et al., 2020a; Le et al., 2018).”

Still, we agree with Reviewer 3 that using ‘bias’ might lead to misinterpretation. As Butler and colleagues (Butler et al., 2021) pointed out, ”It is important to note that regression toward the mean is not a failure, but a feature, of regression and related methods.“ We rewrote the paragraph and clarified the “regression towards the mean” issue. We no longer used the word “bias” here:

Introduction

“Note researchers often subtract chronological age from Brain Age, creating an index known as Brain Age Gap (Franke & Gaser, 2019). A higher value of Brain Age Gap is thought to reflect accelerated/premature aging. Yet, given that Brain Age Gap is calculated based on both Brain Age and chronological age, Brain Age Gap still depends on chronological age (Butler et al., 2021). If, for instance, Brain Age was based on prediction models with poor performance and made a prediction that everyone was 50 years old, individual differences in Brain Age Gap would then depend solely on chronological age (i.e., 50 minus chronological age). Moreover, Brain Age is known to demonstrate the “regression towards the mean” phenomenon (Stigler, 1997). More specifically, because Brain Age is a predicted value of a regression model that predicts chronological age, Brain Age is usually shrunk towards the mean age of samples used for training the model (Butler et al., 2021; de Lange & Cole, 2020; Le et al., 2018). Accordingly, Brain Age predicts chronological age more accurately for individuals who are closer to the mean age while overestimating younger individuals’ chronological age and underestimating older individuals’ chronological age. There are many adjustments proposed to correct for the age dependency, but the outcomes tend to be similar to each other (Beheshti et al., 2019; de Lange & Cole, 2020; Liang et al., 2019; Smith et al., 2019). These adjustments can be applied to Brain Age and Brain Age Gap, creating Corrected Brain Age and Corrected Brain Age Gap, respectively. Corrected Brain Age Gap in particular is viewed as being able to control for age dependency (Butler et al., 2021). Here, we tested the utility of different Brain Age calculations in capturing fluid cognition, over and above chronological age.”

Reviewer 3 Public Review #2:

• "Corrected Brain Age Gap in particular is viewed as being able to control for both age dependency and estimation biases (Butler et al., 2021)" (p3). This summary is not accurate as Butler and colleagues did not use the words "corrected" and "biases" in this context. All that authors say in that paper is that regressing out age from the brain age gap - which is referred to as the modified brain age gap (MBAG) - makes it so that the modified brain age gap is not dependent on age, which is true. This metric is meaningless, though, because it is the variance left over after regressing out age from residuals from a model that was predicting age. If it were not for the fact that regression on residuals is not equivalent to multiple regression (and out of sample estimates), MBAG would be a vector of zeros. Upon reading the Methods, I noticed that the authors use a metric from Le et al. (2018) for the "Corrected Brain Age Gap". If they cite the Butler et al. (2021) paper, I highly recommend sticking with the same notation, metrics and terminology throughout. That would greatly help with the interpretability of the present manuscript, and cross-comparisons between the two.

Response: We thank Reviewer 3 for pointing out the issues surrounding our choices of wording: "corrected" and "biases". We share the same frustration with Reviewer 3 in that different brain-age articles use different terminologies, and we tried to make sure our readers understand our calculations of Brain Age indices in order to compare our results with previous work.

We commented on the word “bias” in our response to Reviewer 3 Public Review #1 above and refrained from using this word in the revised manuscript. Here we commented on the use of the word “Corrected Brain Age Gap". And by doing so, we clarified how we calculated it.

Reviewer 3 is right that we cited the work of Butler and colleagues (2021), but wasn’t accurate to say that we used “a metric from Le et al. (2018) for the "Corrected Brain Age Gap". We, instead, used a method described in de Lange and Cole’s (2020) work. We now added equations to explain this method in our Materials and Method section (see below).

It is important to note that Butler and colleagues (2021) did not come up with any adjustment methods. Instead, Butler and colleagues (2021) discussed three adjustment methods:

1) A method proposed by Beheshiti and colleagues (2019). Butler and colleagues (2021) called the result of this method, Modified Brain Age Gap (MBAG). Importantly, Butler and colleagues (2021) discouraged the use of this method due to “researchers misinterpreting the reduced variability of the MBAG as an improvement in prediction accuracy.” Accordingly in our article, we performed methods (2) and (3) below.

2) A method proposed by de Lange and Cole (2020). We used this method in our article (see below for the equations). Briefly, we first fit a regression line predicting the Brain Age from a chronological age in each training set. We then used the slope and intercept of this regression line to adjust Brain Age in the corresponding test set, resulting in an adjusted index of Brain Age. Butler and colleagues (2021) called this index, “Revised Predicted Age.”, while de Lange and Cole’s (2020) originally called this Corrected Brain Age, “Corrected Predicted Age”. Butler and colleagues (2021) then subtracted the chronological age from this index and called it, “Revised Brain Age Gap (RBAG)”. We would like to follow the original terminology, but we do not want to use the word “Predicted Age” since chronological age can be predicted by other variables beyond the brain. We then settled with the word, "Corrected Brain Age" and “Corrected Brain Age Gap". We listed the terminologies used in the past in our article (see below).

3) A method proposed by Le and colleagues (2018). Here, Butler and colleagues (2021) referred to one of the approaches done by Le and colleagues: “include age as a regressor when doing follow-up analyses.” Essentially this is what we did for the commonality analysis. Le and colleagues (2018)’ approach is the same as examining the unique effects of Brain Age in a multiple regression analysis with Chronological Age and Brain Age as regressors.

While indexes from de Lange and Cole’s (2020) and Le and colleagues’ (2018) methods show poor performance in capturing fluid cognition in the current work, we need to stress that many research groups do not believe that these methods are meaningless. In fact, de Lange and Cole’s method (2020) is one of the most commonly implemented methods that can be seen elsewhere (e.g., Cole et al., 2020; Cumplido-Mayoral et al., 2023; Denissen et al., 2022). This index just does not seem to work well in the case of fluid cognition.

Here is how we described how we calculated Brain Age indexes in the revised manuscript:

Methods

“ Brain Age calculations: Brain Age, Brain Age Gap, Corrected Brain Age and Corrected Brain Age Gap In addition to Brain Age, which is the predicted value from the models predicting chronological age in the test sets, we calculated three other indices to reflect the estimation of brain aging. First, Brain Age Gap reflects the difference between the age predicted by brain MRI and the actual, chronological age. Here we simply subtracted the chronological age from Brain Age:

Brain Age Gapi = Brain Agei - chronological agei , (2)

where i is the individual. Next, to reduce the dependency on chronological age (Butler et al., 2021; de Lange & Cole, 2020; Le et al., 2018), we applied a method described in de Lange and Cole’s (2020), which was implemented elsewhere (Cole et al., 2020; Cumplido-Mayoral et al., 2023; Denissen et al., 2022):

In each outer-fold training set: Brain Agei = 0 + 1 chronological agei + εi, (3)

Then in the corresponding outer-fold test set: Corrected Brain Agei = (Brain Agei - 0)/1, (4)

That is, we first fit a regression line predicting the Brain Age from a chronological age in each outer-fold training set. We then used the slope (1) and intercept (0) of this regression line to adjust Brain Age in the corresponding outer-fold test set, resulting in Corrected Brain Age. Note de Lange and Cole (2020) called this Corrected Brain Age, “Corrected Predicted Age”, while Butler (2021) called it “Revised Predicted Age.”

Lastly, we computed Corrected Brain Age Gap by subtracting the chronological age from the Corrected Brain Age (Butler et al., 2021; Cole et al., 2020; de Lange & Cole, 2020; Denissen et al., 2022):

Corrected Brain Age Gap = Corrected Brain Age - chronological age, (5)

Note Cole and colleagues (2020) called Corrected Brain Age Gap, “brain-predicted age difference (brain-PAD),” while Butler and colleagues (2021) called this index, “Revised Brain Age Gap”.

Reviewer 3 Public Review #3:

• "However, the improvement in predicting chronological age may not necessarily make Brain Age to be better at capturing Cognitionfluid. If, for instance, the age-prediction model had the perfect performance, Brian Age Gap would be exactly zero and would have no utility in capturing Cognitionfluid beyond chronological age" (p3). I largely agree with this statement. I would be really careful to distinguish between brain-age and the brain-age gap here, as the former is a predicted value, and the latter is the residual times -1 (i.e., predicted age - age). Therefore, together they explain all of the variance in age. Changing the first sentence to refer to the brain-age gap would be more accurate in this context. The brain-age gap will never be exactly zero, though, even with perfect prediction on the training set, because subjects in the testing set are different from the subjects in the training set.

Response: Thank you so much for pointing this out. We agree to change “Brain Age” to “Brain Age Gap” in the mentioned sentence.

Reviewer 3 Public Review #4:

• "Can we further improve our ability to capture the decline in cognitionfluid by using, not only Brain Age and chronological age, but also another biomarker, Brain Cognition?". This question is fundamentally getting at whether a predicted value of cognition can predict cognition. Assuming the brain parameters can predict cognition decently, and the original cognitive measure that you were predicting is related to your measure of fluid cognition, the answer should be yes. Upon reading the Methods, it became clear that the cognitive variable in the model predicting cognition using brain features (to get predicted cognition, or as the authors refer to it, brain-cognition) is the same as the measure of fluid cognition that you are trying to assess how well brain-cognition can predict. Assuming the brain parameters can predict fluid cognition at all, it is then inevitable that brain-cognition will predict fluid cognition. Therefore, it is inappropriate to use predicted values of a variable to predict the same variable.

Response: Thank you Reviewer 3 for pointing out this important issue. Reviewer 1 (Recommendations For The Authors #4) and Reviewer 2 (Public Review #4) bought up a similar issue. While Reviewer 3 felt that “it is inappropriate to use predicted values of a variable to predict the same variable,“ Reviewer 2 viewed Brain Cognition as a 'specific/direct' index and Brain Age as a 'generic/indirect' index. And both have merit in their own right.

Similar to Reviewer 2, we believe that the specific index is as important and has commonly been used elsewhere in the context of biomarkers. For instance, to obtain neuroimaging biomarkers for Alzheimer’s, neuroimaging researchers often build a predictive model to predict Alzheimer's diagnosis (Khojaste-Sarakhsi et al., 2022). In fact, outside of neuroimaging, polygenic risk scores (PRSs) in genomics are often used following “to use predicted values of a variable to predict the same variable” (Choi et al., 2020). For instance, a PRS of ADHD that indicates the genetic liability to develop ADHD is based on genome-wide association studies of ADHD (Demontis et al., 2019).

Still, we now agreed that it may not be fair to compare the performance of a specific index (Brain Cognition) and a generic index (Brain Age) directly (as pointed out by Reviewer 3 Public Review #6 below). Accordingly, in the revision, as opposed to treating Brain Cognition and Brain Age as separate biomarkers and comparing them, we treated the capability of Brain Cognition in capturing fluid cognition as the upper limit of Brain Age’s capability in capturing fluid cognition. In other words, the strength of an out-of-sample relationship between Brain Cognition and fluid cognition reflects variation in the brain MRI that is related to fluid cognition. And consequently, the unique effects of Brain Cognition that explain fluid cognition beyond Brain Age and chronological age indicate what is missing from Brain Age -- the amount of co-variation between brain MRI and fluid cognition that cannot be captured by Brain Age. According to Reviewer 2, a generic index (Brain Age) “sacrificed some additional explained variance provided” compared to a specific index (Brain Cognition). Here, we used the commonality analyses to quantify how much scarifying was made by Brain Age. See below for the re-conceptualisation of Brain Age vs. Brain Cognition in the revision:

Abstract

“Lastly, we tested how much Brain Age missed the variation in the brain MRI that could explain fluid cognition. To capture this variation in the brain MRI that explained fluid cognition, we computed Brain Cognition, or a predicted value based on prediction models built to directly predict fluid cognition (as opposed to chronological age) from brain MRI data. We found that Brain Cognition captured up to an additional 11% of the total variation in fluid cognition that was missing from the model with only Brain Age and chronological age, leading to around a 1/3-time improvement of the total variation explained.”

Introduction:

“Third and finally, certain variation in the brain MRI is related to fluid cognition, but to what extent does Brain Age not capture this variation? To estimate the variation in the brain MRI that is related to fluid cognition, we could build prediction models that directly predict fluid cognition (i.e., as opposed to chronological age) from brain MRI data. Previous studies found reasonable predictive performances of these cognition-prediction models, built from certain MRI modalities (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). Analogous to Brain Age, we called the predicted values from these cognition-prediction models, Brain Cognition. The strength of an out-of-sample relationship between Brain Cognition and fluid cognition reflects variation in the brain MRI that is related to fluid cognition and, therefore, indicates the upper limit of Brain Age’s capability in capturing fluid cognition. Consequently, the unique effects of Brain Cognition that explain fluid cognition beyond Brain Age and chronological age indicate what is missing from Brain Age -- the amount of co-variation between brain MRI and fluid cognition that cannot be captured by Brain Age.”

“Finally, we investigated the extent to which Brain Age indices missed the variation in the brain MRI that could explain fluid cognition. Here, we tested Brain Cognition’s unique effects in multiple regression models with a Brain Age index, chronological age and Brain Cognition as regressors to explain fluid cognition.“

Discussion

“Third, how much does Brain Age miss the variation in the brain MRI that could explain fluid cognition? Brain Age and chronological age by themselves captured around 32% of the total variation in fluid cognition. But, around an additional 11% of the variation in fluid cognition could have been captured if we used the prediction models that directly predicted fluid cognition from brain MRI.

“Third, by introducing Brain Cognition, we showed the extent to which Brain Age indices were not able to capture the variation of brain MRI that is related to fluid cognition. Brain Cognition, from certain cognition-prediction models such as the stacked models, has relatively good predictive performance, consistent with previous studies (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). We then examined Brain Cognition using commonality analyses (Nimon et al., 2008) in multiple regression models having a Brain Age index, chronological age and Brain Cognition as regressors to explain fluid cognition. Similar to Brain Age indices, Brain Cognition exhibited large common effects with chronological age. But more importantly, unlike Brain Age indices, Brain Cognition showed large unique effects, up to around 11%. The unique effects of Brain Cognition indicated the amount of co-variation between brain MRI and fluid cognition that was missed by a Brain Age index and chronological age. This missing amount was relatively high, considering that Brain Age and chronological age together explained around 32% of the total variation in fluid cognition. Accordingly, if a Brain Age index was used as a biomarker along with chronological age, we would have missed an opportunity to improve the performance of the model by around one-third of the variation explained.”

Reviewer 3 Public Review #5:

• "However, Brain Age Gap created from the lower-performing age-prediction models explained a higher amount of variation in Cognitionfluid. For instance, the top performing age-prediction model, "Stacked: All excluding Task Contrast", generated Brain Age and Corrected Brain Age that explained the highest amount of variation in Cognitionfluid, but, at the same time, produced Brian Age Gap that explained the least amount of variation in Cognitionfluid" (p7). This is an inevitable consequence of the following relationship between predicted values and residuals (or residuals times -1): y=(y-y ̂ )+y ̂. Let's say that age explains 60% of the variance in fluid cognition, and predicted age (y ̂) explains 40% of the variance in fluid cognition. Then the brain age gap (-(y-y ̂)) should explain 20% of the variance in fluid cognition. If by "Corrected Brain Age" you mean the modified predicted age from Butler et al (2021), the "Corrected Brain Age" result is inevitable because the modified predicted age is essentially just age with a tiny bit of noise added to it. From Figure 4, though, this does not seem to be the case, because the lower left quadrant in panel (a) should be flat and high (about as high as the predictive value of age for fluid cognition). So it is unclear how "Corrected Brain Age" is calculated. It looks like you might be regressing age out of brain-age, though from your description in the Methods section, it is not totally clear. Again, I highly recommend using the terminology and metrics of Butler et al (2021) throughout to reduce confusion. Please also clarify how you used the slope and intercept. In general, given how brain-age metrics tend to be calculated, the following conclusion is inevitable: "As before, the unique effects of Brain Age indices were all relatively small across the four Brain Age indices and across different prediction models" (p10).

Response: We agreed that the results are ‘inevitable’ due to the transformations from Brain Age to other Brain Age indices. However, the consequences of these transformations may not be very clear to readers who are not very familiar with Brain Age literature and to the community at large who think about the implications of Brain Age. This is appreciated by Reviewer 1, who mentioned “While the main message will not come as a surprise to anyone with hands-on experience of using brain-age models, I think it is nonetheless an important message to convey to the community.”

Note we made clarifications on how we calculated each of the Brain Age indices above (see<br /> Reviewer 3 Public Review #2), including how we used the slope and intercept. We chose the terminology closer to the one originally used by de Lange and Cole (2020) and now listed many terminologies others have used to refer to this transformation.

Reviewer 3 Public Review #6:

"On the contrary, the unique effects of Brain Cognition appeared much larger" (p10). This is not a fair comparison if you do not look at the unique effects above and beyond the cognitive variable you predicted in your brain-cognition model. If your outcome measure had been another metric of cognition other than fluid cognition, you would see that brain-cognition does not explain any additional variance in this outcome when you include fluid cognition in the model, just as brain-age would not when including age in the model (minus small amounts due to penalization and out-of-sample estimates). This highlights the fact that using a predicted value to predict anything is worse than using the value itself.

Response Please see our response to Reviewer 3 Public Review #4 above. Briefly, we no long made this comparison. Instead, we now viewed the unique effects of Brain Cognition as a way to test how much Brain Age missed the variation in the brain MRI that could explain fluid cognition.

Reviewer 3 Public Review #7:

"First, how much does Brain Age add to what is already captured by chronological age? The short answer is very little" (p12). This is a really important point, but the paper requires an in-depth discussion of the inevitability of this result, as discussed above.

Response We agree that the tight relationship between Brain Age and chronological age is inevitable. We mentioned this from the get-go in the introduction:

Introduction “Accordingly, by design, Brain Age is tightly close to chronological age. Because chronological age usually has a strong relationship with fluid cognition, to begin with, it is unclear how much Brain Age adds to what is already captured by chronological age.”

To make this point obvious, we quantified the overlap between Brain Age and chronological age using the commonality analysis. We hope that our effort to show the inevitability of this overlap can make people more careful when designing studies involving Brain Age.

Reviewer 3 Public Review #8:

"Third, do we have a solution that can improve our ability to capture Cognitionfluid from brain MRI? The answer is, fortunately, yes. Using Brain Cognition as a biomarker, along with chronological age, seemed to capture a higher amount of variation in Cognitionfluid than only using Brain Age" (p12). I suggest controlling for the cognitive measure you predicted in your brain-cognition model. This will show that brain-cognition is not useful above and beyond cognition, highlighting the fact that it is not a useful endeavor to be using predicted values.

Response This point is similar to Reviewer 3 Public Review #6. Again please see our response to Reviewer 3 Public Review #4 above. Briefly, we no long made this comparison and said whether Brain Cognition is ‘better’ than Brain Age. Instead, we now viewed the unique effects of Brain Cognition as a way to test how much Brain Age missed the variation in the brain MRI that could explain fluid cognition.

Reviewer 3 Public Review #9:

"Accordingly, a race to improve the performance of age-prediction models (Baecker et al., 2021) does not necessarily enhance the utility of Brain Age indices as a biomarker for Cognitionfluid. This calls for a new paradigm. Future research should aim to build prediction models for Brian Age indices that are not necessarily good at predicting age, but at capturing phenotypes of interest, such as Cognitionfluid and beyond" (p13). I whole-heartedly agree with the first two sentences, but strongly disagree with the last. Certainly your results, and the underlying reason as to why you found these results, calls for a new paradigm (or, one might argue, a pre-brain-age paradigm). As of now, your results do not suggest that researchers should keep going down the brain-age path. While it is difficult to prove that there is no transformation of brain-age or the brain-age gap that will be useful, I am nearly sure this is true from the research I have done. If you would like to suggest that the field should continue down this path, I suggest presenting a very good case to support this view.

Response Thank you for your comments on this issue.

Since the submission of our manuscript, other researchers also made a similar observation regarding the disagreement between the predictive performance of age-prediction models and the utility of Brain Age. For instance, in their systematic review, Jirasarie and colleagues (2023, p7) wrote this statement, “Despite mounting evidence, there is a persisting assumption across several studies that the most accurate brain age models will have the most potential for detecting differences in a given phenotype of interest. As a point of illustration, seven of the twenty studies in this review only evaluated the utility of their most accurate model, which in all cases was trained using multimodal features. This approach has also led to researchers to exclusively use T1-weighted and diffusion-weighted MRI scans when developing brain age models36 since such modalities have been shown to have the largest contribution to a model’s predictive power.2,67 However, our review suggests that model accuracy does not necessarily provide meaningful insight about clinical utility (e.g., detection of age-related pathology). Taken with prior studies,16,17 it appears that the most accurate models tend to not be the most useful.”

We now discussed the disagreement between the predictive performance of age-prediction models and the utility of Brain Age, not only in the context of cognitive functioning (Jirsaraie, Kaufmann, et al., 2023) but also in the context of neurological/psychological disorders (Bashyam et al., 2020; Rokicki et al., 2021). Following Reviewer 3’s suggestion, we also added several possible strategies to mitigate this problem of Brain Age, used by us and other groups. Please see below.

Discussion:

“This discrepancy between the predictive performance of age-prediction models and the utility of Brain Age indices as a biomarker is consistent with recent findings (for review, see Jirsaraie, Gorelik, et al., 2023), both in the context of cognitive functioning (Jirsaraie, Kaufmann, et al., 2023) and neurological/psychological disorders (Bashyam et al., 2020; Rokicki et al., 2021). For instance, combining different MRI modalities into the prediction models, similar to our stacked models, often lead to the highest performance of age-prediction models, but does not likely explain the highest variance across different phenotypes, including cognitive functioning and beyond (Jirsaraie, Gorelik, et al., 2023).”

“Next, researchers should not select age-prediction models based solely on age-prediction performance. Instead, researchers could select age-prediction models that explained phenotypes of interest the best. Here we selected age-prediction models based on a set of features (i.e., modalities) of brain MRI. This strategy was found effective not only for fluid cognition as we demonstrated here, but also for neurological and psychological disorders as shown elsewhere (Jirsaraie, Gorelik, et al., 2023; Rokicki et al., 2021). Rokicki and colleagues (2021), for instance, found that, while integrating across MRI modalities led to age-prediction models with the highest age-prediction performance, using only T1 structural MRI gave age-prediction models that were better at classifying Alzheimer’s disease. Similarly, using only cerebral blood flow gave age-prediction models that were better at classifying mild/subjective cognitive impairment, schizophrenia and bipolar disorder.

As opposed to selecting age-prediction models based on a set of features, researchers could also select age-prediction models based on modelling methods. For instance, Jirsaraie and colleagues (2023) compared gradient tree boosting (GTB) and deep-learning brain network (DBN) algorithms in building age-prediction models. They found GTB to have higher age-prediction performance but DBN to have better utility in explaining cognitive functioning. In this case, an algorithm with better utility (e.g., DBN) should be used for explaining a phenotype of interest. Similarly, Bashyam and colleagues (2020) built different DBN-based age-prediction models, varying in age-prediction performance. The DBN models with a higher number of epochs corresponded to higher age-prediction performance. However, DBN-based age-prediction models with a moderate (as opposed to higher or lower) number of epochs were better at classifying Alzheimer’s disease, mild cognitive impairment and schizophrenia. In this case, a model from the same algorithm with better utility (e.g., those DBN with a moderate epoch number) should be used for explaining a phenotype of interest. Accordingly, this calls for a change in research practice, as recently pointed out by Jirasarie and colleagues (2023, p7), “Despite mounting evidence, there is a persisting assumption across several studies that the most accurate brain age models will have the most potential for detecting differences in a given phenotype of interest”. Future neuroimaging research should aim to build age-prediction models that are not necessarily good at predicting age, but at capturing phenotypes of interest.”

Reviewer #1 (Recommendations For The Authors):

In this paper, the authors evaluate the utility of brain age derived metrics for predicting cognitive decline using the HCP aging dataset by performing a commonality analysis in a downstream regression. The main conclusion is that brain age derived metrics do not explain much additional variation in cognition over and above what is already explained by age. The authors propose to use a regression model trained to predict cognition ('brain-cognition') as an alternative that explains more unique variance in the downstream regression.

This is a reasonably good paper and the use of a commonality analysis is a nice contribution to understanding variance partitioning across different covariates. While the main message will not come as a surprise to anyone with hands-on experience of using brain-age models, I think it is nonetheless an important message to convey to the community. With that said, I have some comments that I believe the authors ought to address before publication.

Reviewer 1 Recommendations For The Authors #1:

First, from a conceptual point of view, the authors focus exclusively on cognition as a downstream outcome. This is undeniably important, but is only one application area for brain age models. They are also used for example to provide biomarkers for many brain disorders. What would the results presented here have to say about these application areas? Further, I think that since brain-age models by construction confound relevant biological variation with the accuracy of the regression models used to estimate them, my own opinion about the limits of interpretation of (e.g.) the brain-age gap is as a dimensionless biomarker. This has also been discussed elsewhere (see e.g. https://academic.oup.com/brain/article/143/7/2312/5863667). I would suggest the authors nuance their discussion to provide considerations on these issues.

Response Thank you Reviewer 1 for pointing out two important issues.

The first issue was about applications for brain disorders. We now made a detailed discussion about this, which also addressed Reviewer 3 Public Review #9. Briefly, we now bought up

1) the consistency between our findings on fluid cognition and other recent works on brain disorders,

2) under-fitted age-prediction models from Brain Age studies focusing on neurological/psychological disorders when applied to participants with neurological/psychological disorders because the age-prediction models were built from largely healthy participants,

and 3) suggested solutions we and others made to optimise the utility of Brain Age for both cognitive functioning and brain disorders.

Discussion:

“This discrepancy between the predictive performance of age-prediction models and the utility of Brain Age indices as a biomarker is consistent with recent findings (for review, see Jirsaraie, Gorelik, et al., 2023), both in the context of cognitive functioning (Jirsaraie, Kaufmann, et al., 2023) and neurological/psychological disorders (Bashyam et al., 2020; Rokicki et al., 2021). For instance, combining different MRI modalities into the prediction models, similar to our stacked models, often lead to the highest performance of age-prediction models, but does not likely explain the highest variance across different phenotypes, including cognitive functioning and beyond (Jirsaraie, Gorelik, et al., 2023).”

“There is a notable difference between studies investigating the utility of Brain Age in explaining cognitive functioning, including ours and others (e.g., Butler et al., 2021; Cole, 2020, 2020; Jirsaraie, Kaufmann, et al., 2023) and those explaining neurological/psychological disorders (e.g., Bashyam et al., 2020; Rokicki et al., 2021). That is, those Brain Age studies focusing on neurological/psychological disorders often build age-prediction models from MRI data of largely healthy participants (e.g., controls in a case-control design or large samples in a population-based design), apply the built age-prediction models to participants without vs. with neurological/psychological disorders and compare Brain Age indices between the two groups. This means that age-prediction models from Brain Age studies focusing on neurological/psychological disorders might be under-fitted when applied to participants with neurological/psychological disorders because they were built from largely healthy participants. And thus, the difference in Brain Age indices between participants without vs. with neurological/psychological disorders might be confounded by the under-fitted age-prediction models (i.e., Brain Age may predict chronological age well for the controls, but not for those with a disorder). On the contrary, our study and other Brain Age studies focusing on cognitive functioning often build age-prediction models from MRI data of largely healthy participants and apply the built age-prediction models to participants who are also largely healthy. Accordingly, the age-prediction models for explaining cognitive functioning do not suffer from being under-fitted. We consider this as a strength, not a weakness of our study.”

“Next, researchers should not select age-prediction models based solely on age-prediction performance. Instead, researchers could select age-prediction models that explained phenotypes of interest the best. Here we selected age-prediction models based on a set of features (i.e., modalities) of brain MRI. This strategy was found effective not only for fluid cognition as we demonstrated here, but also for neurological and psychological disorders as shown elsewhere (Jirsaraie, Gorelik, et al., 2023; Rokicki et al., 2021). Rokicki and colleagues (2021), for instance, found that, while integrating across MRI modalities led to age-prediction models with the highest age-prediction performance, using only T1 structural MRI gave age-prediction models that were better at classifying Alzheimer’s disease. Similarly, using only cerebral blood flow gave age-prediction models that were better at classifying mild/subjective cognitive impairment, schizophrenia and bipolar disorder. As opposed to selecting age-prediction models based on a set of features, researchers could also select age-prediction models based on modelling methods. For instance, Jirsaraie and colleagues (2023) compared gradient tree boosting (GTB) and deep-learning brain network (DBN) algorithms in building age-prediction models. They found GTB to have higher age-prediction performance but DBN to have better utility in explaining cognitive functioning. In this case, an algorithm with better utility (e.g., DBN) should be used for explaining a phenotype of interest. Similarly, Bashyam and colleagues (2020) built different DBN-based age-prediction models, varying in age-prediction performance. The DBN models with a higher number of epochs corresponded to higher age-prediction performance. However, DBN-based age-prediction models with a moderate (as opposed to higher or lower) number of epochs were better at classifying Alzheimer’s disease, mild cognitive impairment and schizophrenia. In this case, a model from the same algorithm with better utility (e.g., those DBN with a moderate epoch number) should be used for explaining a phenotype of interest. Accordingly, this calls for a change in research practice, as recently pointed out by Jirasarie and colleagues (2023, p7), “Despite mounting evidence, there is a persisting assumption across several studies that the most accurate brain age models will have the most potential for detecting differences in a given phenotype of interest”. Future neuroimaging research should aim to build age-prediction models that are not necessarily good at predicting age, but at capturing phenotypes of interest.”

The second issue was about “the brain-age gap as a dimensionless biomarker.” We are not so clear on what the reviewer meant by “the dimensionless biomarker.” One possible meaning of the “dimensionless biomarker” is the fact that Brain Age from the same algorithm and same modality can be computed, such that Brain Age can be tightly fit or loosely fit with chronological age. This is what Bashyam and colleagues (2020) did in the article Reviewer 1 referred to. We now wrote about this strategy in the above paragraph in the Discussion.

Alternatively, “the dimensionless biomarker” might be something closer to what Reviewer 2 viewed Brain Age as a “generic/indirect” index (as opposed to a 'specific/direct' index in the case of Brain Cognition) (see Reviewer 2 Public Review #4). We discussed this in our response to Reviewer 3 Public Review #4.

Reviewer 1 Recommendations For The Authors #2:

Second, from a methods perspective, I am quite suspicious of the stacked regression models the authors are using to combine regression models and I suspect they may be overfit. In my experience, stacked models are very prone to overfitting when combined with cross-validation. This is because the predictions from the first level models (i,e. the features that are provided to the second-level 'stacked' models) contain information about the training set and the test set. If cross-validation is not done very carefully (e.g. using multiple hold-out sets), information leakage can easily occur at the second level. Unfortunately, there is not sufficient explanation of the methodological procedures in the current manuscript to fully understand what was done. First, please provide more information to enable the reader to better understand the stacked regression models and if the authors are not using an approach that fully preserves training and test separability, please do so.

Response: We would like to thank Reviewer 1 for the suggestion. We now made it clearer in texts and new figure (see below) that we used nested cross-validation to ensure no information leakage between training and test sets. Regarding the stacked models more specifically, the hyperparameters of the stacked models were tuned in the same inner-fold CV as the non-stacked model (see Figure 7 below). That is, training models for both non-stacked and stacked models did not involve the test set, ensuring that there was no data leakage between training and test sets.

Methods:

“To compute Brain Age and Brain Cognition, we ran two separate prediction models. These prediction models either had chronological age or fluid cognition as the target and standardised brain MRI as the features (Denissen et al., 2022). We used nested cross-validation (CV) to build these models (see Figure 7). We first split the data into five outer folds. We used five outer folds so that each outer fold had around 100 participants. This is to ensure the stability of the test performance across folds. In each outer-fold CV, one of the outer folds was treated as a test set, and the rest was treated as a training set, which was further divided into five inner folds. In each inner-fold CV, one of the inner folds was treated as a validation set and the rest was treated as a training set. We used the inner-fold CV to tune for hyperparameters of the models and the outer-fold CV to evaluate the predictive performance of the models.

