Reviewer #2 (Public Review):

The aim of this study was to relate functional alterations in patients with bvFTD to neurotransmitter maps provided by the JuSpace toolbox in order to better understand the underlying pathological mechanisms of this disease.

A strength of the study is the novelty of this aim. Some weaknesses are the different fMRI parameters of patients belonging to each centre and a better explanation of some methodological choices as well a better description of the JuSpace toolbox.

The authors have achieved their aims and the results seem to support some conclusions, although the results should be interpreted in light of a potential lack of proper control for multiple comparisons.

This work will increase the use of approaches that relate brain abnormalities to neurotransmitters and transcriptomics.

There is an increasing trend to assess the correspondence between neuroimaging alterations and detailed information of neurotransmitters across the brain. This work represents this trend and adds to an increasing body of work doing the same with transcriptomics.

Reviewer #3 (Public Review):

This manuscript analyzed resting state functional MRI metrics related to behavioral variant frontotemporal dementia (bvFTD) for associations with patterns of neurotransmitter system receptor distribution, patterns of neurotransmitter-related gene expression, and profiles of performance on neuropsychological test battery items.

The overarching goal of the work was to assess whether these analyses point to selective vulnerability of some neurotransmitter systems in the symptomatology of bvFTD. The manuscript reports that reductions in fMRI measures of local brain functional activity in bvFTD followed the distribution of specific neurotransmitter systems. No similar findings were identified for MRI-based gray matter volume measurements.

Strengths of the manuscript include its leveraging of publicly available tools for large-scale regional brain mRNA profiles and neurotransmitter receptor distributions. An additional positive step for the literature involves further development of the concept that biomarkers of disruptions to specific functionally-connected networks may guide specific treatment strategies (as a corollary to this work, related to neurotransmitter system disruption) in neurodegenerative disease.

A weakness of the manuscript is that it is not able to directly address the main literature gap described in the Introduction -- namely, whether there is specific vulnerability of certain neuronal types versus other in bvFTD, or whether broader network/region-based neurodegeneration is the driver (and happens to include some selective neurotransmitter-related disruptions). In other words, if "A" is a biomarker of bvFTD, "A" has a partial correlation with "B", and the "AB" correlation has a partial correlation with "C", it seems too far a leap to conclude that "B" (in this case, profiles/distributions of neurotransmitter systems) is the central figure in the cascade.

eLife assessment

The authors present a valuable work suggesting that the superficial, retinorecipient layers of the mouse superior colliculus (SC) may participate in figure-ground segregation and object recognition. These data are based largely on optogenetic perturbations of SC but the strength of evidence is currently incomplete: although the effects are statistically significant, there are significant technical limitations that are not adequately addressed via controls.

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.

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)<br /> 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.<br /> 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.

2) Could other behavioural variables explain the results?<br /> 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?<br /> 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.

3) What is the behavioural strategy of the animals?<br /> 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.

4) Data relating to misses should be included in analyses to provide a complete picture of behaviour and neural responses<br /> 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?<br /> b) 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?

5) Statistical tests do not support the conclusions, are missing or inadequate<br /> 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.<br /> 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.<br /> 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.<br /> 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.<br /> 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.<br /> f) There is no evidence that FGM for phase was different between hit and error trials as stated in line 234.<br /> 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.<br /> h) Bonferroni correction in Fig 1E should correct multiple comparisons across time points, not across tasks (see Table 1).<br /> i) What is the reason to perform some tests one-tailed, others 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.

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

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. 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<br /> - 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?<br /> - 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? How local the inactivation effect is? Where was the silicon probe placed in relation to AAV expression and optical fiber position?

2) Number of sessions and units<br /> - 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.

- 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.

3) Figure-ground modulation in SCs<br /> - 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?<br /> - Could authors describe in more detail how they measure a pupil position and diameter, by showing raw data, pupil size aligned to task events?<br /> - 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?<br /> - 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?

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).

eLife assessment

This is a valuable report that describes that ACE2 expression is upregulated by SARS-CoV-2 infection via activation of transcription factor Sp1 and inhibition of HNF4α through the PI3K/AKT pathway. Inhibition of Sp1 reduces SARS-CoV-2 infection in vitro and in an animal model. This work is solid and will be of interest to those interested in ACE2 biology and its impact in COVID-19.

Joint Public Review:

The authors clearly state the current mystery surrounding transcriptional regulation of ACE2-expression, and how SARS-CoV-2 infection might impact this regulation. Several medications have been identified impacting the gene expression of ACE2, such as colchicine. However, the mechanism behind this regulation of ACE2 gene expression is currently unknown, yet worth investigating. Indeed, getting to know the mechanism behind the transcriptional regulation of ACE2 might lead to development of therapies targeting this expression in order to attenuate COVID-19 severity.<br /> In order to achieve insight in the regulation of ACE2 expression by SARS-CoV-2, the authors used a luciferase reporter based assay to investigate a range of signaling pathways. The authors found that ACE2 expression is upregulated by SARS-CoV-2 infection via activation of transcription factor Sp1 and inhibition of HNF4α through the PI3K/AKT pathway. This led to the discovery that inhibition of Sp1 using mithramycin A reduces SARS-CoV-2 infection in vitro and in an animal model.

Strengths<br /> - The authors used an elegant design for their investigation. Based on a broad luciferase based assay, and keeping in mind the opposite effects of SARS-CoV-2 infection and colchicine administration on the expression of ACE2, they identified transcription factors as potential candidates for regulating ACE2 expression.<br /> - Throughout the several experiments performed, the antagonizing effects of SARS-CoV-2 infection and colchicine on the identified transcription factors (Sp1 and HNF4α) are consistent and therefore strengthen the conclusions.

Weaknesses<br /> - 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.<br /> - 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.<br /> - 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.<br /> - 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.

These results add to the existing knowledge that the characteristics of ACE2 (its functionality and abundance) in the respiratory tract are pivotal to understand infection by SARS-CoV-2. The author conclusions are supported by the results. The identification of the two transcription factors influenced by SARS-CoV-2 infection is valuable, but needs further research to assess whether their effect on ACE2 expression is also seen in other cell types than the one assessed by the authors. More in-depth research will have to follow to assess if and how targeting the identified transcription factors could ultimately benefit patients with COVID-19.

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.

eLife assessment

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

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.

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:<br /> 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:<br /> 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.

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.

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

Reviewer #3 (Public Review):

This paper offers a fundamental advance in our understanding of communication between human sensory neurons and keratinocytes in the skin of humans. The work, which used EM and expansion microscopy, shows that axons tunnel through keratinocytes and form gap junctions along the axon as it passes by or potentially where it is ensheathed by the cell. This is a fairly remarkable arrangement and is seen both in vivo and in vitro.

The major strengths are the quality of the imaging, the use of expansion microscopy to reveal new anatomical information and the new insight the detailed work offers to our understanding of sensory neuroscience. Another major strength is that the work was done in humans, and using human cells in vitro. I think the authors have achieved their goal of thoroughly characterizing this interesting interaction between sensory neurons and keratinocytes. The obvious next step is to understand if these interactions become pathological in neuropathies.

I do think there are some weaknesses that should be addressed, and some questions that are outstanding that the authors might want to discuss. Chief amongst these is the question of what types of sensory neurons form these contacts with keratinocytes and do these change in clinical neuropathies. A more thorough discussion of these issues for future investigation would help to place the findings in the broader context of the field, in my opinion.

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.

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.

eLife assessment:

Interoceptive signals from internal organs activate neurons in the nucleus tractus solitarius (NTS) to help maintain homeostasis. The authors of this paper use gain-of-function and loss-of-function experiments to examine three distinct NTS neuronal populations, individually and in combination, and find that activating (or inhibiting) combinations of these neurons have more robust effects on food intake and body weight than activating (or inhibiting) them individually. The results of this paper are convincing and solid but do not provide mechanistic insights.

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.

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.

Reviewer #2 (Public Review):

Summary:<br /> In this study, Wilmot et al., ran a series of experiments to describe a dopaminergic projection from LC to dHPC, and its functional role in trace fear conditioning (TFC). Using fiber photometry in LC, they show convincingly that the activity of LC TH neurons is increased to both cues and footshock, and that this increases with acquisition or TFC, and decreases during extinction of this association. Projections from LC to dHPC show a similar pattern of activity, and dopamine release (measured by the fluorescent sensor GRAB-DA) is also comparable to calcium activity from LC. While the authors do show that activity at the dopamine D1R/D5R is necessary for TFC, a direct test of the necessity of dopamine release from LC during TFC is not shown.

Strengths:<br /> • The authors clearly and effectively show that the LC-dHPC projection is activated by an aversive outcome (i.e. shock), and that activity in this pathway changes in response to learning about a neutral cue that predicts this shock (i.e. TFC). Furthermore, they show that increased dopamine release in dHPC can be observed if LC is chemogenetically activated. A critical role for dopamine receptors (but not β- and ⍺-adrenergic receptors) in TFC was demonstrated, and intra-dHPC injection of a D1R/D5R antagonist blocks this learning. Finally, dopamine release (measured by GRAB-DA) in dHPC was shown to also occur during trace fear conditioning.

• The authors have conclusively shown that activity at the dopamine receptors in the dPHC during trace fear conditioning is of the same pattern as calcium activity recorded both in LC cell bodies, but more importantly in the axonal projections from LC to dHPC. This is very good evidence that this pathway is recruited during TFC.

Weaknesses:<br /> • The claim that dopamine release in dHPC is caused by LC neurons is not directly tested. Unfortunately, the most critical experiment for the claims that dopamine release comes from LC during conditioning is not tested. A lack of dopamine signal in dHPC caused by inhibition of LC during TFC would show this. It is indeed an interesting observation that chemoegenetic activation of LC causes dopamine release in the dHPC. However, in the absence of concurrent VTA inhibition or lesion, it remains a possibility that the dopamine release is mediated through indirect actions on other dopamine-expressing neurons. The authors do a good job of arguing against this interpretation in the discussion, and the literature seems appropriate for this. However, the title is still an overstatement of the data presented in this study.

• The primary alternative interpretations of the phasic activation experiment are whether only stimulation to the cue events (both on and off), or whether only stimulation to the shock. Thus this experiment would benefit from additional data showing either a no shock control, to show that enhanced activity of the LC to the tone is not inherently aversive, or manipulations to the tone but not to the shock.

• Specificity of the GRAB-NE and GRAB-DA sensors should be either justified through additional experiments testing the alternative antagonist (i.e. GRAB-NE CNO+eticloprode / GRAB-DA CNO+yohimbine) or additional citations that have tested this already. It is critical for the claims of the paper to show that these sensors are specific to dopamine or norepinephrine.

• The role of dopamine in prediction error was tested through a series of conditions whereby the shock was presented either signaled (i.e. predicted), or not. However, another way that prediction error is signaled is through the absence of an expected outcome. Admittedly it might not be possible to observe a decrease in dopamine signaling with this methodology.

• The difference between Fig. 6E and 6H needs to be clarified. What is shown in Fig. 6E is that the response to the shock decreases through experience (i.e. by the 10th trial). However in Fig 6H, there is no difference between signaled and signaled shock, but this is during conditioning, and not after learning (based on my understanding of the methods, line 482).

• Unless I missed it, at no point in the manuscript is the number of subjects described. Please add the n per experiment within each section describing each experiment in the methods (Behavioral procedures). Some more details in the photometry statistical analysis would be helpful. For example, what is the n per group for every data set that is presented? How many trials per analysis?

eLife assessment

This important study enhances our understanding of the brain circuitry responsible for fear conditioning and provides evidence for an under-appreciated role of dopaminergic output projection from the Locus Coeruleus to the dorsal hippocampus in this fear learning. The evidence supporting the conclusion is convincing, although a direct test of dopamine release in the dorsal hippocampus from Locus Coeruleus projections during fear conditioning would strengthen the study. If done, this would likely raise the strength of the evidence to compelling. This paper is of interest to behavioural and neuroscience researchers studying learning, memory, and neural networks.

Reviewer #1 (Public Review):

Summary:<br /> The authors investigate the role of the noradrenergic nucleus Locus Coeruleus (LC) in hippocampally-dependent learning and memory processes. The two stated aims of these experiments are to distinguish between 'tonic and phasic' activity and release in LC neurons and to determine the relative contribution of noradrenaline and dopamine, released from LC terminals, during learning. To address these questions, the investigators used a trace conditioning protocol (a behavior that is well established to be dependent on the hippocampus), coupled with a genetically based toolbox of sensors allowing measurements and manipulation of cell-type specific populations of neurons.

This includes photometric imaging of neuronal activity within the LC through Calcium signaling (Fig 1B), and in the hippocampal target site (Fig 3F), photostimulation of monoamine-containing neurons in the LC Fig 4B), measuring of extracellular dopamine and noradrenergic in the hippocampus with fluorescent sensors (GRABs) (Fig 5B). The study was complemented by a pharmacological approach to demonstrate that dopamine and not noradrenaline were essential for learning this task.

Results show that the calcium signal in the LC increased in response to tone or footshock in an intensity-dependent manner (Fig 1C,D,E F). LC responses can be conditioned and conditioned responses are of higher amplitude than the responses to the to-be-conditioned stimulus (Fig 2D). These results replicate sparse data gleaned over the past four decades using single and multiple-unit electrophysiological recording in LC in rats and monkeys. Calcium imaging LC axonal projections in the hippocampus showed a small but significant increase in response to tone onset and offset and to shock during conditioning.

Gain of function experiments show that enhancing a weak tone stimulus by phasic activation of LC through photostimulation during conditioning, facilitated subsequent memory performance (Fig 4D).

Fluorescent sensors demonstrated the release of both Noradrenaline and Dopamine in the hippocampus in response to activation of LC.

Using conventional pharmacology the essential role of dopamine was confirmed in the learning of this trace conditioning task, corroborating previous reports of hippocampal dopamine involvement in spatial learning.

Strengths:<br /> The experiments confirm many of the results of the past four decades from unit recordings from the LC in behaving rats and monkeys. The available data are sparse, due to the difficulty of recording from this tiny pontine nucleus; the reports emanate from only a few laboratories. Given the large amount of theorizing based on sparse data, it is important that the observations concerning the environmental contingencies driving the activity of LC be corroborated.

That dopamine is released from LC terminals in the forebrain has been known for 20 years (Devoto 2004), but this was largely ignored until recently when a few laboratories demonstrated the functional importance of this projection in hippocampal-dependent learning. The present corroboration should lend further credence and promote further studies of the factors governing this release of dopamine from LC terminals, into specific forebrain regions.

Weaknesses:<br /> --One criticism the authors have made of previous studies was that they have not distinguished between 'tonic' and 'phasic' LC activity and could not demonstrate 'time-locked phasic firing'. This has not been achieved in the present report, as an examination of Fig 1 C,D and 2 C,D shows. Previous reports in rats and monkeys, using unit recording in rats and monkeys clearly show that the latency of LC 'phasic' responses to salient or behaviorally relevant stimuli are in the range of tens of milliseconds, with a very short duration, often followed by a long-lasting inhibition. This kind of temporal precision concerning the phasic response cannot be gleaned from the time scale shown in the Figures (assuming the time scale is in seconds). We can discern a long-lasting increase in tonic firing level for the more salient stimuli (Fig 1C) (although the authors state in the discussion that "we did not observe obvious changes in tonic LC-HPC activity). This calcium imaging methodology as used in the present experiments can give us a general idea of the temporal relation of LC response to the stimulus, but apparently does not afford the millisecond resolution necessary to capture a phasic response, at least as the data are presented in the Figures.

--Much of the data presented here can be regarded as 'proof of concept' i.e. demonstrating that Photometric imaging of calcium signalling yields similar results concerning LC responses to salient or behaviorally relevant stimuli as has been previously reported using electrophysiological unit recording. The role of dopamine as the principal player in hippocampal-dependent learning also corroborates previous reports.

-- No attempt was made to address the important current question of the modular organisation of Locus Coeruleus, although the authors recognize the importance of this question and propose future experiments using their methodology to record simultaneously in several LC projection sites.

Reviewer #3 (Public Review):

Summary:<br /> The manuscript examines an important question, namely how the brain associates events spaced in time. It uses a variety of neural methods including fiber photometry as well as area-specific and pathway-silencing methods with the exquisite dissociation of norepinephrine and dopamine. The data show that neurons in the locus coeruleus (LC) respond to auditory cue onset, offset, and shock. These responses are stronger if the cue is paired with shock in a trace procedure. Optogenetic stimulation similar to the neural response captured by fiber photometry enhances associative learning. LC terminals in the dorsal hippocampus also showed phasic responses during fear conditioning and drove dopamine and norepinephrine responses. Pharmacological methods revealed that dopamine and not norepinephrine is critical for fear learning.

Strengths:<br /> The examination of the neural signal to different tone intensities, different shock intensities, repeated tone presentation (habituation), and conditioning, offers an unprecedented account of the neural signal to non-associative and associative processes. This kind of deconstruction of the elements of conditioning offers a strong account of how the brain processes the stimuli used and their interaction during learning.

Excellent use of data acquired with fiber photometry in the optogenetic interrogation study.

The use of pharmacology to disentangle dopamine and norepinephrine was excellent.

Weaknesses:<br /> While the optogenetic study was lovely, a control using the same stimulation but delivered at different time points would have been a good addition to show how critical the neural signal at tone onset, tone offset, and shock is.

Justification for the focus on D1 receptors was lacking.

The manuscript provides convincing evidence that the neural signal is not an error-correcting one by including a predicted (by a tone) and unpredicted shock. One possibility is that perhaps the unpredicted shock could be predicted by the context. Some clarification on the behavioural procedures would help understand if indeed the unsignaled shock could be predicted by the context or not.

Reviewer #3 (Public Review):

Summary:<br /> The authors set out to characterize the anatomical connectivity profile and the functional responses of chandelier cells (ChCs) in the mouse primary visual cortex. Using retrograde rabies tracing, optogenetics, and in vitro electrophysiology, they found that the primary source of input to ChCs are local layer 5 pyramidal cells, as well as long-range thalamic and cortical connections. ChCs provided input to local layer 2/3 pyramidal neurons, but did not receive reciprocal connections.

With two-photon calcium imaging recordings during passive viewing of drifting gratings, the authors showed that ChCs exhibit weakly selective visual responses, high correlations within their own population, and strong responses during periods of arousal (assessed by locomotion and pupil size). These results were replicated and extended in experiments with natural images and prediction of receptive field structure using a convolutional neural network.

Furthermore, the authors employed a learned visuomotor task in a virtual corridor to show that ChCs exhibit strong responses to mismatches between visual flow and locomotion, locomotion-related activation (similar to what was shown above), and visually-evoked suppression. They also showed the existence of two clusters of pyramidal neurons with functionally different responses - a cluster with "classically visual" responses and a cluster with locomotion- and mismatch-driven responses (the latter more correlated with ChCs). Comparing naive and trained mice, the authors found that visual responses of ChCs are suppressed following task learning, accompanied by a shortening of the axon initial segment (AIS) of pyramidal cells and an increase in the proportion of AIS contacted by ChCs. However, additional controls would be required to identify which component(s) of the experimental paradigm led to the functional and anatomical changes observed.

Finally, using a chemogenetic inactivation of ChCs, the authors propose weak connectivity to pyramidal cells (due to small effects in pyramidal cell activity). However, these results are not unequivocally supported, as the baseline activity of ChCs before inactivation is considerably lower, suggesting a potentially confounding homeostatic plasticity mechanism might already be operating.

Strengths:<br /> The authors bring a comprehensive, state-of-the-art methodology to bear, including rabies tracing, in vivo two-photon calcium imaging, in vitro electrophysiology, optogenetics and chemogenetics, and deep neural networks. Their analyses and statistical tests are sound and for the most part, support their claims. Their results are in line with previous findings and extend them to the primary visual cortex.

Weaknesses:<br /> - Some of the results (e.g. arousal-related responses) are not entirely surprising given that similar results exist in other cortical areas.

- Control analyses regarding locomotion patterns before and after learning the task (Figure 5), and additional control experiments to identify whether functional and anatomical changes following task learning were due to learning, repeated visual exposure, exposure to reward, or visuomotor experience would strengthen the claims made.

- The strength of the results of the chemogenetics experiment is impacted by the lower baseline activity of ChCs that express the KORD receptor. At present, it is not possible to exclude the presence of homeostatic plasticity in the network *before* the inactivation takes place.

eLife assessment

This important work shows compelling evidence that Chandelier cells in the visual cortex receive inputs most prominently from local layer 5 pyramidal neurons, only mildly inhibit L2/3 pyramidal neurons, and respond massively to visuomotor mismatch. It also indicates that visual experience in the virtual tunnel activates a plasticity mechanism in Chandelier cells which could be due to the particular visuo-motor coupling experienced in this setting, although a specific control is lacking for this conclusion. This study will be of interest to neuroscientists involved in cortical circuits, visual processing, and predictive coding research.

Reviewer #1 (Public Review):

Overall, the experiments are well-designed and the results of the study are exciting. We have one major concern, as well as a few minor comments that are detailed in the following.

Major:<br /> 1. The authors suggest that "Visuomotor experience induces functional and structural plasticity of chandelier cells". One puzzling thing here, however, is that mice constantly experience visuomotor coupling throughout life which is not different from experience in the virtual tunnel. Why do the authors think that the coupled experience in the VR induces stronger experience-dependent changes than the coupled experience in the home cage? Could this be a time-dependent effect (e.g. arousal levels could systematically decrease with the number of head-fixed VR sessions)? The control experiment here would be to have a group of mice that experience similar visual flow without coupling between movement and visual flow feedback. Either change would be experience-dependent of course, but having the "visuomotor experience dependent" in the title might be a bit strong given the lack of control for that. We would suggest changing the pitch of the manuscript to one of the conclusions the authors can make cleanly (e.g. Figure 4).

Minor:<br /> 2. "ChCs shape the communication hierarchy of cortical networks providing visual and contextual information." We are not sure what this means.

3. "respond to locomotion and visuomotor mismatch, indicating arousal-related activity" This is not clear. We think we understand what the authors mean but would suggest rephrasing.

4. 'based on morphological properties revealed that 87% (287/329) of labeled neurons were ChCs" Please specify the morphological properties used for the classification somewhere in the methods.

5. We may have missed this - in the patch clamp experiment (Fig.1 H-K), please add information about how many mice/slices these experiments were performed in.

6. "These findings suggest that the rabies-labeled L1-4 neurons providing monosynaptic input to ChCs are predominantly inhibitory neurons". We are not sure this conclusion is warranted given the sparse set of neurons labelled and the low number of cells recorded in the paired patch experiment. We would suggest properly testing (e.g. stain for GABA on the rabies data) or rephrasing.

7. Figure 2E. A direct comparison of dF/F across different cell types can be subject to a problematic interpretation. The transfer function from spikes to calcium can be different from cell type to cell type. Additionally, the two cell populations have been marked with different constructs (despite the fact that it's the same GECI) further reducing the reliability of dF/F comparisons. We would recommend using a different representation here that does not rely on a direct comparison of dF/F responses (e.g. like the "response strength" used in Figure 3B). Assuming calcium dynamics are different in ChCs and PyCs - this similarity in calcium response is likely a coincidence.

8. If ChCs are more strongly driven by locomotion and arousal, then it's a bit counterintuitive that at the beginning of the visual corridor when locomotion speed consistently increases, the activity of ChCs consistently decreases. This does not appear to be driven by suppression by visual stimuli as it is present also in the first and last 20cm of the tunnel where there are no visual stimuli. How do the authors explain this?

9. The authors mention that "ChC responses underwent sensory-evoked plasticity during the repeated visual exposure, even though the visual stimuli were different from those encountered during training in the virtual tunnel". How would this work? And would this mean all visual responses are reduced? What is special about the visual experience in the virtual tunnel? It does not inherently differ from visual experience in the home cage, given that the test stimuli (full field gratings) are different from both.

10. Just as a point to consider for future experiments: For the open-loop control experiments, the visual flow is constant (20cm/s) - ideally, this would be a replay of the running speed the mouse previously generated to match statistics.

11. We would recommend specifying the parameters used for neuropil correction in the methods section.

12. If we understand correctly, the F0 used for the dF/F calculation is different from that used for division. Why is this?

13. Authors compare neuronal responses using "baseline-corrected average". Please specify the parameters of the baseline correction (i.e. what is used as baseline here).

Reviewer #2 (Public Review):

Summary:<br /> Seignette et al. investigated the potential roles of axo-axonic (chandelier) cells (ChCs) in a sensory system, namely visual processing. As introduced by the authors, the axo-axonic cell type has remained (and still is) somehow mysterious in its function. Seignette and colleagues leveraged the development of a transgenic mouse line selective for ChC, and applied a very wide range of techniques: transsynaptic rabies tracing, optogenetic input activation, in vitro electrophysiology, 2-photon recording in vivo, behavior and chemogenetic manipulations, to precisely determine the contribution of ChCs to the primary visual cortex network.

The main findings are 1) the identification of synaptic inputs to ChC, with a majority of local, deep layer principal neurons (PN), 2) the demonstration that ChC is strongly and synchronously activated by visual stimuli with low specificity in naive animals, 3) the recruitment of ChC by arousal/visuomotor mismatch, 4) the induction of functional and structural plasticity at the ChC-PN module, and, 5) the weak disinhibition of PNs induced by ChCs silencing. All these findings are strongly supported by experimental data and thoroughly compared to available evidence.

Strengths:<br /> This article reports an impressive range of very demanding experiments, which were well executed and analyzed, and are presented in a very clear and balanced manner. Moreover, the manuscript is well-written throughout, making it appealing to future readers. It has also been a pleasure to review this article.

In sum, this is an impressive study and an excellent manuscript, that presents no major flaws.

Notably, this study is one of the first studies to report on the activities and potential roles of axo-axonic cells in an active, integrated brain process, beyond locomotion as reported and published in V1. This type of research was much awaited in the fields of interneuron and vision research.

Weaknesses:<br /> There are no fundamental weaknesses; the latter mainly concern the presentation of the main results.

The main weakness may be that the different sections appear somehow disconnected conceptually.

Additionally, some parts deserve a more in-depth clarification/simplification of concepts and analytic methods for scientists outside the subfield of V1 research. Indeed, this paper will be of key interest to researchers of various backgrounds.

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.

Reviewer #2 (Public Review):

In the revised manuscript, the authors aim to investigate brain-wide activation patterns following administration of the anesthetics ketamine and isoflurane, and conduct comparative analysis of these patterns to understand shared and distinct mechanisms of these two anesthetics. To this end, they perform Fos immunohistochemistry in perfused brain sections to label active nuclei, use a custom pipeline to register images to the ABA framework and quantify Fos+ nuclei, and perform multiple complementary analyses to compare activation patterns across groups. This is an interesting line of research and a tour de force in brain-wide Fos quantification.

I appreciate many of the changes that were made in the revised manuscript, including FDR correction and transparency in showing their results with and without transformation. However, several key issues described in our first review have not been addressed.

1-Aside from issues with their data transformation (see below), (a) I think they have some interesting Fos counts data in Figures 4B and 5B that indicate shared and distinct activation patterns after KET vs. ISO based anesthesia. These data are far closer to the raw data than PC analyses and need to be described and analyzed in the first figures long before figures with the more abstracted PC analyses. In other words, you need to show the concrete raw data before describing the highly transformed and abstracted PC analyses. (b) This gets to the main point that when selecting brain areas for follow up analyses, these should be chosen based on the concrete Fos counts data, not the highly transformed and abstracted PC analyses.

2-Now, the choice of data transformation for Fos counts is the most significant problem. First, the authors show in the response letter that not using this transformation (region density/brain density) leads to no clustering. However, they also showed the region-densities without transformation (which we appreciate) and it looks like overall Fos levels in the control group Home (ISO) are a magnitude (~10-fold) higher than those in the control group Saline (KET) across all regions shown. This large difference seems unlikely to be due to a biologically driven effect and seems more likely to be due to a technical issue, such as differences in staining or imaging between experiments. Was the Homecage-ISO experiment or at least the Fos labeling and imaging performed at the same time as for the Saline-Ketamine experiment? Please state the answer to this question in the Results section one way or the other.