In addition to using each of the 18 sets of features in separate prediction models, we drew information across these sets via stacking. Specifically, we computed predicted values from each of the 18 sets of features in the training sets. We then treated different combinations of these predicted values as features to predict the targets in separate “stacked” models. The hyperparameters of the stacked models were tuned in the same inner-fold CV as the non-stacked model (see Figure 7). That is, training models for both non-stacked and stacked models did not involve the test set, ensuring that there was no data leakage between training and test sets. We specified eight stacked models: “All” (i.e., including all 18 sets of features), “All excluding Task FC”, “All excluding Task Contrast”, “Non-Task” (i.e., including only Rest FC and sMRI), “Resting and Task FC”, “Task Contrast and FC”, “Task Contrast” and “Task FC”. Accordingly, in total, there were 26 prediction models for Brain Age and Brain Cognition.

Reviewer 1 Recommendations For The Authors #3:

Third, the authors standardize the elastic net regression coefficients post-hoc. Why did the authors not perform the more standard approach of standardizing the covariates and responses, prior to model estimation, which would yield standardized regression coefficients (in the classical sense) by construction? Please also provide an indication of the different regression strengths that were estimated across the different models and cross-validation splits. Also, how stable were the weights across splits?

Response For model fitting, we did not “standardize the elastic net regression coefficients post-hoc.” Instead, we did all of the standardisation steps prior to model fitting (see Methods below). For regression strengths across different models and cross-validation splits, we now provided predictive performance at each of the five outer-fold test sets in Figure 1 (below). As you may have seen, the predictive performance was quite stable across the cross-validation splits.

For visualising feature importance, We originally only standardised the elastic net regression coefficients post-hoc, so that feature importance plots were in the same scale across folds. However, as mentioned by Reviewer 3 (Recommendations for the Authors #7, below), this might make it difficult to interpret the directionality of the coefficients. In the revised manuscript, we refitted the Elastic Net model to the full dataset without splitting them into five folds and visualised the coefficients on brain images (see below).

Methods

“We controlled for the potential influences of biological sex on the brain features by first residualising biological sex from brain features in each outer-fold training set. We then applied the regression of this residualisation to the corresponding test set. We also standardised the brain features in each outer-fold training set and then used the mean and standard deviation of this outer-fold training set to standardise the test set. All of the standardisation was done prior to fitting the prediction models.”

“To understand how Elastic Net made a prediction based on different brain features, we examined the coefficients of the tuned model. Elastic Net coefficients can be considered as feature importance, such that more positive Elastic Net coefficients lead to more positive predicted values and, similarly, more negative Elastic Net coefficients lead to more negative predicted values (Molnar, 2019; Pat, Wang, Bartonicek, et al., 2022). While the magnitude of Elastic Net coefficients is regularised (thus making it difficult for us to interpret the magnitude itself directly), we could still indicate that a brain feature with a higher magnitude weights relatively stronger in making a prediction. Another benefit of Elastic Net as a penalised regression is that the coefficients are less susceptible to collinearity among features as they have already been regularised (Dormann et al., 2013; Pat, Wang, Bartonicek, et al., 2022).

Given that we used five-fold nested cross validation, different outer folds may have different degrees of ‘’ and ‘l_1 ratio’, making the final coefficients from different folds to be different. For instance, for certain sets of features, penalisation may not play a big part (i.e., higher or lower ‘’ leads to similar predictive performance), resulting in different ‘’ for different folds. To remedy this in the visualisation of Elastic Net feature importance, we refitted the Elastic Net model to the full dataset without splitting them into five folds and visualised the coefficients on brain images using Brainspace (Vos De Wael et al., 2020) and Nilern (Abraham et al., 2014) packages. Note, unlike other sets of features, Task FC and Rest FC were modelled after data reduction via PCA. Thus, for Task FC and Rest FC, we, first, multiplied the absolute PCA scores (extracted from the ‘components_’ attribute of ‘sklearn.decomposition.PCA’) with Elastic Net coefficients and, then, summed the multiplied values across the 75 components, leaving 71,631 ROI-pair indices.”

Reviewer 1 Recommendations For The Authors #4:

I do not really find it surprising that the level of unique explained variance provided by a brain-cognition model is higher than a brain-age model, given that the latter is considerably more accurate (also, in view of the comment above). As such I would recommend to tone down the claims about the utility of this method, also because it is only really applicable to one application area for brain age.

Response Thank you for bringing this issue to our attention. We have now toned down the claims about the utility of Brain Cognition and importantly treated the capability of Brain Cognition in capturing fluid cognition as the upper limit of Brain Age’s capability in capturing fluid cognition. Please see Reviewer 3 Public Review #4 above for a detailed discussion about this issue.

Reviewer 1 Recommendations For The Authors #5:

Please provide more details about the task designs and MRI processing procedures that were employed on this sample so that the reader is not forced to dig through the publications from the consortia contributing the data samples used. For example, comments such as "Here we focused on the pre-processed task fMRI files with a suffix "_PA_Atlas_MSMAll_hp0_clean.dtseries.nii." are not particularly helpful to readers not already familiar with this dataset.

Response Thank you so much for pointing out this important point on the clarity of the description of our MRI methodology. We now added additional details about the data processing done by the HCP-A and by us. We, for instance, explained the meaning of the HCP-A suffix “"_PA_Atlas_MSMAll_hp0_clean.dtseries.nii”. Please see below.

Methods

“HCP-A provides details of parameters for brain MRI elsewhere (Bookheimer et al., 2019; Harms et al., 2018). Here we used MRI data that were pre-processed by the HCP-A with recommended methods, including the MSMALL alignment (Glasser et al., 2016; Robinson et al., 2018) and ICA-FIX (Glasser et al., 2016) for functional MRI. We used multiple brain MRI modalities, covering task functional MRI (task fMRI), resting-state functional MRI (rsfMRI) and structural MRI (sMRI), and organised them into 19 sets of features.

Sets of Features 1-10: Task fMRI contrast (Task Contrast)

Task contrasts reflect fMRI activation relevant to events in each task. Bookheimer and colleagues (2019) provided detailed information about the fMRI in HCP-A. Here we focused on the pre-processed task fMRI Connectivity Informatics Technology Initiative (CIFTI) files with a suffix, “_PA_Atlas_MSMAll_hp0_clean.dtseries.nii.” These CIFTI files encompassed both the cortical mesh surface and subcortical volume (Glasser et al., 2013). Collected using the posterior-to-anterior (PA) phase, these files were aligned using MSMALL (Glasser et al., 2016; Robinson et al., 2018), linear detrended (see https://groups.google.com/a/humanconnectome.org/g/hcp-users/c/ZLJc092h980/m/GiihzQAUAwAJ) and cleaned from potential artifacts using ICA-FIX (Glasser et al., 2016).

To extract Task Contrasts, we regressed the fMRI time series on the convolved task events using a double-gamma canonical hemodynamic response function via FMRIB Software Library (FSL)’s FMRI Expert Analysis Tool (FEAT) (Woolrich et al., 2001). We kept FSL’s default high pass cutoff at 200s (i.e., .005 Hz). We then parcellated the contrast ‘cope’ files, using the Glasser atlas (Gordon et al., 2016) for cortical surface regions and the Freesurfer’s automatic segmentation (aseg) (Fischl et al., 2002) for subcortical regions. This resulted in 379 regions, whose number was, in turn, the number of features for each Task Contrast set of features.

HCP-A collected fMRI data from three tasks: Face Name (Sperling et al., 2001), Conditioned Approach Response Inhibition Task (CARIT) (Somerville et al., 2018) and VISual MOTOR (VISMOTOR) (Ances et al., 2009). First, the Face Name task (Sperling et al., 2001) taps into episodic memory. The task had three blocks. In the encoding block [Encoding], participants were asked to memorise the names of faces shown. These faces were then shown again in the recall block [Recall] when the participants were asked if they could remember the names of the previously shown faces. There was also the distractor block [Distractor] occurring between the encoding and recall blocks. Here participants were distracted by a Go/NoGo task. We computed six contrasts for this Face Name task: [Encode], [Recall], [Distractor], [Encode vs. Distractor], [Recall vs. Distractor] and [Encode vs. Recall].

Second, the CARIT task (Somerville et al., 2018) was adapted from the classic Go/NoGo task and taps into inhibitory control. Participants were asked to press a button to all [Go] but not to two [NoGo] shapes. We computed three contrasts for the CARIT task: [NoGo], [Go] and [NoGo vs. Go].

Third, the VISMOTOR task (Ances et al., 2009) was designed to test simple activation of the motor and visual cortices. Participants saw a checkerboard with a red square either on the left or right. They needed to press a corresponding key to indicate the location of the red square. We computed just one contrast for the VISMOTOR task: [Vismotor], which indicates the presence of the checkerboard vs. baseline.

Sets of Features 11-13: Task fMRI functional connectivity (Task FC)

Task FC reflects functional connectivity (FC ) among the brain regions during each task, which is considered an important source of individual differences (Elliott et al., 2019; Fair et al., 2007; Gratton et al., 2018). We used the same CIFTI file “_PA_Atlas_MSMAll_hp0_clean.dtseries.nii.” as the task contrasts. Unlike Task Contrasts, here we treated the double-gamma, convolved task events as regressors of no interest and focused on the residuals of the regression from each task (Fair et al., 2007). We computed these regressors on FSL, and regressed them in nilearn (Abraham et al., 2014). Following previous work on task FC (Elliott et al., 2019), we applied a highpass at .008 Hz. For parcellation, we used the same atlases as Task Contrast (Fischl et al., 2002; Glasser et al., 2016). We computed Pearson’s correlations of each pair of 379 regions, resulting in a table of 71,631 non-overlapping FC indices for each task. We then applied r-to-z transformation and principal component analysis (PCA) of 75 components (Rasero et al., 2021; Sripada et al., 2019, 2020). Note to avoid data leakage, we conducted the PCA on each training set and applied its definition to the corresponding test set. Accordingly, there were three sets of 75 features for Task FC, one for each task. “

Reviewer 1 Recommendations For The Authors #6:

Similarly, please be more specific about the regression methods used. There are several different parameterisations of the elastic net, please provide equations to describe the method used here so that readers can easily determine how the regularisation parameters should be interpreted. The same goes for the methods used for correcting bias, e.g. what is "de Lange and Cole's (2020) 5th equation"?

Response Thank you. We now made a detailed description of Elastic Net including its equation (see below). We also added more specific details about the methods used for correcting bias in Brain Age indices (see our response to Reviewer 3 Public Review #2 above).

Methods:

“For the machine learning algorithm, we used Elastic Net (Zou & Hastie, 2005). Elastic Net is a general form of penalised regressions (including Lasso and Ridge regression), allowing us to simultaneously draw information across different brain indices to predict one target variable. Penalised regressions are commonly used for building age-prediction models (Jirsaraie, Gorelik, et al., 2023). Previously we showed that the performance of Elastic Net in predicting cognitive abilities is on par, if not better than, many non-linear and more-complicated algorithms (Pat, Wang, Bartonicek, et al., 2022; Tetereva et al., 2022). Moreover, Elastic Net coefficients are readily explainable, allowing us the ability to explain how our age-prediction and cognition-prediction models made the prediction from each brain feature (Molnar, 2019; Pat, Wang, Bartonicek, et al., 2022) (see below).

Elastic Net simultaneously minimises the weighted sum of the features’ coefficients. The degree of penalty to the sum of the feature’s coefficients is determined by a shrinkage hyperparameter ‘’: the greater the , the more the coefficients shrink, and the more regularised the model becomes. Elastic Net also includes another hyperparameter, ‘l_1 ratio’, which determines the degree to which the sum of either the squared (known as ‘Ridge’; l_1 ratio=0) or absolute (known as ‘Lasso’; l_1 ratio=1) coefficients is penalised (Zou & Hastie, 2005). The objective function of Elastic Net as implemented by sklearn (Pedregosa et al., 2011) is defined as: argmin_ ((|(|y-X|)|_2^2)/(2×n_samples )+α×l_1 _ratio×|(||)|_1+0.5×α×(1-l_1 _ratio)×|(|w|)|_2^2 ), (1) where X is the features, y is the target, and  is the coefficient. In our grid search, we tuned two Elastic Net hyperparameters:  using 70 numbers in log space, ranging from .1 and 100, and l_1-ratio using 25 numbers in linear space, ranging from 0 and 1.”

Additional minor points:

Reviewer 1 Recommendations For The Authors #7:

• Please provide more descriptive figure legends, especially for Figs 5 and 6. For example, what do the boldface numbers reflect? What do the asterisks reflect?

Response Thank you for the suggestion. We made changes to the figure legends to make it clearer what the numbers and asterisks reflect.

Reviewer 1 Recommendations For The Authors #8:

• Perhaps this is personal thing, but I find the nomenclature cognition_{fluid} to be quite awkward. Why not just define FC as an acronym?

Response Thank you for the suggestion. We now used the word ‘fluid cognition’ throughout the manuscript.

Reviewer #2 (Recommendations For The Authors):

Suggestions for improved or additional experiments, data or analyses.

Reviewer 2 Recommendations For The Authors #1:

• Since the study did not provide external validation for the indices, it is unclear how well the models would perform and generalize to other samples. Therefore, it is recommended to conduct out-of-sample testing of the models.

Response Thank you for the suggestion. We now added discussions about how consistency between our results and several recent studies that investigated similar issues with Brain Age in different populations, e.g., large samples of older adults in Uk Biobank (Cole, 2020) and younger populations (Butler et al., 2021; Jirsaraie, Kaufmann, et al., 2023), and in a broader context, extending to neurological and psychological disorders (for review, see Jirsaraie, Gorelik, et al., 2023). Please see below.

Please also noted that all of the analyses done were out-of-sample. We used nested cross-validation to evaluate the predictive performance of age- and cognition-prediction models on the outer-fold test sets, which are out-of-sample from the training sets (please see Reviewer 1 Recommendations For The Authors #2). Similarly, we also conducted all of the commonality analyses on the outer-fold test sets.

Discussion

“The small effects of the Corrected Brain Age Gap in explaining fluid cognition of aging individuals found here are consistent with studies in older adults (Cole, 2020) and younger populations (Butler et al., 2021; Jirsaraie, Kaufmann, et al., 2023). Cole (2020) studied the utility of Brain Age on cognitive functioning of large samples (n>17,000) of older adults, aged 45-80 years, from the UK Biobank (Sudlow et al., 2015). He constructed age-prediction models using LASSO, a similar penalised regression to ours and applied the same age-dependency adjustment to ours. Cole (2020) then conducted a multiple regression explaining cognitive functioning from Corrected Brain Age Gap while controlling for chronological age and other potential confounds. He found Corrected Brain Age Gap to be significantly related to performance in four out of six cognitive measures, and among those significant relationships, the effect sizes were small with a maximum of partial eta-squared at .0059. Similarly, Jirsaraie and colleagues (2023) studied the utility of Brain Age on cognitive functioning of youths aged 8-22 years old from the Human Connectome Project in Development (Somerville et al., 2018) and Preschool Depression Study (Luby, 2010). They built age-prediction models using gradient tree boosting (GTB) and deep-learning brain network (DBN) and adjusted the age dependency of Brain Age Gap using Smith and colleagues’ (2019) method. Using multiple regressions, Jirsaraie and colleagues (2023) found weak effects of the adjusted Brain Age Gap on cognitive functioning across five cognitive tasks, five age-prediction models and the two datasets (mean of standardised regression coefficient = -0.09, see their Table S7). Next, Butler and colleagues (2021) studied the utility of Brain Age on cognitive functioning of another group of youths aged 8-22 years old from the Philadelphia Neurodevelopmental Cohort (PNC) (Satterthwaite et al., 2016). Here they used Elastic Net to build age-prediction models and applied another age-dependency adjustment method, proposed by Beheshti and colleagues (2019). Similar to the aforementioned results, Butler and colleagues (2021) found a weak, statistically non-significant correlation between the adjusted Brain Age Gap and cognitive functioning at r=-.01, p=.71. Accordingly, the utility of Brain Age in explaining cognitive functioning beyond chronological age appears to be weak across age groups, different predictive modelling algorithms and age-dependency adjustments.“

“This discrepancy between the predictive performance of age-prediction models and the utility of Brain Age indices as a biomarker is consistent with recent findings (for review, see Jirsaraie, Gorelik, et al., 2023), both in the context of cognitive functioning (Jirsaraie, Kaufmann, et al., 2023) and neurological/psychological disorders (Bashyam et al., 2020; Rokicki et al., 2021). For instance, combining different MRI modalities into the prediction models, similar to our stacked models, often lead to the highest performance of age-prediction models, but does not likely explain the highest variance across different phenotypes, including cognitive functioning and beyond (Jirsaraie, Gorelik, et al., 2023). “

“Third, by introducing Brain Cognition, we showed the extent to which Brain Age indices were not able to capture the variation of brain MRI that is related to fluid cognition. Brain Cognition, from certain cognition-prediction models such as the stacked models, has relatively good predictive performance, consistent with previous studies (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). We then examined Brain Cognition using commonality analyses (Nimon et al., 2008) in multiple regression models having a Brain Age index, chronological age and Brain Cognition as regressors to explain fluid cognition. Similar to Brain Age indices, Brain Cognition exhibited large common effects with chronological age. But more importantly, unlike Brain Age indices, Brain Cognition showed large unique effects, up to around 11%. The unique effects of Brain Cognition indicated the amount of co-variation between brain MRI and fluid cognition that was missed by a Brain Age index and chronological age. This missing amount was relatively high, considering that Brain Age and chronological age together explained around 32% of the total variation in fluid cognition. Accordingly, if a Brain Age index was used as a biomarker along with chronological age, we would have missed an opportunity to improve the performance of the model by around one-third of the variation explained. “

“There is a notable difference between studies investigating the utility of Brain Age in explaining cognitive functioning, including ours and others (e.g., Butler et al., 2021; Cole, 2020, 2020; Jirsaraie, Kaufmann, et al., 2023) and those explaining neurological/psychological disorders (e.g., Bashyam et al., 2020; Rokicki et al., 2021). That is, those Brain Age studies focusing on neurological/psychological disorders often build age-prediction models from MRI data of largely healthy participants (e.g., controls in a case-control design or large samples in a population-based design), apply the built age-prediction models to participants without vs. with neurological/psychological disorders and compare Brain Age indices between the two groups. This means that age-prediction models from Brain Age studies focusing on neurological/psychological disorders might be under-fitted when applied to participants with neurological/psychological disorders because they were built from largely healthy participants. And thus, the difference in Brain Age indices between participants without vs. with neurological/psychological disorders might be confounded by the under-fitted age-prediction models (i.e., Brain Age may predict chronological age well for the controls, but not for those with a disorder). On the contrary, our study and other Brain Age studies focusing on cognitive functioning often build age-prediction models from MRI data of largely healthy participants and apply the built age-prediction models to participants who are also largely healthy. Accordingly, the age-prediction models for explaining cognitive functioning do not suffer from being under-fitted. We consider this as a strength, not a weakness of our study.”

Reviewer 2 Recommendations For The Authors #2:

• Employ Variance Inflation Factor (VIF) to empirically test for multicollinearity.

Response Given high common effects between many of the regressors in the models (e.g., between Brain Age and chronological age), VIF will be high, but this is not a concern for the commonality analysis. We showed now that applying the commonality analysis to multiple regressions allowed us to have robust results against multicollinearity, as demonstrated elsewhere (Ray-Mukherjee et al., 2014, Using commonality analysis in multiple regressions: A tool to decompose regression effects in the face of multicollinearity). Specifically, using the multiple regressions by themselves without the commonality analysis, researchers have to rely on beta estimates, which are strongly affected by multicollinearity (e.g., a phenomenon known as the Suppression Effect). However, by applying the commonality analysis on top of multiple regressions, researchers can then rely on R2 estimates, which are less affected by multicollinearity. This can be seen in our case (Figure 5 and 6) where Brain Age indices had the same unique effects regardless of the level of common effects they had with chronological age (e.g., Brain Age vs. Corrected Brain Age Gap from stacked models).

To directly demonstrate the robustness of the current commonality analysis regarding multicollinearity, we applied the commonality analysis to Ridge regressions (see Supplementary Figures 3 and 5 below). Ridge regression is a method designed to deal with multicollinearity (Dormann et al., 2013). As seen below, the results from commonality analyses applied to Ridge regressions are closely matched with our original results.

Methods

“Note to ensure that the commonality analysis results were robust against multicollinearity (Ray-Mukherjee et al., 2014), we also repeated the same commonality analyses done here on Ridge regression, as opposed to multiple regression. Ridge regression is a method designed to deal with multicollinearity (Dormann et al., 2013). See Supplementary Figure 3 for the Ridge regression with chronological age and each Brain Age index as regressors and Supplementary Figure 5 for the Ridge regression with chronological age, each Brain Age and Brain Cognition index as regressors. Briefly, the results from commonality analyses applied to Ridge regressions are closely matched with our results done using multiple regression.”

Reviewer 2 Recommendations For The Authors #3:

• Incorporate non-linearities in the correction of brain-age indices, such as separate terms in the regression or statistical analyses.

Response Thank you for the suggestion. We now added a non-linear term of chronological age in our multiple-regression models explaining fluid cognition (see Supplementary Figure 4 and 6 below). Originally we did not have the quadratic term for chronological age in our model since the relationship between chronological age and fluid cognition was relatively linear (see Figure 1 above). Accordingly, as expected, adding the quadratic term for chronological age as suggested did not change the pattern of the results of the commonality analyses.

Methods

“Similarly, to ensure that we were able to capture the non-linear pattern of chronological age in explaining fluid cognition, we added a quadratic term of chronological age to our multiple-regression models in the commonality analyses. See Supplementary Figure 4 for the multiple regression with chronological age, square chronological age and each Brain Age index as regressors and Supplementary Figure 6 for the multiple regression with chronological age, square chronological age, each Brain Age index and Brain Cognition as regressors. Briefly, adding the quadratic term for chronological age did not change the pattern of the results of the commonality analyses.”

Reviewer 2 Recommendations For The Authors #4:

• It would be helpful to include the complete set of results in the appendix - for instance, the statistical significance for each component for the final commonality analysis.

Response Figures 5 and 6 (see above) already have asterisks to reflect the statistical significance of the unique effects. Because of this, we do not believe we need more figures/tables in the appendix to show statistical significance.

Recommendations for improving the writing and presentation.

Reviewer 2 Recommendations For The Authors #5:

• The authors are encouraged to refrain from using terms such as 'fortunately', 'unfortunately', and 'unsettling', as they may appear inappropriate when referring to empirical findings.

Response We agree with this suggestion and no long used those words.

Reviewer 2 Recommendations For The Authors #6:

• It would be helpful to clarify in the methods that you end up with 5 test folds.

Response We now made a clarification why we chose 5 test folds.

Methods

“We used nested cross-validation (CV) to build these models (see Figure 7). We first split the data into five outer folds. We used five outer folds so that each outer fold had around 100 participants. This is to ensure the stability of the test performance across folds.”

Minor corrections to the text and figures.

Reviewer 2 Recommendations For The Authors #7:

• Why use months, not years for chronological age? This seems inappropriate given the age range.

Response We originally used months since they were units used in our prediction modelling. However, to make the figures easier to understand, we now used years.

Reviewer 2 Recommendations For The Authors #8:

• The formatting, especially regarding the text embedded within the figures, could benefit from significant improvements.

Response Thank you for the suggestion. We made changes to the text embedded within the figures. They should be more readable now

Reviewer 2 Recommendations For The Authors #9:

• The legend for the neuroimaging feature labels is missing, and the captions are incomplete.

Response Please see Figure 2 above. We now revised by adding the letter L and R for the laterality of the brain images. We made some changes to the captions to make sure they are complete.

Reviewer 2 Recommendations For The Authors #10:

• Figure 5's caption: SD has a missing decimal point).

Response The numbers are not SD. The numbers to the left of the figure represent the unique effects of chronological age in %, the numbers in the middle of the figure represent the common effects between chronological age and Brain Age index in %, and the numbers to the right of the figure represent the unique effects of Brain Age Index in %. We now used the same one decimal point for these number

Reviewer #3 (Recommendations For The Authors):

The main question of this article is as follows: “To what extent does having information on Brain Age improve our ability to capture declines in fluid cognition beyond knowing a person’s chronological age?” While this question is worthwhile, considering most of the field is confused about the nature of brain age, the authors are currently missing an opportunity to convey the inevitability of their results given how Brain Age and the Brain Age Gap are calculated. They also misleadingly convey that Brain Cognition is somehow superior to Brain Age. If the authors work on conveying the inevitability of their results and redo (or remove) their section on Brain Cognition, I can see how their results would be enlightening to the general neuroimaging community that is interested in the concept of brain age. See below for specific critiques.

Response Please see our response to Reviewer 3 Public Review Overall. Note we no longer argue that Brain Cognition is superior to Brain Age (Reviewer 3 Public Review #4). Rather, we treated the capability of Brain Cognition in capturing fluid cognition as the upper limit of Brain Age’s capability in capturing fluid cognition. We used the unique effects of Brain Cognition that explain fluid cognition beyond Brain Age and chronological age to indicate how much Brain Age misses the variation in the brain MRI that could explain fluid cognition.

Reviewer 3 Recommendations For The Authors #1:

“There are many adjustments proposed to correct for this estimation bias” (p3) → Regression to the mean is not a sign of bias. Any decent loss function will result in over- predicting the age of younger individuals and under-predicting the age of older individuals. This is a direct result of minimizing an error term (e.g., mean squared error). Therefore, it is inappropriate to refer to regression to the mean as a sign of bias. This misconception has led to a great deal of inappropriate analyses, including “correcting” the brain age gap by regressing out age.

Response Please see our response to Reviewer 3 Public Review#1

Reviewer 3 Recommendations For The Authors #2:

“Corrected Brain Age Gap in particular is viewed as being able to control for both age dependency and estimation biases (Butler et al., 2021).” (p3) → This summary is not accurate as Butler and colleagues did not use the words "corrected" and "biases" in this context. All that authors say in that paper is that regressing out age from the brain age gap - which is referred to as the modified brain age gap (MBAG) - makes it so that the modified brain age gap is not dependent on age, which is true. This metric is meaningless, though, because it is the variance left over after regressing out age from residuals from a model that was predicting age. If it were not for the fact that regression on residuals is not equivalent to multiple regression (and out of sample estimates), MBAG would be a vector of zeros. Upon reading your Methods, I noticed that you are using a metric for Le et al. (2018) for your “Corrected Brain Age Gap”. If they cite the Butler et al. (2021) paper, I highly recommend sticking with the same notation, metrics and terminology throughout. That would greatly help with the interpretability of your paper, and cross-comparisons between the two.

Response Please see our response to Reviewer 3 Public Review #2.

Reviewer 3 Recommendations For The Authors #3:

“However, the improvement in predicting chronological age may not necessarily make Brain Age to be better at capturing Cognitionfluid. If, for instance, the age-prediction model had the perfect performance, Brian Age Gap would be exactly zero and would have no utility in capturing Cognitionfluid beyond chronological age.” (p3) → I largely agree with this statement. I would be really careful to distinguish between Brain Age and the Brain Age Gap here, as the former is a predicted value, and the latter is the residual times -1 (predicted age - age). Therefore, together they explain all of the variance in age. If you change the first sentence to refer to the Brain Age Gap, this statement makes more sense. The Brain Age Gap will never be exactly zero, though, even with perfect prediction on the training set, because subjects in the testing set are different from the subjects in the training set.

Response Please see our response to Reviewer 3 Public Review #3.

Reviewer 3 Recommendations For The Authors #4:

“Can we further improve our ability to capture the decline in cognitionfluid by using, not only Brain Age and chronological age, but also another biomarker, Brain Cognition?” → This question is fundamentally getting at whether a predicted value of cognition can predict cognition. Assuming the brain parameters can predict cognition decently, and the original cognitive measure that you were predicting is related to your measure of fluid cognition, the answer should be yes. This seems like an uninteresting question to me. Upon reading your Methods, it became clear that the cognitive variable in the model predicting cognition using brain features (to get predicted cognition, or as you refer to it, Brain Cognition) is the same as the measure of fluid cognition that you are trying to assess how well Brain Cognition can predict. Assuming the brain parameters can predict fluid cognition at all, of course Brain Cognition will predict fluid cognition. This is inevitable. You should never use predicted values of a variable to predict the same variable.

Response Please see our response to Reviewer 3 Public Review #4.

Reviewer 3 Recommendations For The Authors #5:

“We also examined if these better-performing age-prediction models improved the ability of Brain Age in explaining Cognitionfluid.” → Improved above and beyond what?

Response We referred to if better-performing age-prediction models improved the ability of Brain Age in explaining fluid cognition over and above lower-performing age-prediction models. We made changes to the Introduction to clarify this change.

Reviewer 3 Recommendations For The Authors #6:

Figure 1 b & c → It is a little difficult to read the text by the horizontal bars in your plots. Please make the text smaller so that there is more space between the words vertically, or even better, make the plots slightly bigger. Please also put the predicted values on the y-axis. This is standard practice for displaying regression results. To make more room, you can get rid of your rPearson or your R2 plot, considering the latter is simply the square of the former. If you want to make it clear that the association is positive between all of your variables, I would keep rPearson.

Response Thank you so much for the suggestions.

1) We now made sure that the text by the horizontal bars in Figure 1b and c is readable.

2) Note in prediction model/machine-learning literature, it is more common to plot observed/real values on the y-axis. Here is the logic of our practice: values in the x-axis are the predicted values based on the model, and we would like to see if the changes in the predicted values correspond to the changes in the observed/real value in the y-axis.

3) Regarding Pearson correlation vs R2, please note that we wrote ”for R2, we used the sum of squares definition (i.e., R2 = 1 – (sum of squares residuals/total sum of squares)) per a previous recommendation (Poldrack et al., 2020).” As such, R2 is NOT the square of the Pearson correlation. In fact, in Poldrack and colleages’s “Establishment of Best Practices for Evidence for Prediction” paper (2020), they discourage 1) the use of Pearson correlation by itself and 2) the use of the correlation coefficient square as R2 (as opposed to sum of squares definition):

“It is common in the literature to use the correlation between predicted and actual values as a measure of predictive performance; of the 64 studies in our literature review that performed prediction analyses on continuous outcomes, 30 reported such correlations as a measure of predictive performance. This reporting is problematic for several reasons. First, correlation is not sensitive to scaling of the data; thus, a high correlation can exist even when predicted values are discrepant from actual values. Second, correlation can sometimes be biased, particularly in the case of leave-one-out cross-validation. As demonstrated in Figure 4, the correlation between predicted and actual values can be strongly negative when no predictive information is present in the model. A further problem arises when the variance explained (R2) is incorrectly computed by squaring the correlation coefficient. Although this computation is appropriate when the model is obtained using the same data, it is not appropriate for out-of-sample testing23; instead, the amount of variance explained should be computed using the sum-of-squares formulation (as implemented in software packages such as scikit-learn).”

“A further problem arises when the variance explained (R2) is incorrectly computed by squaring the correlation coefficient. Although this computation is appropriate when the model is obtained using the same data, it is not appropriate for out-of-sample testing23; instead, the amount of variance explained should be computed using the sum-of-squares formulation (as implemented in software packages such as scikit-learn).”

Accordingly, we decided to keep both R2 and Pearson correlation (along with MAE) in our Figure 1.

Reviewer 3 Recommendations For The Authors #7:

Figure 2 “We calculated feature importance by, first, standardizing Elastic Net weights across brain features of each set of features from each test fold.” → What do you mean by “standardize” here? Rescale to be mean 0, variance 1? If so, this seems like a misleading transformation, because it gives the impression that the relationships are negative, when they are not necessarily. Also, why did you choose to use elastic net weights in any form as measures of effect size (or importance)? The raw values are inherently penalized, which means they are under-estimates of the true effect size. It would be more meaningful (and less biased) to plot the raw correlations.

Response For the first question regarding standardisation, we addressed this issue in our response to Reviewer 1 Recommendations For The Authors #3. Briefly, we agreed with Reviewer 3 that standardisation (with mean = 0, SD = 1) might make it difficult to interpret the directionality of the coefficients. For visualising feature importance in the revised manuscript, we refitted the Elastic Net model to the full dataset without splitting them into five folds and visualised the coefficients on brain images (see below).

For the second question regarding why using Elastic Net coefficients as feature importance (as opposed to correlations), we need to mention the goal of feature importance: to understand how the model makes a prediction based on different brain features (Molnar, 2019). Correlations between a target and each brain feature do not achieve this. Instead, they will show univariate/marginal relationships between a target and a brain feature. What we want to visualise is how the model made a prediction, which in the case of Elastic Net, the prediction is based on the sum of the features’ coefficients. In other words, the multivariate models (including Elastic Net) focus on marginal relationships that take into account all brain features within each set of features.