3-Second, they need to deal with this large difference in overall staining or imaging for these two (Home/ISO and Saline/KET) experiments more directly; their current normalization choice does not really account for the large overall differences in mean values and variability in Fos counts (e.g. due to labeling and imaging differences).

3a-I think one option (not perfect but I think better than the current normalization choice) could be z-scoring each treatment to its respective control. They can analyze these z-scored data first, and then in later figures show PC analyses of these data and assess whether the two treatments separate on PC1/2. And if they don't separate, then they don't separate, and you have to go with these results.

3b-Alternatively, they need to figure out the overall intensity distributions from the different runs (if that the main reason of markedly different counts) and adjust their thresholds for Fos-positive cell detection based on this. I would expect that the saline and HC groups should have similar levels of activation, so they could use these as the 'control' group to determine a Fos-positive intensity threshold that gets applied to the corresponding 'treatment' group.

3c- If neither 3a nor 3b is an option then they need to show the outcomes of their analysis when using the untransformed data in the main figures (the untransformed data plots in their responses to reviewer are currently not in the main or supplementary figs) and discuss these as well.

eLife assessment

This potentially important study used single-cell whole-brain imaging of the immediate early gene Fos to identify the brain areas recruited by two anesthetics, ketamine and isoflurane. The utilization of a custom software package to align and analyze brain images for c-Fos positive cells stands out as an impressive component of the approach. The results suggest these anesthetics might induce anesthesia via different brain regions and pathways, and raw fos showed shared and distinct activation patterns after ketamine- v. isoflurane- vs. based anesthesia. However, the support for the primary conclusions is incomplete owing largely to concerns with the data transformation. The results could also be influenced by differences in route of administration between the drugs and depth of anesthesia. With these issues addressed, this paper would be of interest to preclinical and clinical scientists working with anesthetic and dissociative drugs.

Reviewer #1 (Public Review):

Overall, the manuscript has been improved by addressing some of the concerns, however, I am still very confused about the data analysis due to the use of data transformation (relative %fos), the fact that some graphs only show regions that are significant and the interpretation of the PCA analysis which I find inappropriate. Moreover, many answers in the rebuttal did not make it to the final manuscript and are not discussed and limitations raised by the reviewers are not discussed either.

1a. The addition of the EEG/EMG is useful, however, this information is not discussed. For instance, there are differences in EEG/EMG between the two groups (only Ket significantly increased delta/theta power, and only ISO decreased EMG power). These results should be discussed as well as the limitation of not having physiological measures of anesthesia to control for the anesthesia depth.<br /> 1b. The possibility that the differences in fos observed may be due to the doses used should be discussed.<br /> 1c. The possibility that the differences in fos observed may be due kinetic of anesthetic used should be discussed.

2b. I am confused because Fig 2C seems to show significant decrease in %fos in the hypothalamus, midbrain and cerebellum after KET, while the author responded that " in our analysis, we did not detect regions with significant downregulation when comparing anesthetized mice with controls." Moreover the new figure in the rebuttal in response to reviewer 2 suggests that Ket increases Fos in almost every single region (green vs blue) which is not the conclusion of the paper.

3. There are still critical misinterpretations of the PCA analysis. For instance, it is mentioned that "KET is associated with the activation of cortical regions (as evidenced by positive PC1 coefficients in MOB, AON, MO, ACA, and ORB) and the inhibition of subcortical areas (indicated by negative coefficients) " as well as "KET displays cortical activation and subcortical inhibition, whereas ISO shows a contrasting preference, activating the cerebral nucleus (CNU) and the hypothalamus while inhibiting cortical areas. To reduce inter-individual variability." These interpretations are in complete contradiction with the answer 2b above that there was no region that had decreased Fos by either anesthetic.

4. I still do not understand the rationale for the use of that metric. The use of a % of total Fos makes the data for each region dependent on the data of the other regions which wrongly leads to the conclusion that some regions are inhibited while they are not when looking at the raw data. Moreover, the interdependence of the variable (relative density) may affect the covariance structure which the PCA relies upon. Why not using the PCA on the logarithm of the raw data or on a relative density compared to the control group on a region-per-region basis instead of the whole brain?

Fig. 2B: it's unclear to me why the regions are connected by a line. Such representation is normally used for time series/within-subject series. What is the rationale for the order of the regions and the use of the line? The line connecting randomly organized regions is meaningless and confusing.

Fig 6A. the correlation matrices are difficult to interpret because of the low resolution and arbitrary order of brain regions. I recommend using hierarchical clustering and/or a combination of hierarchical clustering and anatomical organization (e.g. PMID: 31937658). While it is difficult to add the name of the regions on the graph I recommend providing supplementary figures with large high-resolution figures with the name of each brain region so the reader can actually identify the correlation between specific brain regions and the whole brain,

Rationale for Metric Choice: Note that I do not dispute the choice of the log which is appropriate, it is the choice of using the relative density that I am questioning.

5. I am still having difficulties understanding Fig. 3.<br /> Panel A: The lack of identification for the dots in panel A makes it impossible to understand which regions are relevant.<br /> Panel B: what is the metric that the up/down arrow summarizes? Fos density? Relative density? PC1/2?<br /> Panel C: it's unclear to me why the regions are connected by a line. Such representation is normally used for time series/within-subject series. What is the rationale for the order of the regions?

Reviewer #3 (Public Review):

The present study presents a comprehensive exploration of the distinct impacts of Isoflurane and Ketamine on c-Fos expression throughout the brain. To understand the varying responses across individual brain regions to each anesthetic, the researchers employ principal component analysis (PCA) and c-Fos-based functional network analysis. The methodology employed in this research is both methodical and expansive. Notably, the utilization of a custom software package to align and analyze brain images for c-Fos positive cells stands out as an impressive addition to their approach. This innovative technique enables effective quantification of neural activity and enhances our understanding of how anesthetic drugs influence brain networks as a whole.

The primary novelty of this paper lies in the comparative analysis of two anesthetics, Ketamine and Isoflurane, and their respective impacts on brain-wide c-Fos expression. The study reveals the distinct pathways through which these anesthetics induce loss of consciousness. Ketamine primarily influences the cerebral cortex, while Isoflurane targets subcortical brain regions. This finding highlights the differing mechanisms of action employed by these two anesthetics-a top-down approach for Ketamine and a bottom-up mechanism for Isoflurane. Furthermore, this study uncovers commonly activated brain regions under both anesthetics, advancing our knowledge about the mechanisms underlying general anesthesia.

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.

Reviewer #3 (Public Review):

Summary:<br /> The study conducted by Ouasti et al. is an elegant investigation of fission yeast CAF-1, employing a diverse array of technologies to dissect its functions and their interdependence. These functions play a critical role in specifying interactions vital for DNA replication, heterochromatin maintenance, and DNA damage repair, and their dynamics involve multiple interactions. The authors have extensively utilized various in vitro and in vivo tools to validate their model and emphasize the dynamic nature of this complex.

Strengths:<br /> Their work is supported by robust experimental data from multiple techniques, including NMR and SAXS, which validate their molecular model. They conducted in vitro interactions using EMSA and isothermal microcalorimetry, in vitro histone deposition using Xenopus high-speed egg extract, and systematically generated and tested various genetic mutants for functionality in in vivo assays. They successfully delineated domain-specific functions using in vitro assays and could validate their roles to large extent using genetic mutants. One significant revelation from this study is the unfolded nature of the acidic domain, observed to fold when binding to histones. Additionally, the authors also elucidated the role of the long KER helix in mediating DNA binding and enhancing the association of CAF-1 with PCNA. The paper effectively addresses its primary objective and is strong.

Weaknesses:<br /> A few relatively minor unresolved aspects persist, which, if clarified or experimentally addressed by the authors, could further bolster the study.

1. The precise function of the WHD domain remains elusive. Its deletion does not result in DNA damage accumulation or defects in heterochromatin maintenance. This raises questions about the biological significance of this domain and whether it is dispensable. While in vitro assays revealed defects in chromatin assembly using this mutant (Figure 5), confirming these phenotypes through in vivo assays would provide additional assurance that the lack of function is not simply due to the in vitro system lacking PTMs or other regulatory factors.

2. The observation of increased Pcf2-gfp foci in pcf1-ED* cells, particularly in mono-nucleated (G2-phase) and bi-nucleated cells with septum marks (S-phase), might suggest the presence of replication stress. This could imply incomplete replication in specific regions, leading to the persistence of Caf1-ED*-PCNA factories throughout the cell cycle. To further confirm this, detecting accumulated single-stranded DNA (ssDNA) regions outside of S-phase using RPA as an ssDNA marker could be informative.

3. Moreover, considering the authors' strong assertion of histone binding defects in ED* through in vitro assays (Figure 2d and S2a), these claims could be further substantiated, especially considering that some degree of histone deposition might still persist in vivo in the ED* mutant (Figure 7d, viable though growth defective double ED*+hip1D mutants). For example, the approach, akin to the one employed in Fig. 6a (FLAG-IPs of various Pcf1-FLAG-tagged mutants), could also enable a comparison of the association of different mutants with histones and PCNA, providing a more thorough validation of their findings.

4. It would be valuable for the authors to speculate on the necessity of having disordered regions in CAF1. Specifically, exploring the overall distribution of these domains within disordered/unfolded structures could provide insightful perspectives. Additionally, it's intriguing to note that the significant disparities observed among mutants (ED*, PIP*, and KER*) in in vitro assays seem to become more generic in vivo, except for the indispensability of the WHD-domain. Could these disordered regions potentially play a crucial role in the phase separation of replication factories? Considering these questions could offer valuable insights into the underlying mechanisms at play.

eLife assessment

This important study advances our understanding of the machinery that couples DNA synthesis with the deposition of histone proteins onto newly synthesized DNA. A solid array of experiments combines NMR, protein biochemistry, and in vivo analyses of Chromatin Assembly Factor-1 of fission yeast. The work is of interest to researchers in the field of chromosome/chromatin biology as well as epigenetics.

Reviewer #1 (Public Review):

Summary:<br /> This paper makes important contributions to the structural analysis of the DNA replication-linked nucleosome assembly machine termed Chromatin Assembly Factor-1 (CAF-1). The authors focus on the interplay of domains that bind DNA, histones, and replication clamp protein PCNA.

Strengths:<br /> The authors analyze soluble complexes containing full-length versions of all three fission yeast CAF-1 subunits, an important accomplishment given that many previous structural and biophysical studies have focused on truncated complexes. New data here supports previous experiments indicating that the KER domain is a long alpha helix that binds DNA. Via NMR, the authors discover structural changes at the histone binding site, defined here with high resolution. Most strikingly, the experiments here show that for the S. pombe CAF-1 complex, the WHD domain at the C-terminus of the large subunit lacks DNA binding activity observed in the human and budding yeast homologs, indicating a surprising divergence in the evolution of this complex. Together, these are important contributions to the understanding of how the CAF-1 complex works.

Weaknesses:<br /> 1. There are some aspects of the experimentation that are incompletely described:

In the SEC data (Fig. S1C) it appears that Pcf1 in the absence of other proteins forms three major peaks. Two are labeled as "1a" (eluting at ~8 mL) and "1b" (~10-11 mL). It appears that Pcf1 alone or in complex with either or both of the other two subunits forms two different high molecular weight complexes (e.g. 4a/4b, 5a/5b, 6a/6b). There is also a third peak in the analysis of Pcf1 alone, which isn't named here, eluting at ~14 mL, overlapping the peaks labeled 2a, 4c, and 5c.

The text describing these different macromolecular complexes seems incomplete (p. 3, lines 32-33): "When isolated, both Pcf2 and Pcf3 are monomeric while Pcf1 forms large soluble oligomers". Which of the three Pcf1-alone peaks are oligomers, and how do we know? What is the third peak? The gel analysis across these chromatograms should be shown.

More importantly, was a particular SEC peak of the three-subunit CAF-1 complex (i.e. 4a or 4b) characterized in the further experimentation, or were the data obtained from the input material prior to the separation of the different peaks? If the latter, how might this have affected the results? Do the forms inter-convert spontaneously?

2. Given the strong structural predication about the roles of residues L359 and F380 (Fig. 2f), these should be mutated to determine effects on histone binding.

3. Could it be that the apparent lack of histone deposition by the delta-WHD mutant complex occurs because this mutant complex is unstable when added to the Xenopus extract?

Reviewer #2 (Public Review):

Summary:<br /> The authors describe the structure-functional relationship of domains in S. pombe CAF-1, which promotes DNA replication-coupled deposition of histone H3-H4 dimer. The authors nicely showed that the ED domain with an intrinsically disordered structure binds to histone H3-H4, that the KER domain binds to DNA, and that, in addition to a PIP box, the KER domain also contributes to the PCNA binding. The ED and KER domains as well as the WHD domain are essential for nucleosome assembly in vitro. The ED, KER domains, and the PIP box are important for the maintenance of heterochromatin.

Strengths:<br /> The combination of structural analysis using NMR and Alphafold2 modeling with biophysical and biochemical analysis provided strong evidence on the role of the different domain structures of the large subunit of SpCAF-1, spPCF-1 in the binding to histone H3-H4, DNA as well as PCNA. The conclusion was further supported by genetic analysis of the various pcf1 mutants. The large amounts of data provided in the paper support the authors' conclusion very well.

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.

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.

Reviewer #1 (Public Review):

Summary:<br /> 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:<br /> 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.

Weaknesses:<br /> 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.

Reinforcement learning mechanisms:<br /> 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.

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.

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 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.

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.

Agent-based simulations:<br /> 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.

Reviewer #2 (Public Review):

Summary:<br /> 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:<br /> 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.

Weaknesses:<br /> 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.

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.

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.

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.

In conclusion, the manuscript was well written and for the most part easy to follow. The format of 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.

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.