Elastic Net coefficients can be considered as feature importance, such that more positive Elastic Net coefficients lead to more positive predicted values and, similarly, more negative Elastic Net coefficients lead to more negative predicted values (Molnar, 2019; Pat, Wang, Bartonicek, et al., 2022). While the magnitude of Elastic Net coefficients is regularised (thus making it difficult for us to interpret the magnitude itself directly), we could still indicate that a brain feature with a higher magnitude weights relatively stronger in making a prediction. Another benefit of Elastic Net as a penalised regression is that the coefficients are less susceptible to collinearity among features as they have already been regularised (Dormann et al., 2013; Pat, Wang, Bartonicek, et al., 2022).

Reviewer 3 Recommendations For The Authors #8:

Figure 3 → Again, what exactly do you mean by “standardised” here?

Response It means mean subtraction followed by the division by an SD. Though we no longer applies standardisation for feature importance. See our response to Reviewer 1 Recommendations For The Authors #3 and Reviewer 3 Recommendations For The Authors #7.

Reviewer 3 Recommendations For The Authors #9:

“However, Brain Age Gap created from the lower-performing age-prediction models explained a higher amount of variation in Cognitionfluid. For instance, the top performing age-prediction model, “Stacked: All excluding Task Contrast”, generated Brain Age and Corrected Brain Age that explained the highest amount of variation in Cognitionfluid, but, at the same time, produced Brian Age Gap that explained the least amount of variation in Cognitionfluid.” (p7) → Yes, but you did not need to run any models to show this, considering it is an inevitable consequence of the following relationship between predicted values and residuals (or residuals times -1): 𝑦 = (𝑦 − 𝑦% ) + 𝑦% . Let’s say that age explains 60% of the variance in fluid cognition, and predicted age ( 𝑦% ) explains 40% of the variance in fluid cognition. Then the brain age gap (−(𝑦 − 𝑦% )) should explain 20% of the variance in fluid cognition. If by “Corrected Brain Age” you mean the modified predicted age from the Butler paper, the “Corrected Brain Age” result is inevitable because the modified predicted age is essentially just age with a tiny bit of noise added to it. From Figure 4, though, this does not seem to be the case, because the lower left quadrant in panel a should be flat and high (about as high as the predictive value of age for fluid cognition). So how are you calculating “Corrected Brain Age”? It looks like you might be regressing age out of Brain Age, though from your description the Methods (How exactly do you use the slope and intercept? You need equation of you are going to stick with this terminology), it is not totally clear. I highly recommend using terminology and metrics from the Butler et al. (2021) paper throughout to reduce confusion.

Response Please see our response to Reviewer 3 Public Review #5

Reviewer 3 Recommendations For The Authors #10:

“On the contrary, an amount of variation in Cognitionfluid explained by Corrected Brain Age Gap was relatively small (maximum R2 = .041) across age-prediction models and did not relate to the predictive performance of the age-prediction models.” (p7) → If by “Corrected Brain Age Gap” you mean MBAG from The Butler paper, yes, this is also inevitable, considering MBAG would be a vector of zeros if it were not for regression on residuals (and out of sample estimates), as I mentioned earlier. Also, it is not clear why you used “on the contrary” as a transition here.

Response Please see our response to Reviewer 3 Public Review #2 for the ‘MBAG’ term. Briefly, we didn’t use Butler and colleagues' (2021) MBAG, but rather we used the method described in de Lange and Cole’s (2020), which was called RBAG by Butler and colleagues.

de Lange and Cole’s (2020) method, was commonly implemented elsewhere (Cole et al., 2020; Cumplido-Mayoral et al., 2023; Denissen et al., 2022). Accordingly, researchers who use Brain Age do not usually view this method as capturing a meaningless biomarker. Yet, the small effects of the Corrected Brain Age Gap in explaining fluid cognition of aging individuals found here are consistent with studies in older adults (Cole, 2020) and younger populations (Butler et al., 2021; Jirsaraie, Kaufmann, et al., 2023) (see our response to Reviewer 2 Recommendations For The Authors #1).

“On the contrary” refers to the fact that the other three Brain Age indices (i.e., those that did not account for the relationship between Brain Age and chronological age) showed a much higher amount of variation in fluid cognition explained. As mentioned above (our response to Reviewer 2 Public Review #7), our argument resonates Butler and colleagues’ (2021) suggestion (p. 4097): “As such, it is critical that readers of past literature note whether or not age was controlled for when testing for effects on the BAG, as this has not always been common practice (e.g., Beheshti et al., 2018; Cole, Underwood, et al., 2017; Franke et al., 2015; Gaser et al., 2013; Liem et al., 2017; Nenadi c et al., 2017; Steffener et al., 2016)”.

Reviewer 3 Recommendations For The Authors #11:

“As before, the unique effects of Brain Age indices were all relatively small across the four Brain Age indices and across different prediction models.” (p10) → Yes, again, this is inevitable considering how they are calculated. You can show these analyses to demonstrate your results in data, if you want, but ignoring the inevitability given how these variables are calculated is misleading.

Response Accounting for the relationship between Brain Age and chronological age when examining the utility of Brain Age is not misleading. Similar to previous recommendations (Butler et al., 2021; Le et al., 2018), we believe that not doing so is misleading. That is, without accounting for the relationship between Brain Age and chronological age, Brain Age will likely explain the same variation of the phenotype of interest as chronological age. Please see our response to Reviewer 3 Recommendations For The Authors #18 below.

Reviewer 3 Recommendations For The Authors #12:

“On the contrary, the unique effects of Brain Cognition appeared much larger.” (p10) → This is not a fair comparison if you don’t look at the unique effects above and beyond the cognitive variable you predicted (fluid cognition) in your Brain Cognition model. When you do this, you will see that Brain Cognition is useless when you include fluid cognition in the model, just as Brain Age would be in predicting age when you include age in the model. This highlights the fact that using predicted values of a metric to predict that metric is a pointless path to take, and that using a predicted value to predict anything is worse than using the value itself.

Response Please see our response to Reviewer 3 Public Review #6.

Reviewer 3 Recommendations For The Authors #13:

“First, how much does Brain Age add to what is already captured by chronological age? The short answer is very little.” (p12) → This is a really important point, but your paper requires an in-depth discussion of the inevitability of this result, which I have discussed previously in this review.

Response Please see our response to Reviewer 3 Public Review #7.

Reviewer 3 Recommendations For The Authors #14:

“Second, do better-performing age-prediction models improve the ability of Brain Age to capture Cognitionfluid? Unfortunately, the answer is no.” (p12) → You need to be clear that you are talking about above and beyond age here.

Response Thank you so much for your suggestion. We now made the change to this sentence accordingly.

Discussion

“Second, do better-performing age-prediction models improve the utility of Brain Age to capture fluid cognition above and beyond chronological age? The answer is also no.”

Reviewer 3 Recommendations For The Authors #15:

“Third, do we have a solution that can improve our ability to capture Cognitionfluid from brain MRI? The answer is, fortunately, yes. Using Brain Cognition as a biomarker, along with chronological age, seemed to capture a higher amount of variation in Cognitionfluid than only using Brain Age.” (p12) → Again, try controlling for the cognitive measure you predicted in your Brain Cognition model. This will show that Brain Cognition is not useful above and beyond cognition, highlighting the fact that it is not a useful endeavor to be using predicted values.

Response Please see our response to Reviewer 3 Public Review #8.

Reviewer 3 Recommendations For The Authors #16:

“Accordingly, a race to improve the performance of age-prediction models (Baecker et al., 2021) does not necessarily enhance the utility of Brain Age indices as a biomarker for Cognitionfluid. This calls for a new paradigm. Future research should aim to build prediction models for Brian Age indices that are not necessarily good at predicting age, but at capturing phenotypes of interest, such as Cognitionfluid and beyond.” (p13) → I whole-heartedly agree with the first two sentences, and strongly disagree with the last. Certainly your results, and the underlying reason as to why you found these results, calls for a new paradigm (or, one might argue, a pre-brain age paradigm). They do not, however, suggest that we should keep going down the Brain Age path. In fact, I think it should be abandoned all together. While it is difficult to prove that there is no transformation of Brain Age or the Brain Age Gap that will be useful, I am nearly sure this is true from the research I have done. Therefore, if you would like to suggest that the field should continue down this path, you need to present a very good case to support this view.

Response Please see our response to Reviewer 3 Public Review #9.

Reviewer 3 Recommendations For The Authors #17:

“Perhaps this is because the estimation of the influences of chronological age was done in the training set.” (p13) → I believe this is the case, and it is testable. Try re-running your analyses where parameters are estimated and performance is evaluated on the same data.

Response Yes, we agreed with this. Based on the equations we used, this is inevitable.

Reviewer 3 Recommendations For The Authors #18:

“Similar to a previous recommendation (Butler et al., 2021), we suggest focusing on Corrected Brain Age Gap.” (p13) → To be clear, the authors did not use the term “Corrected” because it is very misleading. The authors also did not suggest that we proceed with any brain age metric; rather they mentioned that the modified brain age gap is independent of age. Note the following passage: “Further, the interpretability of the modified brain age gap (MBAG) itself is limited by the fact that it is a prediction error from a regression to remove the effects of age from a residual obtained through a regression to predict age. By virtue of these limitations, we suggest that the modified version may not provide useful information about precocity or delay in brain development. In light of this, as well as the complexities associated with interpretations of the BAG and its dependence on age, we suggest that further methodological and theoretical work is warranted.” I recognize that that this statement is hedged, as is often required in the publication process, but I am all but certain that MBAG/BAG/modified predicted age are useless constructs. Therefore, if you are going to suggest that people continue to use them, opposed to suggesting that further methodological or theoretical work is warranted, you need to make a strong case, which you did not try to make here. If anything, your results support abandoning the age- prediction endeavor altogether.

Response Please see our response to Reviewer 3 Public Review #2 for the term. Briefly, we didn’t use Butler and colleagues’ (2021) MBAG, but rather RBAG. This index was originally described in de Lange and Cole’s (2020), and has now been implemented elsewhere (Cole et al., 2020; Cumplido-Mayoral et al., 2023; Denissen et al., 2022).

We do not intend to encourage people to abandon the Brain Age endeavour altogether. However, we made main three suggestions for future research on Brain Age to ensure its utility. First, they should account for the relationship between Brain Age and chronological age either using Corrected Brain Age Gap (or other similar adjustments) or, better, examining the unique effects of Brain Age indices after controlling for chronological age through commonality analyses (see below). This is similar to the suggestion made by Le and colleagues (2018) and later rephased by Butler and colleagues (2021). More specifically, Le and colleagues (2018) mentioned (p. 10): “Based on our observations in both real and simulated data, we recommend that the relationship between chronological age and BrainAGE should be accounted for. The two methods proposed in this study are either: (1) regress age on BrainAGE, producing BrainAGER, which is centered on 0 regardless of a participant's actual age or (2) include age as a regressor when doing follow-up analyses.”

Second, we suggested that researchers should not select age-prediction models based solely on age-prediction performance (see our response to Reviewer 1 Recommendations For The Authors #1).

Third, we suggested that researchers should test how much Brain Age miss the variation in the brain MRI that could explain fluid cognition or other phenotypes of interest (see our response to Reviewer 2 Public Review #4).

Discussion

“What does it mean then for researchers/clinicians who would like to use Brain Age as a biomarker? First, they have to be aware of the overlap in variation between Brain Age and chronological age and should focus on the contribution of Brain Age over and above chronological age. Using Brain Age Gap will not fix this. Butler and colleagues (2021) recently highlighted this point, “These results indicate that the association between cognition and the BAG are driven by the association between age and cognitive performance. As such, it is critical that readers of past literature note whether or not age was controlled for when testing for effects on the BAG, as this has not always been common practice (p. 4097).” Similar to previous recommendations (Butler et al., 2021; Le et al., 2018), we suggest future work should account for the relationship between Brain Age and chronological age, either using Corrected Brain Age Gap (or other similar adjustments) or, better, examining unique effects of Brain Age indices after controlling for chronological age through commonality analyses. Note we prefer using unique effects over beta estimates from multiple regressions, given that unique effects do not change as a function of collinearity among regressors (Ray-Mukherjee et al., 2014). In our case, Brain Age indices had the same unique effects regardless of the level of common effects they had with chronological age (e.g., Brain Age vs. Corrected Brain Age Gap from stacked models). In the case of fluid cognition, the unique effects might be too small to be clinically meaningful as shown here and previously (Butler et al., 2021; Cole, 2020; Jirsaraie, Kaufmann, et al., 2023).”

Reviewer 3 Recommendations For The Authors #19:

“To compute Brain Age and Brain Cognition, we ran two separate prediction models. These prediction models either had chronological age or Cognitionfluid as the target.” (p16) → You should make it clear in the main text of your paper that the cognition variable in your Brain Cognition models is the same as what you refer to as Cognitionfluid. Some of your analyses would have been much more reasonable if you had two different measures of cognition.

Response Thank you so much for the suggestion. We believe, given the re-conceptualisation of Brain Cognition as the main text

Introduction

“certain variation in the brain MRI is related to fluid cognition, but to what extent does Brain Age not capture this variation? To estimate the variation in the brain MRI that is related to fluid cognition, we could build prediction models that directly predict fluid cognition (i.e., as opposed to chronological age) from brain MRI data.”

Reviewer 3 Recommendations For The Authors #20:

“We controlled for the potential influences of biological sex on the brain features by first residualizing biological sex from brain features in the training set.” (p16) → Why? Your question is about prediction, not causal inference.

Response While the question is about prediction, we still would like to, as much as possible, be confident about what kind of information we drew from. Here we focused on brain data and controlled for other variables that might not be neuronal. For instance, we controlled for movement and physiological noise using ICA-FIX (Glasser et al., 2016). Following conventional practices in brain-based predictive modelling, we also treated biological sex as another sort of noise (Vieira et al., 2022). The difference between movement/physiological noise and biological sex is that the former varies across TRs, and the latter varies across individuals. Thus we controlled for movement and physiological noise within each participant and controlled for biological sex within a group of participants who belonged to the same training set.

Reviewer 3 Recommendations For The Authors #20:

“Lastly, we computer Corrected Brain Age Gap by subtracting the chronological age from the Corrected Brain Age (Butler et al., 2021; Le et al., 2018).” (p17) → The modified brain age gap in that paper is the residuals from regressing BAG on age (see equation 6). I highly recommend using that terminology and notation throughout to provide consistency and interpretability across papers.

Response Please see our response to Reviewer 3 Public Review #2 for the term.

Reviewer 3 Recommendations For The Authors #21: Equations (pgs 17-19) → Please use statistical notation instead of pseudo-R code.

Response We rewrote all of the equations using statistical notations.

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Author Response

Reviewer #1 (Public Review):

Summary:

In the manuscript titled "Disease modeling and pharmacological rescue of autosomal dominant Retinitis Pigmentosa associated with RHO copy number variation" the authors describe the use of patient iPSC-derived retinal organoids to evaluate the pathobiology of a RHO-CNV in a family with dominant retinitis pigmentosa (RP). They find significantly increased expression of rhodopsin, especially within the photoreceptor cell body, and defects in photoreceptor cell outer segment formation/maturation. In addition, they demonstrate how an inhibitor of NR2E3 (a rod transcription factor required for inducing rhodopsin expression), can be used to rescue the disease phenotype.

Strengths:

The manuscript is very well written, the illustrations and data presented are compelling, and the authors' interpretation/discussion of their findings is logical.

Weaknesses:

A weakness, which the authors have addressed in the discussion section, is the lack of an isogenic control, which would allow for direct analysis of the RHO-CNV in the absence of the other genetic sequence contained within the duplicated region. As the authors suggest, CRISPR correction of a large CNV in the absence of inducing unwanted on-target editing events in patient iPSCs is often very challenging. Given that they have used a no-disease iPSC line obtained from a family member, controlled for organoid differentiation kinetics/maturation state, and that no other complete disease-causing gene is contained within the duplicated region, it is unlikely that the addition of an isogenic control would yield significantly different results.

Aims and conclusions:

This reviewer is of the opinion that the authors have achieved their aims and that their results support their conclusions.

Discussion:

The authors have provided adequate discussion on the utility of the methods and data as well as the impact of their work on the field.

We thank the reviewer for their insightful, and encouraging review of our work that has taken several years to get to current stage.

Reviewer #2 (Public Review):

Summary:

The manuscript by Kandoi et al. describes a new 3D retinal organoid model of a mono-allelic copy number variant of the rhodopsin gene that was previously shown to induce autosomal dominant retinitis pigmentosa via a dominant negative mechanism in patients. With advancements in the low-cost genomics application to detect copy number variations, this is a timely article that highlights a potential disease mechanism that goes beyond the retina field. The evidence is relatively strong that the rod photoreceptor phenotype observed in an adult patient with RP in vivo is similar to that phenotype observed in human stem cell-derived retinal organoids. Increases in RHO expression detected by qPCR, RNA-seq, and IHC support this phenotype. Importantly, the amelioration of photoreceptor rhodopsin mislocalization and related defects using the small molecule drug photoregulin demonstrates an important potential clinical application.

Overall, the authors succeeded in providing solid evidence that copy number variation via a genomic RHO duplication leads to abnormalities in rod photoreceptors that can be partially blocked by photoregulin. However, there are several points that should be addressed that will enhance this paper.

Strengths:

• The use of patient-derived organoids from patients that have visual defects is a major strength of this work and adds relevance to the disease phenotype.

• The rod phenotype assessed by qPCR, RNA-seq, and IHC supports a phenotype that shares similarities with the patient.

• The use of a small molecule drug that selectively targets rod photoreceptors, as opposed to cones, is a noteworthy strength.

We thank the reviewers for highlighting the key strengths of the paper.

Weaknesses:

1) The chromosomal segment that was duplicated had 3 copies of RHO in addition to three copies of each of the flanking genes (IFT122, HIF100, PLXND1). Discussion of the involvement of these genes would be helpful. Would duplication of any of these genes alone cause or contribute to adRP? As an example, a missense mutation in IFT122 was previously implicated in photoreceptor loss (PMID: 33606121 PMCID: PMC8519925).

Thank you for your comment. It is an interesting question on the contribution of the other duplicated genes. Of these, IFT122 is particularly interesting as pointed out. We did a thorough survey through literature and our genetic testing partner’s database, BluePrint Genetics. We did not find any human retinal degeneration cases with variants in IFT122. IFT122 has been shown to cause recessive phenotype in dogs and in complete knockout zebrafish model but dominant or overexpression has not been shown to have a phenotype. Interestingly, recessive biallelic IFT122 mutation can cause Cranioectodermal Dysplasia (Sensenbrenner syndrome, PMID: 24689072) and none of these patient exhibited retinal dystrophy. HIF100 is an epigenetic modifier gene while PLXND1 is expressed in endothelial cells. We will include a discussion on this in the revised manuscript.

2) Related to #1, have the authors considered inserting extra copies of RHO (and/or the flanking genes) of these at a genomic safe harbor site? Although not required, this would allow one to study cells with isogenic-matched genetic backgrounds and would partially address the technical challenge of repairing a 188kb duplication, which as the authors note would be difficult to do. Demonstrating that excess copy numbers in different genetic backgrounds would be a huge contribution to the field. At a minimum, a discussion of the role of the nearby genes should be included.

Thank you for your suggestion. We plan to test the relative role of 1-3 extra copies of RHO driven off a NRL promoter in order to drive it only in rods in our future mechanistic analysis studies. We will include a discussion on the potential role of the other genes in the revised manuscript.

3) In the patient, the central foveal region was spared suggesting that cones were normal. Was there a similar assessment that cones are unaffected in retinal organoids?

We will include this data in our revised manuscript but overall did not see a cone defect in RHO CNV organoids. Additionally, although it is true that the central foveal region was relatively spared in this patient, the cones are definitely not normal. The macular cones that remain have been damaged by chronic edema, and photoreceptor and RPE atrophy has progressed into the macula, sparing only the foveal cones.

4) Pathway analysis indicated that glycosylation was perturbed and this was proposed as an explanation as to why rhodopsin was mislocalized. Have the authors verified that there is an actual decrease in glycosylation?

These studies are ongoing. We are currently looking into the details of cellular pathophysiology focusing on RHO trafficking in RHO-CNV including role of glycosylation and other post-translational modifications defects.

5) Line 182: by what criteria are the authors able to state that " there were no clear visible anatomical changes in apical-basal retinal cell type distribution during the early differentiation timeframe (data not shown)." Was this based on histological staining with antibodies, nuclear counter-staining, or some other evaluation?

This was based on both IHC for various cell type markers and nuclear (DAPI) staining.

6) Figure 2C - the appearance of the inner segments in RC and RM looks very different from one another. Have the authors ruled out the possibility that the RC organoid cell isn't a cone? In addition, the RM structure has what appears to be a well-defined OLM which would suggest well-formed Muller glia. Do these structures also exist in RC organoids? Typically the OLM does form in older organoids. In addition, was this representative in numerous EM preparations?

For clarification on EM data, we will include additional images in the revision as supplementary data. We have not carefully compared OLM between the patient and control organoids but do observe them in both conditions in the older organoids. The EM preparations were made from multiple organoids from two different batches with consistent results.

7) What criteria were used to assess cell loss? Has any TUNEL labeling been performed to confirm cell loss? From the existing data, it seems that rod outer segments appear to be affected in organoids. However, it's not clear if the photoreceptors themselves actually die in this model.

TUNEL was used to assess cell loss and it was not significantly different between the control and patient organoids at the timepoints examined. We did not expect a change as the disease in the patient developed over decades.

8) Figure 5B. The RHO staining in the vehicle-treated sample is perturbed relative to the PR3 treatments as indicated in the text. In the vehicle-treated sample, the number of DAPI-positive cells that are completely negative proximal to the inner segments suggests that there might be non-rod cells there. Have the authors confirmed whether these are cones? Labels would be helpful in the left vehicle panel as the morphology looks very different than the treated samples.

Thank you very much for the various suggestions and these will be included in the revised manuscript version. A number of the cells in the negative regions are OTX2+/NRL- and likely to be cones (Figure 4 A and B). Unfortunately, we do not have a very good cone nuclear marker as RXRγ does not consistently stain mature cones.

9) It is interesting that in addition to increases in RHO, and photo-transduction, there are also increases in PTPRT which is related to synaptic adhesion. Is there evidence of ectopic neurites that result from PTPRT over-expression?

You are absolutely correct that PTPRT data is very interesting. PTPRT requires similar PTMs like RHO in photoreceptors for its synaptic localization. We did not specifically look at ectopic neurites and test that in the revision. It will interesting to follow-up on its expression pattern to see if it gets processed or localized normally if we can find a working antibody. It is also possible that the gene-expression increase due to feedback upregulation secondary to improper protein processing.

Reviewer #3 (Public Review):

This manuscript reports a novel pedigree with four intact copies of RHO on a single chromosome which appears to lead to overexpression of rhodopsin and a corresponding autosomal dominant form of RP. The authors generate retinal organoids from patient- and control-derived cells, characterize the phenotypes of the organoids, and then attempt to 'treat' aberrant rhodopsin expression/mislocalization in the patient organoids using a small molecule called photoregulin 3 (PR3). While this novel genetic mechanism for adRP is interesting, the organoid work is not compelling. There are multiple problems related to the technical approaches, the presentation of the results, and the interpretations of the data. I will present my concerns roughly in the order in which they appear in the manuscript.

Major concerns:

(1) Individual human retinal organoids in culture can show a wide range of differentiation phenotypes with respect to the expression of specific markers, percentages of given cell types, etc. For this reason, it can be very difficult to make rigorous, quantitative comparisons between 'wild-type' and 'mutant' organoids. Despite this difficulty, the author of the present manuscript frequently presents results in an impressionistic manner without quantitation. Furthermore, there is no indication that the investigator who performed the phenotypic analyses was blind with respect to the genotype. In my opinion, such blinding is essential for the analysis of phenotypes in retinal organoids. To give an example, in lines 193-194 the authors write "we observed that while the patient organoids developing connecting cilium and the inner segments similar to control organoids, they failed to extend outer segments". Outer segments almost never form normally in human retinal organoids, even when derived from 'wild-type' cells. Thus, I consider it wholly inadequate to simply state that outer segment formation 'failed' without a rigorous, quantitative, and blinded comparison of patient and control organoids.

We agree it is challenging to generate outer segments in retinal organoids but we are not the first to show this. This has been demonstrated by multiple independent labs (Mayerl et al (PMID: 36206764), Wahlin et al (PMID: 28396597), West at al (PMID: 35334217) including ours (Chirco et al (PMID: 34653402). To clarify, we did not observe any OS like tissue in the patient organoids across multiple EM preps of a number of organoids from two independent 300+ day experiments which matched the phase microscopy data presented in Fig2B.

(2) The presentation of qPCR results in Figure 3A is very confusing. First, the authors normalize expression to that of CRX, but they don't really explain why. In lines 210-211, they write "CRX, a ubiquitously expressing photoreceptor gene maintained from development to adulthood." Several parts of this sentence are misleading or incomplete. First, CRX is not 'ubiquitously expressed' (which usually means 'in all cell types') nor is it photoreceptor-specific: CRX is expressed in rods, cones, and bipolar cells. Furthermore, CRX expression levels are not constant in photoreceptors throughout development/adulthood. So, for these reasons alone, CRX is a poor choice for the normalization of photoreceptor gene expression.

As you are aware, all housekeeping genes have shortcomings when used for normalizing PCR data. We went with CRX as within the timepoints chosen, it is not expected to change much and thus represent a good equalizer for relative photoreceptor numbers between the organoids and conditions. While we agree that CRX is weakly expressed in bipolar cells (Yamamoto et al 2020), it is not expected to bias the data too much as we have not seen nor have other reported a huge relative difference in bipolar cell number in organoids. We also confirm this by showing equivalent expression of OTX2, RCVRN and NRL between all conditions.

Second, the authors' interpretation of the qPCR results (lines 216-218) is very confusing. The authors appear to be saying that there is a statistically significant increase in RHO levels between D120 and D300. However, the same change is observed in both control and patient organoids and is not unexpected, since the organoids are more mature at D300. The key comparison is between control and patient organoids at D300. At this time point, there appears to be no difference between control and patient. The authors don't even point this out in the main text.

Thank you for the comment and we apologize if this confused you. However, as can been seen in the graph in Figure 3A, we do compare expression of genes including RHO between control and patient organoids at two different time points. There are four conditions: D120-RC, D120-RM, D300-RC and D300-RM with individual data points and error bars for each condition. There is a statistically significant increase at both time points upon comparing the control and patient organoids for RHO. We compared RHO expression between patient organoids at the two time points and it was not statistically different.

Third, the variability in the number of photoreceptor cells in individual organoids makes a whole-organoid comparison by qPCR fraught with difficulty. It seems to me that what is needed here is a comparison of RHO transcript levels in isolated rod photoreceptors.

We agree that this makes it challenging. This was the exact reasoning for using CRX for normalization since it is predominantly present in photoreceptors. This was validated by the data showing no difference in expression of photoreceptor markers OTX2, RCVRN or NRL between the organoids.

(3) I cannot understand what the authors are comparing in the bulk RNA-seq analysis presented in the paragraph starting with line 222 and in the paragraph starting with line 306. They write "we performed bulk-RNA sequencing on 300-days-old retinal organoids (n=3 independent biological replicates). Patient retinal organoids demonstrated upregulated transcriptomic levels of RHO... comparable to the qRT-PCR data." From the wording, it suggests that they are comparing bulk RNA-seq of patients and control organoids at D300. However, this is not stated anywhere in the main text, the figure legend, or the Methods. Yet, the subsequent line "comparable to the qRT-PCR data" makes no sense, because the qPCR comparison was between patient samples at two different time points, D120 and D300, not between patient and control. Thus, the reader is left with no clear idea of what is even being compared by RNA-seq analysis.

We apologize if the conditions were not obvious and will clarify this in the revised version. The conditions compared are control and patient organoids at D300. Regarding comparison to RT-PCR, as stated above, the comparison shown is between patient and control organoids at two different timepoints.

Remarkably, the exact same lack of clarity as to what is being compared is found in the second RNA-seq analysis presented in the paragraph starting with line 306. Here the authors write "We further carried out bulk RNA-sequencing analysis to comprehensively characterize three different groups of organoids, 0.25 μM PR3-treated and vehicle-treated patient organoids and control (RC) organoids from three independent differentiation experiments. Consistent with the qRT-PCR gene expression analysis, the results showed a significant downregulation in RHO and other rod phototransduction genes." Here, the authors make it clear that they have performed RNA-seq on three types of samples: PR3-treated patient organoids, vehicle-treated patient organoids, and control organoids (presumably not treated). Yet, in the next sentence, they state "the results showed a significant downregulation in RHO", but they don't state what two of the three conditions are being compared! Although I can assume that the comparison presented in Fig. 6A is between patient vehicle-treated and PR3-treated organoids, this is nowhere explicitly stated in the manuscript.

Thank you for the comment and we will explicitly state various comparisons in the revised version.

(4) There are multiple flaws in the analysis and interpretation of the PR3 treatment results. The authors wrote (lines 289-2945) "We treated long-term cultured 300-days-old, RHO-CNV patient retinal organoids with varying concentrations of PR3 (0.1, 0.25 and 0.5 μM) for one week and assessed the effects on RHO mRNA expression and protein localization. Immunofluorescence staining of PR3-treated organoids displayed a partial rescue of RHO localization with optimal trafficking observed in the 0.25 μM PR3-treated organoids (Figure 5B). None of the organoids showed any evidence of toxicity post-treatment."

There are multiple problems here. First, the results are impressionistic and not quantitative. Second, it's not clear that the investigator was blinded with respect to the treatment condition. Third, in the sections presented, the organoids look much more disorganized in the PR3-treated conditions than in the control. In particular, the ONL looks much more poorly formed. Overall, I'd say the organoids looked considerably worse in the 0.25 and 0.5 microM conditions than in the control, but I don't know whether or not the images are representative. Without rigorously quantitative and blinded analysis, it is impossible to draw solid conclusions here. Lastly, the authors state that "none of the organoids showed any evidence of toxicity post-treatment," but do not explain what criteria were used to determine that there was no toxicity.

Thank you for your critical insight. The RHO localization data is qualitative as it is very difficult to accurately quantify rhodopsin trafficking within the cell in the organoid. Thus, for quantitative comparison, we have provided expression level changes. Regarding toxicity, we analyzed the organoids by morphology and TUNEL and did not observe significant difference between the conditions. This closely mimics mouse data on PR3 which suppressed rod function in mice following IP injection without any obvious toxicity.

(5) qPCR-based quantitation of rod gene expression changes in response to PR3 treatment is not well-designed. In lines 294-297 the authors wrote "PR3 drove a significant downregulation of RHO in a dose-dependent manner. Following qRT-PCR analysis, we observed a 2-to-5 log2FC decrease in RHO expression, along with smaller decreases in other rod-specific genes including NR2E3, GNAT1 and PDE6B." I assume these analyses were performed on cDNA derived from whole organoids. There are two problems with this analysis/interpretation. First, a decrease in rod gene expression can be caused by a decrease in the number of rods in the treated organoids (e.g., by cell death) or by a decrease in the expression of rod genes within individual rods. The authors do not distinguish between these two possibilities. Second, as stated above, the percentage of cells that are rods in a given organoid can vary from organoid to organoid. So, to determine whether there is downregulation of rod gene expression, one should ideally perform the qPCR analysis on purified rods.

The reviewer is correct in pointing the potential reasons for reduction in RHO levels following PR3 treatment. Thus, we have provided NRL expression levels in the graph to show that this key rod-specific gene does not change suggesting equivalent number of rod photoreceptor cells. The suggestion of using purified rods is not practical here, as we do not have any way to sort human rods due to the lack of a rod-specific cell surface marker.

(6) In Figure 4B 'RM' panels, the authors show RHO staining around the somata of 'rods' but the inset images suggest that several of these cells lack both NRL and OTX2 staining in their nuclei. All rods should be positive for NRL. Conversely, the same image shows a layer of cells scleral to the cells with putative RHO somal staining which do not show somal staining, and yet they do appear to be positive for NRL and OTX2. What is going on here? The authors need to provide interpretations for these findings.