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 a disruption of the interaction between the PsbT subunit and D1 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.

eLife assessment:

This study adds a fundamental new perspective to a long-standing question: What controls the repair of photosystem II (PSII), a key process in maintaining and optimizing photosynthesis? The work supports a role for chemical modification in the recognition and subsequent degradation of a key protein subunit of PSII by a bacterial-type protease, suggesting that tryptophan oxidation of components of the photosynthetic apparatus after high light stress plays a critical role in initiating the PSII repair system. The evidence supporting the authors' conclusions is solid.

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.

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?

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.

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.

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:

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. 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). 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. 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?

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.

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?

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.

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. 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. 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.

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).

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.

eLife assessment

This important study makes use of AlphaFold2 to predict the models of tens of cohesin subcomplexes from different species. The models, which are in most cases consistent with published cohesin variants with compromised in vitro and in vivo cohesin activity, provide convincing evidence that leads to testable hypotheses of cohesin dynamics and regulation. More broadly, this study serves as an example of how to use AlphaFold2 to build models of protein complexes that involve the docking of flexible regions to globular domains.

Reviewer #1 (Public Review):

There are a number of outstanding questions concerning how cohesin turnover on DNA is controlled by various accessory factors and how such turnover is controlled by post-translational modification. In this paper, Nasmyth et al. perform a series of AlphaFold structure predictions that aim to address several of these outstanding questions. Their structure predictions suggest that the release factor WAPL forms a ternary complex with PDS5 and SA/SCC3. This ternary complex appears to be able to bind the N-terminal end of SCC1, suggesting how formation of such a complex could stabilize an open state of the cohesin ring. Additional calculations suggest how the Eco/ESCO acetyltransferases and Sororin engage the SMC3 head domain presumably to protect against WAPL-mediated release.

This work thus demonstrates the power of AF prediction methods and how they can lead to a number of interesting and testable hypotheses that can transform our understanding of cohesin regulation. These findings require orthogonal experimental validation, but authors argue convincingly that such validation should not be a pre-requisite to publication.

In their revised version, the authors did not systematically include model confidence scores, and it therefore remains difficult for the reader to evaluate the reliability of the models obtained. The authors correctly point out that such metrics are available on figshare. It is therefore possible to obtain such information. The caveat is that it remains to the user to identify and extract the relevant information. While they claim that they have labeled N- and C-termini in their figures, no such labeling can be seen in the revised version. Addition of such labels, at least for some of the figures, would help the user to navigate the models.

The authors have now updated figure legends to indicate which protein is referred to by the chain labels shown in PAE plots.

It is exciting to see AF-multimer predictions being applied to cohesin. As some of the reported interactions are not universally conserved and some involve relatively small interfaces the possibility arises that these interfaces show poor or borderline confidence scores. As some of these interfaces map to mutants that have previously been obtained by hypothesis-free genetic screens and mutational analyses, they appear nevertheless valid. Thus, an important point to make is that even interfaces that show modest confidence scores may turn out to be valid while others may be not.

Reviewer #2 (Public Review):

The ATPase protein machine cohesin shapes the genome by loop extrusion and holds sister chromatids together by topological entrapment. When executing these functions, cohesin is tightly regulated by multiple cofactors, such as Scc2/Nipbl, Pds5, Wapl, and Eco1/Esco1/2, and it undergoes dynamic conformational changes with ATP binding and hydrolysis. The mechanisms by which cohesin extrudes DNA loops and medicates siter-chromatid cohesion are still not understood. A major reason for the lack of understanding of cohesin dynamics and regulation is the failure to capture the structures of intact cohesin in different nucleotide-bound states and in complex with various regulators. So far only the ATP state cohesin bound to NIPBL and DNA have been experimentally determined.

In this manuscript, Nasmyth et al. made use of the powerful protein structure prediction tool, AlphaFold2 (AF), to predict the models of tens of cohesin subcomplexes from different species. The results provide important insight into how the Smc3-Scc1 DNA exiting gate is opened, how Pds5 and Wapl maintain the opened gate, how Pds5 and Scc3/SA recruit different cofactors, how Eco1 and Sororin antagonize Wapl, and how Scc2/Nipbl interacts with Scc3/SA. The models are for the most part consistent with published mutations in these proteins that affect cohesin's functions in vitro and in vivo and raise testable hypotheses of cohesin dynamics and regulation. This study also serves as an example of how to use AF to build models of protein complexes that involve the docking of flexible regions to globular domains.

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.

eLife assessment

This study presents useful findings regarding the impact of forest cover and fragmentation on the prevalence of malaria in non-human primates. The evidence supporting the claims of the authors is, however, incomplete, as the sampling design cannot adequately address the geospatial issues that this study focuses on.

Joint Public Review:

The study as a concept is well designed, although there is still one issue I see in the methodology.

I still have concerns with their attempts to combine the different scales of data. While the use of point data is great, it limits the sample size, and they have included the district to country level data to try and increase the sample size. The problem is that although they try to get an overall estimate at the district/state/country by taking 10 random sample points, which could be a method to get an estimate for the district/state/country. It would be a suitable method if the primates were evenly distributed across the district/state/country. The reality is that the primates are not evenly distributed across the district/state/country therefore the random point sampling is not a reasonable method to get an estimate of the environmental variables in relation to the macaques. For example if you had a mountainous country and you took 10 random points to estimate altitude, you would end up with a large number, but if all the animals of interest lived on the coast, your average altitude is meaningless in relation to the animals of interest as they are all living at low altitude. The fact that the model relies less on highly variable components and places more reliance on less variable components, is really not relevant as the district/state/country measurements have no real meaning in relation to the distribution of masques.

A simple possible way forward could be to run the model without the district/state/country samples and see what the outcome is. If the outcome is similar then the random point method may be viable (but if it gives the same outcome as ignoring those samples then you don't need the district/state/country samples). If you get a totally different outcome then it should raise concerns about using the district/state/country samples.

This paper is a really nice piece of work and is a valuable contribution but the district/state/country sample issue really needs to be addressed.

Reviewer #2 (Public Review):

Summary:<br /> This work tests the hypothesis that water coordination in WNK kinases is linked to allosteric control of activity. It is proposed that dimeric WNK is inactive and bound to some conserved water molecules, and that monomerization/activation involves departure of these waters. New data here include a crystal structure of monomeric WNK1 which shows missing waters compared to the dimeric structure, in support of the hypothesis. Mutant proteins of a different isozyme (WNK3) designed to disrupt water coordination were produced, and activity and quaternary structure were measured. The results with WNK3 do not clearly support or refute the hypothesis as there is no systematic correlation between mutations designed to disrupt water coordination and activity or quaternary structure.

Strengths:<br /> The most interesting result presented here is that P1 crystals of WNK1 convert to P21 in the presence of PEG400 and still diffract (rather than being destroyed as the crystal contacts change, as one would expect). All of the assays for activity and osmolyte sensing are carried out well.

Weaknesses:<br /> The rationale for using WNK3 for the mutagenesis study is that it is more sensitive to osmotic pressure than WNK1. I think that WNK1 would have been a better platform because of the direct correlation to the structural work leading to the hypothesis being tested. All of the crystallographic work is WNK1; it is not logical to jump to WNK3 without other practical considerations.

Osmolyte sensing was tested by measuring ATP consumption as a function of PEG400 (Figure 6). Data for the subset of mutants analyzed by this assay showed increasing activity. It is not clear why the same collection of mutant proteins analyzed in the experiments of Figure 5 was not also measured for osmolyte sensing in Figure 6.

The last set of data presented uses light scattering to test whether the WNK3 mutant proteins exhibit quaternary structural changes consistent with the monomer/dimer hypothesis. If they did, one would expect a higher degree of monomer for those that are activated by mutation, and a lower amount of monomer (like wt) for those that are not. Instead, one of the mutant proteins that showed the most chloride inhibition (Y346F) had a quaternary structure similar to the wt protein, and others have similar monomer/dimer mixtures but distinct chloride inhibition profiles (K307A and M301A). I don't see how the light scattering data contribute to this story other than to refute the hypothesis by showing a lack of correlation between quaternary structure, water binding, and activity. This is another reason why the disconnect between WNK1 and WNK3 could be a problem. All of the detailed structural work with WNK1 must be assumed with WNK3; perhaps the light scattering data are contradicting this assumption?

eLife assessment

This study presents a potentially valuable investigation of water coordination in a specific kinase family with a focus on the regulation of osmosensing protein kinases. X-ray crystallographic approaches combined with functional assays are used to address the hypothesis that bound water participates in the osmosensing mechanism as an allosteric kinase inhibitor. Evidence for changes in kinase conformation and space group of the crystal as a function of added low molecular weight polyethylene glycol is solid, but there alternative interpretations for much of the other data cannot be excluded and the work thus remains incomplete. With stronger evidence and/or alternative explanations explored, the work would be of considerable interest to the kinase field as well as colleagues studying allosteric regulation of protein function.

Reviewer #1 (Public Review):

Summary:<br /> This manuscript addresses the regulation of the osmosensing protein kinases, WNK1 and WNK3. Prior work by the authors has shown that these enzymes are activated by PEG400 or ethylene glycol and inhibited by chloride ion, and that activation is associated with a conformational transition from dimer to monomer. In X-ray structures of the WNK1/SA inactive dimer, a water-mediated hydrogen bond network was observed between the catalytic loop (CL) and the activation loop (AL), named CWN1. This led to the proposal that bound water may be part of the osmosensing mechanism.

The current study carries this work further, by applying PEG400 to Xtals of dimeric WNK1/SA. This results in a change in kinase conformation and space group, along with 4-9 fewer waters in CWN1 and the complete disappearance of another water cluster (CWN2) located at the dimer interface. Six conserved residues lining the CWN1 pocket in WNK3 are mutated to determine effects on activity and inhibition by chloride ion (measured by AL autophosphorylation) and monomer-dimer interconversion (light scattering).

The results show that two mutants (E314Q/A in WNK3) at a site central to the water cluster result in increased kinase activity (autophosphorylation), and increased SLS, interpreted as aggregation. Three sites (D279A, Y346F, M301A) inhibit kinase activity with varying effects on oligomerization - Y346A and M301A retain monomer-dimer ratios similar to WT while D279N promotes aggregation. K236A and K307A show activity and monomer:dimer ratios similar to WT. Selected mutants (E314Q, D279N, Y346F) and WT appear to retain osmosensitivity with comparable activation by PEG400.

The study concludes that osmolytes may activate the kinase by removing waters from the CWN1 and CWN2 clusters, suggesting that waters might be considered allosteric ligands that promote the inactive structure of WNKs. The differing effects of mutations may be ascribed to disruption of the water networks as well as inhibitory perturbations at the active site.

Strengths:<br /> This study presents a novel and unique function for bound water, and its potential role to explain osmosensory regulation. The mechanism is innovative and the new structures and mutational data presented by the work will be useful for further investigations of the mechanisms that enable cells to respond to osmotic pressure.

Weaknesses:<br /> Given that all mutants tested showed the same degree of activation by PEG400, it seemed possible that PEG400 might be an allosteric activator of WNK1/3 through direct binding interactions. Perhaps PEG400 eliminates CWN1/2 waters by inducing conformational changes so that water loss is an effect not a cause of activation. To address this it would be helpful to comment on whether new electron densities appeared in the X-ray structure of WNK1/SA/PEG400 that might reflect PEG400 interactions with chains A or B. It would also be helpful to discuss any experiments that might have been done in previous work to examine the direct binding of glycerol and other osmolytes to WNKs.

The study would benefit from a deeper discussion about how to reconcile the different effects of mutations. For example, wouldn't most or all of the mutations be expected to disrupt the water network, and relieve the proposed autoinhibition? This seemed especially true for some of the residues, like Y420(Y346), D353(D279), and K310(K236), which based on Fig 3 appeared to interact with waters that were removed by PEG400.

Alternatively, perhaps the waters in CWN2 are more important for maintaining the autoinhibited structure. This possibility would be useful to discuss, and perhaps comment on what may be known about the energetic contributions of bound water towards stabilizing dimers.

It would also be useful to comment on why aggregation of E319Q/A shouldn't inhibit kinase activity instead of activating it.

The X-ray work was done entirely with WNK1 while the mutational work was done entirely with WNK3. Therefore, a simple explanation for the disconnect between structure and mutations might be that WNK1 and WNK3 differ enough that predictions from the structure of one are not applicable to mutations of the other. It would be helpful to describe past work comparing the structure and regulation of WNK1 and WNK3 that support the assumption of their interchangeability.

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.

Reviewer #2 (Public Review):

Summary:

The manuscript's main claim is that the absence of H2-O, a component of the MHC II presentation pathway, promotes regulatory T cell development and function.

Unfortunately, the submitted material is not sufficient for proper evaluation of the manuscript, both in terms of the significance of the findings and the strength of the supporting evidence.

Major issues include:

- the scRNAseq (shown in Fig. 5) is too rudimentary to allow any conclusion. Statements in the text (eg "Principle Component Analysis (PCA) of the normalized scRNA-seq data identified 11 distinct CD4 T cell clusters", line 166) suggest that additional expertise should be leveraged for these analyses.

- Most flow cytometry data (Figs. 1 and 2) shows marginal (at best) differences on y-axis truncated bar graphs, with no original data plot, gating strategies, etc., severely challenging conclusions drawn from this data.

eLife assessment

This paper seeks to understand how the presentation of peptides by medullary thymic epithelial cells may be regulated by the MHCII peptide loading modulator, H2-O, and how this may affect the selection of regulatory T (Treg) cells. Further work is needed to ensure that the findings are robust: currently the analysis of data is inadequate and inconsistencies in the reported findings are not placed in context with results from other groups. The current version does not provide sufficient support for the claims regarding the effects on Treg cell selection.

Reviewer #1 (Public Review):

The non-classical MHCII-like protein H2-M is essential for the loading of peptides on MHCII. The discovery that DM was partnered with a second MHCII-like protein, H2-O, which squelched or modified its activity was confounding. It was immediately speculated that H2-O was likely diminished self-peptide presentation. This led to the hypothesis that H2-O was involved in preventing unwanted CD4 T cell activation, thereby making autoimmunity less likely. 25 years of analysis of H2-O deficient mice have, indeed, shown that the self-peptide repertoire in the absence of H2-O is modestly altered. Demonstrating that autoimmunity results from this altered peptide repertoire has been decidedly less convincing. Old mice are reported to have increased serum anti-nuclear antibody titers, but mice prone to type 1 diabetes (T1D) and systemic lupus erythematosus (SLE) were not impacted by the loss of H2-O (Lee et al, 2021). Induction of the multiple sclerosis-like disease, EAE, in mice, was also shown to not be impacted by Lee et al 2021, although in a previous paper (Welsh et al 2020), the authors of this current manuscript suggest otherwise. Unfortunately, these discrepancies are not acknowledged by the authors, and the papers are, for the most part, not referenced.

In addition to antigen-presenting cells, H2-O is also found in MHCII-expressing medullary epithelial cells, suggesting it might play a role in T-cell selection. Direct data to support this idea, however, has, at most, shown a minimal impact. In this manuscript, the authors follow up on their previous paper (Welsh et al, 2020) to further evaluate changes to T cell development. The conclusions are that H2-O impacts Treg development and changes the frequency and homeostasis of CD4 T cells. Although these would be interesting results, the data analysis is flawed, the presentation is incomplete, and the conclusions are exaggerated.

T-cell development analysis shown in Figs. 1 and 2 use the discovery from the Hogquist lab (Breed et all 2019) that thymocytes destined for clonal deletion can be differentiated from those still "auditioning" for selection by FACS for expression of cleaved caspase 3. Detection relies on complex FACS analysis that requires the exclusion of multiple populations, followed by accurate gating on CD5+TCRb+ cells (see Hogquist Fig. 1A). The authors apparently neglected to use the essential gating steps, but rather only used CD4 and CCR7 expression (Fig. 1A). This deviation from the Hogquist approach makes interpretation of Figs 1 and 2 meaningless. Even if this is an oversight in the description of the experiments, key conclusions are drawn from minimal changes to CD69 expression. CD69 is expressed as a continuum in the thymus (a "shoulder") making gating somewhat subjective and prone to variation from experiment to experiment. At the minimum, FACS data should be shown to indicate how these changes were measured, plus variations from mouse to mouse should be plotted, with statistics. FACS data needs to be shown to define how the complex semi-mature, M1, and M2 populations were defined (see Hogquist Fig. 2) from which key conclusions are drawn.

To make the data more robust, 1) cell numbers must be included for all experiments;

2) rather than normalizing results to "the average H2-O WT levels", the actual data should be included;

3) figures should be more completely labeled/described;

4) FACS gating strategies should be clearly laid out (again, see Hogquist for examples). Furthermore, efforts must be made to explain why results are so different from analyses of H2-O deficient mice that have been published by many other groups. For example, the reported "dramatic increase in the proportion of CD3+CD4+ T cells" is not consistent with previous reports starting with Lars Karlsson's initial report (Liljedahl et al 1998). Extensive spontaneous activation of CD4 T cells has also not been reported in other papers that have studied these mice. Again, the paper is not placed in the context of the long, very thorough analysis of both the H2-O deficient mice and the study of H2-O/DO and H2-M/DM in general.

eLife assessment

The ExA-SPIM methodology developed will be important to the field of light sheet microscopy as the new technology provides an impressive field of view making it possible to image the entire expanded mouse brain at cellular and subcellular resolution. The authors provide solid evidence that mostly supports the conclusions. Certain statements were deemed to be overstating the method's capabilities, in particular, the claim of "near isotropic resolution" is not supported by the data as there is a large discrepancy between the x/y and z-resolution. Improved characterization of the new technology and a more expanded discussion of prior work would also be beneficial to the reader.

Reviewer #1 (Public Review):

Summary:<br /> Glaser et al present ExA-SPIM, a light-sheet microscope platform with large volumetric coverage (Field of view 85mm^2, working distance 35mm), designed to image expanded mouse brains in their entirety. The authors also present an expansion method optimized for whole mouse brains and an acquisition software suite. The microscope is employed in imaging an expanded mouse brain, the macaque motor cortex, and human brain slices of white matter.

This is impressive work and represents a leap over existing light-sheet microscopes. As an example, it offers a fivefold higher resolution than mesoSPIM (https://mesospim.org/), a popular platform for imaging large cleared samples. Thus while this work is rooted in optical engineering, it manifests a huge step forward and has the potential to become an important tool in the neurosciences.

Strengths:<br /> -ExA-SPIM features an exceptional combination of field of view, working distance, resolution, and throughput.

-An expanded mouse brain can be acquired with only 15 tiles, lowering the burden on computational stitching. That the brain does not need to be mechanically sectioned is also seen as an important capability.

-The image data is compelling, and tracing of neurons has been performed. This demonstrates the potential of the microscope platform.

Weaknesses:<br /> -There is a general question about the scaling laws of lenses, and expansion microscopy, which in my opinion remained unanswered: In the context of whole brain imaging, a larger expansion factor requires a microscope system with larger volumetric coverage, which in turn will have lower resolution (Figure 1B). So what is optimal? Could one alternatively image a cleared (non-expanded) brain with a high-resolution ASLM system (Chakraborty, Tonmoy, Nature Methods 2019, potentially upgraded with custom objectives) and get a similar effective resolution as the authors get with expansion? This is not meant to diminish the achievement, but it was unclear if the gains in resolution from the expansion factor are traded off by the scaling laws of current optical systems.

-It was unclear if 300 nm lateral and 800 nm axial resolution is enough for many questions in neuroscience. Segmenting spines, distinguishing pre- and postsynaptic densities, or tracing densely labeled neurons might be challenging. A discussion about the necessary resolution levels in neuroscience would be appreciated.

-Would it be possible to characterize the aberrations that might be still present after whole brain expansion? One approach could be to image small fluorescent nanospheres behind the expanded brain and recover the pupil function via phase retrieval. But even full width half maximum (FWHM) measurements of the nanospheres' images would give some idea of the magnitude of the aberrations.

Reviewer #2 (Public Review):

Summary:<br /> In this manuscript, Glaser et al. describe a new selective plane illumination microscope designed to image a large field of view that is optimized for expanded and cleared tissue samples. For the most part, the microscope design follows a standard formula that is common among many systems (e.g. Keller PJ et al Science 2008, Pitrone PG et al. Nature Methods 2013, Dean KM et al. Biophys J 2015, and Voigt FF et al. Nature Methods 2019). The primary conceptual and technical novelty is to use a detection objective from the metrology industry that has a large field of view and a large area camera. The authors characterize the system resolution, field curvature, and chromatic focal shift by measuring fluorescent beads in a hydrogel and then show example images of expanded samples from mouse, macaque, and human brain tissue.

Strengths:<br /> I commend the authors for making all of the documentation, models, and acquisition software openly accessible and believe that this will help assist others who would like to replicate the instrument. I anticipate that the protocols for imaging large expanded tissues (such as an entire mouse brain) will also be useful to the community.

Weaknesses:<br /> The characterization of the instrument needs to be improved to validate the claims. If the manuscript claims that the instrument allows for robust automated neuronal tracing, then this should be included in the data.

eLife assessment

This study is a useful analysis of the organization of synaptic proteins of a developing synapse in the binocular path visual system and how it is impacted by manipulations in activity. The original images collected by STORM microscopy are state-of-the-art in terms of the high-resolution view of the protein components of a synapse in intact tissue. However, the analysis is incomplete and does not fully support several of the conclusions of the study.

Reviewer #1 (Public Review):

Summary:<br /> This publication applies 3D super-resolution STORM imaging to understanding the role of developmental neural activity in the clustering of retinal inputs to the mouse dorsal lateral geniculate nucleus (dLGN). The authors argue that retinal ganglion cell (RGC) synaptic boutons start forming clusters early in postnatal development (P2). They then argue that these clusters contribute to eye-specific segregation of retinal inputs by activity-dependent stabilization of nearby boutons from the same eye. The data provided is N=3 animals for each condition of P2, P4, and P8 animals in wild-type mice and in mice where early patterns of structured retinal activity are blocked.

Strengths:<br /> The 3D storm imaging of pre and postsynaptic elements provides convincing high-resolution localization of synapses.

The experimental design of comparing ipsilateral and contralateral RGC axon boutons in a region of the dLGN that is known to become contralateral is elegant. The design makes it possible to relate fixed time point structural data to a known outcome of activity-dependent remodeling.

Weaknesses:<br /> Based on previous literature, it is known that synapse density, synapse clustering, and synaptic specificity increase during postnatal development. Previous work has also shown that both the changes in synaptic clustering and synaptic specificity are affected by retinal activity. The data and analysis provided by the authors add little unambiguous evidence that advances this understanding.

General problem 1: Most of the statistical analysis is limited to ANOVA comparison of axons from the contralateral and ipsilateral retina in the contralateral dLGN. The hypothesis that ipsilateral and contralateral axons would be statistically identical in the contralateral dLGN is not a plausible hypothesis so rejecting the hypothesis with P < X does not advance the authors' arguments beyond what was already known.

General problem 2: Most of the interpretation of data is qualitative. While error bars are provided, these error bars are not used to draw conclusions. Given the small sample size (N=3), there is a large degree of uncertainty regarding the magnitude of changes (synapse size, number, specificity). The authors base their conclusions on the averages of these values when the likely degree of uncertainty could allow for the opposite interpretation.

General problem 3: Two of the four results sections depend on using the frequency of single active zone vGlut2 clusters near multiple active zone vGlut2 as a proxy for synaptic stabilization of the single active zone vGlut2 clusters by the multiple active zone vGlut2 clusters. The authors argue that the increased frequency of same-eye single active zone clusters relative to opposite-eye single active zone clusters means that multiple active zone vGlut2 clusters are selectively stabilizing single active zone clusters. There are other plausible explanations for this observation that are not eliminated. An increased frequency of nearby single active zone clusters would also occur if RGC axons form more than one synapse in the dLGN. Eye-specific segregation is, by definition, a relative increase in the frequency of nearby boutons from the same eye. The authors were, therefore, guaranteed to observe a non-random relationship between boutons from the same eye. The authors do compare their measures to a random model, but I could not find a description of the model. I would expect that the model would need to account for RGC arbor size, arbor structure, bouton number, and segregation independent of multi-active-zone vGlut2 clusters. The most common randomization for the type of analysis described here, a shift in the positions of single-active zone boutons, would not be adequate.

In discussing the claimed cluster-induced stabilization of nearby boutons, the authors state that the specificity increases with age due to activity-dependent refinement. Their quantification does not support an increase in specificity with age. In fact, the high degree of clustering "specificity" they observe at P2 argues for the trivial same axon explanation.

Analysis of specific claims:

Result Section 1

Most of the figures show mean, error bars, and asterisks, but not the three data points from which these statistics are derived. Large changes in variance from condition to condition suggest that displaying the data points would provide more useful information.

Claim 1: Contralateral density increases more than ipsilateral in the contralateral region over the course of development. This claim is supported by the qualitative comparison of means and error bars in Figure 2D. The argument could be made quantitative by providing a confidence interval for synapse density increase for dominant and non-dominant synapse density. A confidence interval could then be generated for the difference in this change between the two groups. Currently, the most striking effect is a big difference in variance between P4 and P8 for dominant eye complex synapses. Given that N=3, I assume there is one extreme outlier here.

Claim 2: The fraction of multiple-active zone vGlut2 clusters increases with age. This claim is weakly supported by a qualitative reading of panel 1E. The error bars overlap so it is difficult to know what the range of possible increases could be. In the text, the authors report mean differences without confidence intervals (or any other statistics). The reported results should, therefore, be interpreted as a description of their three mice and not as evidence about mice in general.

Figure S1. Panel A makes the point that the study could not be done without STORM by comparing the STORM images to "Conventional" images. The images are over-saturated low-resolution images. A reasonable comparison would be to a high-quality quality confocal image acquired with a high NA objective (~1.4) and low laser power (PSF ~ 0.2 x 0.2 x 0.6 um) that was acquired over the same amount of time it takes to acquire a STORM volume.

Result section 2.

Claim 1: The ipsi/contra (in contra LGN) difference in VGluT2 cluster volume increases with development. While there are many p-values listed, the main point is not directly quantified. A reasonable way to quantify the relative increase in volume could be in the form: the non-dominant volumes were 75%-95%(?) of the dominant volume at P2 and 60%-80% (?) at P8. The difference in change was -5 to 15%(?).

Claim 2: Complex synapses (vGlut2 clusters with multiple active zones) represent clusters of simple synapses and not single large boutons with multiple active zones. The authors argue that because vGlut2 cluster volume scales roughly linearly with active zone number, the vGlut2 clusters are composed of multiple boutons each containing a single active zone. Their analysis does not rule out the (known to be true) possibility that RGC bouton sizes are much larger in boutons with multiple active zones. The correlation of volume and active zone number, by itself, does not resolve the issue. A good argument for multiple boutons might be that the variance is smallest in clusters with 4 active zones (looks like it in the plot) since they would be the average of four active zones to vesicle pool ratios. It is very likely that the multi-active zone vGlut2 clusters represent some clustering and some multi-synaptic boutons. The reference cited by the authors as evidence for the presence of single active zone boutons in young tissue does not rule out the existence of multiple active zone boutons.

Several arguments are made that depend on the interpretation of "not statistically significant" (n.s.) meaning that "two groups are the same" instead of "we don't know if they are different". This interpretation is incorrect and materially impacts the conclusions.

Several arguments are made that interpret statistical significance for one group and a lack of statistical significance for another group meaning that the effect was bigger in the first group. This interpretation is incorrect and materially impacts the conclusions.

Result Section 3.

Claim 1: Complex synapses stabilize simple synapses. There are alternative explanations (mentioned above) for the observed clustering that negate the conclusions. 1) Boutons from the same axon tend to be found near one another. 2) Any form of eye-specific segregation would produce non-random associations in the analysis as performed. The authors compare each observation to a random model, but I cannot determine from the text if the model adequately accounts for alternative explanations.

The authors claim that specificity increases over time. Figure 3b (middle) shows that the number of synapses near complex synapses might increase with time (needs confidence interval for effect size), but does not show that specificity (original relative to randomized) increases with time. The fact that nearby simple synapse density is always (P2) very different from random suggests a primarily non-activity-dependent explanation. The simplest explanation is that same-side boutons could be from the same axon whereas different-side axons could not be.