Since RHO is a cytoplasmic marker and photoreceptor are tightly packed, it is difficult to make a 1:1 comparison to NRL/OTX2 nuclear marker to RHO. Additionally, as the RHO+ cytoplasm moves towards scleral surface, it is expected to pass adjacent to other nuclei. Few of the rods do still have normal Rhodopsin trafficking and it is likely these will not have somal RHO similar to control conditions. We do rarely observe these cells as highlighted by the occasional RHO in IS/OS of RM organoids in the figure. We do agree that the NRL staining in the figure 4B (>D250) is not extremely crisp and we will include an updated figure in the revised version.

Author Response

Reviewer #1 (Public Review):

Summary: This study presents fundamental new insights into vesicular monoamine transport and the binding pose of the clinical drug tetrabenazine (TBZ) to the mammalian VMAT2 transporter. Specifically, this study reports the first structure for the mammalian VMAT (SLC18) family of vesicular monoamine transporters. It provides insights into the mechanism by which this inhibitor traps VMAT2 into a 'dead-end' conformation. The structure also provides some evidence for a novel gating mechanism within VMAT2, which may have wider implications for understanding the mechanism of transport in the wider SLC18 family.

Strengths: The structure is high quality, and the method used to determine the structure via fusing mVenus and the anti-GFP nanobody to the amino and carboxyl termini is novel. The binding and transport data are convincing, although limited. The binding position of TBZ is of high value, given its role in treating Huntington's chorea and for being a 'dead-end' inhibitor for VMAT2.

Weaknesses: The lack of additional mutational data and/or analyses on the impact of pH on ligand binding reduces the insights from these experiments. This reduces the strength of the conclusions that can be drawn about the mechanism of binding and transport or the novelty of the gating mechanism discussed above.

We greatly appreciate this summary and thank reviewer #1 for their comments and suggested experiments which we believe will further strengthen this work. We agree with these comments and plan to include more mutagenesis data in a revised manuscript in order to address this point and expand further on the mechanistic details of transport.

Reviewer #2 (Public Review):

Overview:

As a report of the first structure of VMAT2, indeed the first structure of any vesicular monoamine transporter, this manuscript represents an important milestone in the field of neurotransmitter transport. VMAT2 belongs to a large family (the major facilitator superfamily, MFS) containing transporters from all living species. There is a wealth of information relating to the way that MFS transporters bind substrates, undergo conformational changes to transport them across the membrane, and couple these events to the transmembrane movement of ions. VMAT2 couples the movement of protons out of synaptic vesicles to the vesicular uptake of biogenic amines (serotonin, dopamine, and norepinephrine) from the cytoplasm. The new structure presented in this manuscript can be expected to contribute to an understanding of this proton/amine antiport process.

The structure contains a molecule of the inhibitor TBZ bound in a central cavity, with no access to either luminal or cytoplasmic compartments. The authors carefully analyze which residues interact with bound TBZ and measure TBZ binding to VMAT2 mutated at some of those residues. These measurements allow well-reasoned conclusions about the differences in inhibitor selectivity between VMAT1 and VMAT2 and differences in affinity between TBZ derivatives.

The structure also reveals polar networks within the protein and hydrophobic residues in positions that may allow them to open and close pathways between the central binding site and the cytoplasm or the vesicle lumen. The authors propose the involvement of these networks and hydrophobic residues in the coupling of transport to proton translocation and conformational changes. However, these proposals are quite speculative in the absence of supporting structures and experimentation that would test specific mechanistic details.

Thank you for these comments and summary describing this work. We agree that the involvement of polar networks has not been experimentally tested; these are proposed as a possible mechanism, but we have not made mechanistic conclusions on how protons are translocated and coupled to transport. We believe we have made it clear in the manuscript when describing the polar networks that the corresponding discussion is largely descriptive and speculative and will further stress that in a future revision. We would like to point out however, that many of the polar and charged residues which make up these networks have been studied and that there is a wealth of biochemical and functional experiments in the literature which implicate these residues in this process. Yet, we agree that establishing the precise mechanistic details will require additional structures and likely also extensive computational experiments. We have cited these papers that have characterized these polar residues extensively throughout the text (30-32,37,49,55).

We would like to submit that we have not proposed that the hydrophobic gates are involved in proton translocation. Gating residues, by definition, block access to the binding site (29,30,48); and since our structure is occluded, we directly observe the residues which participate in both gates. We have also performed extensive mutagenesis studies of many of these hydrophobic gating residues and our binding data are consistent with this conclusion. Transport experiments with mutations at these gates might be helpful toward gaining a deeper understanding of transport mechanism but given the current structural data it is conceivable that these residues play a role in gating neurotransmitter.

Critique:

Although the structure presented in this MS is clearly important, I feel that the authors have overstated several of the conclusions that can be drawn from it. I don't agree that the structure clearly indicates why TBZ is a non-competitive inhibitor; the proposal that specific hydrophobic residues function as gates will depend on lumen- and cytoplasm-facing structures for verification; the polar networks could have any number of functions - indeed it would be surprising if they were all involved in proton transport. Several of these issues could be resolved by a clearer illustration of the data, but I believe that a more rigorous description of the conclusions and where they fall between firm findings and speculation would help the reader put the results in perspective.

The central argument made by this reviewer that is repeated throughout this critique is that more structures of various states are needed to make mechanistic conclusions with respect to how TBZ binds and alternating access. While additional structures would certainly add mechanistic detail, they are not required to make these conclusions. In fact, as we point out throughout the text, these conclusions have already been made in various publications which we have cited and discussed. Decades of mutagenesis, binding, transport, inhibition, and accessibility measurements all support the conclusion that TBZ binds from the luminal side and that VMAT2 uses an alternating mechanism to transport neurotransmitter (30-32,35-37,55). Structures are neither required nor sufficient to make such claims and more structures of various apo states in different conformations would not provide any additional support to this question. If the predominant apo state was luminal open, cytoplasm open or occluded, this would not prove how TBZ enters VMAT2. Structural data alone does not provide these details; biochemical data does and structures are useful for understanding the details of how these mechanisms work. Thus, our structure provides the molecular framework for understanding the binding site, conformation, gating, and polar networks and we have interpreted our own biochemical data as well as the available biochemical data in the literature in the context of our structure.

The structure indicates why TBZ is a non-competitive inhibitor (35,36) because it is not possible for neurotransmitters to compete for binding to this state. Neurotransmitter initially binds to the cytosolic facing state where the intracellular gates are open, inhibition by binding to this state would result in a competitive mechanism. Since TBZ is non-competitive, it must bind through the luminal-open state where the luminal gate is open. Further conformational change produces the occluded conformation with both the luminal and intracellular gates closed which is what we observe in the structure. This finding is supported by numerous biochemical and functional experiments and by extensive analysis of mutants in the gates using binding assays, transport experiments and cysteine accessibility experiments. We have cited and discussed these key papers (30-32,35-37,55) throughout the text and our results support the conclusions drawn from these works.

Non-competitive inhibition occurs when the action of an inhibitor can't be overcome by increasing substrate concentration. The structure shows TBZ sequestered in the central cavity with no access to either cytoplasm or lumen. The explanation of competitive vs non-competitive inhibition depends entirely on how TBZ got there. If it is bound from the cytoplasm, cytoplasmic substrate should have been able to compete with TBZ and overcome the inhibition. If it is bound from the lumen, or from within the bilayer, cytoplasmic substrate would not be able to compete, and inhibition would be non-competitive. The structure does not tell us how TBZ got there, only that it was eventually occluded from both aqueous compartments and the bilayer.

TBZ is accepted to be a non-competitive inhibitor, based on decades of research, and not based solely on our structure (30-32,35,36). Our structure provides insight into the molecular mechanism by which non-competitive inhibition occurs. Previous studies have shown that TBZ enters through the luminal side of the transporter, resulting in non-competitive inhibition by binding to a conformation of the transporter which does not bind cytosolic neurotransmitter. We agree our structure does not prove how TBZ ‘got there’, but other studies have addressed this question (30-32, 35, 36) and have been discussed in detail.

The issue of how VMAT2 opens access to the central binding site from luminal and cytoplasmic sides is an important and interesting one, and comparison with other MFS structures in cytoplasmic-open or extracellular/luminal-open is a very reasonable approach. However, any conclusions for VMAT2 should be clearly indicated as speculative in the absence of comparable open structures of VMAT2. As a matter of presentation, I found the illustrations in ED Fig. 6 to be less helpful than they could have been. Specifically, illustrations that focus on the proposed gates, comparing that region of the new structure with the corresponding region of either VGLUT or GLUT4 would better help the reader to compare the position of the proposed gate residues with the corresponding region of the open structure. I realize that is the intended purpose of ED Fig. 6b and 6c, but currently, those show the entire protein, and a focus on the gate regions might make the proposed gate movements clearer. I also appreciate the difference between the Alphafold prediction and the new structure, but I'm not convinced that ED Fig. 6a adds anything helpful.

Thank you for the suggestion. We will prepare a new figure that focuses on the gates to make this clearer. The comparison with Alphafold is valuable since the luminal loops and gates are not well modeled. Many groups are using these structures to do biochemical and computational experiments and perhaps even to design small-molecules. Since Alphafold differs substantially in this area, it might be of interest to those in the community doing this type of work.

The polar networks described in the manuscript provide interesting possibilities for interactions with substrates and protons whose binding to VMAT2 must control conformational change. Aside from the description of these networks, there is little evidence presented to assess the role of these networks in transport. Are the networks conserved in other closely related transporters? How could the interaction of the networks with substrate or protons affect conformational change? Of course, any potential role proposed for the networks would be highly speculative at this point, and any discussion of their role should point out their speculative nature and the need for experimental verification. Some speculation, however, can be useful for focusing the field's attention on future directions. However, statements in the abstract (three distinct polar networks... play a role in proton transduction.) and the discussion (...are likely also involved in mediating proton transduction.) should be clearly presented as speculation until they are validated experimentally.

We agree these statements are speculative, which we acknowledged in the text. We will further emphasize this point in a future revision. Please note, however, that many of these residues have been highlighted in other studies (30-32,37,49,55), and we have cited them in the text. Please see previous response.

Most of these residues are indeed highly conserved. It is a good idea to highlight this in our sequence alignment of related transporters. We will do so in our revised manuscript.

The strongest aspect of this work (aside from the structure itself) is the analysis of TBZ binding. There is a problematic aspect to this analysis. The discussion on how TBZ stabilizes the occluded conformation of VMAT2 is premature without structures of apo-VMAT2 and possibly structures with other ligands bound. We don't really know at this point whether VMAT2 might be in the same occluded conformation in the absence of TBZ. Any statements regarding the effect of interactions between VMAT2 and TBZ depend on demonstrating that TBZ has a conformational effect. The same applies to the discussion of the role of W318 on conformation and to the loops proposed to "occlude the luminal side of the transporter" (line 131).

Please see the response to this argument presented earlier. The occluded structure clearly shows the residues serving as gates. To understand how the gates open is a separate question. This does require additional structures and computations which are beyond the scope of this work. Our structure is interpreted in the context of all available biochemical data.

The description of VMAT2 mechanism makes many assumptions that are based on studies with other MFS transporters. Rather than stating these assumptions as fact (VMAT2 functions by alternating access...), it would be preferable to explain why a reader should believe these assumptions. In general, this discussion presents conclusions as established facts rather than proposals that need to be tested experimentally.

Indeed, the structural details of alternating access in MFS transporters are based on structures of other related proteins and we have cited review articles that describe this (29,30,48). We would like to highlight that these assumptions are not without merit, as previous studies investigating predicted gating residues (the same residues resolved in our structure) were based on studies of other MFS transporters and the demonstrated biochemical results are consistent with an alternating access transporter. These biochemical experiments also clearly demonstrate that a broadly similar mechanism of alternating access is used by VMAT2, see (30-32,48) which we have cited extensively when discussing these mechanisms.

The MD simulations are not described well enough for a general reader. What is the significance of the different runs? ED Fig. 4d is not high enough resolution to see the details.

We plan to provide additional experimental details and data to support the computational experiments in a revision. See response to reviewer #3.

Reviewer #3 (Public Review):

Summary:

The vesicular monoamine transporter is a key component in neuronal signaling and is implicated in diseases such as Parkinson's. Understanding of monoamine processing and our ability to target that process therapeutically has been to date provided by structural modeling and extensive biochemical studies. However, structural data is required to establish these findings more firmly.

Strengths:

Dalton et al resolved a structure of VMAT2 in the presence of an important inhibitor, tetrabenazine, with the protein in detergent micelles, using cryo-EM and with the aid of domains fused to its N- and C-terminal ends. The resolution of the maps allows clear assignment of the amino acids in the core of the protein. The structure is in good agreement with a wealth of experimental and structural prediction data and provides important insights into the binding site for tetrabenazine and selectivity relative to analogous compounds.

Weaknesses:

The authors follow up their structures with molecular dynamics simulations. The simulations resulted in repositioning of the ligand, which does not seem to be well founded, and raises questions about the methodological choices made for the simulations.

We appreciate the comments of reviewer #3 and thank them for these suggestions regarding the MD simulations. We will be supplying additional information to address the questions of reviewer #2 and #3 regarding the MD simulations including 1) movies which show there is not a substantial repositioning of ligand in any of the three runs 2) a table showing protonation states of residues and TBZ 3) data which shows that the number of waters which enter the binding site is relatively few compared with simulations of dopamine bound VMAT2 4) in run 2, more waters have entered the binding site vs. run 1 and 3 which likely explains why there is a small repositioning of TBZ.

We will also be providing a substantially improved map in a revised manuscript where the peripheral TMHs and loops are better resolved.

Author Response

The following is the authors’ response to the original reviews.

We would like to thank the reviewers for their helpful comments which we have addressed, point-by-point, below:

Reviewer #1:

1) It might be useful to add more details to the methods (especially lines 191-196) to make them a bit more user-friendly for an audience who still may be unfamiliar with the relatively new and complex Mendelian randomisation technique.

The following information has been included in this section of the methods, to describe the different MR models in more detail:

“The IVW MR model will produce biased effect estimates in the presence of horizontal pleiotropy, i.e. where one or more genetic variant(s) included in the instrument affect the outcome by a pathway other than through the exposure. In the weighted median model, each genetic variant is weighted according to its distance from the median effect of all genetic variants. Thus, the weighted median model will provide an unbiased estimate when at least 50% of the information in an instrument comes from genetic variants that are not horizontally pleiotropic. The weighted mode model uses a similar approach but weights genetic instruments according to the mean effect. In this model, over 50% of the weight of the genetic instrument can be contributed to by genetic variants which are horizontally pleiotropic, but the most common amount of pleiotropy must be zero (known as the Zero Modal Pleiotropy Assumption (ZEMPA))[Hartwig et al., 2017].”

2) I was just wondering why MR egger was not carried out as part of this analysis?

We did consider also employing the MR Egger model as a further sensitivity analysis. However, given we were already employing the weighted median and weighted mode models, and given that MR-Egger suffers from reduced statistical power in comparison to the other models, we reasoned that adding in a further MR model would not add further clarity to our analyses, particularly given the relatively small sample size.

3) Although it is included in Figure 1 flowchart, I think it is also important to explain clearly in the written text way only n=6,118 of n=13,988 children in ALSPAC study were included in this study and the reason for this.

The following information has been included in the paragraph describing the ALSPAC study in the methods:

“Sufficient information was available on 6,221 of these individuals to be included in our analysis, as metabolomics was not performed for all individuals in the ALSPAC study.”

4) It is mentioned within the discussion 'the NMR metabolomics platform utilised in the analyses outlined here has limited coverage of fatty acids'. I think it might be useful to also add this detail into the methods section to aid readers when they are making their own interpretation whilst reading the results section.

The following sentence has been included in the methods section:

“This metabolomics platform has limited coverage of fatty acids.”

5) However, I feel that the conclusion should be tempered slightly as although this study alongside other similar MR studies provides evidence of an association between genetic liability to CRC and levels of metabolites at certain ages, I do not think there is enough evidence at this stage to say that genetic liability for CRC actually alters the levels of metabolites.

The first sentence of the conclusion has been changed to:

“Our analysis provides evidence that genetic liability to CRC is associated with altered levels of metabolites at certain ages, some of which may have a causal role in CRC development.”

Reviewer #2:

1) The background is lacking introduction to the different components of the metabolic features tested. For instance, there is a broader discussion about polyunsaturated fatty acids (PUFA) in the discussion, however, this should have been introduced and defined already before that. What metabolites are included in that term (PUFA)? Are there other studies on PUFA and CRC?

The following information has been included in the background section:

“In particular, previous work has highlighted polyunsaturated fatty acids (PUFA) as potentially having a role in colorectal cancer development. The term PUFA includes omega-3 and -6 fatty acids. Recent MR work has highlighted a possible link between PUFAs, in particular omega 6 PUFAs, and colorectal cancer risk.”

2) There seem to be indications for horizontal pleiotropy given the changed estimates when genetic variants in the FADS loci are removed. Could multivariable MR methods have been used to account for pleiotropy and differentiate individual fatty acid effects?

Multivariable MR can be employed to investigate the effects of horizontal pleiotropy. However, the multiple exposures must have sufficiently distinct underlying genetic architecture in order to instrument each one whilst adjusting for the other, as determined by conditional F-statistics. Given the correlations across metabolite levels, this is unlikely to be the case.

3) The ALSPAC sample sizes are decreasing across the different age groups, which is not strange given the longitudinal collection. However, does the altered sample composition affect the results? Have sensitivity analyses been done on the complete set of individuals from age 8-25?

The altered sample composition could be affecting results. The limitations section of the discussion has been amended to reflect this:

“Secondly, mostly due to the longitudinal nature of the ASLAPC study, our sample at each time point is composed of slightly different individuals. This could be influencing our results, and should be taken into account when comparing across time points.”

We have not completed any sensitivity analyses to investigate this.

4) Although beyond the scope of this paper, sex-stratified GWAS analyses on metabolites can easily be done in UK Biobank.

We thank the reviewer for this suggestion, and agree that this would be an interesting future analysis. We have amended the discussion to mention this:

“Fourthly, our analysis would benefit from being repeated with sex-stratified data. Although such GWAS results for metabolites are not currently available, the data to perform such GWAS are available in UK Biobank for future analyses.”

5) Very minor, there is a difference in reporting a number of decimals in ALSPAC results. There is also a difference in reporting the units for the results comparing text and figures (per SD higher CRC liability or per doubling). Please include sample sizes and data sources in the figure legends as they should be stand-alone items.

We have amended the ALSPAC results to all have two decimal places, reporting units have been altered and figure legends to include sample sizes and data sources.

Author Response

We thank the reviewers for their suggestions. We are confident in the model that predicts odor vs odor (OCT-MCH) preference using calcium activity, but we acknowledge the relative weakness of the model that predicts odor (OCT) vs air preference. We are preparing an updated manuscript that will prioritize our interpretation of the OCT-MCH results and more fully document uncertainties around our estimates of prediction capacity.

Reviewer #1 (Public Review):

Summary: The authors seek to establish what aspects of nervous system structure and function may explain behavioral differences across individual fruit flies. The behavior in question is a preference for one odor or another in a choice assay. The variables related to neural function are odor responses in olfactory receptor neurons or in the second-order projection neurons, measured via calcium imaging. A different variable related to neural structure is the density of a presynaptic protein BRP. The authors measure these variables in the same fly along with the behavioral bias in the odor assays. Then they look for correlations across flies between the structure-function data and the behavior.

Strengths: Where behavioral biases originate is a question of fundamental interest in the field. In an earlier paper (Honegger 2019) this group showed that flies do vary with regard to odor preference, and that there exists neural variation in olfactory circuits, but did not connect the two in the same animal. Here they do, which is a categorical advance, and opens the door to establishing a correlation. The authors inspect many such possible correlations. The underlying experiments reflect a great deal of work, and appear to be done carefully. The reporting is clear and transparent: All the data underlying the conclusions are shown, and associated code is available online.

We are glad to hear the reviewer is supportive of the general question and approach.

Weaknesses: The results are overstated. The correlations reported here are uniformly small, and don't inspire confidence that there is any causal connection. The main problems are

We are working on a revision that overhauls the interpretations of the results. We recognize that the current version inadequately distinguishes the results that we have high confidence in (specifically, PC2 of our Ca++ data as a predictor of OCT-MCH preference) versus results that are suggestive but not definitive (such as the PC1 of Ca++ data as a predictor of Air-OCT preference).

It’s true that the correlations are small, with r2 values typically in the 0.1-0.2 range. That said, we would call it a victory if we could explain 10 to 20% of the variance of a behavior measure, captured in a 3 minute experiment, with a circuit correlate. This is particularly true because, as the reviewer notes, the behavioral measurement is noisy.

1) The target effect to be explained is itself very weak. Odor preference of a given fly varies considerably across time. The systematic bias distinguishing one fly from another is small compared to the variability. Because the neural measurements are by necessity separated in time from the behavior, this noise places serious limits on any correlation between the two.

This is broadly correct, though to quibble, it’s our measurement of odor preference which varies considerably over time. We are reasonably confident that the more variance in our measurements can be attributed to sampling error than changes to true preference over time. As evidence, the correlation in sequential measures of individual odor preference, with delays of 3 hours or 24 hours, are not obviously different. We are separately working on methodological improvements to get more precise estimates of persistent individual odor preference, using averages of multiple, spaced measurements. This is promising, but beyond the scope of this study.

2) The correlations reported here are uniformly weak and not robust. In several of the key figures, the elimination of one or two outlier flies completely abolishes the relationship. The confidence bounds on the claimed correlations are very broad. These uncertainties propagate to undermine the eventual claims for a correspondence between neural and behavioral measures.

We are broadly receptive to this criticism. The lack of robustness of some results comes from the fundamental challenge of this work: measuring behavior is noisy at the individual level. Measuring Ca++ is also somewhat noisy. Correlating the two will be underpowered unless the sample size is huge (which is impractical, as each data point requires a dissection and live imaging session) or the effect size is large (which is generally not the case in biology). In the current version we tried to in some sense to avoid discussing these challenges head-on, instead trying to focus on what we thought were the conclusions justified by our experiments with sample sizes ranging from 20 to 60. We are working on a revision that is more candid about these challenges.

That said, we believe the result we view as the most exciting — that PC2 of Ca++ responses predicts OCT-MCH preference — is robust. 1) It is based on a training set with 47 individuals and a test set composed of 22 individuals. The p-value is sufficiently low in each of these sets (0.0063 and 0.0069, respectively) to pass an overly stringent Bonferonni correction for the 5 tests (each PC) in this analysis. 2) The BRP immunohistochemistry provides independent evidence that is consistent with this result — PC2 that predicts behavior (p = 0.03 from only one test) and has loadings that contrast DC2 and DM2. Taken together, these results are well above the field-standard bar of statistical robustness.

In the revision we are working on, we are explicit that this is the (one) result we have high confidence in. We believe this result convincingly links Ca++ and behavior, and warrants spotlighting. We have less confidence in other results, and say so, and we hope this addresses concerns about overstating our results.

3) Some aspects of the statistical treatment are unusual. Typically a model is proposed for the relationship between neuronal signals and behavior, and the model predictions are correlated with the actual behavioral data. The normal practice is to train the model on part of the data and test it on another part. But here the training set at times includes the testing set, which tends to give high correlations from overfitting. Other times the testing set gives much higher correlations than the training set, and then the results from the testing set are reported. Where the authors explored many possible relationships, it is unclear whether the significance tests account for the many tested hypotheses. The main text quotes the key results without confidence limits.

Our primary analyses are exactly what the reviewer describes, scatter plots and correlations of actual behavioral measures against predicted measures. We produced test data in separate experiments, conducted weeks to months after models were fit on training data. This is more rigorous than splitting into training and test sets data collected in a single session, as batch/environmental effects reduce the independence of data collected within a single session.

We only collected a test set when our training set produced a promising correlation between predicted and actual behavioral measures. We never used data from test sets to train models. In our main figures, we showed scatter plots that combined test and training data, as the training and test partitions had similar correlations.

We are unsure what the reviewer means by instances where we explored many possible relationships. The greatest number of comparisons that could lead to the rejection of a null hypothesis was 5 (corresponding to the top 5 PCs of Ca++ response variation or Brp signal). We were explicit that the p-values reported were nominal. As mentioned above, applying a Bonferroni correction for n=5 comparisons to either the training or test correlations from the Ca++ to OCT-MCH preference model remains significant at alpha=0.05.

Our revision will include confidence limits.

Reviewer #2 (Public Review):

Summary:

The authors aimed to identify the neural sources of behavioral variation in a decision between odor and air, or between two odors.

Strengths:

-The question is of fundamental importance.

-The behavioral studies are automated, and high-throughput.

-The data analyses are sophisticated and appropriate.

-The paper is clear and well-written aside from some strong wording.

-The figures beautifully illustrate their results.

-The modeling efforts mechanistically ground observed data correlations.

We are glad to read that the reviewer sees these strengths in the study. We hope the forthcoming revision will address the strong wording.

Weaknesses:

-The correlations between behavioral variations and neural activity/synapse morphology are (i) relatively weak, (ii) framed using the inappropriate words "predict", "link", and "explain", and (iii) sometimes non-intuitive (e.g., PC 1 of neural activity).

Taking each of these points in turn: i) It would indeed be nicer if our empirical correlations are higher. One quibble: we primarily report relatively weak correlations between measurements of behavior and Ca++/Brp. This could be the case even when the correlation between true behavior and Ca++/Brp is higher. Our analysis of the potential correlation between latent behavioral and Ca++ signals was an attempt to tease these relationships apart. The analysis suggests that there could, in fact, be a high underlying correlation between behavior and these circuit features (though the error bars on these inferences are wide).

ii) We are working to guarantee that all such words are used appropriately. “Predict” can often be appropriate in this context, as a model predicts true data values. Explain can also be appropriate, as X “explaining” a portion of the variance of Y is synonymous with X and Y being correlated. We cannot think of formal uses of “link,” and are revising the manuscript to resolve any inappropriate word choice.

iii) If the underlying biology is rooted in non-intuitive relationships, there’s unfortunately not much we can do about it. We chose to use PCs of our Ca++/Brp data as predictors to deal with the challenge of having many potential predictors (odor-glomerular responses) and relatively few output variables (behavioral bias). Thus, using PCs is a conservative approach to deal with multiple comparisons. Because PCs are just linear transformations of the original data, interpreting them is relatively easy, and in interpreting PC1 and PC2, we were able to identify simple interpretations (total activity and the difference between DC2 and DM2 activation, respectively). All in all, we remain satisfied with this approach as a means to both 1) limit multiple comparisons and 2) interpret simple meanings from predictive PCs.

-No attempts were made to perturb the relevant circuits to establish a causal relationship between behavioral variations and functional/morphological variations.

We did conduct such experiments, but we did not report them because they had negative results that we could not definitively interpret. We used constitutive and inducible effectors to alter the physiology of ORNs projecting to DC2 and DM2. We also used UAS-LRP4 and UAS-LRP4-RNAi to attempt to increase and decrease the extent of Brp puncta in ORNs projecting to DC2 and DM2. None of these manipulations had a significant effect on mean odor preference in the OCT-MCH choice, which was the behavioral focus of these experiments. We were unable to determine if the effectors had the intended effects in the targeted Gal4 lines, particularly in the LRP experiments, so we could not rule out that our negative finding reflected a technical failure. We are reviewing these results to determine if they warrant including as a negative finding in the revision.

We believe that even if these negative results are not technical failures, they are not necessarily inconsistent with the analyses correlating features of DC2 and DM2 to behavior. Specifically, we suspect that there are correlated fluctuations in glomerular Ca++ responses and Brp across individuals, due to fluctuations in the developmental spatial patterning of the antennal lobe. Thus, the DC2-DM2 predictor may represent a slice/subset of predictors distributed across the antennal lobe. This would also explain how we “got lucky” to find two glomeruli as predictors of behavior, when were only able to image a small portion of the glomeruli. In analyses we did not report, we explored this possibility using the AL computational model. We are likely to include this interpretation in the revised discussion.

Reviewer #3 (Public Review):

Churgin et. al. seeks to understand the neural substrates of individual odor preference in the Drosophila antennal lobe, using paired behavioral testing and calcium imaging from ORNs and PNs in the same flies, and testing whether ORN and PN odor responses can predict behavioral preference. The manuscript's main claims are that ORN activity in response to a panel of odors is predictive of the individual's preference for 3-octanol (3-OCT) relative to clean air, and that activity in the projection neurons is predictive of both 3-OCT vs. air preference and 3-OCT vs. 4-methylcyclohexanol (MCH). They find that the difference in density of fluorescently-tagged brp (a presynaptic marker) in two glomeruli (DC2 and DM2) trends towards predicting behavioral preference between 3-oct vs. MCH. Implementing a model of the antennal lobe based on the available connectome data, they find that glomerulus-level variation in response reminiscent of the variation that they observe can be generated by resampling variables associated with the glomeruli, such as ORN identity and glomerular synapse density.

Strengths:

The authors investigate a highly significant and impactful problem of interest to all experimental biologists, nearly all of whom must often conduct their measurements in many different individuals and so have a vested interest in understanding this problem. The manuscript represents a lot of work, with challenging paired behavioral and neural measurements.

Weaknesses:

The overall impression is that the authors are attempting to explain complex, highly variable behavioral output with a comparatively limited set of neural measurements…

We would say that we are attempting to explain a simple, highly variable behavioral measure with a comparatively limited set of neural measurements. I.e. we make no claims to explain the complex behavioral components of odor choice, like locomotion, reversals at the odor boundary, etc.

Given the degree of behavioral variability they observe within an individual (Figure 1- supp 1) which implies temporal/state/measurement variation in behavior, it's unclear that their degree of sampling can resolve true individual variability (what they call "idiosyncrasy") in neural responses, given the additional temporal/state/measurement variation in neural responses.

We are confident that different Ca++ recordings are statistically different. This is borne out in the analysis of repeated Ca++ recordings in this study, which finds that the significant PCs of Ca++ variation contain 77% of the variation in that data. That this variation is persistent over time and across hemispheres was assessed in Honegger & Smith, et al., 2019. We are thus confident that there is true individuality in neural responses (Note, we prefer not to call it “individual variability” as this could refer to variability within individuals, not variability across individuals.) It is a separate question of whether individual differences in neural responses bear some relation to individual differences in behavioral biases. That was the focus of this study, and our finding of a robust correlation between PC2 of Ca++ responses and OCT-MCH preference indicates a relation. Because behavior and Ca++ were collected with an hours-to-day long gap, this implies that there are latent versions of both behavioral bias and Ca++ response that are stable on timescales at least that long.

The statistical analyses in the manuscript are underdeveloped, and it's unclear the degree to which the correlations reported have explanatory (causative) power in accounting for organismal behavior.

With respect, we do not think our statistical analyses are underdeveloped, though we acknowledge that the detailed reviewer suggestions included the helpful suggestion to include uncertainty in the estimation of confidence intervals around the point estimate of the strength of correlation between latent behavioral and Ca++ response states. We are considering those suggestions and anticipate responding to them in the revision.

It is indeed a separate question whether the correlations we observed represent causal links from Ca++ to behavior (though our yoked experiment suggests there is not a behavior-to-Ca++ causal relationship — at least one where odor experience through behavior is an upstream cause). We attempted to be precise in indicating that our observations are correlations. That is why we used that word in the title, as an example. In the revision, we are working to make sure this is appropriately reflected in all word choice across the paper.

Author Response

The following is the authors’ response to the original reviews.

We would like to thank you for your thoughtful review and constructive feedback on our manuscript. We have implemented numerous revisions throughout the manuscript to address your comments and suggestions. Below, our point-by-point responses to the reviewers' remarks. We hope that our revisions adequately address all raised concerns.

Reviewer #1

One major drawback of the manuscript is the fact that the data were collected from male subjects only. One might expect similar behavioral outcomes from male and female rats receiving 2shock and 10-shock training. However, increasing attention to sex as a biological variable has revealed an interesting truth, namely that males and females can engage distinct neural pathways to arrive at the same behavioral destination. It should not be taken for granted that retrieval of aversive contextual associations would reproduce the same networks in females, and, as such, the manuscript does not give a complete accounting of the phenomenon under study.

We thank the reviewer for highlighting the importance of sex differences in fear memory and for encouraging us to discuss this issue. We agree that males and females can engage different behavioral and circuit mechanisms and that our findings may not be generalizable to female rats. We expanded the discussion section to state this limitation and to suggest future directions for research on sex differences in fear memory:

“In addition, a growing body of evidence underscores the differences between males and females concerning fear memories (Fleischer and Frick, 2023). Given that our study was conducted only with male rats, future studies exploring sex differences will be instrumental in providing a more complete account of the network-level mechanisms underlying fear memory strength.”