Claim 2: vGlut2 clusters more than 1.5 um away from multi-active zone vGlut2 clusters are not statistically significantly different in size than vGlut2 clusters within 1.5 um of multi-active zone vGlut2 clusters. Therefore "activity-dependent synapse stabilization mechanisms do not impact simple synapse vesicle pool size". The specific measure of 1.5 um from multi-active zone vGlut2 clusters does not represent all possible synapse stabilization mechanisms.

Result Section 4.

Claim: The proximity of complex synapses with nearby simple synapses to other complex synapses with nearby simple synapses from the same eye is used to argue that activity is responsible for all this clustering.

It is difficult to derive anything from the quantification besides 'not-random'. That is a problem because we already know that axons from the left and right eye segregate during the period being studied. All the measures in Section 4 are influenced by eye-specific segregation. Given this known bias, demonstrating a non-random relationship (P<br /> The results can be stated as: If you are a contralateral complex synapse, contralateral complex synapses that are also close to contralateral simple synapses will, on average, be slightly closer to you than contralateral complex synapses that are not close to contralateral ipsilateral synapses. That would be true if there is any eye-specific segregation (which there is).

It is an overinterpretation of the data to claim that the lack of a clear correlation between vGlut2 cluster volume and distance to vGlut2 clusters with multiple active zones provides support for the claim that "presynaptic protein organization is not influenced by mechanisms governing synaptic clustering".

Reviewer #2 (Public Review):

Summary:<br /> In this manuscript, Zhang and Speer examine changes in the spatial organization of synaptic proteins during eye-specific segregation, a developmental period when axons from the two eyes initially mingle and gradually segregate into eye-specific regions of the dorsal lateral geniculate. The authors use STORM microscopy and immunostain presynaptic (VGluT2, Bassoon) and postsynaptic (Homer) proteins to identify synaptic release sites. Activity-dependent changes in this spatial organization are identified by comparing the β2KO mice to WT mice. They describe two types of presynaptic organization based on Bassoon clustering, the complex and the simple synapse. By analyzing the relative densities and distances between these proteins over age, the authors conclude that the complex synapses promote the clustering of simple synapses nearby to form the future mature glomerular synaptic structure.

Strengths:<br /> The data presented is of good quality and provides an unprecedented view at high resolution of the presynaptic components of the retinogeniculate synapse during active developmental remodeling. This approach offers an advance to the previous mouse EM studies of this synapse because of the CTB label allows identification of the eye from which the presynaptic terminal arises. Using this approach, the authors find that simple synapses cluster close to complex synapses over age, that complex synapse density increases with age.

Weaknesses:<br /> From these data, the authors conclude that the complex synapse serves to "promote clustering of like-eye synapses and prohibit synapse clustering from the opposite eye". However, the authors show no causal data to support these ideas. There are a number of issues that the authors should consider:

1. Clustering of retinal synapses is in part due to the fact that retinal inputs synapse on the proximal dendrites. With increased synaptogenesis, there will be increased density of retinal terminals that are closely localized. And with development, perhaps simple synapses mature into complex synapses. Simple synapses may also represent ones that are in the process of being eliminated as previously described by Campbell and Shatz, JNeurosci 1992 (consider citing). Can the authors distinguish these scenarios from the ones that they conclude?

2. The argument that "complex" synapses are the aggregate of "simple" synapses (Fig 2, S2) is not convincing.

3. The authors use of the β2KO mice to assess changes in the organization of synaptic proteins in retinal terminals that have disrupted retinal waves. However, β2-nAChRs are also expressed in the dLGN and other areas of the brain and glutamatergic synapse development has been reported in the CNS independent of the disruption in retinal waves. This issue should be considered when interpreting the total reduced retinal synapse density in the dLGN of the mutant.

4. Outside of a total synapse density difference between WT and β2KO mice, the changes in the spatial organization of synaptic proteins over development do not seem that different. In fact % simple synapses near complex synapses from the non-dominant eye in the mutant is not that different from WT at P8 (Fig 3C), an age when eye-specific segregation is very different between the genotypes. Can the authors explain this discrepancy?

5. The authors use nomenclature that has been previously used and associated with other aspects of retinogeniculate properties. For example, the phrases "simple" and "complex" synapses have been used to describe single boutons or aggregates of boutons from numerous retinal axons, whereas in this manuscript the phrases are used to describe vesicle clusters/release sites with no knowledge of whether they are from single or multiple boutons. Likewise, the use of the word "glomerulus" has been used in the context of the retinogeniculate synapse to refer to a specific pattern of bouton aggregates that involves inhibitory and neuromodulatory inputs. It is not clear how the release sites described by the authors fit in this picture. Finally the use of the word "punishment" is associated with a body of literature regarding the immune system and retinogeniculate refinement-which is not addressed in this study. This double use of the phrases can lead to confusion in the field and should be clarified by clear definitions of how they are used in the current study.

Reviewer #3 (Public Review):

Summary:<br /> This manuscript is a follow-up to a recent study of synaptic development based on a powerful data set that combines anterograde labeling, immunofluorescence labeling of synaptic proteins, and STORM imaging (Cell Reports 2023). Specifically, they use anti-Vglut2 label to determine the size of the presynaptic structure (which they describe as the vesicle pool size), anti-Bassoon to label a number of active zones, and anti-Homer to identify postsynaptic densities. In their previous study, they compared the detailed synaptic structure across the development of synapses made with contra-projecting vs ipsi-projecting RGCs and compared this developmental profile with a mouse model with reduced retinal waves. In this study, they produce a new analysis on the same data set in which they classify synapses into "complex" vs. "simple" and assess the number and spacing of these synapses. From these measurements, they make conclusions regarding the processes that lead to synapse competition/stabilization.

Strengths:<br /> This is a fantastic data set for describing the structural details of synapse development in a part of the brain undergoing activity-dependent synaptic rearrangements. The fact that they can differentiate eye of origin is also a plus.

Weaknesses:<br /> The lack of details provided for the classification scheme as well as the interpretation of small effect sizes limit the interpretations that can be made based on these findings.

1. The criteria to classify synapses as simple vs. complex is critical for all of the analysis in this study. Therefore this criteria for classification should be much more explicit and tested for robustness. As stated in the methods, it is based on the number of active zones which are designated by the number of Bassoon clusters associated with a Vglut2 cluster (line 697). A second part of the criteria is the size of the presynaptic terminal as assayed by "greater Vglut2 signal" (line 116). So how are these thresholds determined? For Bassoon clusters, is one voxel sufficient? Two? If it's one, how often do they see a Bassoon positive voxel with no Vglut2 cluster and therefore may represent "noise"? There is no distribution of Bassoon volumes that is provided that might be the basis for selecting this number of sites. Unfortunately, the images are not helpful. For example, does P8 WT in Figure 1B have 7 or 2? According to Figure 2C, it appears the numbers are closer to 2-4.

The Vglut volume measurements also do not seem to provide a clear criterion. Figure 2 shows that the distributions of Vglut2 cluster volumes for complex and for simple synapses are significantly overlapping.

The authors need to clarify the quantitative approach used for this classification strategy and test how sensitive the results of the study are to how robust this strategy is

2. Effect sizes are quite small and all comparisons are made on medians of distributions. This leads to an n=3 biological replicates for all comparisons. Hence this small n may lead to significant results based on ANOVAS/t-tests, but the statistical power of these effects is quite weak. To accurately represent the variance in their data, the authors should show all three data points for each category (with a SD error bar when possible). They should also include the number of synapses in each category (e.g. the numerators in Figure 1D and the denominators for Figure 1E). For other figures, there are additional statistical questions described below.

3. The authors need to add a caveat regarding their classification of synapses as "complex" vs. "simple" since this is a terminology that already exists in the field and it is not clear that these STORM images are measuring the same thing. For example, in EM studies, "complex" refers to multiple RGCs converging on the same single postsynaptic site. The authors here acknowledge that they cannot assign different AZs to different RGCs so this comparison is an assumption. In Figure 2 they argue this is a good assumption based on the finding that the Vglut column/active zone is constant and therefore each represents a single RGC. However, the authors should acknowledge that they are actually seeing quite different percentages than those in EM studies. For example, in Monavarfeshani et al, eLife 2018, there were no complex synapses found at P8. (Note this study also found many more complex vs. simple synapses in the adult - 70% vs. the 20% found in the current study - but this difference could be a developmental effect). In the future, the authors may want to take another data set in the adult dLGN to make a direct comparison based on numbers and see if their classification method for complex/simple maps onto the one that currently exists in the literature.

4. Figure 3 assays the relative distribution of simple vs. complex synapses. They found that a larger percentage of simple synapses were within 1.5 microns of complex synapses than you would expect by chance for both ipsi and contra projecting RGCs, and hence conclude that complex synapses are sites of synaptic clustering. In contrast, there was no clustering of ipsi-simple to contra-complex synapses and vice versa. The authors also argue that this clustering decreases between P4 and P8 for ipsi projecting RGCs.

This analysis needs much more rigor before any conclusions can be drawn. First, the authors need to justify the 1.5-micron criteria for clustering and how robust their results are to variations in this distance. Second, these age effects need to be tested for statistical significance with an ANOVA (all the stats presented are pairwise comparisons to means expected by random distributions at each age). Finally, the authors should consider what n's to use here - is it still grouped by biological replicate? Why not use individual synapses across mice? If they do biological replicates, then they should again show error bars for each data point in their biological replicates. And they should include the number of synapses that went into these measurements in the caption.

5. Line 211-212 - the authors conclude that the absence of clustered ipsi-simple synapses indicates a failure to stabilize (Figure 3). Yet, the link between this measurement and synapse stabilization is not clear. In particular, the conclusion that "isolated" synapses are the ones that will be eliminated seems to be countered by their finding in Figure 3D/E which shows that there is no difference in vesicle pool volume between near and far synapses. If isolated synapses are indeed the ones that fail to stabilize by P8, wouldn't you expect them to be weaker/have fewer vesicles? Also, it's hard to tell if there is an age-dependent effect since the data presented in Figures 3D/E are merged across ages.

eLife assessment

This fundamental study has the potential to substantially advance our understanding of human locomotion in complex real-world settings. The evidence supporting the conclusions is solid, although the quantitative analysis and presentation of results lack clarity. The work will be of interest to neuroscientists, kinesiologists, computer scientists, and engineers working on human locomotion.

Reviewer #1 (Public Review):

Summary:<br /> The work of Muller and colleagues concerns the question of where we place our feet when passing uneven terrain, in particular how we trade-off path length against the steepness of each single step. The authors find that paths are chosen that are consistently less steep and deviate from the straight line more than an average random path, suggesting that participants indeed trade-off steepness for path length. They show that this might be related to biomechanical properties, specifically the leg length of the walkers. In addition, they show using a neural network model that participants could choose the footholds based on their sensory (visual) information about depth.

Strengths:<br /> The work is a natural continuation of some of the researchers' earlier work that related the immediately following steps to gaze [17]. Methodologically, the work is very impressive and presents a further step forward towards understanding real-world locomotion and its interaction with sampling visual information. While some of the results may seem somewhat trivial in hindsight (as always in this kind of study), I still think this is a very important approach to understanding locomotion in the wild better.

Weaknesses:<br /> The manuscript as it stands has several issues with the reporting of the results and the statistics. In particular, it is hard to assess the inter-individual variability, as some of the data are aggregated across individuals, while in other cases only central tendencies (means or medians) are reported without providing measures of variability; this is critical, in particular as N=9 is a rather small sample size. It would also be helpful to see the actual data for some of the information merely described in the text (e.g., the dependence of \Delta H on path length). When reporting statistical analyses, test statistics and degrees of freedom should be given (or other variants that unambiguously describe the analysis). The CNN analysis chosen to link the step data to visual sampling (gaze and depth features) should be motivated more clearly, and it should describe how training and test sets were generated and separated for this analysis. There are also some parts of figures, where it is unclear what is shown or where units are missing. The details are listed in the private review section, as I believe that all of these issues can be fixed in principle without additional experiments.

Reviewer #2 (Public Review):

Summary:<br /> This manuscript examines how humans walk over uneven terrain using vision to decide where to step. There is a huge lack of evidence about this because the vast majority of locomotion studies have focused on steady, well-controlled conditions, and not on decisions made in the real world. The author team has already made great advances in this topic, but there has been no practical way to map 3D terrain features in naturalistic environments. They have now developed a way to integrate such measurements along with gaze and step tracking, which allows quantitative evaluation of the proposed trade-offs between stepping vertically onto vs. stepping around obstacles, along with how far people look to decide where to step.

Strengths:<br /> 1. I am impressed by the overarching outlook of the researchers. They seek to understand human decision-making in real-world locomotion tasks, a topic of obvious relevance to the human condition but not often examined in research. The field has been biased toward well-controlled studies, which have scientific advantages but also serious limitations. A well-controlled study may eliminate human decisions and favor steady or periodic motions in laboratory conditions that facilitate reliable and repeatable data collection. The present study discards all of these usually-favorable factors for rather uncontrolled conditions, yet still finds a way to explore real-world behaviors in a quantitative manner. It is an ambitious and forward-thinking approach, used to tackle an ecologically relevant question.

2. There are serious technical challenges to a study of this kind. It is true that there are existing solutions for motion tracking, eye tracking, and most recently, 3D terrain mapping. However most of the solutions do not have turn-key simplicity and require significant technical expertise. To integrate multiple such solutions together is even more challenging. The authors are to be commended on the technical integration here.

3. In the absence of prior studies on this issue, it was necessary to invent new analysis methods to go with the new experimental measures. This is non-trivial and places an added burden on the authors to communicate the new methods. It's harder to be at the forefront in the choice of topic, technical experimental techniques, and analysis methods all at once.

Weaknesses:<br /> 1. I am predisposed to agree with all of the major conclusions, which seem reasonable and likely to be correct. Ignoring that bias, I was confused by much of the analysis. There is an argument that the chosen paths were not random, based on a comparison of probability distributions that I could not understand. There are plots described as "turn probability vs. X" where the axes are unlabeled and the data range above 1. I hope the authors can provide a clearer description to support the findings. This manuscript stands to be cited well as THE evidence for looking ahead to plan steps, but that is only meaningful if others can understand (and ultimately replicate) the evidence.