The aversive associative memories described by the authors are characterized as mild or strong. More analysis of the meaning of memory strength, and its relationship to conditioning parameters, is needed.

In particular, the authors should discuss issues such as amount of training, US magnitude, and rate of shock delivery. If amount of training is important, would 2 vs 10 presentations of a milder shock produce the same networks at retrieval? Would a larger shock require fewer presentations to isolate amygdalar regions from the rest of the network? If the shocks were presented at the same rate during training, would you get the same result in both groups? More data examining these questions would be ideal, but, in the absence of that, a discussion of these issues is needed and missing from the manuscript in its current form.

We appreciate the reviewer's feedback on the characterization of the fear memories in our study and agree that the labels "mild" and "strong" could oversimplify the complex nature of fear memories. Our study's main objective was not to delineate how varying conditioning protocols result in 'mild' or 'strong' fear memories, but to employ protocols of different intensities known to produce distinct behaviors, and then discern their brain differences. Our categorization was rooted in the resulting behavioral expressions, classifying 'mild' memories as those triggering sub-maximal fear responses with low generalization and a potential for extinction learning and reconsolidation. Conversely, 'strong' memories were defined by peak or near-peak fear responses, high generalization, and impeded extinction and reconsolidation processes. To isolate the number of foot shocks as the sole variable, we kept both shock intensity and session duration constant. While this decision allowed for a clear comparative analysis, we acknowledge its limitations in exploring other influential factors.

A more ideal approach would be to reverse this process—first experimenting with several different conditioning parameters and then observing the resulting behaviors and brain mechanisms—but given the additional workload that would entail, particularly when combined with the c-fos and network analyses, we opted for our current approach. Nevertheless, we hope our study will stimulate research that goes deeper into the nuances of fear conditioning protocols, fostering a better understanding of adaptive and maladaptive fear memories. This is now discussed in the discussion session:

“To generate mild and strong fear memories, we based our conditioning parameters on methods that have shown distinct behavioral outcomes in prior studies (Haubrich et al., 2020, 2015; Holehonnur et al., 2016; Poulos et al., 2016; Wang et al., 2009). To ensure a focused comparative analysis, our conditioning protocols differed only in the number of foot shocks, and maintained consistent shock intensities and session durations. Yet, the number of shocks is not the only factors that can affect the strength of fear memories (Gazarini et al., 2023). Other conditioning parameters, such as shock intensity, its predictability, and inter-shock intervals, can also play crucial roles. Moreover, different fear measures like freezing behavior, fear-potentiated startle, and inhibitory avoidance might manifest differently following varying conditioning protocols, adding another layer of complexity. A comprehensive understanding of fear memory strength will benefit from further studies scrutinizing these parameters and memory attributes.”

Reviewer #2

One alternative account to the weak vs. strong memory distinction made in the paper is the opportunity for extinction in the 2S compared to the 10S group. In the 2S group, the last shock occurs in the 3rd minute, leaving 9 minutes of context exposure without reinforcement to follow. This is not the case for the 10S group. If context fear extinction is engaged during this time, then this would mean that two memories (acquisition and extinction) are taking place in the 2S group, weakening the fear memory in this group, setting up the ground for stronger effects of extinction, less generalization and of course potential greater connectivity required for representing and linking these memories. Indeed, the IL, a brain area linked to extinction, is more predominant in the connectivity map of the 2S compared to the 10S group. While testing this alternative is beyond the scope of this paper, it will need to be discussed.

We thank the reviewer for raising this interesting point. We agree that the structure of the 2S protocol might inadvertently provide an opportunity for within-session extinction. However, we would like to clarify that we made a mistake in the description of the 2S training protocol. The timing of the shock deliveries was not at the second and third minutes as stated (a usual protocol in the literature), but at the sixth and seventh minutes. We apologize for this mistake and are thankful for your help in identifying this discrepancy which had unfortunately persisted despite multiple proofreading rounds. We have amended this detail in the methods section of our manuscript.

Nevertheless, we recognize that the subsequent minutes post-shock in the 2S group may still provide a window for potential extinction. To address this possibility, we scored the freezing expression during the training session minute by minute. In the 2S group, two videos were corrupted, and it was only possible to score freezing in six out of eight animals (this is acknowledged in the methods section). As presented in Figure 1.A (middle plot), freezing behavior increased post-shocks and showed no decline towards the session's end. These findings suggest that within-session extinction did not occur during our conditioning session. This analysis is now integrated into the relevant results subsection.

Methodological detail is lacking re the timeline of study, and connectivity analyses.

Thank you for your feedback. The formula for the discrimination index is now explained in the methods section. The new plot showing freezing behavior during training shows the exact time bin when shocks were delivered. We have expanded the description of the connectivity analysis.

Reviewer #3

Major concerns)

1) Previous studies including Karim's lab have shown that protein synthesis in the hippocampus is required for the reconsolidation of contextual fear memory and that the retrieval of contextual fear memory activates gene expression such as c-fos in the hippocampus. However, the authors failed to confirm this observation. This may be due to the small number of rats or some technical problems.

Thank you for this insightful observation. We believe that the absence of the expected increase in hippocampal c-fos activation is due to the unique experimental design employed for our control group. In our study, control rats were subjected to an equivalent duration of context exposure without receiving shocks. As a result, these animals formed and retrieved a neutral, rather than fearful, contextual memory. This likely elevated cfos levels in the hippocampus in comparison to the more traditional home-cage condition frequently used in earlier studies. We used the NS (no shock) protocol for our control group to specifically elucidate the impact of the number of shock presentations on memory formation, therefore the context exposure was kept the same across groups. Importantly, this aspect did not affect our connectivity analysis, since it is influenced by the relative variance across structures than on the absolute magnitude of c-fos expression. We now emphasize the nature of our control group in the discussion:

“Importantly, our control animals were exposed to the conditioning chamber for an equivalent duration without being subjected to shocks, thus encoding and recalling a non-fearful contextual memory.”

2) The author's computation analyses suggested differences in neural networks activated by the retrieval of mild and strong fear memories. The results of computer analysis are interesting. However, it is not clear whether such results are actually occurring in vivo. At this moment, the author's findings are not a conclusion, but rather a suggestion or hypothesis. Therefore, it is also important to conduct interventional experiments to evaluate the validity of the authors' findings. Specifically, the authors' results could be validated by analyzing the effects of inhibition of specific brain regions on mild and strong fear memories retrieval using such as DREADD and other methods. These experiments seem hard, but would greatly improve the quality of the manuscript.

We appreciate the reviewer's perspective and acknowledge the limitations of our current findings. While our data based on c-fos expression suggests functional connections reflective of neural activity during fear memory recall, we agree that it is not possible to deduce causality from this alone. Instead, our study aimed to uncover the network-level distinctions between mild and strong memories, laying the groundwork for subsequent, in-depth investigations of the causal relationships within these identified pathways. We agree that corroborating our findings with interventional experiments, such as using DREADDs, is an important next step. We also agree that such experiments would enhance our study and hope future research will address these points. These points were included in the discussion session:

“To further elucidate the underlying mechanisms of fear memory strength in vivo, understanding the specific roles of individual network elements in fear regulation becomes essential. Future research will be important to probe the causal interplay among distinct nodes and edges, both individually and in combination, in shaping diverse aspects of fear expression.”

Reviewer #2 (Recommendations For The Authors):

Methodological detail is lacking:

How is the discrimination index calculated?

We have included this information in the methods section: “The generalization index was calculated as Freezing in Test B / (Freezing in Test A + Freezing in Test B).”

A distinction between complete spontaneous recovery (10S group) vs. partial spontaneous recovery (2S group) vs. extinction retention needs to be considered in discussing the extinction data.

Thank you for this suggestion. To address this point, we now include Tukey’s post hoc comparisons between the first and last bins of extinction and the test session. The results show that in the 2S group, freezing during test remained consistent with the levels observed in the final extinction bin and was lower than the levels in the initial extinction bin. Conversely, in the 10S group, freezing levels increased from the final extinction bin to the test, reaching levels comparable to those observed in the initial extinction bin.

Detail regarding the connectivity analyses is missing from the methods. For example the calculation of the r value distractions should be detailed in the methods not just the results, more detail regarding calculations is needed for the degree of centrality, betweenness centrality, nodal efficiency, small world analyses etc.

We appreciate the reviewer’s feedback. We have expanded the description of the connectivity analysis.

Justification for 'excluding edges with r values lower than the average plus one standard deviation of all 292 networks (Figure 4.B; r < 0.61)' is needed.

Thank you for your encouraging us to elaborate on the rationale behind our thresholding method. We acknowledge that there is no consensus in the literature on the optimal thresholding method for functional networks. Our primary objective with thresholding was to retain the most robust connections while minimizing potential noise from weakly correlated regions. Instead of opting for an arbitrary threshold, we determined our cut-off based on the average plus one standard deviation across all networks. Theoretically, this retains approximately the top 16% of connections. Given our 12 regions of interest, this translates to roughly 10 connections per network. This count is sufficient for a nuanced analysis of the network structures and between group comparisons.Importantly, our method inherently accounts for variations in interregional correlations across groups. Groups with a distribution skewed towards higher r values will naturally have more edges, highlighting the enhanced synchronized activity between certain regions. On the other hand, networks with tendencies towards lower r-values will exhibit fewer connections. Thus, our thresholding method is rooted in the data’s distribution and result in networks that reflect the differences across groups.

We added the following sentence to the methods session summarizing this rationale:

“This thresholding approach was used to provide a cut-off based on the data’s inherent distribution, therefore retaining the top edges according to the data variance. “

Line 81 - 'brain areas' is missing after '12'.

Thank you, this is now fixed.

Tile for 2. is somewhat odd. Thought the following may be better, but obviously leaving this up to the author's discretion: 'Commonalities and differences in brain activation induced by recall of mild and strong fear memories'

Thank you for this suggestion. We agree with the title suggested by the reviewer, and it was replaced in the manuscript.

Reviewer #3 (Recommendations For The Authors):

1) Previous studies including Karim's lab have shown that protein synthesis in the hippocampus is required for the reconsolidation of contextual fear memory and that the retrieval of contextual fear memory activates gene expression such as c-fos in the hippocampus. However, the authors failed to confirm this observation. This may be due to the small number of rats or some technical problems.

Thank you for this suggestion. As explained above, we believe that this is due to the nature of our control group, which is now highlighted in the discussion section.

2) The author's computation analyses suggested differences in neural networks activated by the retrieval of mild and strong fear memories. The results of computer analysis are interesting. However, it is not clear whether such results are actually occurring in vivo. At this moment, the author's findings are not a conclusion, but rather a suggestion or hypothesis. Therefore, it is also important to conduct interventional experiments to evaluate the validity of the authors' findings. Specifically, the authors' results could be validated by analyzing the effects of inhibition of specific brain regions on mild and strong fear memories retrieval using such as DRRED and other methods. These experiments seem hard, but would greatly improve the quality of the manuscript.

Thank you for your valuable feedback. As explained above, these points are now included in the discussion section.

Minor comments)

1) cfos should be c-fos or c-Fos.

Thank you for your correction. All instances of ‘cfos’ were replaced by ‘c-fos’.

2) Line 275; "Compared to the to re-exposure to" should be "Compared to the to re-exposure to".

Thank you for your correction. This is now fixed.

Author Response

The following is the authors’ response to the original reviews.

eLife assessment

This study has uncovered some important initial findings about how certain extracellular vehicles (EVs) from the mother might impact the energy usage of an embryo. While the study's findings are in general solid, some experiments lack statistical power due to small sample sizes. The study's title might be a bit too assertive as the evidence linking maternal mtDNA transmission to changes in embryo energy use is still correlative.

We would like to express our sincere gratitude to the editors and reviewers for their invaluable comments on this work. Their feedback has been instrumental in enhancing the quality of our manuscript; we have incorporated their suggestions to the best of our abilities.

Reviewer #1 (Public Review):

Q1. Bolumar et al. isolated and characterized EV subpopulations, apoptotic bodies (AB), Microvesicles (MV), and Exosomes (EXO), from endometrial fluid through the female menstrual cycle. By performing DNA sequencing, they found the MVs contain more specific DNA sequences than other EVs, and specifically, more mtDNA were encapsulated in MVs. They also found a reduction of mtDNA content in the human endometrium at the receptive and post-receptive period that is associated with an increase in mitophagy activity in the cells, and a higher mtDNA content in the secreted MVs was found at the same time. Last, they demonstrated that the endometrial Ishikawa cell-derived EVs could be taken by the mouse embryos and resulted in altered embryo metabolism.

This is a very interesting study and is the first one demonstrating the direct transmission of maternal mtDNA to embryos through EVs.

A1. Thank you for your kind comments.

Reviewer #2 (Public Review):

Q2. In Bolumar, Moncayo-Arlandi et al. the authors explore whether endometrium-derived extracellular vesicles contribute mtDNA to embryos and therefore influence embryo metabolism and respiration. The manuscript combines techniques for isolating different populations of extracellular vesicles, DNA sequencing, embryo culture, and respiration assays performed on human endometrial samples and mouse embryos.

Vesicle isolation is technically difficult and therefore collection from human samples is commendable. Also, the influence of maternally derived mtDNA on the bioenergetics of embryos is unknown and therefore novel. However, several experiments presented in the manuscript fail to reach statistical significance, likely due to the small sample sizes. Additionally, the experiments do not demonstrate a direct effect of mtDNA transfer on embryo bioenergetics. This has the unfortunate consequence of making several of the authors' conclusions speculative.

In my opinion the manuscript supports the following of the authors' claims:

1) Different amounts of mtDNA are shed in human endometrial extracellular vesicles during different phases of the menstrual cycle

2) Endometrial microvesicles are more enriched for mitochondrial DNA sequences compared to other types of microvesicles present in the human samples

3) Fluorescently labelled DNA from extracellular vesicles derived from an endometrial adenocarcinoma cell line can be incorporated into hatched mouse embryos.

4) Culture of mouse embryos with endometrial extracellular vesicles can influence embryo respiration and the effect is greater when cultured with isolated exosomes compared to other isolated microvesicles

A2. Thank you for your detailed feedback. We have made every effort to enhance the manuscript in this revised version, ensuring that our conclusions are grounded in solid evidence and that they avoid any speculation.

My main concerns with the manuscript:

Q3. The authors demonstrate that microvesicles contain the most mtDNA, however, they also demonstrate that only isolated exosomes influence embryo respiration. These are two separate populations of extracellular vesicles.

A3. This manuscript focuses on the DNA content secreted by the endometrium and captured by the embryo. We identified both mitochondrial DNA and genomic DNA. We have found that mitochondrial DNA is predominantly secreted and encapsulated within microvesicles, while all three types of vesicles encapsulate genomic DNA. Specifically, based on the results we presented in Response A8 to the reviewers and included in the latest version of the manuscript, we observed that exosomes contain the highest amount of genomic DNA. Furthermore, exosomes have the greatest impact on embryo bioenergetics, suggesting that this DNA content may primarily exert this effect. We have thoroughly revised the manuscript, focusing our message on DNA content.

Q4. mtDNA is not specifically identified as being taken up by embryos only DNA.

A4. We agree with the reviewer; as we mention in answer A9, EdU does not specifically label mitochondrial DNA. To solve this issue, we incubated a synthetic molecule of labeled mtDNA with embryos and analyzed mtDNA incorporation using confocal microscopy. We co-cultured hatched mouse embryos (3.5 days) with an ATP8 sequence conjugated with Biotin overnight at 37ºC and 5% CO2. We then permeabilized embryos, incubated them with Streptavidine-Cy3 for 45 min, and visualized the results using an SP8 confocal microscope (Leica). We observed mtDNA internalization by cells of the hatched embryos; please see new supplementary Figure 7 and lines 234-237 on page 9 and lines 583-592 M&M on page 21.

Q5. The authors do not rule out that other components packaged in extracellular vesicles could be the factors influencing embryo metabolism.

A5. The vesicular subtypes contain molecules beyond DNA, such as microRNAs, proteins, or lipids. Our laboratory has studied the transmission of vesicles and their relationship with their contents (particularly microRNAs) and their connection to maternal-fetal communication. In this study, we focused on genomic/mitochondrial DNA. We cannot exclude the possibility that other molecules may influence metabolism; this statement is already noted in the discussion section on lines 328-331 on page 12.

Q6. Taken together, these concerns seem to contradict the implication of the title of the manuscript – the authors do not demonstrate that inheritance of maternal mtDNA has a direct causative effect on embryo metabolism.

A6. We have modified the title to better align with the manuscript’s results. The proposed new title for the manuscript is “Vertical transmission of maternal DNA through extracellular vesicles modulates embryo bioenergetics during the periconceptional period.”

Reviewer #1 (Recommendations for The Authors):

Q7. Would it be possible to validate the mtDNA content and mitophagy activity in different periods using the Ishikawa cells?

A7. Unfortunately, this validation cannot be achieved with in vitro cultures of cell lines, especially with a cell line such as the endometrial adenocarcinoma-derived Ishikawa cell line. While mimicking the menstrual cycle (as observed in Figure 3 of the manuscript) is entirely artificial, we believe that the statistically significant results obtained in human samples faithfully represent the biological processes involved. Using a cell line, in our opinion, would not provide us with novel information.

Q8. Characterization of the EVs subpopulations from Ishikawa cells and direct evidence to show the EdU labeled DNA is contained in the EVs are necessary.

A8. To address this concern, we designed a novel experiment. We cultured Ishikawa cells in the presence of Edu, isolated the three types of vesicles, and evaluated labeled DNA content by flow cytometry (as illustrated in Supplementary Figure 5). All three types of vesicles exhibited positive EdU-DNA labeling; notably, the exosomal fraction demonstrated substantially higher DNA content than the other vesicle populations. Please see new supplementary Figure 5 and lines 217-218 on page 9, and lines 576-582 of the M&M on pages 20-21.

Q9. Would EdU incorporate into the genomic DNA or mitochondrial DNA?

A9. EdU (5-ethynyl-2′-deoxyuridine) is a nucleoside analog of thymidine and becomes incorporated into DNA during active DNA synthesis. EdU labels all newly synthesized DNA, both genomic and mitochondrial; however, we cannot differentiate between them with this technique.

Q10. It is difficult to assess whether the EV-derived DNA was taken by the TE or ICM without immunostaining of cell lineage markers in mouse embryos.

A10. We did not aim to label the inner cell mass, as the vesicles primarily enter through trophectodermal cells. The images presented in Figure 4 and Supplementary Figure 5 depict trophectoderm cells.

Q11. It is also valuable to perform co-staining of Mitotracker to show the co-localization of EdU labelled DNA and the mitochondrial.

A11. Per the reviewer's suggestion, we conducted an experiment as described in the following text. We isolated MVs from the culture media of EdU-treated Ishikawa cells and co-incubated them with embryos overnight. The resulting images (See Author response image 1) show an embryo subjected to staining with EdU-tagged DNA labeled with Alexa Fluor 488 (green), Mitotracker Deep Red (red), and nuclei (blue). Detailed views of the embryo are presented in panels A and B. Notably, we observed co-localization of mitochondria and EdU-tagged DNA, as indicated by the white arrows. Despite this intriguing finding, we chose not to include these results in the initial version of the manuscript; however, if the editor deems it appropriate, we would be delighted to incorporate them into the final version. The experimental procedure for co-localization of EdU DNA-tagged with mitochondria involved the following steps: Mitotracker Deep Red FM (Thermo Fisher Scientific, M22426) was added to the embryo media at a final concentration of 200 nM, and the embryos were subsequently incubated for 45-60 minutes prior to fixation.

Author response image 1.

Co-localization of mitochondria and EdU-tagged DNA in mouse embryos. Representative micrograph of an embryo co-incubated with MVs isolated from the culture media of Ishikawa cells treated with EdU. EdU-tagged DNA was labeled with Alexa Fluro 488 (green). Mitotracker Deep Red (mitochondria; red) and nuclei (blue). A and B) magnified images of the embryo show detailed co-localization of mitochondria and EdU-tagged DNA (white arrows). Negative control) Embryos incubated with MVs isolated from control Ishikawa cells (without EdU incubation) and stained with the click-it reaction cocktail. A and B showed magnified images of the embryo. Notice the absence of EdU-Alexa Fluro 488 signals (green).

Reviewer #2 (Recommendations for The Authors):

Q12. It would be helpful if the authors could provide citations and rationale for why they chose specific molecular markers to validate the different population of extracellular vesicles.

A12. Different extracellular populations are defined by molecular marker signatures that reflect their origin. VDAC1 forms ionic channels in the mitochondrial membrane, has a role in triggering apoptosis, and has been described as characteristic of ABs.[1]

The ER protein Calreticulin has also been used as an AB marker [2]; however, other studies have noted the presence of Calreticulin in MVs. [1] This apparent non-specificity may derive from apoptotic processes, during which the ER membrane fragments and forms vesicles smaller than ABs, which would contain Calreticulin and sediment at higher centrifugal forces.[3,4] In fact, proteomic studies have linked the presence of Calreticulin with vesicular fractions of a size range relevant for MVs [5] and ABs [6].

ARF6, a GTP-binding protein implicated in cargo sorting and promoting MV formation, has been proposed as an MV marker. [7,8]

Classic markers of EXOs include molecules involved in biogenesis, such as tetraspanins (CD63, CD9, CD81), Alix, TSG101, and flotillin-1.[9,10] Nonetheless, studies have recently reported the widespread nature of such markers among various EV populations, although with different relative abundances (such as is the case for CD9, CD63, HSC70, and flotillin-1[11]). Notably, certain molecular markers (such as TSG101[1,11]) have been ratified as specific to EXOs.

References

1. D. K. Jeppesen, M. L. Hvam, B. Primdahl-Bengtson, A. T. Boysen, B. Whitehead, L. Dyrskjøt, T. F. Orntoft, K. A. Howard, M. S. Ostenfeld, J. Extracell. Vesicle. 2014, 3, 25011, doi: 10.3402/jev.v3.25011.

2. J. van Deun, P. Mestdagh, R. Sormunen, V. Cocquyt, K. Vermaelen, J. Vandesompele, M. Bracke, O. De Wever, A. Hendrix, J. Extracell. Vesicles. 2014, 3:24858, doi: 10.3402/jev.v3.24858.

3. L. Abas, C. Luschnig, Anal. Biochem. 2010, 401, 217-227, doi: 10.1016/j.ab.2010.02.030.

4. C. Lavoie, J. Lanoix, F. W. Kan, J. Paiement, J. Cell Sci. 1996, 109(6), 1415-1425.

5. M. Tong, T. Kleffmann, S. Pradhan, C. L. Johansson, J. DeSousa, P. R. Stone, J. L. James, Q. Chen, L. W. Chamley, Hum. Reprod. 2016, 31(4), 687-699, doi: 10.1093/humrep/dew004.

6. P. Pantham, C. A. Viall, Q. Chen, T. Kleffmann, C. G. Print, L. W. Chamley, Placenta. 2015, 36, 1463e1473, doi: 10.1016/j.placenta.2015.10.006.

7. V. Muralidharan-Chari, J. Clancy, C. Plou, M. Romao, P. Chavrier, G. Raposo, C. D'Souza-Schorey, Curr. Biol. 2009, 19, 1875-1885.

8. C. Tricarico, J. Clancy, C. D'Souza-Schorey, Small GTPases. 2016, 0(0), 1-13.

9. M. Colombo, G. Raposo, C. Théry, Annu. Rev. Cell. Dev. Biol. 2014, 30, 255-289, doi: 10.1146/annurev-cellbio-101512-122326.

10. S. Mathivanan, H. Ji, R. J. Simpson, J. Proteomics. 2010, 73(10), 1907-1920.

11. J. Kowal, G. Arras, M. Colombo, M. Jouve, J. P. Morath, B. Primdal-Bengtson, F. Dingli, D. Loew, M. Tkach, C. Théry, Proc. Natl. Acad. Sci. U. S. A. 2016, 113(8), E968-77.

Q13. The PCA analysis in supplementary figure 4 A&B needs more explanation for why they think separation of the two conditions based on principal component 1 is sufficient. The small number of replicates makes me concerned because principal component 2 does not show similarity of replicates for the DNase treated samples. Also, 4C has no description in the figure legend.

A13. The PCA results show a clear separation between the two conditions; we believe this separation is primarily driven by the differences observed in principal component 1 (PC1). We would like to address the concerns raised by the reviewer with the following points:

1. Interpretation of PCs: In PCA, the principal components represent orthogonal axes capturing the highest variance in the data. PC1 accounts for 56% and 57% of the variance in the two conditions, respectively. The significant variance explained by PC1 suggests that it effectively captures the major sources of variation between the samples.

2. Sample Replicates and Variability: The concern regarding the small number of replicates is acknowledged, and we understand its impact on the analysis. Despite the limited number of replicates, the consistent pattern of separation in PC1 between the two conditions provides confidence in the observed separation. We also agree that PC2 does not show an apparent similarity among the DNase-treated samples; however, this does not diminish the significance of PC1, which robustly separates the two conditions.

We include the Figure legend for 4C: “C) Principal component analysis shows EV sample grouping due to specificity in coding-gene sequences.

Q14. I am confused by the phrasing in the last two sentences of the top paragraph on page 7. Why would apoptotic bodies all have similar content if they encapsulate a greater amount of material making their contents less specific? Please clarify.

A14. This sentence intended to convey the fact that apoptotic bodies (ABs) are formed from apoptotic cells, they are larger in size, and their content is more non-specific - this non-specific nature arises as they do not encapsulate molecules specifically, unlike the other two types of vesicles. For more detailed information on ABs in human reproduction, we published an extensive review in 2018 (see below).

Simon C, Greening DW, Bolumar D, Balaguer N, Salamonsen LA, Vilella F. Extracellular Vesicles in Human Reproduction in Health and Disease. Endocr. Rev. 2018 Jun 1;39(3):292-332. doi: 10.1210/er.2017-00229. PMID: 29390102.

Q15. The first and last sentences of the last paragraph of page 8 seem to contradict each other. Please clarify.

A15. We observe an enrichment in the amount of mitochondrial DNA in samples during the receptive and post-receptive phases. While the data may not show statistical significance, we observed a trend towards greater enrichment in receptivity compared to pre-receptivity. The lack of significant differences could be attributed to inherent variability among patients. We have also altered the text on page 8 to avoid confusion.

Q16. Quantification of the rates of DNA incorporation into embryos would strengthen Figure 4 and Supplementary Figure 5.

A16. We acknowledge the reviewer's feedback, and in response, we conducted an assay to quantify the total DNA incorporated into the embryos. We isolated EVs from the control Ishikawa cell culture media and EdU-treated Ishikawa cell culture media to achieve this. Subsequently, we co-incubated both types of EVs with ten embryos overnight in G2 plus media at 37ºC and 5% CO2.

After co-incubation, we collected embryos and the culture media containing co-incubated EVs. We then isolated total DNA using the QIAamp® DNA Mini kit (Qiagen; 51304). To label the EdU-DNA particles, we performed a click-it reaction using the Click-iT™ EdU Alexa Fluor™ 488 flow cytometry assay Kit (Thermo Fisher Scientific, ref: C10420) per the manufacturer's instructions. Subsequently, we cleaned and purified DNA using AMPure beads XP (Beckman Coulter, A63882) and eluted DNA in 150 L of 0.1 M Tris-EDTA. Finally, we measured the fluorescence of each sample using a Victor3 plate reader (PerkinElmer). To ensure accuracy, we subtracted the background signal from non-labeled DNA-derived EVs and embryos incubated without EVs for each sample. Despite conducting the experiment twice, we encountered challenges in obtaining clear results, possibly due to the limitation of the technique's resolution.

Q17. If mtDNA is most enriched in MVs but only embryos cultured with Exos demonstrated differences in respiration the authors need to comment on this discrepancy.

A17. We ask the reviewer to refer to Answer A3; we have thoroughly revised the manuscript, focusing our message on DNA content.

Q18. The authors should change the definitive language in the title of the manuscript because all evidence presented is correlative.

A18.We have modified the title to better align with the manuscript's results. The proposed new title for the manuscript is “Vertical transmission of maternal DNA through extracellular vesicles modulates embryo bioenergetics during the periconceptional period.”

Q19. I realize this is beyond what the authors intend for the scope of this paper, however, on page 6 the authors describe membranous structures within the ABs but say they couldn't study their presence with organelle-specific markers. Why? Presence of organelles in these vesicles is very interesting!

A19. As the reviewer rightly points out, we did not study ABs in this manuscript. Analysis of the electron microscopy images suggests the presence of fragments of organelles, most likely originating from apoptotic processes; however, we did not use any specific markers to confirm our assertion. We have modified the text to avoid any confusion. Please see Page 6, Lines 120-121, for further details.

Author Response

We thank the reviewers and editorial team for the positive reaction to our paper and for the constructive recommendations and comments on our work. Here we provide a brief provisional response to key points that were identified. We will give a detailed point-by-point response with highlighted changes in our manuscript when we upload the revised version of our paper.

Reviewer 1:

Statistical evaluation of the null

In Experiment 2, we inferred the existence of a null effect of image category on suppression depth based on frequentist statistics. At the reviewer’s suggestion we performed a statistical evaluation of the evidence in favour of the null effect using a Bayesian repeated measures ANOVA implemented in JASP. That analysis provides strong evidence for the null (BF01= 20.38) and will be included in the final version of the paper.

Likelihood of exceptional cases

We acknowledge that our selection of categories is only a sampling of possible categories to which our novel tCFS method can be applied for deriving suppression depth. Other possibilities that come to mind include objects that emerge from specific configurations of simple 'tokens' such as dots (such as actions defined by biological motion (Watson et al., 2004)) or different shaped tokens configured to generate pareidolia faces (Zhou et al., 2021). We will expand on the possibility of these exceptional cases impacting bCFS and reCFS thresholds in the discussion of our revised manuscript.

Reviewer 2:

In response to the claim “the paper overreaches by claiming breakthrough thresholds are insufficient for drawing certain conclusions about subconscious processing.”

We agree that breakthrough thresholds can provide useful information to draw conclusions about unconscious processing – as our procedure is predicated on breakthrough thresholds. Our key point is that breakthrough provides only half of the needed information and will amend our manuscript accordingly. In so doing, we will also shift our focus toward the influence of semantics and low-level factors, including discussion of the possibility that suppression depth and bCFS thresholds could be driven by statistically orthogonal factors.

Reviewer 3:

On the appropriateness of log-transformed contrast

Our motivation to quantify suppression depth after log-transform to decibel scale was two-fold. First, we recognised that the traditional use of a linear contrast ramp in bCFS is at odds with the well-characterised profile of contrast discrimination thresholds which obey a power law (Legge, 1981) and the observations that neural contrast response functions show the same compressive non-linearity in many different cortical processing areas (e.g.: V1, V2, V3, V4, MT, MST, FST, TEO. See Ekstrom et al., 2009). Increasing contrast in linear steps could thus lead to a rapid saturation of the response function, which may account for the overshoot that has been reported in many canonical bCFS studies. For example, in Jiang et al. (2007), target contrast reached 100% after 1 second, yet average suppression times for faces and inverted faces were 1.36 and 1.76 seconds respectively. As contrast response functions in visual neurons saturate at high contrast, the upper levels of a linear contrast ramp have less and less effect on the target's strength. This approach to response asymptote may have exaggerated small differences between stimulus conditions and may have inflated some previously reported differences. In sum, the use of a log-transformed contrast ramp allows finer increments in contrast to be explored before saturation, a simple manipulation which we hope will be adopted by our field.

Second, by quantifying suppression depth as a decibel change, we enable the comparison of suppression depth between experiments and laboratories, which inevitably differ in presentation environments. As a comparison, a reaction-time for bCFS of 1.36 s cannot easily be compared without access to near-identical stimulation and testing environments. In addition, once ramp contrast is log-transformed it effectively linearises the neural contrast response function. This means that different studies that use different contrast levels for masker or target can be directly compared because a given suppression depth (for example, 15 dB) is the same proportionate difference between bCFS and reCFS regardless of the contrasts used in the particular study.

We also acknowledge that different stimulus categories may engage neural and visual processing associated with different contrast gain values (e.g., magno- vs parvo-mediated processing). But the breaks and returns to suppression of a given stimulus category would be dependent on the same contrast gain function appropriate for that stimulus which thus permits their direct comparison. Indeed, this is why our novel approach offers a promising technique for comparing suppression depth associated with various stimulus categories (a point mentioned above). Viewed in this way, differences in actual durations of break times (such as we report in our paper) may tell us more about differences in gain control within neural mechanisms responsible for processing of those categories.

Consider that preferential processing could shift both bCFS and reCFS thresholds together

This is related to the point raised in the previous comment. A stimulus that is preferentially processed (such as a face) could have lower bCFS and reCFS thresholds than other stimuli such that it emerges into awareness at a lower contrast but also remains visible at lower contrasts. We plan to address this interpretation of our data in our revised discussion and highlight that this type of preferential processing could well occur, and yet could still produce the same uniform suppression depth.

Can the effect of contrast ramp be explained by slower RTs?

A 500 ms reaction time estimate would not account for the magnitude of the changes observed in Experiment 3. Suppression depths in our slow, medium, and fast contrast ramps were 9.64 dB, 14.64 dB and 18.97 dB, respectively (produced by step sizes of .035, .07 and .105 dB per video frame at 60 fps). At each rate, assuming a 500 ms reaction time for both thresholds (1 second total) would capture a change of 2.1 dB, 4.2 dB, 6.3 dB. This difference cannot account for the size of the effects observed between our different ramp speeds.

Non-zero switch rate probability affecting ramping

We agree that for a given ramp speed there is a variable probability of a switch in perceptual state for both bCFS and reCFS portions of the trial. To put it in other words, for a given ramp speed and a given observer the distribution of durations at which transitions occur will exhibit variance. We see that variance in our data (just as it’s present in conventional binocular rivalry duration histograms), as a non-zero probability of switches at very short durations (for example). One might surmise that slower ramp speeds would afford more opportunity for stochastic transitions to occur and that the measured suppression depths for slow ramps are underestimates of the suppression depth produced by contrast adaptation. Yet by the same token, the same underestimation would occur during fast ramp speeds, indicating that that difference may be even larger than we reported. In our revision we will spell this out in more detail, and indicate that a non-zero probability of switches at any time may lead to an underestimation of all recorded suppression depths.

In our data, we believe the contribution of these stochastic switches are minimal. Our current Supplementary Figure 1(d) indicates that there is a non-zero probability of responses early in each ramp (e.g. durations < 2 seconds), yet these are a small proportion of all percept durations. This small proportion is clear in the empirical cumulative density function of percept durations, which we include in Author response image 1, and will address in our detailed response. Notably, during slow-ramp conditions, average percept durations actually increased, implying a resistance to any effect of early stochastic switching. We plan to expand on our analysis of these reaction-time differences in our revised manuscript.

Author response image 1.

The specificity of the DHO fit

In our revised manuscript we will increase the justification for this model, and plan to include a comparison of model fits over time (as opposed to response number in the current manuscript).

References

Ekstrom, L. B., Roelfsema, P. R., Arsenault, J. T., Kolster, H., & Vanduffel, W. (2009). Modulation of the contrast response function by electrical microstimulation of the macaque frontal eye field. The Journal of Neuroscience: The Official Journal of the Society for Neuroscience, 29(34), 10683–10694.

Jiang, Y., Costello, P., & He, S. (2007). Processing of invisible stimuli: advantage of upright faces and recognizable words in overcoming interocular suppression. Psychological Science, 18(4), 349–355.

Legge, G. E. (1981). A power law for contrast discrimination. Vision Research, 21(4), 457–467.

Watson, T. L., Pearson, J., & Clifford, C. W. G. (2004). Perceptual grouping of biological motion promotes binocular rivalry. Current Biology: CB, 14(18), 1670–1674.

Zhou, L.-F., Wang, K., He, L., & Meng, M. (2021). Twofold advantages of face processing with or without visual awareness. Journal of Experimental Psychology. Human Perception and Performance, 47(6), 784–794.

Author Response

The following is the authors’ response to the current reviews.

Comment. “The manuscript demonstrates that FGF4, FGF8, and FGF9 exhibit distinct binding modes towards FGFRs”

No, this paper is not about ligand binding, and there are NO binding data in the manuscript. This paper is about ligand-dependent functional bias. Previously, differential effects of ligands on the signaling of one FGFR have been attributed to differences in ligand binding, but that paradigm is incomplete, if not incorrect. This manuscript is the first demonstration that three FGF ligands induce bias in FGFR1 signaling. FGF8 preferentially activates some of the probed downstream responses (FRS2 phosphorylation and extracellular matrix loss), while FGF4 and FGF9 preferentially activate different probed responses (FGFR1 phosphorylation and growth arrest). The bias we report here cannot be the result of differences in ligand binding. Indeed, if the differences between ligands are only in the binding strength, then a strongly binding ligand at low concentration will act identically to weakly binding ligand at high concentration. Our article thus changes the current paradigm about how FGF ligands activate FGFR signaling.

Comment. It is also proposed that FGF8 exhibits "biased ligand" characteristics.

We do not “propose” the existence of ligand bias, we demonstrate it in the manuscript by following the latest IUPHAR community guidelines on bias identification and quantification (Kolb et al, 2022). We calculate bias coefficients, and we analyze the results using statistical tools.

Comment. …“Unproven and speculative structural differences in the FGF-FGFR1 dimers”.

This statement is not correct, as it is directly contradicted by the differences reported in Figure 6. This Figure presents the results of a quantitative FRET assay performed at high ligand concentration, which ensures that there are no monomeric receptors. Under these conditions, the measured FRET efficiency depends only on the dimer conformation. The measured differences in FRET efficiencies reveal distinct differences in the FGFR1 TM domain dimer conformations when FGF8 is bound to the extracellular domain of FGFR1, as compared to FGF4 and FGF9. The difference can be observed in the raw FRET data in Figure 6A. While these data do not reveal the exact molecular origin of the structural differences, they unequivocally prove that there are structural differences when different ligands are bound.

References

Kolb P, Kenakin T, Alexander SPH, Bermudez M, et al. Community guidelines for GPCR ligand bias: IUPHAR review 32. Br J Pharmacol. 2022;179, 3651-3674.

The following is the authors’ response to the previous reviews.

eLife assessment. This manuscript describes useful data on the mechanisms underlying the activation of the receptor tyrosine kinase FGFR1 and stimulation of intracellular signaling pathways in response to FGF4, FGF8, or FGF9 binding to the extracellular domain of FGFR1. Solid quantitative binding experiments are presented to demonstrate that FGF4, FGF8, and FGF9 exhibit distinct binding affinities towards FGFRs.

No, this paper is not about binding, and there is NO binding data in the manuscript. This paper is about function. This is the first demonstration that three FGF ligands induce bias in FGFR1 signaling. Thus far, differential effects in the signaling of one FGFR have been attributed to differences in ligand binding, but this current paradigm is incomplete/incorrect. Our article changes the current paradigm in how FGF activate downstream FGFR signaling.

We have clarified this point by adding the following text in the Discussion.

"Thus far, differential effects in the signaling of one FGFR in response to different FGF ligands have been attributed to differences in ligand binding. It can be reasoned, however, that differences in ligand binding strengths, alone, cannot explain differential signaling. Indeed, if the differences between ligands are only in the binding strength, then a strongly binding ligand at low concentration will act identically to weakly binding ligand at high concentration. Here we discovered, using tools that are novel for the RTK field, that there are qualitative differences in the actions of the ligands. FGF8 preferentially activates some of the probed downstream responses (FRS2 phosphorylation and collagen loss), while FGF4 and FGF9 preferentially activate different probed responses (FGFR1 phosphorylation and growth arrest). These effects occur in addition to previously measured differences in ligand binding coefficients (87).”

We have also re-written the abstract.

“Abstract

“The mechanism of differential signaling of multiple FGF ligands through a single FGF receptor is poorly understood. Here, we use biophysical tools to quantify multiple aspects of FGFR1 signaling in response to FGF4, FGF8 and FGF9: potency, efficacy, bias, ligand-induced oligomerization and downregulation, and conformation of the active FGFR1 dimers. We find that the three ligands exhibit distinctly different potencies and efficacies for inducing responses in cells. We further discover qualitative differences in the actions of the three FGFs through FGFR1, as FGF8 preferentially activates some of the probed downstream responses (FRS2 phosphorylation and extracellular matrix loss), while FGF4 and FGF9 preferentially activate different probed responses (FGFR1 phosphorylation and cell growth arrest). Thus, FGF8 is a biased ligand, when compared to FGF4 and FGF9. Förster resonance energy transfer experiments reveal a correlation between biased signaling and the conformation of the FGFR1 transmembrane domain dimer. Our findings expand the mechanistic understanding of FGF signaling during development and bring the poorly understood concept of receptor tyrosine kinase ligand bias into the spotlight.”

Reviewer #1 (Public Review):

Comment. Quantitative binding experiments presented in the manuscript demonstrate that FGF4, FGF8, and FGF9 exhibit distinct binding affinities towards FGFRs.

This paper is not about binding, and there is NO binding data in the manuscript. This paper is about function. Please see our response to the Elife assessment.

Comment. It is also proposed that FGF8 exhibits "biased ligand" characteristics that is manifested via binding and activation FGFR1 mediated by "structural differences in the FGF- FGFR1 dimers, which impact the interactions of the FGFR1 transmembrane helices, leading to differential recruitment and activation of the downstream signaling adapter FRS2".

We do not “propose” the existence of ligand bias, we demonstrate it in the manuscript by following the latest IUPHAR community guidelines on bias identification and quantification (Kolb et al, 2022). Specifically, we construct bias plots, we calculate bias coefficients, and we analyze the results using statistical tools.

Also, please note that ligand bias has no direct connection to binding strength, so the statement that biased ligand characteristics “is manifested via binding” is not correct.

Comment. In the absence of any structural experimental data of different forms of FGFR dimers stimulated by FGF ligands the model presents in the manuscript is speculative and misleading.

Figure 6 presents the “structural experimental data”. A quantitative FRET assay is performed at high ligand concentration, which ensures that there are no monomeric receptors. Under these conditions, the measured FRET efficiency depends only on the dimer conformation. The measured FRET efficiencies reveal distinct differences in the FGFR1 TM domain dimer conformations when the ligand FGF8 is bound to the extracellular domain of FGFR1, as compared to the cases of FGF4 and FGF8.

Because the Rosetta modeling of the kinase domains in the previous version of the paper is not based on experimental data, we have removed the modeling from the Results, and we have removed all references to it in the Discussion. Thus, all that is shown and discussed in the revised paper is based on experimental data.

We have substituted two paragraphs in the discussion with the following two sentences:

“The experimental data in Figure 6 hint at the possibility that ligand bias arises due to differences in FGFR1 dimer conformations. If this is so, then conformational differences in the signaling complex in the plasma membrane underlie biased signaling for both RTKs and GPCRs, the two largest receptor families in the human genome”.

References

Kolb P, Kenakin T, Alexander SPH, Bermudez M, et al. Community guidelines for GPCR ligand bias: IUPHAR review 32. Br J Pharmacol. 2022;179, 3651-3674.

Author Response:

Reviewer #1:

Summary:

This research study utilizes a realistic motoneuron model to explore the potential to trace back the appropriate levels of excitation, inhibition, and neuromodulation in the firing patterns of motoneurons observed in in-vitro and in-vivo experiments in mammals. The research employs high-performance computing power to achieve its objectives. The work introduces a new framework that enhances understanding of the neural inputs to motoneuron pools, thereby opening up new avenues for hypothesis testing research.

Strengths: The significance of the study holds relevance for all neuroscientists. Motoneurons are a unique class of neurons with known distribution of outputs for a wide range of voluntary and involuntary motor commands, and their physiological function is precisely understood. More importantly, they can be recorded in-vivo using minimally invasive methods, and they are directly impacted by many neurodegenerative diseases at the spinal cord level. The computational framework developed in this research offers the potential to reverse engineer the synaptic input distribution when assessing motor unit activity in humans, which holds particular importance. Overall, the strength of the findings focuses on providing a novel framework for studying and understanding the inputs that govern motoneuron behavior, with broad applications in neuroscience and potential implications for understanding neurodegenerative diseases. It highlights the significance of the study for various research domains, making it valuable to the scientific community.

Weaknesses: The exact levels of inhibition, excitation, and neuromodulatory inputs to neural networks are unknown. Therefore the work is based on fine-tuned measures that are indirectly based on experimental results. However, obtaining such physiological information is challenging and currently impossible. From a computational perspective it is a challenge that in theory can be solved. Thus, although we have no ground-truth evidence, this framework can provide compelling evidence for all hypothesis testing research and potentially solve this physiological problem with the use of computers.

We agree with the reviewer. This work was intended to determine the feasibility of reverse engineering motor unit firing patterns, using neuron models with a high degree realism. Given the results support this feasibility, our model and technique will therefore serve to construct new hypotheses as well as testing them.

Reviewer #2:

The study presents an extensive computational approach to identify the motor neuron input from the characteristics of single motor neuron discharge patterns during a ramp up/down contraction. This reverse engineering approach is relevant due to limitations in our ability to estimate this input experimentally. Using well-established models of single motor neurons, a (very) large number of simulations were performed that allowed identification of this relation. In this way, the results enable researchers to measure motor neuron behavior and from those results determine the underlying neural input scheme. Overall, the results are very convincing and represent an important step forward in understanding the neural strategies for controlling movement.

Nevertheless, I would suggest that the authors consider the following recommendations to strengthen the message further. First, I believe that the relation between individual motor neuron behavioral characteristics (delta F, brace height etc.) and the motor neuron input properties can be illustrated more clearly. Although this is explained in the text, I believe that this is not optimally supported by figures. Figure 6 to some extent shows this, but figures 8 and 9 as well as Table 1 shows primarily the goodness of fit rather than the actual fit.

We agree with the reviewer that showing the relationship between the motor neuron behavioral characteristics (delta F, brace height etc.) and the motor neuron input properties would be a great addition to the manuscript. Because the regression models have multiple dimensions (7 inputs and 3 outputs) it is difficult to show the relationship in a static image. We thought it best to show the goodness of fit even though it is more abstract and less intuitive. We added a supplemental diagram to Figure 8 to show the structure of the reverse engineered model that was fit (see Figure 8D).

Author response image 1: Figure 8. Residual plots showing the goodness of fit of the different predicted values: (A) Inhibition, (B) Neuromodulation and (C) excitatory Weight Ratio. The summary plots are for the models showing highest 𝑅2 results in Table 1. The predicted values are calculated using the features extracted from the firing rates (see Figure 7, section Machine learning inference of motor pool characteristics and Regression using motoneuron outputs to predict input organization). Diagram (D) shows the multidimensionality of the RE models (see Model fits) which have 7 feature inputs (see Feature Extraction) predicting 3 outputs (Inhibition, Neuromodulation and Weight Ratio).

Second, I would have expected the discussion to have addressed specifically the question of which of the two primary schemes (push-pull, balanced) is the most prevalent. This is the main research question of the study, but it is to some degree left unanswered. Now that the authors have identified the relation between the characteristics of motor neuron behaviors (which has been reported in many previous studies), why not exploit this finding by summarizing the results of previous studies (at least a few representative ones) and discuss the most likely underlying input scheme? Is there a consistent trend towards one of the schemes, or are both strategies commonly used?

We agree with the reviewer that our discussion should have addressed which of the two primary schemes – push-pull or balanced – is the most prevalent. At first glance, the upper right of Figure 6 looks the most realistic when compared to real data. We thus would expect that the push-pull scheme to dominate for the given task. We added a brief section (Push-Pull vs Balance Motor Command) in the discussion to address the reviewer’s comments. This section is not exhaustive but frames the debate using relevant literature. We are also now preparing to deploy these techniques on real data.

In addition, it seems striking to me that highly non-linear excitation profiles are necessary to obtain a linear CST ramp in many model configurations. Although somewhat speculative, one may expect that an approximately linear relation is desired for robust and intuitive motor control. It seems to me that humans generally have a good ability to accurately grade the magnitude of the motor output, which implies that either a non-linear relation has been learnt (complex task), or that the central nervous system can generally rely on a somewhat linear relation between the neural drive to the muscle and the output (simpler task).

We agree with the reviewer, and we were surprised by these results. Our motoneuron pool is equipped with persistent inward currents (PICs) which are nonlinear. Therefore, for the motoneuron to produce a linear output the central nervous system would have to incorporate these nonlinearities into its commands.

Following this reasoning, it could be interesting to report also for which input scheme, the excitation profile is most linear. I understand that this is not the primary aim of the study, but it may be an interesting way to elaborate on the finding that in many cases non-linear excitation profiles were needed to produce the linear ramp.

This is a very interesting point. The most realistic firing patterns – with respect to human data – are found in the parameter regions in the upper right in Figure 6, which in fact produce the most nonlinear input (see push-pull pattern in Figure 4C). However, in future studies we hope to separate the total motor command illustrated here into descending and feedback commands. This may result in a more linear descending drive.

Author Response

The following is the authors’ response to the original reviews.

We thank all the reviewers for their comments and constructive feedback regarding our manuscript. We have made many changes to strengthen the manuscript, including addition of two new experiments (presented in Fig. S1) that help to clarify the nature and scope of activation of late response genes in striatal neurons. Our specific responses to individual reviewer comments are provided below.

Reviewer #1

Public review

Weaknesses: The timing and the location of the accessibility changes are meaningfully different from other similar studies, which should be discussed. The authors provide good data for the function of a single enhancer near Pdyn, but could contextualize this with respect to other regulatory elements nearby.

In the revised manuscript, we have expanded our discussion of the differences between chromatin accessibility changes observed in this study and those found in prior reports in different systems. These differences are also addressed in extended detail below. Unfortunately, limitations on resources and time prevented a deeper exploration of additional candidate enhancers near the Pdyn locus. However, we believe our efforts to characterize an activity-dependent enhancer in the Pdyn locus provides a useful starting point, and future studies may seek to more completely define the contributions of nearby regulatory elements.

Recommendations For The Authors

1) At 1hr after stimulation in previous papers (Su 2017 which is reference #8 of FernandezAlbert Nat Neurosci. 2019 October ; 22(10): 1718-1730.) there are large increases in accessibility directly over the IEGs, consistent with the concerted transcription of these genes following stimulation. It is surprising that the authors do not see this here, either at 1hr or at 4hr. This difference in results needs to be addressed.

We thank the reviewer for bringing this discrepancy to our attention. Indeed, Su et al. 2017 and Fernandez-Albert et al. 2019 both describe increases in chromatin accessibility at IEG promoters. There are several experimental differences that could be contributing to differences between our study and previously published studies. Two major reasons include the developmental timepoint of the tissue/cells and the cell type/brain region that is being assayed. Su et al. assayed chromatin accessibility in ex vivo slices containing the dentate gyrus from adult mice, while Fernandez-Albert et al. assayed chromatin accessibility in forebrain principal neurons of adult mice following kainic acid injection. Bulk ATAC-Seq experiments described in the present manuscript were generated from cultured embryonic rat striatal neurons. Additionally, baseline chromatin accessibility seems to be significantly different between forebrain principal neurons studied in Fernandez-Albert et al. 2019 and the current study. For example, in Figure 3a of Fernandez-Albert et al. 2019, the Npas4 gene body is not accessible in a saline treated animal. In vehicle treated, cultured embryonic rat striatal neurons, the Fos gene body and associated enhancers are accessible at baseline (Fig. S3), and do not increase with KCl depolarization.

We have expanded our discussion of this discrepancy in the discussion section of the revised manuscript, and included additional citations addressing this difference.

2) It is also somewhat surprising that the authors see almost no regions that show changes in accessibility at 1hr and then a very large number of differentially accessible regions at 4hr. This is quite different from the more rapid changes shown for example in Figure 7f in the human GABA neurons even though these are also studies in culture with rapid calcium channel opening. Can the authors speculate on the reason for the difference?

Many previously published studies that use cultured neurons include a pre-treatment in which spontaneous neuronal activity is inhibited with the sodium channel blocker tetrodotoxin (SanchezPriego et al. Cell Reports, 2022; Kim et al. Nature, 2010; Malik et al. Nature Neuroscience, 2014). The Sanchez-Priego et al. Cell Reports manuscript also blocked NMDA receptor activity with the competitive NMDAR antagonist D-AP5 for 12 hours prior to depolarization. Rapid changes in chromatin accessibility observed in other studies at <1 hour timepoints could be due to prior silencing of the cells and subsequent reduction in the accessibility and transcriptional activity of IEGs. Decreased baseline accessibility and transcriptional activity of IEGs can be observed in Figure 1a of Malik et al. 2014, which displays ChIP-Seq tracks for both RNA pol II and H3K27ac. At baseline, H3K27ac and RNA pol II enrichment is low throughout the Fos locus. Subsequent depolarization of silenced neurons drives accessibility and transcription of the Fos gene and associated enhancers. In contrast, we found accessible chromatin at Fos enhancer elements at baseline (without stimulation; Fig. S3).

The experiments described in the current study do not include any pre-treatment with tetrodotoxin or D-AP5, and thus the neurons are expected to be spontaneously active. This baseline electrophysiological activity may result in increased accessibility and transcription at IEG loci, which ultimately makes it difficult to identify activity-dependent increases in IEG accessibility at timepoints <1 hour. Furthermore, a previously published manuscript from our lab (Carullo et al. Nucleic Acids Research, 2020) conducted ATAC-seq on cultured embryonic rat cortical, hippocampal, and striatal neurons and found that transcribed enhancers for IEG loci (including Fos) had decreased chromatin accessibility following depolarization when compared to vehicle treatment. These differences in experimental design (including cell type, model organism, developmental timepoint, and treatment paradigm) may all contribute to differences in the temporal dynamics of chromatin remodeling between the current manuscript and previously published studies.

3) Experimentally it can be challenging to repress a single enhancer and show a significant effect on gene regulation which makes the repression in Fig 6c somewhat unexpected. There are several regions near Pdyn that show activity-dependent changes in accessibility in the human cells (Fig. 7e) and presumably in the rat neurons too (Fig. 5a shows a few but most of the intervening region is cut out). Did the authors target any of these other regions?

We chose the identified regulatory element upstream of the Pdyn TSS because it met several criteria that we determined are important for characterizing LRG enhancers. These criteria are outlined in the Results: “1) located in non-coding regions of the genome, 2) inaccessible at baseline and accessible following depolarization, and 3) inaccessible when depolarization was paired with protein synthesis inhibition.” Indeed, ATAC-seq experiments presented in the current study demonstrate that thousands of genomic regions undergo reprogramming, and many of these regions meet these criteria (including additional loci near Pdyn). However, we lacked the time and resources to systematically investigate all other enhancers, and did not target any other regions within the Pdyn locus. While many enhancers may regulate a single gene, the identified enhancer seems to be particularly important for activity-dependent Pdyn gene expression. Importantly, CRISPRi-based repression of this enhancer (Fig. 6c) did not reduce basal Pdyn expression as compared to a non-targeting control, but completely blocked stimulus-dependent induction of Pdyn transcription. We believe this is a useful starting point, and future studies may seek to more completely define the contributions of nearby regulatory elements.

4) The authors should clarify in the methods or figure legends the number of independent replicate libraries for each experiment and were the RNA and ATAC libraries made from the same or different experiments.

We thank the reviewer for bringing this to our attention. We have clarified the number of replicates in the methods as outlined below. Additionally, RNA and ATAC libraries were generated from different experiments, and this information is also now included in the methods.

Within the ATAC-Seq library preparation and analysis methods section: “ATAC-seq libraries were generated from experiments independent of the RNA-seq experiments. For the ATAC-seq experiment of neurons treated with vehicle or KCl for 1 h, there were 3 replicates within each treatment group (3 Veh, 3 KCl). For the ATAC-seq experiment of neurons treated with vehicle or KCl for 4 h, there were 3 replicates within each treatment group (3 Veh, 3 KCl). For the ATAC-seq experiment of neurons pre-treated with DMSO or Anisomycin, there were 4 replicates within each treatment group (4 DMSO + Veh, 4 DMSO + KCl, 4 Anisomycin + KCl).”

Within the RNA-seq library preparation and analysis methods section: “RNA-seq libraries were generated from experiments independent of the ATAC-seq experiments. For the RNA-seq experiment of neurons treated with vehicle or KCl for 1 h, there were 3 replicates within the KCl group and 4 replicates within the vehicle group. For the RNA-seq experiment of neurons treated with vehicle or KCl for 4 h, there were 4 replicates within each group (4 Veh, 4 KCl).”

Reviewer #2

Public review

First of all, at a conceptual level, most of the findings related to the induction of particular transcriptional programs upon neuronal activation the changes in chromatin state, and the need for protein translation for proper induction of LRGs have been broadly characterized previously in the literature (Tyssowski et al., Neuron, 2018; Ibarra et al., Mol. Syst. Biol., 2022; and also reviewed by Yap and Greenberg, Neuron, 2018). In addition, it is not so obvious why to focus on Pdyn gene regulatory regions among the thousands of genes upregulated and with modified chromatin landscape after neuronal activation. The authors highlight three particular traits of this gene as the reason to choose it, but those traits are probably shared by most of the genes that are part of the LRGs set.

We thank the reviewer for these comments, and have included these important publications as citations in our manuscript. With over 5,000 differentially accessible chromatin regions following KCl stimulation, it was not possible to follow up on all regulatory regions or linked genes in a rigorous way. Therefore, we selected a target candidate enhancer near the Pdyn locus for mechanistic studies. In addition to the criteria highlighted in the manuscript, we chose this locus due to decades of literature establishing the importance of prodynorphin in the striatum, and the role of this gene in human neuropsychiatric diseases. We would argue that this increases the relevance of more detailed exploration of this gene, and makes our results applicable to a broader pre-existing literature.

At the methodological level, some attention should be put into the timings chosen for generating the data. The authors claim that these time points (1h and 4hrs) identify the first (i.e IEGs) and second (i.e LRGs) waves of transcription. However, at 4hrs the highest over-expressed genes are still IEGs, as shown in the volcano plots of Figure 1B and 1C, showing a high overlap with up-regulated genes found at 1h (Figure 1D). This might suggest that the 4hrs time point is somewhere in between the first and second wave of transcription, probably missing some of the still-to-be-induced LRGs of the latest one.

Given that the depolarization applied in RNA-seq and ATAC-seq experiments is continuous, it was not unexpected to find IEGs present at both 1 h and 4 h timepoints. The revised manuscript contains a new experiment (Fig. S1d-f) demonstrating that a shorter depolarization period (1 h KCl followed by a 3 h wash off period) also induces Fos mRNA, but to a much lower extent than 4 h continuous stimulation. In contrast, both short (1 h) and long (4 h) depolarization periods induce Pdyn to equivalent levels when measured at 4 h after the onset of the stimulus. These experiments support our conclusion that LRGs require a temporal delay, and not simply extended stimulation. Nevertheless, the reviewer is correct that a 4 h timepoint may potentially miss some LRGs that are induced even later. We plan to explore the full timecourse of LRG induction in future studies.

Finally, while only prosed as a suggestion, the assumption that from the data generated in this article, we can envision a mechanism by which AP-1 family of transcription factors interacts with the SWI/SNF chromatin remodeling complex is going too far, as no evidence is provided implicated SWI/SNF in the data presented in the manuscript.

While speculative in the current context, we felt that it was important to highlight this prior literature to identify potential mechanisms that may link IEGs (specifically, AP-1 members) to chromatin remodeling machinery. We have altered this section of the discussion to emphasize that this link is speculative in the context of neuronal chromatin remodeling.

Recommendations For The Authors

1) I couldn't find the number of replicates generated for each dataset, neither for RNA nor for ATAC-seq. It could be worth adding these data to the figure legends or in the material and methods.

We thank the reviewer for bringing this to our attention. The number of replicates generated for each dataset are now included in the methods section (see response to Reviewer #1, comment #4 above).

2) In Figure 1D, Gene Ontology terms appear significant only for each of the individual datasets. While this might be expected for the 1h time-point, the 4hrs time-point comprises a big extent of the genes up-regulated at 1h as well, and it is surprising no term related to chromatin or transcription regulation appears as significant. Is this due to the fact that the analysis has been conducted with two separated lists of genes and only the top terms are shown without crossing the data? This could be misleading for the reader and maybe a comparative GO term analysis might be better such as using CluterProfiler or similar tools, that might allow for real comparison of terms enriched in each dataset.

We thank the reviewer for pointing this out. For Figure 1d, GO term analysis was conducted with two separated gene lists, each consisting of timepoint-specific upregulated DEGs. Thus, 772 genes were included for the analysis of 4 h GO terms and 39 genes were included for the analysis of 1 h GO terms. Previously, comparisons of cellular component GO terms included in the current study only included the top 10 GO terms. The revised manuscript contains an updated analysis that compares all enriched GO terms and identifies that three of the top 10 cellular component GO terms for the 1 h gene set are also identified as significantly enriched in the 4 h gene set. We have revised the graph in Fig. 1f to reflect this updated analysis. Overall, our conclusions (that 1 h and 4 h DEG sets fall into distinct functional categories) remains supported by this analysis.

3) In Figure 3D, the graphs show the density of motifs within the DARs in units of "Motifs/Kb/peak" while the x-axis represents the peaks coordinates from -500bp to +500bp. It is not clear to me how this graph is generated and how within 1000bp the profiles can reach values of 18-20 Motifs/Kb/peak. Could this be clarified?

The motif enrichment score was calculated by identifying the number of total motifs within defined 50bp genomic bins surrounding the center of the DAR regions. HOMER builds enrichment histograms that normalize motif presence to set size (e.g., number of peaks or DARs), and also to genomic space (base pairs). While HOMER’s default histogram represents motifs/bp/peak, we converted this to motifs/kb/peak for ease of interpretation. However, to avoid confusion we have returned the y axis labels to the default HOMER settings (motifs/bp/peak). The normalization and units for this graph have been clarified in the methods section.

4) In Figure 4C the newly generated ATAC-seq data is just "targeted" analyzed, showing global tendencies are maintained between the initial generated data and this one. It could be interesting, however, to see the number of DARs obtained in these conditions, especially to see if some DARs are observed in the Anisomycin condition that might be translation-independent.

The experiment described in Figure 4 was designed to both validate the 5,312 DARs and understand the role of protein translation in activity-dependent chromatin remodeling. One way to begin identifying translation-independent DARs is to compare the DMSO + Vehicle group to the Anisomycin + KCl group. With this comparison, any 4 h DAR that has increased accessibility in the Anisomycin + KCl group may be translation-independent as pretreatment with anisomycin did not prevent chromatin remodeling. After conducting this analysis, we identified a very small percentage (3.44%) of 5,312 4 h DARs that still exhibited significantly increased accessibility when pre-treated with Anisomycin. This small number is consistent with the robust effects of anisomycin on KCl-dependent remodeling shown in Fig. 4c-d. However, to confirm that these were in fact translation-independent activity-regulated DARs, we would need to perform direct comparison of chromatin accessibility between neurons pre-treated with Anisomycin and then treated with either vehicle or KCl. Since we did not include an anisomycin only group in experiments in Fig. 4, we cannot confidently claim whether this 3.4% of DARs are translationindependent. Nevertheless, we agree with the reviewer that this is an interesting avenue of future exploration.

Reviewer #3

Public review

1) Throughout the paper, the authors emphasize a "temporal decoupling" of transcriptional and chromatin response to depolarization, based on a lack of significant chromatin changes at 1h, despite IEG transcription. However, previous publications show significant chromatin remodeling at 1h (e.g. Su et al., NN 2017 in adult dentate gyrus) or 2h (Kim et al., Nature 2010; Malik et al., NN 2014 in cultured embryonic cortical neurons). The discussion briefly mentions this contrast, but it remains difficult to conclude decisively whether there is temporal decoupling when such decoupling is not found consistently. If one is to make broad conclusions about basic neural chromatin response to depolarization, it would be ideal to know under which conditions there is temporal decoupling, or if this is a region-specific phenomenon.

Indeed, prior studies referred to in our manuscript have identified chromatin remodeling at earlier timepoints than we identified here. As addressed above (Reviewer #1, comments 1 & 2), it is possible that this discrepancy arises due to the difference in experimental model system, differences in the type of stimulation applied, pretreatment protocols used to silence neurons prior to activation, or even differences in developmental stage. Differences in each of these parameters make it difficult to make straightforward comparisons between datasets and results in this manuscript. It is possible that other cell types induce IEGs more quickly (or more robustly) in response to stimulation, which could lead to earlier chromatin remodeling. However, the common patterns of chromatin reorganization (e.g., the fact that changes are enriched at AP-1 motifs and are found in intergenic regions at putative enhancers) lend support for the idea that the transcriptional waves identified here can also be found in other cell types and in other contexts.