2. I wish a bit more and simpler data could be provided. It is great that step parameter distributions are shown, but I am left wondering how this compares to level walking. The distributions also seem to use absolute values for slope and direction, for understandable reasons, but that also probably skews the actual distribution. Presumably, there should be (and is) a peak at zero slope and zero direction, but absolute values mean that non-zero steps may appear approximately doubled in frequency, compared to separate positive and negative. I would hope to see actual distributions, which moreover are likely not independent and probably have a covariance structure. The covariance might help with the argument that steps are not random, and might even be an easy way to suggest the trade-off between turning and stepping vertically. This is not to disregard the present use of absolute values but to suggest some basic summary of the data before taking that step.

3. Along these same lines, the manuscript could do more to enable others to digest and go further with the approach, and to facilitate interpretability of results. I like the use of a neural network to demonstrate the predictiveness of stepping, but aside from above-chance probability, what else can inform us about what visual data drives that? Similarly, the step distributions and height-turn trade-off curves are somewhat opaque and do not make it easy to envision further efforts by others, for example, people who want to model locomotion. For that, clearer (and perhaps) simpler measures would be helpful.

I am absolutely in support of this manuscript and expect it to have a high impact. I do feel that it could benefit from clarification of the analysis and how it supports the conclusions.

Reviewer #3 (Public Review):

Summary:<br /> The systematic way in which path selection is parametrically investigated is the main contribution.

Strengths:<br /> The authors have developed an impressive workflow to study gait and gaze in natural terrain.

Weaknesses:<br /> 1. The training and validation data of the CNN are not explained fully making it unclear if the data tells us anything about the visual features used to guide steering.

It is not clear how or on what data the network was trained (training vs. validation vs. un-peeked test data), and justification of the choices made. There is no discussion of possible overfitting. The network could be learning just e.g. specific rock arrangements. If the network is overfitting the "features" it uses could be very artefactual, pixel-level patterns and not the kinds of "features" the human reader immediately has in mind.

2. The use of descriptive terminology should be made systematic.

Specifically, the following terms are used without giving a single, clear definition for them: path, step, step location, foot plant, foothold, future foothold, foot location, future foot location, foot position.

I think some terms are being used interchangeably. I would really highly recommend a diagrammatic cartoon sketch, showing the definitions of all these terms in a single figure, and then sticking to them in the main text.

3. More coverage of different interpretations / less interpretation in the abstract/introduction would be prudent

The authors discuss the path selection very much on the basis of energetic costs and gait stability. At least mention should be given to other plausible parameters the participants might be optimizing (or that indeed they may be just satisficing).

That is, it is taken as "given" that energetic cost is the major driver of path selection in your task, and that the relevant perception relies on internal models. Neither of these is a priori obvious nor is it as far as I can tell shown by the data (optimizing other variables, satisficing behavior, or online "direct perception" cannot be ruled out).

eLife assessment

This study provides useful findings on how phonetic properties of words, i.e., their difficulty and prior knowledge, influence the outcome of targeted memory reactivation (TMR) during sleep. Unfortunately, the small sample size together with a between-subject design, renders the evidence incomplete, thus warranting future work to shed further light on the impact of TMR in language learning.

Reviewer #1 (Public Review):

Summary:<br /> The authors aim to consider the effects of phonotactics on the effectiveness of memory reactivation during sleep. They have created artificial words that are either typical or atypical and showed that reactivation improves memory for the latter but not the former.

Strengths:<br /> This is an interesting design and a creative way of manipulating memory strength and typicality. In addition, the spectral analysis on both the wakefulness data and the sleep data is well done. The article is clearly written and provides a relevant and comprehensive of the literature and of how the results contribute to it.

Weaknesses:<br /> 1. Unlike most research involving artificial language or language in general, the task engaged in this manuscript did not require (or test) learning of meaning or translation. Instead, the artificial words were arbitrarily categorised and memory was tested for that categorisation. This somewhat limits the interpretation of the results as they pertain to language science, and qualifies comparisons with other language-related sleep studies that the manuscript builds on.

2. The details of the behavioural task are hard to understand as described in the manuscript. Specifically, I wasn't able to understand when words were to be responded to with the left or right button. What were the instructions? Were half of the words randomly paired with left and half with right and then half of each rewarded and half unrewarded? Or was the task to know if a word was rewarded or not and right/left responses reflected the participants' guesses as to the reward (yes/no)? Please explain this fully in the methods, but also briefly in the caption to Figure 1 (e.g., panel C) and in the Results section.

3. Relatedly, it is unclear how reward or lack thereof would translate cleanly into a categorisation of hits/misses/correct rejections/false alarms, as explained in the text and shown in Figure 1D. If the item was of the non-rewarded class and the participant got it correct, they avoided loss. Why would that be considered a correct rejection, as the text suggests? It is no less of a hit than the rewarded-correct, it's just the trial was set up in a way that limits gains. This seems to mix together signal detection nomenclature (in which reward is uniform and there are two options, one of which is correct and one isn't) and loss-aversion types of studies (in which reward is different for two types of stimuli, but for each type you can have H/M/CR/FA separably). Again, it might all stem from me not understanding the task, but at the very least this required extended explanations. Once the authors address this, they should also update Fig 1D. This complexity makes the results relatively hard to interpret and the merit of the manuscript hard to access. Unless there are strong hypotheses about reward's impact on memory (which, as far as I can see, are not at the core of the paper), there should be no difference in the manner in which the currently labelled "hits" and "CR" are deemed - both are correct memories. Treating them differently may have implications on the d', which is the main memory measure in the paper, and possibly on measures of decision bias that are used as well.

4. The study starts off with a sample size of N=39 but excludes 17 participants for some crucial analyses. This is a high number, and it's not entirely clear from the text whether exclusion criteria were pre-registered or decided upon before looking at the data. Having said that, some criteria seem very reasonable (e.g., excluding participants who were not fully exposed to words during sleep). It would still be helpful to see that the trend remains when including all participants who had sufficient exposure during sleep. Also, please carefully mention for each analysis what the N was.

5. Relatedly, the final N is low for a between-subjects study (N=11 per group). This is adequately mentioned as a limitation, but since it does qualify the results, it seemed important to mention it in the public review.

6. The linguistic statistics used for establishing the artificial words are all based on American English, and are therefore in misalignment with the spoken language of the participants (which was German). The authors should address this limitation and discuss possible differences between the languages. Also, if the authors checked whether participants were fluent in English they should report these results and possibly consider them in their analyses. In all fairness, the behavioural effects presented in Figure 2A are convincing, providing a valuable manipulation test.

7. With regard to the higher probability of nested spindles for the high- vs low-PP cueing conditions, the authors should try and explore whether what the results show is a general increase for spindles altogether (as has been reported in the past to be correlated with TMR benefit and sleep more generally) or a specific increase in nested spindles (with no significant change in the absolute numbers of post-cue spindles). In both cases, the results would be interesting, but differentiating the two is necessary in order to make the claim that nesting is what increased rather than spindle density altogether, regardless of the SW phase.

Reviewer #2 (Public Review):

Summary:<br /> The work by Klaassen & Rasch investigates the influence of word learning difficulty on sleep-associated consolidation and reactivation. They elicited reactivation during sleep by applying targeted memory reactivation (TMR) and manipulated word learning difficulty by creating words more similar (easy) or more dissimilar (difficult) to our language. In one group of participants, they applied TMR of easy words and in another group of participants, they applied TMR of difficult words (between-subjects design). They showed that TMR leads to higher memory benefits in the easy compared to the difficult word group. On a neural level, they showed an increase in spindle power (in the up-state of an evoked response) when easy words were presented during sleep.

Strengths:<br /> The authors investigate a research question relevant to the field, that is, which experiences are actually consolidated during sleep. To address this question, they developed an innovative task and manipulated difficulty in an elegant way.

Overall, the paper is clearly structured, and results and methods are described in an understandable way. The analysis approach is solid.

Weaknesses:<br /> 1.Sample size<br /> For a between-subjects design, the sample size is too small (N = 22). The main finding (also found in the title "Difficulty in artificial word learning impacts targeted memory reactivation") is based on an independent samples t-test with 11 participants/group.

The authors explicitly mention the small sample size and the between-subjects design as a limitation in their discussion. Nevertheless, making meaningful inferences based on studies with such a small sample size is difficult, if not impossible.

2.Choice of task<br /> Even though the task itself is innovative, there would have been tasks better suited to address the research question. The main disadvantage the task and the operationalisation of memory performance (d') have is that single-trial performance cannot be calculated. Consequently, choosing individual items for TMR is not possible.

Additionally, TMR of low vs. high difficulty is conducted between subjects (and independently of pre-sleep memory performance) which is a consequence of the task design.

The motivation for why this task has been used is missing in the paper.

Reviewer #3 (Public Review):

Summary:<br /> In this study, the authors investigated the effects of targeted memory reactivation (TMR) during sleep on memory retention for artificial words with varying levels of phonotactical similarity to real words. The authors report that the high phonotactic probability (PP) words showed a more pronounced EEG alpha decrease during encoding and were more easily learned than the low PP words. Following TMR during sleep, participants who had been cued with the high PP TMR, remembered those words better than 0, whilst no such difference was found in the other conditions. Accordingly, the authors report higher EEG spindle band power during slow-wave up-states for the high PP as compared to low PP TMR trials. Overall, the authors conclude that artificial words that are easier to learn, benefit more from TMR than those which are difficult to learn.

Strengths:<br /> 1. The authors have carefully designed the artificial stimuli to investigate the effectiveness of TMR on words that are easy to learn and difficult to learn due to their levels of similarity with prior word-sound knowledge. Their approach of varying the level of phonotactic probability enables them to have better control over phonotactical familiarity than in a natural language and are thus able to disentangle which properties of word learning contribute to TMR success.

2. The use of EEG during wakeful encoding and sleep TMR sheds new light on the neural correlates of high PP vs. low PP both during wakeful encoding and cue-induced retrieval during sleep.

Weaknesses:<br /> 1. The present analyses are based on a small sample and comparisons between participants. Considering that the TMR benefits are based on changes in memory categorization between participants, it could be argued that the individuals in the high PP group were more susceptible to TMR than those in the low PP group for reasons other than the phonotactic probabilities of the stimuli (e.g., these individuals might be more attentive to sounds in the environment during sleep). While the authors acknowledge the small sample size and between-subjects comparison as a limitation, a discussion of an alternative interpretation of the data is missing.

2. While the one-tailed comparison between the high PP condition and 0 is significant, the ANOVA comparing the four conditions (between subjects: cued/non-cued, within-subjects: high/low PP) does not show a significant effect. With a non-significant interaction, I would consider it statistically inappropriate to conduct post-hoc tests comparing the conditions against each other. Furthermore, it is unclear whether the p-values reported for the t-tests have been corrected for multiple comparisons. Thus, these findings should be interpreted with caution.

3. With the assumption that the artificial words in the study have different levels of phonotactic similarity to prior word-sound knowledge, it was surprising to find that the phonotactic probabilities were calculated based on an American English lexicon whilst the participants were German speakers. While it may be the case that the between-language lexicons overlap, it would be reassuring to see some evidence of this, as the level of phonotactic probability is a key manipulation in the study.

4. Another manipulation in the study is that participants learn whether the words are linked to a monetary reward or not, however, the rationale for this manipulation is unclear. For instance, it is unclear whether the authors expect the reward to interact with the TMR effects.

eLife assessment

This paper reports useful findings regarding gut bacteria that metabolize dietary flavonoids, which can enhance, reduce, or otherwise alter the flavonoid bioactivities. With a newly developed bioinformatics tool, the authors predict bacterial species that can metabolize parts of the flavonoid tilianin. Formal proof of concept is missing, but if experimentally confirmed, the study will change the way we think about metabolism of flavonoids and would be of broad interest regarding gut bacterial metabolism. Most of the analyses are compelling, but others require further inquiry.

Reviewer #1 (Public Review):

Summary:

Flavonoids are abundant in plant-based foods. They have been widely recognized for their health-promoting properties. There is increasing evidence that the effects of dietary flavonoids depend on their metabolism by gut bacteria, which can enhance, reduce or otherwise alter the flavonoids' bioactivities. On the other hand, little is known regarding the enzymes and species that can utilize flavonoids as metabolic substrates.

In the current manuscript, the authors analyzed the possibility to predict the degradation of flavonoids that we take up with our food by gut bacteria. In contrast to plants, bacteria do not contain obvious degradation enzymes.

Strengths:

To predict such enzymes with a broad substrate specificity (enzyme promiscuity) the authors optimized/modified a bioinformatic tool to predict whether a gut bacterial enzyme could catalyze a flavonoid reaction based on the chemical reaction similarity of the enzyme's native reaction and known flavonoid reactions in plants.<br /> They predicted such enzyme activities in genomes of bacteria that had been shown to occur in the human gut. Then, they cultivated selected bacteria with the predicted enzymatic activities and in fact showed, that they can degrade parts of these flavonoids. Together with the bioinformatic and mass spectrometry they identified a metabolization pathway of the flavonoid tilianin that spanned multiple species, i.e., Bifidobacterium longum subsp. animalis, Blautia coccoides, and Flavonifractor plautii. Lastly, the authors showed that tilianin metabolites exhibit protective effects against H2O2 through reactive oxygen species scavenging activity and thus, improve viability of a neuronal cell line, while the parent compound, tilianin, was ineffective. This protective effect might be due to gut microbiota-dependent physiological effects of dietary flavonoids.

Weaknesses:

1) To confirm the bioinformatic-based predictions the authors used in vitro culture experiments and LC-MS experiments. Although these in vitro experiments clearly add value to the bioinformatic prediction, they fall short of providing firm evidence for the predictions because they do not show whether the predicted enzymes really catalyze the predicted reactions. In theory, there could be other enzymes not identified bioinformatically that catalyze the reactions.

2) It is not clear how the authors selected the bacterial species. Did they analyze meta genome sequences or hundreds of genomes of gut bacteria? Did they analyze bacteria isolated from the gut or rather type strains? What about other bacterial species in the gut? Do they also encode relevant enzymes? If yes, how many do? This needs to be clarified.