2) The UMAP analysis is a novel way to probe transcription factor enrichment, but it's unclear what this is actually showing. The authors sought to ask whether "DARs could be separated based on transcription factor motifs in these regions." However, the motifs present in any genomic stretch are fixed based on genomic sequence, so it seems like this analysis might be asking whether certain motifs are more likely to be physically clustered together in the genome, in activity-regulated regions (rather than certain transcription factors acting in concert, as is implied in discussion). While still potentially interesting, this analysis does not seem to give much additional insight into activity-dependent chromatin remodeling beyond the motif enrichment analysis already performed. Nevertheless, to draw stronger conclusions, it would be necessary to compare clustering to a random set of genomic regions of the same length/size to interpret the clustering here. It would also be useful to know whether the ISL1 motif is also enriched in ubiquitously accessible genomic regions in the striatum (and not just DARs).

We agree that additional analysis is needed to explore enrichment of various transcription factor motifs and activity at differently accessible regions of the genome. The motif enrichment analysis in Figure 3 demonstrated the types of motifs that were enriched in DARs (Fig. 3a-c), the overall degree of enrichment (Fig. 3c), and the distribution of those motifs across DAR sites (Fig. 3d). This analysis allowed us to understand whether motifs for cell-defining transcription factors like ISL1 are enriched uniquely in DARs, or are also found in other regions that are accessible at baseline (see direct comparisons between vehicle/baseline peaks and DARs in Fig. 3d). However, these approaches represent enrichment across all DARs as group, and do not show TF presence/absence at any specific DAR. The UMAP analysis presented in Figure 3e allowed identification of DAR clusters based on the presence or absence of specific transcription factor motifs, and allowed us to represent specific DARs in a reduced two-dimensional space. Because this analysis identifies the existence of distinct motifs within single DARs, it allowed us to speculate as to the possibility of transcription factor cooperation within DARs, or the meaning of DAR clusters that appear to be defined by specific motifs (e.g., KLF10 in Fig. 3f). Given the information that this adds to the initial analyses, we argue that its inclusion in the manuscript is useful and potentially informative for generating follow-up hypotheses.

3) The authors identify late-response gene enhancers by 3 criteria. However, only Pdyn was highlighted thereafter. How many putative DARs met these three criteria in striatum? Only Pdyn?

As illustrated in Figures 2 and 4, nearly all of the DARs in our dataset met these criteria, which included presence in non-coding genomic regions, increase in accessibility following stimulation, and prevention of chromatin accessibility changes by protein synthesis inhibition. We did not mean to indicate that the Pdyn locus was unique in this way. In addition to the criteria highlighted in the manuscript, we chose this locus due to decades of literature establishing the importance of prodynorphin in the striatum, and the role of this gene in human neuropsychiatric diseases. We would argue that this increases the relevance of more detailed exploration of the regulator mechanisms that control expression of this gene, and makes our results applicable to a broader pre-existing literature. The revised manuscript includes additional experiments that examine Pdyn expression changes in response to different stimuli, which help to justify the focus on this gene from the beginning of the manuscript.

Recommendations For The Authors

1) Figure 1 volcano plots show a scatter primarily in the up-regulated portion at both the 1-h and 4-h time points. However, the Venn diagrams show largely similar numbers of up- and downregulated genes at the 4-h time point. Is the clustering of down-regulated genes tighter/more overlapping? If so, semi-translucent volcano dots or some acknowledgment of the visual discrepancy would be useful.

We thank the reviewer for bringing this to our attention. Down-regulated genes are clustering tighter on the volcano plot due to smaller fold changes. This visual discrepancy is acknowledged by the numeric indicators of up- and down-regulated genes in the upper left-hand corner of the volcano plot.

2) Methods for RNA and ATAC seq analysis align to human genome Hg38, rather than rat?

RNA- and ATAC-Seq analyses from rat neurons were aligned to the mRatBn7.2/Rn7 rat genome. RNA- and ATAC-Seq analyses from human neurons were aligned to the Hg38 human genome. We have updated the methods to make this clear.

3) The introduction states that different classes of neurons induce distinct LRGs. Please add a citation. Citations are also needed for the last statement WRT consequences of chromatin remodeling near LRGs not being concretely linked to LRG transcription.

We thank the reviewer for pointing this out. The revised manuscript now includes additional citations supporting each of these statements.

4) Specify somewhere in Methods that DEGs were compared to vehicle for both 1-h and 4-h (and not 4 vs 1 h).

We thank the reviewer for bringing this to our attention. We have updated the methods to include: “DEGs were calculated by comparing the KCl and Vehicle treatment groups at each respective timepoint.”

5) In Figure 2E, why are the enrichments exactly opposite, especially given these are two different types of input (all baseline peaks vs DARs)?

Odds ratios were calculated by comparing baseline peaks (i.e., ATAC-seq peaks identified in vehicle treated cells) to KCl-induced DARs. This allowed us to identify the enrichment of DARs in specific genomic annotations in comparison to the genomic features that are accessible at baseline, rather than making comparisons to random probe sets or genomic space dedicated to these distinct annotations. This analysis identified that relative to baseline peaks, DARs are significantly depleted in coding regions of the genome and enriched in non-coding regions of the genome. However, given this analysis we agree that it does not make sense to graph both the vehicle (baseline) and DARs on this graph, given that enrichment of each set is determined relative to the other (creating the reciprocal enrichment in this panel). We have updated Fig. 2e to only include points for 4 h DARs.

6) Some references are off. One that I noted was "...chromatin remodeling in the mouse dentate gyrus following 1 h of electricoconvulsive stimulation" should be Su et al 2017 not Malik 2014. For the statement that IEGs are critical regulators of non-neuronal IEGs, the authors may want to add Hrvatin 2017 ref.

We thank the reviewer for bringing this to our attention. We have revised the manuscript to include the correct citation for this claim, and also to incude the Hrvatin, et al reference.

7) It would be helpful for the authors to write out the whole gene name for Pdyn somewhere.

We have updated the text to include the gene name for Pdyn, both in the abstract and also in the introduction of the manuscript.

8) Figure 5f: For ease, please include what is high vs low in the figure caption in addition to the main text.

We thank the reviewer for bringing this to our attention. We have updated the figure caption and main text to include what is high vs low in Pseudotime estimates in Fig. 5f.

9) How are the tracks ordered in Fig8c?

Tracks within Fig. 8c demonstrate snATAC-seq signal at the Pdyn gene locus for transcriptionally distinct cell types within the NAc. The tracks are ordered by cluster size (nuclei number) in the snATAC-seq dataset.

Author Respose

The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review):

The authors prepared several Acinetobacter baumannii strains from which an essential protein of known or unknown function can be depleted. They chose to study one of the proteins (AdvA) in more detail. AdvA is a known essential cell division protein that accumulates at cell division sites together with other such proteins. No clear homologs are present in model bacteria such as E.coli, and the precise role(s) of AdvA is still unclear. The authors rename AdvA here as Aeg1. The authors searched for suppressors of lethality caused by AdvA-depletion and recovered an allele of ftsA (E202K) that is capable of doing so. Based on similar superfission alleles previously recovered in other division genes in E.coli, they test several mutant genes and find that certain alleles in ftsB, L and W can also suppress lethality of AdvA-minus cells.

In addition, the authors perform bacterial two-hybrid assays and protein sublocalization studies of AdvA and of other division proteins, but the results of these studies are either not new (confirming previous work) or not convincing.

We appreciate the vigor of this reviewer.

We agreed that the essentiality of AdvA/Aeg1 described in our submission is not new, we believed our work has firmly established its role as a cell division protein. The earlier work by the labs of Geisinger and Isberg labs (1) showed its essentiality and the cell morphology changes upon its depletion (Fig. 3 of ref. 1 in the end of this rebuttal letter). This protein was one of the many proteins addressed in their study and their results only suggests its role in cell division due to the close phenotypical relationships between AdvA/Aeg1 and genes associated with chromosome replication/segregation and cell division.

Reviewer #2 (Public Review):

In this study the authors confirm that one of the genes classified as essential in a Tn-mutagenesis study in A. baumannii is in fact an essential gene. It is also present in other closely related Gram-negative bacteria and the authors designated it Aeg1. Depletion of Aeg1 leads to cell filamentation and it appears that the requirement for Aeg1 can be suppressed by what appear to be activation mutations in various genes. Overall, it appears that Aeg1 is involved in cell division but many of the images suffer from poor quality - it may be due to conversion to PDF. One of the main issues is that depletion of Aeg1 is carried out for such long times (18 hr) (Fig. 2, 4 and 5). Depleting a cell division protein for such long times may have pleiotropic effects on cell physiology. A. baumannii grows quite fast and even with a small inoculum, cells will probably be in stationary phase. If Aeg1 is that essential cells should be quite filamentous 2-3 hours after Ara removal when they are still in exponential phase. Also, it would be better to see the recovery to small cells if cells are not grown such a long time before Ara is added back. Overall, Aeg1 is potentially interesting, but studies are needed to define its place in the assembly pathway for this to be published. What proteins are at the division site when Aeg1 is depleted and what proteins are required for Aeg1 to localize to the division site. These experiments should be done when cell are depleted of proteins for only 1 -2 hours.

We appreciate these insightful suggestions and have followed them to make necessary modifications in the revised manuscript, including:

1st, We have redone the experiment for Fig. 1C to obtain images of higher resolution.

2nd, We have more carefully examined the kinetics of the depletion of Aeg1-mCherry upon removal of the inducer arabinose from medium. We first evaluated the protein of Aeg1-mCherry at 2, 4, and 6 h after withdrawing arabinose and found that at the 2 h and 4 h time points mCherry-Aeg1was still readily detectable (Fig. S4). Importantly, we found that removal of arabinose for 6 h rendered Aeg1-mCherry undetectable in approximately 90% of the cells. We thus used the 6 h inducer depletion to examine the effects of Aeg1 depletion.

In experiments aiming to analyze the co-localization of Aeg1 with other core divisome proteins, cultures of strains derived from Δaeg1(PBAD::mCherry-Aeg1) harboring the GFP fusions were induced by ara for 16 h. The saturated bacterial cultures were then diluted into fresh LB broth without ara for 6 h to induce the elongation morphology. IPTG (0.25 mM) and ara (0.25%) were added to induce the expression of fusion proteins for 4 h before samples were processed for microscopic analysis. Our results indicate that Aeg1 colocalized with ZipA, FtsK, FtsL, FtsB, and FtsW (Fig. 4C), which is consistent with results from the protein interaction experiments using the bacterial two-hybrid assay.

To determine the impact of Aeg1 depletion on cellular localization of the several core cell divisome proteins. In cells in which Aeg1 had been depleted (by removing the inducer arabinose), all of the examined core division proteins displayed midcell mistargeting, including ZipA, FtsK, FtsB, FtsL, and FtsN (Fig. 5A).

Reviewer #1 (Recommendations For The Authors):

Specific remarks 1) The manuscript title is misleading in that the 'novel cell division protein' studied in this paper has already been identified as such, and studied in some detail, by the Geisinger and Isberg labs (refs 37 and 20).

We agreed with this point. Because of the data presented by Geisinger and Isberg labs (1) that demonstrated its essentiality and morphological changes upon its depletion (Fig. 3 in ref 1), we have changed the title to “A unique cell division protein critical for the assembly of the bacterial divisome”.

2) The Isberg/Geisinger labs named this division protein AdvA in 2020 (ref 37). The authors of the present manuscript should follow this terminology, as there is no compelling reason to rename the protein Aeg1 here. It will only confuse the field.

We named this protein Aeg1 because we identified and named it before the work by Geisinger and Isberg labs (1) was published and this name has been used in all of our records. In addition, this is a part of our research exploring hypothetical essential genes in A. baumannii and we thus would like to keep the name in this manuscript.

3) Membrane topology of AdvA? Line 103-104: The authors predict a single transmembrane domain in AdvA (Aeg1). However, reference 37 predicted two, and some prediction programs (e.g. CCTOP) predict three with the N-terminus periplasmic. A good understanding of the membrane topology of AdvA is important, if not only for the design of credible BACTH two-hybrid assays. Figure 6 indicates that the authors assume that the N-terminus of AdvA is periplasmic with the bulk of the protein cytoplasmic. But then they choose to use pKT25::AdvA for two-hybrid assays, which would place the CyaA T25 domain periplasmic as well. This should not yield faithful interaction data as both the T25 and T18 domains need to be cytoplasmic to restore CyaA activity.

The Bacterial Adenylate Cyclase-Based Two-Hybrid (BACTH) technique is a powerful tool for studying protein-protein interactions, especially those involving integral membrane or membrane-associated proteins. It overcomes the limitations of traditional two-hybrid systems by allowing the detection of interactions that occur within the membrane or in other difficult-to-study protein environments (2). This method has been successfully used to analyze the relationships among bacterial cell division proteins (e.g., ref 3 and 4). Furthermore，our results from bacterial two-hybrid and immunofluorescence techniques are consistent. As a result, the results presented here should be valid.

4) Strains and plasmids, Table S4 Far more detail is needed. a) Please provide complete genotypes of strains and, especially, of the plasmids used, including replication origin, antibiotic resistance markers, promoters, promoter repressors, inducible genes/fusions to be expressed, and the placement of genetic tags (T25, T18, XFP, Flag, etcetera).

We have added the information to Table S4.

b) In addition, provide details on how each strain/plasmid was constructed in the Methods section or as supplement. Currently, you only provide some details on one or two of the strains or plasmids.

We have added the necessary details about how the constructs and plasmids used in this study were made.

5) Lines 114-129, Fig 2. AdvA is needed for cell division. a) Similar results were already described by refs 37 and 20, so this is merely confirmatory.

We revised the description accordingly.

b) Refs 37 and 20 should be referenced here, as well as in the section above where you find AdvA to be essential for viability on rich medium.

We have added the appropriate reference as suggested.

c) The micrographs in panel C are of poor quality. Consider higher magnification and resolution.

We have redone the experiments and images of higher resolution have been used in the revised manuscript.

6) Lines 130-143, selection for suppressors of AdvA-depletion. I would expect quite a few mutations in araC repressor on the plasmid in this screen, rendering the promoter more constitutive (i.e. arabinose-independent). Did these not appear?

This is an interesting point. Unfortunately, we did not recover suppression mutants which mutations on araC or other elements of the BAD promoter. Given the complexity of AraC-mediated regulation (5), such mutants likely are rare or we did not screen enough candidates.

7) Lines 173-178, Fig3E. Sublocalization of AdvA-mCherry. a) The micrographs in Fig. 3E are very poor and I can not see any specific localization, or barely any signal whatsoever, of the AdvA-mCherry fusion. Thus, this result is not convincing

We have replaced this image with a new one of higher-resolution.

b) In contrast, accumulation of an AdvA-GFP fusion at constriction sites was already clearly and convincingly shown in ref 37.

We have revised the text to reflect this fact.

c) So, this section needs convincing images, as well as a reference to ref 37.

We have added an image of higher resolution and revised the text accordingly. Thank you

8) Lines 179-188, Fig4a-b. BACTH assays

a) As noted above (see point 3), the T25-AdvA fusion would likely place the T25 domain in the periplasm, casting doubt on the validity of these results.

b) Similarly, the T18-ZipA fusion would place the T18 domain in the periplasm, casting further doubt.

The Bacterial Adenylate Cyclase-Based Two-Hybrid (BACTH) technique is a powerful tool for studying protein-protein interactions, especially those involving integral membrane or membrane-associated proteins. It overcomes the limitations of traditional two-hybrid systems by allowing the detection of interactions that occur within the membrane or in other difficult-to-study protein environments (2). This method has been successfully used to analyze the relationships among bacterial cell division proteins (e.g., ref 3 and 4). Furthermore，our results from bacterial two-hybrid and immunofluorescence techniques are consistent. As a result, the results presented here should be valid.

9) Lines 189-201, Fig4c, co-localization of proteins in AdvA-depleted filaments. These co-localization results are not convincing for several reasons:

a) None of the proteins accumulate in specific ring-like structures, as might be expected for ZipA, at least. One possible reason is that division rings are not made at all due to the partial depletion of AdvA in these cells. But another possible reason is that some or all the fusions are simply non-functional. Do any of these proteins (co-)localize to the septal ring in wt cells?

b) At least for the GFP-ZipA fusion, there is good reason to predict it is not functional, as correct membrane insertion of the fusion would place GFP in the periplasm. In E. coli this prevents GFP from becoming fluorescent in the first place. So the fluorescence seen here may reflect failure of the fusion to insert properly.

c) Another possible reason for rings being absent is that the fusions are massively overexpressed. The plasmids are multicopy, the BAD and TAC promoters are strong, and the used levels of inducers (Ara and IPTG) are high. How do fusion levels compare to that of native proteins? Perhaps some of the bright spots we see are inclusion bodies or other types of non-specific protein aggregates.

We appreciate these excellent suggestions and have carried out experiments to investigate the (co-)localization of these proteins at the septal ring in Δaeg1 cells under conditions of low-level inducers (Ara and IPTG) and reduced induction time.

Cultures of strains derived from Δaeg1(PBAD::mCherry-Aeg1) harboring the GFP fusions were induced by ara for 16 h, saturated bacterial cultures were then diluted into fresh LB broth without ara for 6 h to induce the elongation morphology. IPTG (0.2 mM) and ara (0.2%) were added to induce the expression of fusion proteins for 4 h before samples were processed for microscopic analysis. Consistent with results from the protein interaction experiments using the bacterial two-hybrid assay, Aeg1 colocalized with ZipA, FtsK, FtsL, FtsB, and FtsW (Fig. 4C). Thus, Aeg1 interacts with multiple core cell divisome proteins of A. baumannii.

In cells of the wild-type A. baumannii strain, we have observed cell elongation upon overexpression of FtsL, FtsB, FtsW, or FtsN. This raises concerns regarding the physiological relevance of the results obtained in wild-type cells. Of note, the phenotype of cell elongation following overexpression of division proteins has been observed in Escherichia coli by several groups (6-11).

10) Lines 202-214, Fig5a, localization of division proteins in AdvA-depleted filaments. These localization results are not convincing for the same reasons outlined above (see point 9).

a) Do any of the fusions localize correctly under similar expression conditions, but in normally dividing cells?

In wild-type A. baumannii cells, cell elongation occurs upon overexpression of FtsL, FtsB, FtsW or FtsN, which raises the concern that the results from the suggested experiments may not physiologically relevant.

b) Even the regular structures seen with GFP-FtsZ do not resemble rings, but appear more like blobs. Perhaps fixation with glutaraldehyde would preserve structures better?

We have followed the suggestion to use glutaraldehyde fixation for cell fixation. The new images have been used in the revised manuscript.

11) Other points:

a) Line 97, Fig1. Is AdvA essential on minimal medium (~ slow growth) as well?

We have performed this experiment. Yes, AdvA/Aeg1 is essential for A. baumannii growth in the Vogel-Bonner minimal medium with succinate (VBS) as the sole carbon source (12) (Fig S1).

b) Fig1. What residues are actually missing (or replaced?) in the delta-TM version of AdvA?

We have added the information, residues 1-23 have been removed.

c) Fig1D. Also, the delta-TM version of HA-AdvA runs slower than HA-AdvA itself. Why?

We have also been puzzled by this phenomenon that full-length AdvA/Aeg1 migrated faster than the delta-TM mutant. Interestingly, this discrepancy did not occur when the proteins were expressed in E. coli (see Author response image 1). We do not have a good explanation for this phenomenon.

Author response image 1.

The expression of the Aeg1 and Aeg1∆TM in A. baumannii and E. coli. Total proteins resolved by SDS-PAGE was probed by immunoblotting with the HA-specific antibody. The metabolic enzyme isocitrate dehydrogenase (ICDH) was probed as a loading control. Similar results were obtained in three independent experiments.

d) Lines 159, 165 and elsewhere. The mutation in E. coli is actually FtsA(R286W), not Q286W.

We have corrected this error. Thank you!

e) Line 161. These alleles of ftsA should be referenced properly: ref 33 for I143L and ref 29 for E124A.

We have made the correction. Thank you!

f) Line 692, you incorrectly switched the two CyaA domains here.

We have corrected this error.

g) Fig4b. Is 'none' a vector control (pUT18C-Flag)?

We have specified the control, it is the vector pUT18C-Flag.

h) Lines 727-729. I don't understand this sentence. Please explain.

We have revised this sentence.

Reviewer #2 (Recommendations For The Authors):

Line 159 and Fig. 2 Panel D. I am not sure that this panel should be in the paper for two reasons: 1) FtsA from E. coli and A. baumannii are only 50% identical and its not clear that one can make corresponding mutations and expect similar behavior. FtsA* from E. coli is R286W not Q286W. R286 does not appear to be conserved in A. baumannii. Also, what you label as Q286 appears to be Q285. Please check. 2) the alleles that are tested in this panel do not rescue the deletion of Aeg1. This may be due to the instability of the mutant proteins. It would be better to characterize the mutant that you have isolated - is it a superfission mutation; that is does it produce small cells in a strain that contains WT Aeg1?

Thank you! We have more carefully examined the relevant sites in these proteins. We did not observe the small cell phenotype when FtsAE202K was overexpressed in WT strains (please see Author response image 2).

Author response image 2

The overexpression of FtsAE202K did not cause a small cell phenotype in A. baumannii. Bacterial strains derived from WT (Ptac::FtsAE202K) grown in LB broth overnight were diluted into fresh medium with the inducer and the cultures were induced with IPTG for 4 h prior to being processed for imaging (A). Total proteins were resolved by SDS-PAGE and proteins transferred onto nitrocellulose membranes were detected by immunoblotting with the HA-specific antibody. ICDH was probed as a loading control (B, right panels). Images were representatives of three parallel cultures. Bar, 10 µm.

The images in Fig. 3, Panel C are quite poor (perhaps the original images [not PDF] are better). It is difficult to see the localization.

We have redone the experiments and replaced the images with ones of higher resolution.

Fig. 4. Panel C. This is an effort to show that Aeg1 colocalizes with known cell division proteins. Since in Fig. 3, panel C it is claimed that Aeg1 localizes to the division site, them it must colocalize with known division proteins. Doing the long term depletion of Aeg1 is likely causing artefacts. The localization of proteins seems very erratic. A better experiment would be to express the GFP fusions to the known proteins and then deplete Aeg1 and see what happens. Does depletion of Aeg1 prevent the localization of FtsZ, FtsK or FtsN? Another important question is if one of the known cell division proteins is depleted does Aeg1 localize to division sites. Since it is speculated that Aeg1 interacts with ZipA and FtsN, these proteins could be depleted and see if Aeg1 localizes.

We greatly appreciate your insightful suggestions. We have carefully redone these experiments as follows: Each of the testing strains was grown in LB broth with ara overnight prior to being diluted into fresh medium without ara for 6 h to induce the elongation morphology. IPTG (0.25 mM) and ara (0.25%) were added to induce the expression of fusion proteins for 4 h before samples were processed for microscopic analysis. Consistent with results from the protein interaction experiments using the bacterial two-hybrid assay, we observed that Aeg1 colocalized with ZipA, FtsK, FtsL, FtsB, or FtsW (Fig. 4C).

In cells not expressing Aeg1, all of the examined core division proteins including FtsZ, FtsK, and FtsN displayed midcell mistargeting, (Fig. 5A).

As for the localization of Aeg1 upon depleting ZipA or FtsN, this is an ongoing project in our lab. Such information is beyond the scope of this manuscript.

Fig. 5. Panel A. again the images are not of good quality. Also, why deplete for 18 hrs. This is too long.

We have redone these experiments and images of higher resolution are now used in the revised manuscript. After extensive test, we have chosen to use a 6-h depletion, which gave us the window to observe the phenotype (Fig. 5A).

Line 25. Change 'so' to 'as'

Corrected as suggested. Thank you!

Line 28. "Induces' to 'induce'

We have made the suggested correction. Thank you!

Line 43. Change 'of' to 'with'

Corrected as suggested. Thank you!

Line 74. Change 'determine' to 'test'

Corrected as suggested. Thank you!

Line 89. Delete 'of the'

We have made the suggested correction. Thank you!

Line 102. Some strains of E. coli? Does that mean there are strains that do not contain Aeg1? What are they?

Yes, this is indeed the case, the common strains of E. coli derived from strain K12 does not have a discernable homolog of aeg1. This gene is present in some clinic E. coli isolates (e.g. HAY5567682, HBI862710, HAY5567682, MDD9849866, EFE8345364, and KAE9874289).

Line 112. Note this TM domain has a rare topology as it is similar to ZipA. Please mention that this is a Type 1b.

We have made the suggested revision. Thank you!

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Author Response

The following is the authors’ response to the original reviews.

We thank the reviewers for their generous comments on the manuscript and have made edits to address their concerns. The manuscript has been restructured and the reference (PMID: 35738428) has been added to the review. We addressed the reviewer's comment below.

Reviewer #1 (Recommendations For The Authors):

Regarding SBSMMA, the authors may complement their discussion by mentioning recent work (PMID: 35738428) where SBSMMA was used to exemplify a potential fragment-based design approach for developing allosteric effectors for kinases.

Thank you for the suggestion, we have added a short summary of the work where SBSMMA is used as a basis for developing small molecules to target kinases using fragment-based design approach.

Author Response

The following is the authors’ response to the original reviews.

We would like to thank you and the two reviewers for their constructive feed-back on our manuscript entitled: "Substrate evaporation drives collective construction in termites".

Here, we submit a revised version in which -we believe- we fill the missing details identified by the reviewers and we clarify the presentation of our results.

From the eLife assessment we can identify a few main points that the reviewers found unclear or not well developed in our previous manuscript:

• Insufficient details about computer simulation models. Is the match between simulations and experiments qualitative or quantitative?

• Request for clarifications related to the wall stimulus: is evaporation stronger at the high-curvature wall corners or similar along all the wall edge? Why is there less consistency in the experimental results with the wall stimulus, with a minority of wall experiments in which something different happens?

• Quantitative estimation of the humidity gradients in our experimental setup.

• "Confirmation" that termites can sense humidity gradients of magnitude and scale comparable with those encountered in our experiments.

• Request for additional background information about the considered termite species and their construction habits.

The reviewers also made a number of interesting suggestions and other comments:

• Suggestion of possible explanations and interpretations for a purported discrepancy with a previous work by Calovi and collaborators.

• Suggestion of alternative experimental approaches (array of probes, alternative experimental setups).

We address all these points below.

Details about computer simulation models

There are two different types of computer simulations in our experiments: 1. simulations of evaporation on the initial structure, and 2. simulations of structure growth based on curvature.

1) Simulations of evaporation We recall that these simulations rely on the hypothesis that humidity transport happens in a diffusive way, that is evaporation rate is proportional to the humidity gradient. New details on the implementation of these diffusive simulations are now added in section S.VI. We also adapted figures 4A and 4B which are now expressed in units more comparable to the expected humidity field in experiments. Essentially, we show that the model under-estimates the absolute magnitude of the humidity gradient |∇ℎ| in our setup while it correctly predicts the relative importance of the same field across the topography.

First, it is instructive to report the value of |∇ℎ| predicted by diffusive simulations with the bottom boundary at 100% humidity (like the clay disk), and the top boundary of the simulation box at 70% like our experimental room. Note that, at a given temperature, relative humidity and absolute humidity are proportional, so we will assume here that temperature is constant and always refer to relative humidity. Thus, humidity gradient will be measured in 𝑚𝑚−1 exactly like curvature. One than has:

• flat disk, |∇ℎ| ∼0.01mm−1

• wall tips, |∇ℎ| ∼0.13mm−1

• wall top edge |∇ℎ| ∼0.1mm−1

• pillar tips |∇ℎ| ∼0.19mm−1,

First we remark, that the value of |∇ℎ| on the flat portion of the disk is 10 times smaller of the estimation |∇ℎ|0 ∼0.5mm−1 of the same quantity in our experiments, which is now given in the manuscript and discussed in a specific paragraph below. This discrepancy is due to the fact that our simulations overestimate the size of the diffusive region (i.e. the simulation box) to 18mm while we expect the diffusive layer to be much thinner (i.e. 𝛿 ∼2mm). Note also that, as in all diffusive problems, the humidity gradient on any point of the bottom boundary (i.e. on the clay surface) depends on the distance of that point from the top boundary, for example the closer are the boundaries the stronger is the gradient. This is a very general feature of diffusive problems: the gradient of the diffusing field depends on the distance from the boundaries, where the value of the field is given. Note also that, in principle, the size of the simulation box does not only affect the overall magnitude of the humidity gradient but also its shape. However, one observes that in our simulations the topographic cues are only 30% closer to the top boundary compared to the flat, bottom, surface, but the local gradient is 10 to 20 times larger. This evidence suggests that the ’curvature’ effect is much stronger than the ’distance’ effect, and supports the fact that our approximation does not affect in a significant way the estimation of the relative importance of the humidity gradient at the bottom surface. We then conclude that our diffusive simulations do not provide a correct estimation of the order of magnitude of |∇ℎ|, but well capture its relative variations across the topography.

2) Structure growth based on curvature. As observed by the reviewer, the dynamical simulations included here refer to a model that was developed in a previous study, thus we chose to not include all the details of the simulations in the present one. At this stage, that model is still phenomenological: for example we cannot provide a physical estimation of the dimensionless parameter 𝑑 which controls the typical size of the structure produced by the simulations of the model. Thus in principle, the comparisons with real experiments cannot be other than "qualitative". Indeed, to push such a comparison further is not necessarily of interest, given the minimal and mean field character of our model, and the extreme complexity of the natural system which is studied here. However, our experimental setup was specifically designed to overcome this limit, which is designing topographies where the curvature cues where modulated in a way which is almost discrete, with flat regions, and regions where curvature is strong ’for termites’, i.e. the curvature radius is of the order of termite body size. Our experimental results greatly validate our choice because deposition patterns also show an almost ’discrete’ shape, with specific regions attracting most of the depositing actions. Thus, we claim that the significance of the agreement is strong, and we suggest that when stimuli and response both behave in a quasi-discrete manner, the difference between qualitative and quantitative is not well defined. Finally, we recall that in all the discussion above curvature and humidity gradient can be exchanged, as we already pointed out in the manuscript. Consistently, the humidity gradient show a strong variation between the curved regions and the flat ones.

Results with the wall stimulus One important point coming out from the reviews is that we did not clearly present the results with the wall stimulus. These concerns are best summarized by a comment from reviewer 2, who states: “evaporation rates seem inconclusive in the wall geometry, yet the termites still deposit material at the high-curvature wall corners”.

We acknowledge that the interpretation of results of experiments with the wall stimulus must address three key points: 1- Salt deposition experiment are inconclusive in showing variation of the evaporation rate, across the top of the wall; 2- A portion (4/11) of termite experiments do not show a clear pellet deposition pattern by termites; 3- Conversely, in the remaining portion (7/11), most experiments still show a clear pellet deposition on the corners of the wall, in spite of small differences in evaporation between the corners and the top edge (like in our Fig. 3B). These points are now addressed in the manuscript and discussed below.

The variation of the humidity gradient between the corners of the wall, and the wall’s top edge is relatively small while both are regions of relatively high curvature and higher evaporation as compared to the the flat surface of the clay disk. We now report precise values of the humidity gradient from numerical simulations, as discussed above. These indicate that humidity gradient at the wall corners and upper edge is respectively 10 and 7 times larger than on the flat bottom, but evaporation at the wall tips is only 0.3 times larger than on the wall upper edge.

Experiments with the saline solution qualitatively confirm the same result of an evaporation pattern more evenly distributed on the wall stimulus (point 1) than on the pillars.

Taken together, these results might explain why not all wall experiments end up with depositions at the tips (point 2): simply, in the wall experiments the relative importance of the deposition cue between tips and wall upper edge is not high enough to always guide termite behavior in a deterministic way.

But we should also point to the fact that the evaporation simulations presented in figure 4 and the experiments with the saline solution both reflect the humidity field on the clay templates before termite construction has started. As soon as termites start adding pellets to the wall, effectively starting to build a pillar, the humidity gradient will be reinforced at the locations of pellet deposition, and a self-reinforcing process is initiated, similar to our dynamical simulations based on local curvature. This explains why eventually termite activity can result in clear and localized depositions (point 3) also with the wall stimulus.

Incidentally, we would like to include here another consideration: the nest of Coptotermes termites comprise a “scaffold” with multiple interconnected pillars. In other termite genera, the prevalent nest structure is one made by surfaces, rather than pillars, such as in Nasutitermes nests, Apicotermes, Psammotermes, or again some fungus growing structures in Macrotermes and Synacanthotermes). The fact that the wall stimulus presents some potential to stimulate construction everywhere on its edge is intriguing as it might provide some cues on the construction of different nest architectures.

Quantitative estimation of the humidity gradient in our setup The moisture gradients in our experiments and simulations was only presented in a non-quantitative manner, because we were mainly interested in identifying locations of high and low evaporation. But, combining scaling arguments already discussed in S.IX and the the results of our evaporation simulations, one can produce a lower boundary for the magnitude of the humidity gradient |∇ℎ|, predict its higher value at key positions on our setup, and compare it with humidity variations experienced by termites in their natural environment. These considerations are now included in the manuscript and discussed below.

First, we define a reference value |∇ℎ|0 for the humidity gradient on the (flat) clay disk, which can be estimated using the boundary layer thickness 𝛿 ∼2mm (see section IX.A of the SI) and the variation of relative humidity Δℎ between the clay disk surface and the exterior which was Δℎ =30% (the difference between the fully wetted substrate, and room air humidity at 70% saturation). Note that |∇ℎ|0 constitutes a lower boundary for the expected values of the humidity gradient in our setup, as confirmed by our experiments with saline solution. We can then write:

Next, the results of diffusive simulations shown in figure 4A and 4B indicate that the humidity gradient at highly curved regions of the topographic cues is at least 10 times larger than |∇ℎ|0 which allows to estimate an upper boundary for |∇ℎ| in our experimental setup, say |∇ℎ|𝑚𝑎𝑥 ∼1mm−1. Humidity sensing capabilities of termites Our hypothesis that humidity gradients could guide termite building behavior implicitly assumes that termites can sense humidity gradients comparable with those existing in our experiments.

Humidity is important to all termites because of their small size and unsclerotized body. Coptotermes termites in particular are wetwood termites that can only survive in high-humidity environments such as moist wood or soil. It is well documented that coptotermes termites (like other termites and cockroaches) have humidity receptors in their antennae, and behavioral studies indicate that they can discriminate between chambers with different humidity content.

For example, a study by Gautam and Henderson (2011, Environmental entomology, 40:1232) provided chambers with different relative humidity and, after 12 hours, almost all termites were in the highest humidity chamber (98% RH), leaving the other chambers with 75% or less RH empty. These results (which are similar also to other results testing termite response to chambers with different soil moisture) indicate that -given a sufficient amount of time- termites can detect a difference of humidity from 75% to 98% over a spatial scale of centimeters.

The quantitative estimation of the humidity gradient described above indicates that in our experimental setup termites can experience humidity variations of 15% over a distance of only 1mm and even shorter, while the length of a single termite antenna is about 1.5 mm.

In other words, the humidity gradients that we estimate for our experiments are well above those that termites were able to discriminate in previous experiments. Future experiments should aim to test the exact limits of resolution of the humidity-sensing ability of termites (e.g. in an environment where humidity is close to 100% everywhere), and the mechanisms how they sense the gradient (e.g. comparing information from the two antennae, or by integrating humidity information over time).

By definition, |∇ℎ|0 corresponds to a variation of humidity between a fully saturated atmosphere (i.e. 100%), comparable to the nest interior, and a "humid" atmosphere (i.e. 70%) comparable to the natural environment where termites live (say the nest exterior), occurring over a distance (2mm) which is comparable with their body size.

We can then conclude that even the lower boundary |∇ℎ|0 of the humidity gradient corresponds to an atmosphere variation to which termites must be used, i.e. nest interior vs nest exterior, happening across one body length. If we add that the upper boundary |∇ℎ|𝑚𝑎𝑥 is one order of magnitude higher, it appears extremely unlikely that they could not detect these gradients.

Additional background information about our considered termite species and their construction habits

We have now added some details about the life history and nesting habits of termites in the Coptotermes genus in a new paragraph in section SI. Essentially, these are wetwood termites that nest in moist wood or soil, and their nests present a typical structure comprising a scaffold of interconnected pillars (we now show a picture of a typical structure from one of our lab-reared colonies).

After the initial submission of our manuscript we have also obtained a more precise taxonomic identification of the termites we used, which indicated that our termites are better identified as Coptotermes gestroi than Coptotermes formosanus. The two species are extremely close and can also interbreed in the areas where they co-occur, but in this case C. gestroi is a better match. Hence, we have amended the name in the manuscript and in the supplementary material.

Differences with previous results by Calovi and collaborators

We believe that there is no real discrepancy between our results and those described by Calovi et al. (2019, Phil. Trans. Roy. Soc. B 374:20180374). What they measure-termite aggregation and activity- is similar to what we also observe in our experiments: termites aggregate in concave regions, such as at the base of the wall in our experiments, and they collect pellets at the locations that they visit more often. And, above all, we observe that concavities promote digging activity, which in turns promote aggregation as already observed in previous studies like Green et al. (2017, Proc. Roy. Soc. B 284:20162730). The main difference is that in our analyses we treat separately the three measurements of termite occupancy, pellet collection and pellet deposition, and in this way we identify a role of convexity for pellet deposition.

It is possible that, apart from the differences in language and interpretations between our study and the study by Calovi, there were also real differences in termite building behavior between the two studies that we couldn’t fully appreciate from our own reading of the article by Calovi, but which the reviewer has spotted. The reviewer makes a very interesting suggestion that some of these differences might be due to the different humidity level used in our experiment, compared to the experiment by Calovi and collaborators. Room humidity was high, at around 70% in our experiments. The humidity in Calovi’s experiments was possibly even higher as they performed their experiments in a closed box, but we could not find precise reported information on the humidity level in their publication.

Given that it is not clear that the building behavior in our experiments was qualitatively different from the building behavior in Calovi and collaborators’ experiments, and given that we don’t know the precise humidity value used in Calovi’s experiments (plus, we worked on different termite species that could have different sensitivity to humidity) we decided that -based on the information that we have- we could not meaningfully expand our discussion of similarities and differences with Calovi’s study in our manuscript.

It is clear, though, and we completely agree with the referee on this point, that in light of Calovi’s and our own new results, it would now be extremely interesting if future experiments could characterize termite construction activity across a range of finely controlled air humidity values. Anecdotally, in preliminary experiments we did include some trials in which termites were hosted in a completely closed box, and we observed much reduced construction activity in those conditions. However, the fact that we could not easily track termite activity and pellet collections / depositions in those conditions (because of the box), together with the fact that the building activity itself was reduced, made us to converge towards the open arena experiments that we describe here.

Suggestion of alternative experimental approaches One reviewer made interesting suggestions for alternative experiments, including using an array of humidity probes for measuring humidity, or a different experimental setup -analogous to those used in previous experiments by Bardunias and collaborators-. It is often the case that only at the end of a series of experiments we identify an alternative, and possibly better, way of doing the same experiment. In future, if we have the opportunity to run other similar experiments again, we will likely experiment with these suggestions. When we first designed our own experiments, one of our priorities was to be able to film all termites in the arena at all time, so that potentially we could also study individual termite behavior and task specialization. This partly constrained the type of experimental setups that we could use.

One aspect that clearly emerged from our work and from the revision process is that any future experiments related to this topic should achieve a very precise control of air humidity, and test a wider range of stimuli of more varied and controlled size, humidity and curvature. Since our own experiments were conducted, three of us have moved to different institutions, which imposes practical constraints for us on working on the same termites in a similar way, but the suggestions from the reviewers will be helpful as we are planning our future research.

We hope that the explanations above and the details that we have changed in the manuscript itself have contributed to clarify unclear aspects of our study.

Author Response

The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review):

This work describes a structural analysis of the tripartite HipBST toxin-antitoxin (TA) system, which is related to the canonical two-component HipBA system composed of the HipA serine-threonine kinase toxin and the HipB antitoxin. The crystal structure of the kinase-inactive HipBST complex of the Enteropathogenic E. coli O127:H6 was solved and revealed that HipBST forms a hetero-hexameric complex composed of a dimer of HipBST heterotrimers that interact via the HipB subunit. The HipS antitoxin shows a structural resemblance to HipA N-terminal region and the HipT toxin represents to the core kinase domain of HipA, indicating that in HipBST the hipA toxin gene was likely split in two genes, namely hipS and hipT.

-The structure also reveals a conserved and essential Trp residue within the HipS antitoxin, which likely prevents the conserved "Gly-rich loop" of HipT from adopting an inward conformation needed for ATP binding. This work also shows that the regulating Gly-rich loop of the HipT toxin contains conserved phosphoserine residues essential for HipT toxicity that are key players within the HipT active site interacting network and which likely control antitoxin binding and/or activity.

Strengths:

The manuscript is well written and the experimental work well executed. It shows that major features of the classical two-component HipAB TA system have somehow been rerouted in the case of the tripartite HipBST. This includes the N-terminal domain of the HipA toxin, which now functions as bona fide antitoxin, and the partly relegated HipB antitoxin, which could only function as a transcription regulator. In addition, this work shows a new mode of inhibition of a kinase toxin and highlights the impact of the phosphorylation state of key toxin residues in controlling the activity of the antitoxin.

Weaknesses:

A major weakness of this work is the lack of data concerning the role of HipB, which likely does not act as an antitoxin. Does it act as a transcriptional regulator of the hipBST operon and to what extent both HipS and HipT contribute to such regulation? These are still open questions.

We thank the reviewer for their feedback and have included a supplementary figure (Figure 1 supplement 2) and accompanying text that shows the transcriptional role of HipB, and how HipS and HipT influence this regulatory effect.

In addition, there is no in-depth structural comparison between the structure of the HipBST solved in the work and the two recent structures of HipBST from Legionella. This is also a major weakness of this work.

A structural comparison to the recent structures from Legionella has now been included in the discussion, including Figure 6 supplement 1.

Reviewer #2 (Public Review):

The work by Bærentsen et al., entitled "Structural basis for regulation of a tripartite toxin-antitoxin system by dual phosphorylation" deals with the structural aspects of the control of the hipBST TA operon, the role of auto-phosphorylation in the activation and neutralisation of the enzyme and the direct effects of HipS and HipB in neutralisation. This is a follow-up to the Vang Nielsen et al., and Gerdes et al., papers from the same authors on this very unique TA module, that brings forth a thorough and well written dissection of an unusually complex regulatory system.

This is a much improved manuscript, the paper is more focused and the message is now clear.

Reviewer #1 (Recommendations For The Authors):

My main recommendation would be to include an in-depth structural comparison between the structure of the HipBST solved in the work and the two recent structures of similar HipBST from Legionella.

We thank the reviewer and have included a new supplementary figure (Figure 6 supplement 1) and expanded the comparison in the discussion to accommodate this.

Reviewer #2 (Recommendations For The Authors):

So I only have some minor comments.

1) The authors should accompany Fig.1 (a supplementary panel is sufficient) with a surface electrostatic representation of the complex to better illustrate the potential role of the complex in transcription auto-regulation.

We have included a new panel in Figure 1 supplement 3 to show the electrostatic surface of the DNA-binding domains of HipB of HipBST and HipBASo.

2) When the Gly-rich loop is first introduced, please provide from which residue to which residue the loop expands.

Corrected for both the first mention of the Gly-rich loop of HipA and HipT.

3) In Fig 2. The authors try to show how the interaction of the main helix of HipS with HipT is different in HipBST compared to HipAB. I think it would be helpful if these two panel show the surface of HipT and HipA coloured by electrostatics so that not only the differences in HipS become apparent, but also the local differences between both toxins.

We thank the reviewer for this excellent idea, and the electrostatics did in fact reveal that the region of the toxins are different. We have updated figure 2b to show this difference.

4) Fig. 4 Shows the experimental SAXS curves for the HipT D210Q variants SIS (blue), SID (red), and DIS (orange). In each case a black curve is fitted to the data (presumably the fitting of the model-derived scattering curve to the data). Could the authors clarify this in the figure?

We agree that this information is missing in the legend. The black curves are the fits for the models based on the crystal structure after rigid-body refinements and inclusion of a structure factor to account for oligomerization of the complexes. This is now included in the figure caption.

5) Also regarding the SAXS analysis, in the manuscript the authors state that all three models "gave good fits to the data" as assessed by the fitting χ2. These χ2 values should be explicit in the figure or the figure legend.

We thank the reviewer for this suggestion. The chi squared values for the best fits are now given in the text.

In addition, is the SAXS data (the parameters derived from the experimental scattering, including the MW) consistent with the lack of HipS from the complex? (it should be...).

This is a good point, however, the partial oligomerization (dimerization) of the complexes (heterohexamers) and the variation of the dimerization degree between samples prevent extraction of useful mass values from the I(0) determinations. Therefore, we decided not to give the values explicitly in the text but only state “…consistent with analysis of the forward scattering that revealed partial oligomerisation of the samples with an average mass corresponding to roughly a dimer of the HipBST heterohexamer.”

6) Please improve this sentence: "Moreover, since it has previously been shown that only the HipT Gly-rich loop never is observed in doubly phosphorylated form with both Ser57 and Ser59 modified simultaneously, it is unlikely that the effects are due to autophosphorylation of the remaining serine residue in either case (Vang Nielsen et al., 2019)."

Done

Author Response

We are happy that the novelty and strengths of the study have been appreciated by the editor/s and reviewer/s. We thank the editor/s and reviewer/s for a considerably detailed and constructive review of the manuscript. Here are the responses and proposed revisions from the authors.

• The weakness, as pointed out in the editorial comment regarding the absence of data on role of Piezo1 in migrating T cells in varying physico-chemical conditions were, in the opinion of the authors, beyond the scope of the present manuscript. Moreover, introducing external forces using invasive techniques followed by assessment of Piezo1 function was intentionally avoided. That was the reason for using the non-invasive microscopy technique like IRM to assess membrane tension generation in migrating T cells.

• With regard to the explanation sought for the statement 'these high tension edges are usually further emphasized at later time points', the edges are visible right from 1 min (Supp fig 2B) and seen to be emphasized at 30 min. In Fig 2D, we find the 3 min time point at which increased tension at edges is visible together with a clear difference in median tension too. Fig. 2c and Supp fig 2C are averaged over all cells - hence it is possible that at a time point when a particular cell still shows higher tension at edges the median tension of Fig 2C is not significantly different. Also, if only a thin section of cell-edge enhances tension - it may contribute to a second peak without affecting the median much.

• With regard to the query regarding experimental replicates, all data shown is derived from at least 3 experimental replicates for Jurkat cells or independent blood donors for primary CD4+ T lymphocytes as specified in the respective figure legends.

• With regard to the comments on nonavailability of representative images/videos for Figures 1 A and B, in the revised manuscript we will add representative video of GFP (-) and GFP (+) tracks. The transwell experiments were assessed by collecting cells from the bottom chamber followed by flow cytometry. We did not take microscopic images of the bottom chambers before collecting the cells.

Author Response

The following is the authors’ response to the original reviews.

We would like to thank the editor and all the reviewers for their time and thoughtful consideration of our manuscript. We appreciate the valuable comments. Our provisional response to the “public review” has been published and now we have corrected factual errors and enhanced the clarity of writings based on the “recommendations for the authors.” We believe these corrections will improve the quality and accuracy of our manuscript.

Specific responses to the reviewers' recommendations for the authors are as follows:

Reviewer #1 (Recommendations For The Authors):

1) Is the Slack current amplitude dependent on the Nav subtype? Differences in Slack current amplitude might explain the sensitization of Slack to quinidine.

We appreciate the reviewer for raising this point. We examined Slack current amplitudes upon co-expression of Slack with specific NaV subtypes in HEK293 cells. The results have shown that there are no significant differences in Slack current amplitudes upon co-expression of Slack with different NaV channel subtypes (Author response image 1), suggesting whole-cell Slack current amplitudes cannot explain the varied ability of NaV subtypes to sensitize Slack to quinidine blockade.

Author response image 1.

The amplitudes of Slack currents upon co-expression of Slack with specific NaV subtypes in HEK293 cells. ns, p > 0.05, one-way ANOVA followed by Bonferroni’s post hoc test.

2) Is the open probability changed by the presence of Nav1.6 and/or by the other Nav subtypes? Changes in open probability might explain the Nav1.6 induced sensitization of Slack to quinidine block.

We appreciate the reviewer for raising this point. To investigate the effect of different NaV channel subtypes on Slack open probability, we will perform the single-channel recordings in future studies.

3) Could the authors elaborate more on the coupling between INaT mediated sensitization of Slack to block by quinidine and the Nav1.6 N-and C-tail induced sensitization?

We appreciate the reviewer for raising this point. We fully agree the importance of investigating the detailed mechanism underlying the sensitization of Slack to quinidine blockade. To address the questions, we plan to employ structural biological methods, such as cryo-electron microscopy (cryo-EM).

4) Line 85: The authors use an outdated nomenclature of AMPAR subtypes. I would suggest changing to GluA1, GluA2, GluA3 and GluA4.

We appreciate the reviewer’s suggestion. We have changed the term “GluR” to “GluA” in the revised manuscript.

The authors do not explain the rationale by using the different homomeric AMPAR subtypes. Most often the AMPARs express as heteromeric receptors decorated by auxiliary subunits. Also, is the GluA2 the edited version?

We thank the reviewer for raising this point. While AMPARs are often expressed as heteromeric receptors with auxiliary subunits, we focused on the homomeric AMPAR subtypes for initial screening. Through our investigation, we found no significant effects on sensitizing Slack to quinidine blockade. Additionally, the GluA2 used in our study is unedited.

5) Line 144: I expect a reduction in current amplitude caused by blocking INaT and INaP is tested at +100mV?

We thank the reviewer for raising this point. The reduction in current amplitude was indeed tested at +100 mV and we have included this information in the revised manuscript.

6) Line 157 and line 162: Reference to Supplementary table S3 should be Table S2.

We thank the reviewer for pointing this out. The reference to "Table S3" has been corrected to "Table S2" in the revised manuscript.

7) How many times did the authors repeat the co-immunoprecipitation? Some of the bands are very weak, and repeats are necessary for all blots.

We thank the reviewer for raising this concern. We performed the co-immunoprecipitation experiments three times independently.

8) Line 288: The authors are showing the chimeric construct in Figures 7A and B but are referring to the full length Nav1.6 in the main text line 288.

We apologize for the confusion. We have clarified in the revised manuscript that we used NaV1.5/6NC in our study.

9) Figure 1 line 23: 1 uM quinidine must be 30 uM quinidine?

We thank the reviewer for catching this error. We have corrected the concentration value in the caption of Figure 1 from "1 μΜ" to "30 μΜ" in the revised manuscript.

10) Figure 2 line 53: I expect IC50 is measured at +100mV? Same question for line 60 in same figure text.

We thank the reviewer for pointing this out. We have now included this information in the revised manuscript.

11) Figure 4B color coding is confusing.

We apologize for the confusion. We would like to clarify that Fig. 4B illustrates the domain architecture of the human NaV channel pore-forming α subunit, and we have changed the color from dark blue to black in the revised figure.

12) Figure S6: Text for figure S6E and S6F has been swapped (line 96 to 106).

We thank the reviewer for raising this point. We have rectified the swapped captions for Fig. S6E and Fig. S6F in the revised manuscript.

13) Methods section line 652: Kainite acid should be changed to kainic acid

We thank the reviewer for catching this typo. The term “kainite acid” has been corrected to “kainic acid” in the revised manuscript.

Reviewer #2 (Recommendations For The Authors):

1) Discuss limitations about the use of non-neuronal cells or cultured primary neurons rather than a more intact system.

We thank the reviewer for raising this point. We have discussed the limitations about the use of non-neuronal cells or cultured primary neurons rather than a more intact system (line 344 to line 348).

2) Riluzole is not a selective drug, so the limitations of this drug should be discussed.

We thank the reviewer for raising this point. We have discussed the limitations of riluzole in the revised manuscript (line 360 to line 364).

3) Remove the term in vivo.

We thank the reviewer for raising this point. In our experiments, although we did not conduct experiments directly in living organisms, our results demonstrated the coimmunoprecipitation of NaV1.6 with Slack in homogenates from mouse cortical and hippocampal tissues (Fig. 3C). This result may support that the interaction between Slack and NaV1.6 occurs in vivo.

4) Figure 1

①C Why does Nav1.2 have a small inward current before the large inward current in the inset? The slope of the rising phase of the larger sodium current seems greater than Nav1.6 or Nav1.5. Was this examined?

We apologize for the confusion. We would like to clarify that the small inward current can be attributed to the current of membrane capacitance (slow capacitance or C-slow). The larger inward current is mediated by NaV1.2. Additionally, we did not compare the slope of the rising phase of NaV subtypes sodium currents but primarily focused on the current amplitudes.

②D-E

For Nav1.5 the sodium current is very large compared to Nav1.6. Is it possible the greater effect of quinidine for Nav1.6 is due to the lesser sodium current of Nav1.6?

We thank the reviewer for raising this point. We would like to clarify that our results indicate that transient sodium currents contribute to the sensitization of Slack to quinidine blockade (Fig. 2C,E). Therefore, it is unlikely that the greater effect observed for NaV1.6 in sensitizing Slack is due to its lower sodium currents.

③The differences between WT and KO in G -H are hard to appreciate. Could quantification be shown? The text uses words like "block" but this is not clear from the figure. It seems that the replacement of Na+ with Li+ did not block the outward current or effect of quinidine.

We apologize for the confusion. We would like to clarify the methods used in this experiment. The lithium ion (Li+) is a much weaker activator of sodium-activated potassium channel Slack than sodium ion (Na+)1,2.

1. Zhang Z, Rosenhouse-Dantsker A, Tang QY, Noskov S, Logothetis DE. The RCK2 domain uses a coordination site present in Kir channels to confer sodium sensitivity to Slo2.2 channels. J Neurosci. Jun 2 2010;30(22):7554-62. doi:10.1523/JNEUROSCI.0525-10.2010

2. Kaczmarek LK. Slack, Slick and Sodium-Activated Potassium Channels. ISRN Neurosci. Apr 18 2013;2013(2013)doi:10.1155/2013/354262

Therefore, we replaced Na+ with Li+ in the bath solution to measure the current amplitudes of sodium-activated potassium currents (IKNa)3.

1. Budelli G, Hage TA, Wei A, et al. Na+-activated K+ channels express a large delayed outward current in neurons during normal physiology. Nat Neurosci. Jun 2009;12(6):745-50. doi:10.1038/nn.2313

The following equation was used for quantification:

Furthermore, the remaining IKNa after application of 3 μM quinidine in the bath solution was measured as the following:

The quantification results were presented in Fig. 1K. The term "block" used in the text referred to the inhibitory effect of quinidine on IKNa.

④In K, for the WT, why is the effect of quinidine only striking for the largest currents?

We thank the reviewer for raising this point. After conducting an analysis, we found no correlation between the inhibitory effect of quinidine and the amplitudes of baseline IKNa in WT neurons (p = 0.6294) (Author response image 2). Therefore, the effect of quinidine is not solely limited to targeting the larger currents.

Author response image 2.

The correlation between the inhibitory effect of quinidine and the amplitudes of baseline IKNa in WT neurons (data from manuscript Fig. 1K). r = 0.1555, p=0.6294, Pearson correlation analysis.

5) Figure 2

①A. The argument could be better made if the same concentration of quinidine were used for Slack and Slack + Nav1.6. It is recognized a greater sensitivity to quinidine is to be shown but as presented the figure is a bit confusing.

We apologize for the confusion. We would like to clarify that the presented concentrations of quinidine were chosen to be near the IC50 values for Slack and Slack+NaV1.6.

②C. Can the authors add the effect of quinidine to the condition where the prepulse potential was - 90?

We apologize for the confusion. We would like to clarify that the condition of prepulse potential at -90 mV is the same as the condition in Fig. 1. We only changed one experiment condition where the prepulse potential was changed to -40 mV from -90 mV.

6) Figure 3.

①line 80 should be coronal not coronary

We thank the reviewer for catching this error. We have corrected the term “coronary” to “coronal” in the caption of Figure 3.

②A. Clarify these 6 panels.

We thank the reviewer for raising this point. We have clarified the captions of Fig. 3A in the revised manuscript.

③Please enlarge fonts in D.

We thank the reviewer’s suggestion. We’ve enlarged the fonts in Fig. 3D in the revised manuscript.

④F. The variances should be checked with a test to determine if they are significantly different because they look different - if so, data can be transformed and if transformed data have variances that are equivalent a t-test can be used on the transformed data. Otherwise, Mann-Whitney should be used.

We thank the reviewer for pointing this out. We have reanalyzed the data in Fig. 3F using Mann Whitney test after identifying the different variances in the two groups.

7) Figure 7. The images need more clarity. They are very hard to see. Text is also hard to see.

We apologize for the lack of clarity in the images and text. we would like to provide a concise summary of the key findings shown in this figure.

Figure 7 illustrates an innovative intervention for treating SlackG269S-induced seizures in mice by disrupting the Slack-NaV1.6 interaction. Our results showed that blocking NaV1.6-mediated sodium influx significantly reduced Slack current amplitudes (Fig. 2D,G), suggesting that the Slack-NaV1.6 interaction contributes to the current amplitudes of epilepsy-related Slack mutant variants, aggravating the gain-of-function phenotype. Additionally, Slack’s C-terminus is involved in the Slack-NaV1.6 interaction (Fig. 5D). We assumed that overexpressing Slack’s C-terminus can disrupt the Slack-NaV1.6 interaction (compete with Slack) and thereby encounter the current amplitudes of epilepsy-related Slack mutant variants.

In HEK293 cells, overexpression of Slack’s C-terminus indeed significantly reduced the current amplitudes of epilepsy-related SlackG288S and SlackR398Q upon co-expression with NaV1.5/6NC (Fig. 7A,B). Subsequently, we evaluated this intervention in an in vivo epilepsy model by introducing the Slack G269S variant into C57BL/6N mice using AAV injection, mimicking the human Slack mutation G288S that we previously identified (Fig. 7C-G).

②It is not clear how data were obtained because injection of kainic acid does not lead to a convulsive seizure every 10 min for several hours, which is what appears to be shown. Individual seizures are just at the beginning and then they merge at the start of status epilepticus. After the onset of status epilepticus the animals twitch, have varied movements, sometime rear and fall, but there is not a return to normal behavior. Therefore one can not call them individual seizures. In some strains of mice, however, individual convulsive seizures do occur (even if the EEG shows status epilepticus is occurring) but there are rarely more than 5 over several hours and the graph has many more. Please explain.

We apologize for the confusion. Regarding the data acquisition in relation to kainic acid injection, we initiated the timing following intraperitoneal injection of kainic acid and recorded the seizure scores of per mouse at ten-minute intervals, following the methodology described in previous studies4.

1. Huang Z, Walker MC, Shah MM. Loss of dendritic HCN1 subunits enhances cortical excitability and epileptogenesis. J Neurosci. Sep 2 2009;29(35):10979-88. doi:10.1523/JNEUROSCI.1531-09.2009

The seizure scores were determined using a modified Racine, Pinal, and Rovner scale5,6: (1) Facial movements; (2) head nodding; (3) forelimb clonus; (4) dorsal extension (rearing); (5) Loss of balance and falling; (6) Repeated rearing and failing; (7) Violent jumping and running; (8) Stage 7 with periods of tonus; (9) Dead.

1. Pinel JP, Rovner LI. Electrode placement and kindling-induced experimental epilepsy. Exp Neurol. Jan 15 1978;58(2):335-46. doi:10.1016/0014-4886(78)90145-0

2. Racine RJ. Modification of seizure activity by electrical stimulation. II. Motor seizure. Electroencephalogr Clin Neurophysiol. Mar 1972;32(3):281-94. doi:10.1016/0013- 4694(72)90177-0

8) The graphical abstract is quite complicated and somewhat hard to follow. Please simplify and clarify. One aspect of the abstract to clarify is the direction of what is first and second and third (etc.) because arrows point to many directions.

We thank the review for raising this point. In the revised manuscript, we have included numbering of three components within the graphical abstract:

1. Pathological phenotype: Increased Slack currents.

2. Two types of interventions:

2a. Disruption of the Slack-NaV1.6 interaction.

2b. NaV1.6-mediated sensitization of Slack to quinidine blockade.

1. Therapeutic effects: Reduced Slack currents.

Reviewer #3 (Recommendations For The Authors):

1) A reference to homozygous knockout is made in the abstract; however, only heterozygous mice are mentioned in the methods section. The genotype of the mice needs to be made clear in the manuscript. Furthermore, at what age were these mice used in the study. Since homozygous knockout of NaV1.6 is lethal at a very young age (<4 wks), it would be important to clarify that point as well.

We thank the reviewer for pointing this out. In the revised manuscript, we have included information about the source of the primary cortical neurons used in our study. These neurons were obtained from postnatal homozygous NaV1.6 knockout C3HeB/FeJ mice and their wild-type littermate controls.

2) Coimmunoprecipitation studies in Fig. 3C are not convincing. There appears to be a signal in the control lane. Furthermore, it appears that brightness levels were adjusted of that image, thereby removing completely the background.

We thank the reviewer for pointing this out. We have replaced Fig. 3C with an unadjusted version in the revised manuscript.

3) In Fig. 1B, the authors indicate that 30 microM of quinidine was used, while the corresponding figure legend suggest that 1 microM. Please clarify.

We apologize for this error. We have corrected the concentration value in the caption of Figure 1 from "1 μΜ" to "30 μΜ" in the revised manuscript.

4) How long were the cells exposed to quinidine before the functional measurement were performed?

We thank the reviewer for pointing this out. The cells were exposed to the bath solution with quinidine for about one minute before applying step pulses.

5) In Fig. 6B-D, it is not clear to what extent co-expression of Slack mutants and NaV1.6 increases sodium-activated potassium current.

We thank the reviewer for pointing this out. We notice that the current amplitudes of Slack mutants exhibit a considerable degree of variation, ranging from less than 1 nA to over 20 nA (n = 5-8). To accurately measure the effects of NaV1.6 on increasing current amplitudes of Slack mutants, we plan to apply tetrodotoxin in the bath solution to block NaV1.6 sodium currents upon coexpression of Slack mutants with NaV1.6.

6) In Fig.7A and B, it appears that some recordings had no sodium-activated potassium currents. Why were these included in analysis? How was transfection efficacy assessed?

We apologize for the confusion. We would like to clarify that all recordings included in analysis indeed exhibited outward sodium-activated potassium currents. The current density data in Fig. 7A-B are listed in Author response table 1 (in pA/pF):

Author response table 1.

Regarding the assessment of transfection efficacy, we estimated it approximately by using fluorescence proteins as reporters, which were co-expressed with the relevant proteins via the selfcleaving 2A peptide.

7) Greater detail needs to be provided for the generation of NaV1.5 and NaV1.6 chimeras. Specifically, what AA residues were changed between sodium channel isoforms?

We thank reviewer for pointing this out. In the revised manuscript, we have included the specific amino acid residues that were changed between NaV1.5 and NaV1.6 to generate the chimeric constructs.

8) In line 481, the authors refer to Fig. S2d instead of Fig. S6D. This should be corrected. Furthermore, the unusual shift in sodium current kinetics that the authors observe might be due in part to junction potential. Did the authors take that into consideration?

We apologize for this error. The reference to "Fig. S2d" has been corrected to "Fig. S6D" in the revised manuscript.

Regarding the unusual shift observed in the sodium current kinetics, we agree with the reviewer's suggestion that the junction potential may contribute to this phenomenon. During patch-clamp recordings, we ensure that the junction potential was properly compensated by the amplifier. Additionally, the replacement of CsF in pipette solution may have contributed to the observed unusual shift, as CsF in pipette solution has been reported to shift the voltage dependence of activation and fast/slow inactivation of NaV channels towards more negative potentials7.

1. Korngreen A. Advanced patch-clamp analysis for neuroscientists. Neuromethods. Humana Press; 2016:xii, 350 pages.

9) Legends for Fig.S6E and S6F are flipped. Please correct.

We apologize for this error. We have rectified the flipped captions for figure S6E and S6F in the revised manuscript.

10) Variance should be provided for the IC50 values and kinetic parameters of the sodium channels in the supplemental tables.

We thank the reviewer for raising this point. We have included the 95% confidence interval (95%CI) for the IC50 values and kinetic parameters in the revised supplementary tables.