3) The reported data on E. coli is difficult to understand. Has E. coli a different degradation pathway leading to the observed disappearance of tilianins?

Reviewer #2 (Public Review):

The manuscript deals with an interesting topic in metabolism: the so-called underground metabolism enabled by enzymes with broad substrate specificity. This is mainly relevant in secondary metabolisms. The authors deal, in particular, with the conversion of flavonoids, which have health-promoting effects. They present an algorithm for predicting the moonlight activities of enzymes, which must be given as inputs. Moreover, the authors performed experiments on the antioxidant activities of the flavonoids under study.

My focus was on the bioinformatics part. Overall, the bioinformatics part is not a major scientific achievement in my eyes, or it is too poorly described to see its merits. There may be difficulties understanding the presented algorithm.

Comments:

The prediction algorithm should be explained much better. Although the manuscript is quite long, it does not describe the approaches sufficiently well. It is quite hard to read.

As far as I can see, the method was only tested with a small sample of different flavonoid substances.

Major comments<br /> (1) I see the following contradiction. Line 18/19: "As flavonoids are not natural substrates of gut bacterial enzymes" and lines 76/77: "commensal gut microorganisms do not have specialized enzymes that utilize flavonoids as their native substrates" versus lines 72-74: "flavonoids ..., which makes them available to be metabolized". How can they be metabolized given what is said in the first two phrases?<br /> (2) It should be explained better what is meant by "reaction class" (e.g. in lines 97 and 99). Is this the same as the EC number (in the Enzyme Catalogue)? The term "reaction class" is indeed used in the KEGG database. On the webpage<br /> https://www.genome.jp/brite/br08204<br /> it seems indeed as if the terms "reaction class" and EC number are somehow equivalent. However, the term "RClass RC00392" in line 557 of the manuscript points to a difference in meaning.<br /> (3) The prediction algorithm should be explained much better. For example, in the Figure showing the workflow, it is shown that an EC number should be given as input. However, if we search for enzymes which could potentially degrade a given flavonoid, we may not know any suitable EC number. Line 122: "To match a given enzyme with its non-native polyphenolic substrates..." However, where can we take the enzyme name/EC number from? Moreover, given that it is assumed that the reaction is performed by underground metabolism, should the enzyme given as input come from another organism, for example, a plant?<br /> (4) Lines 521-523: Our prediction tool can take either a single enzyme in the form of Enzyme Commission (EC) number (e.g. "ec:2.1.1.75"), or a KEGG organism-identifier (e.g. "cpv") or a consortium, a list of different organism-identifiers, as input." I do not understand the wording "or a consortium". According to the Figure showing the workflow, it should read "and a consortium".<br /> (5) In the Materials and Methods section, the KEGG PATHWAY database is mentioned. This comes somewhat out of the blue. What is the connection to the "reaction class" concept in KEGG? Or is the PATHWAY database only used for extracting the negative controls?<br /> (6) Line 142,143. "Our analysis shows that RClass-based similarity can predict the correct reactions for known flavonoid-metabolizing enzymes". How do the authors know that the results are correct? If it is easy to check, then I assume the test whether a given enzyme is able to catalyze reactions with flavonoids can be done manually in KEGG, so that a computer algorithm is unnecessary.<br /> (7) Elaborating on the previous point - I have the impression that the algorithm is a rather simple search routine for finding reactions in the KEGG database that match certain criteria. This might be a helpful tool to save time in comparison to doing the search manually. However, at least the bioinformatics part of the paper is not a major scientific achievement as far as I can see.<br /> (8) It is not sufficiently clear whether the prediction algorithm only works for the example shown in the top figure (tilianin, acacetin etc), which would be quite a restricted application, or for many or even all flavonoids. In line 565, the authors say: "our tabulated 312 unique flavonoids", while in the upper part of the MS, e.g. in lines 26 and 109, only the pathway starting from tilianin is mentioned.<br /> (9) In which programming language was the algorithm implemented?<br /> (10) The connection between the theoretical and experimental parts of the paper is not fully clear. Some of the experiments serve to test the predictions, which is fine. The experiments on free radicals, however, seem to be somewhat unrelated.

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.

eLife assessment

This important study reveals ELF3 as a putative candidate driver of luminal progenitor (LP) transformation. Up-regulation of ELF3 during replicative stress conditions and in BRCA1 deficient cells may permit cell proliferation by suppressing genome instability. While the hypothesis is compelling, the experimental support is still incomplete, as it does not adequately demonstrate the role of ELF3 in LP cells per se. The mechanistic underpinnings by which ELF3 promotes cell tolerance to DNA damage were not fully explored either. With improvements, the work has the potential to enhance our understanding of how BRCA1 deficiency fuels LP transformation and thereby breast tumorigenesis.

Reviewer #1 (Public Review):

The authors set out to define the molecular basis for LP as the origin of BRCA1-deficient breast cancers. They showed that LPs have the highest level of replicative stress, and hypothesise that this may account for their tendency to transform. They went on to identify ELF3 as a candidate driver of LP transformation and showed that ELF3 expression is up-regulated in response to replicative stress as well as BRCA1 deficiency. They went on to show that ELF3 inactivation led to a higher level of DNA damage, which may result from compromised replicative stress responses.

While the manuscript supports the interesting idea wherein ELF3 may fuel LP cell transformation, it remains obscure how ELF3 promotes cell tolerance to DNA damage. Interestingly the authors proposed that ELF3 suppresses excessive genomic instability, but in my opinion, I do not see any evidence that supports this claim. In fact, one might think that genomic instability is key to cell transformation.

Reviewer #2 (Public Review):

Summary:<br /> The manuscript focuses on a persistent question of why germline mutations in BRCA1 which impair homology-directed repair of DNA double-strand breaks predispose to primarily breast and ovarian cancers but not other tissues. The authors propose that replication stress is elevated in the luminal progenitor (LP) cells and apply the gene signature from Dreyer et al as a measure of replication stress in populations of cells selected by FACS previously (published by Lim et al.) and suggest an enrichment of replication stress among the LP cells. This is followed by single-cell RNA seq data from a small number of breast tissues from a small number of BRCA1 mutation carriers but the pathogenic variants are not listed. The authors perform an elegant analysis of the effects of BRCA1 knockdown in MCF10A cells, but these cells are not considered a model of LP cells.

Overall, the manuscript suffers from significant gaps and leaps in logic among the datasets used. The connection to luminal progenitor cells is not adequately established because the models used are not representative of this population of cells. Therefore, the central hypothesis is not sufficiently justified.

Strengths:<br /> The inducible knockdown of BRCA1 provided compelling data pointing to an upregulation of ELF3 in this setting as well as a small number of other genes. It would be useful to discuss the other genes for completeness and explain the logic for focusing on ELF3. Nonetheless, the connection with ELF 3 is reasonable. The authors provide significant data showing a role for ELF3 in breast epithelial cells and its role in cell survival.

Weaknesses:<br /> The initial observations in primary breast cells have small sample sizes. The mutations in BRCA1 seem to be presumed to be all the same, but we know that pathogenic variants differ among individuals and range from missense mutations affecting interactions with one critical partner to large-scale truncations of the protein.

The figure legends are missing critical details that make it difficult for the reader to evaluate the data. The data support the notion that ELF3 may participate in relieving replication stress, but does not appear to be limited to LP cells as proposed in the hypothesis.

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.

Reviewer #1 (Public Review):

Summary:<br /> Ciliary rootlet is a structure associated with the ciliary basal body (centriole) with beautiful striation observed by electron microscopy. It has been known for more than a century, but its function and protein arrangement are still unknown. This work reconstructed the near-atomic resolution 3D structure of the rootlet using cryo-electron tomography, discovered a number of interesting filamentous structures inside, and built a molecular model of the rootlet.

Strengths:<br /> The authors exploited the currently possible ability of cryo-ET and used it appropriately to describe the 3D structure of the rootlet. They carefully conducted subtomogram averaging and classification, which enabled an unprecedented detailed view of this structure. The dual use of (nearly) intact rootlets from cilia and extracted (demembraned) rootlets enabled them to describe with confidence how D1/D2/A bands form periodic structures and cross with longitudinal filaments, which are likely coiled-coil.

Weaknesses:<br /> Some more clarifications are needed. This reviewer believes that the authors can address them.

eLife assessment

This fundamental study offers a compelling molecular model for the organization of rootlets, a critical organelle that links cilia to the basal body, ensuring proper anchoring. While previous research has explored rootlet structure and organization, this study delivers an unprecedented level of resolution, important to the centrosome and cilia field. The model proposed by the authors will serve as a reference for future studies.

Reviewer #2 (Public Review):

Summary:<br /> This work performs structural analysis on isolated or purified rootlets.

Strengths:<br /> To date, most studies of this cellular assembly have been from fluorescence microscopy, conventional TEM methods, or through biochemical analysis of constituents. It is clearly a challenging target for structural analysis due to its complexity and heterogeneity. The authors combine observations from cryo-electron tomograms, automated segmentations, subtomogram averaging, and previous data from the literature to present an overall model of how the rootlet is organised.

Their model will serve as a jumping-off point for future studies, and as such it is something of considerable value and interest.

Weaknesses:<br /> It is speculative but is presented as such, and is well-reasoned, plausible, and thorough.

Reviewer #3 (Public Review):

Summary:<br /> The study offers a compelling molecular model for the organization of rootlets, a critical organelle that links cilia to the basal body. Striations have been observed in rootlets, but their assembly, composition, and function remain unknown. While previous research has explored rootlet structure and organization, this study delivers an unprecedented level of resolution, valuable to the centrosome and cilia field. The authors isolated rootlets from mice's eyes. They apply EM to partially purified rootlets (first negative stain, then cryoET). From these micrographs, they observed striations along the membranes along the rootlet but no regular spacing was observed.

The thickness of the sample and membranes prevented good contrast in the tomograms. Thus they further purified the rootlets using detergent, which allowed them to obtain cryoET micrographs of the rootlets with greater details. The tomograms were segmented and further processed to improve the features of the rootlet structures. From their analysis, they described 3 regular cross-striations and amorphous densities, which are connected perpendicularly to filaments along the length of the rootlets. They propose that various proteins provide the striations and rootletin forms parallel coiled coils that run along the rootlet. Overall their data provide a detailed model for the molecular organization of the rootlet.

The major strength is that this high-quality study uses state-of-the-art cryo-electron tomography, sub-tomogram averaging, and image analysis to provide a model of the molecular organization of rootlets. The micrographs are exceptional, with excellent contrast and details, which also implies the sample preparation was well optimized to provide excellent samples for cryo-ET. The manuscript is also clear and accessible.

To further validate their model, it would have been useful to identify some components in the EM maps through complementary approaches (mass spectrometry, mutants disrupting certain features, CLEM). Some potential candidates are mentioned in the discussion.

This research marks a significant step forward in our understanding of rootlets' molecular organization.

eLife assessment

This is a fundamental study into human spinal neurulation, which substantially advances our understanding of human neural tube closure. Crucial unanswered questions in the field currently rely on model systems, not faithful to human development. The evidence provided is convincing, with a large number of specimens and the use of state-of-the-art methodology providing robustness. The work will be of broad interest to developmental biologists, embryologists, and medical professionals working on neural tube defects, and will act as a precious reference resource for future studies.

Reviewer #1 (Public Review):

Summary:<br /> The authors analyzed 102 human embryos in order to address outstanding questions about human lower spinal development and secondary neural tube formation. Through whole embryo imaging and histologic analysis, they provide exceptional quantification of the timing of posterior neuropore closure, rate of lower spinal somite formation, and formation and regression of the human "tail." Their analysis also provides convincing qualitative evidence of the cellular and molecular mechanisms at play during lower spinal development by identifying the presence of caspase-dependent programmed cell death and the dynamic expression of FGF8/WNT3A within the elongating embryo. Interestingly, they identify multiple polarized lumens within the site of secondary neural tube formation and add a solid argument for the mode of formation of this structure; however, in its current state, the evidence for a conclusive morphogenetic mechanism remains elusive. Finally, the authors provide a substantial review of the existing publications related to human lower spinal development, creating an excellent reference and demonstrating the importance of continuing to utilize each of these precious samples for furthering our understanding of human development.

Strengths:<br /> This manuscript provides an excellent window into the key morphogenetic events of human caudal neural tube formation. Figures 1 and 2 provide beautiful images and quantification of the developmental events, enabling comparison to models that are currently in use, including model organisms and the developing spinal organoid field. The characterization of somite development and later regression is particularly important.

Next, the authors addressed current questions regarding the molecular pathways present during the elongation of the embryo and later regression of the tail structure. The in situ hybridization experiments in Figures 5 and 6 demonstrate important evidence for a maintained neuromesodermal progenitor pool of stem cells that promote axial elongation. Additionally, the identification of caspase-dependent cell death within the human tail provides an explanation for the mechanism of this regression, especially given the notable lack of presence of any gross necrosis.

Finally, as mentioned above, the non-trivial collection and review of the existing human secondary neural tube and body formation literature is an important tool and organizes and synthesizes ~ 100 years of observations from precious human samples.

Weaknesses:<br /> While there are no glaringly incorrect claims from the authors, several of the conclusions could benefit from a form of quantification to support their observations:

1) The identification of the proximal to distal degeneration of the tailgut within the human tail is difficult to distinguish with the current images present in Figure 3. A picture within a picture of the area containing the tail gut could be provided to prominently demonstrate the cellular architecture. Additionally, quantification of the localization of apoptosis would strongly support this observation, as well as provide a visualization of the tail's regression overall. For example, a graph plotting the number of apoptotic cells versus the rostral to caudal locations of the transverse sections while accounting for the CS stage of each analyzed embryo could be created; this could even be further broken down by region of tail, for example, tailgut, ventral ectodermal ridge, somite, etc.

2) The identification of the mode of formation of the secondary neural tube is probably the most interesting question to be addressed, however, Figure 7's evidence is not completely satisfying in its current form. While I agree that it is unlikely that multiple polarization foci form within the most caudal part of the tail and coalesce more rostrally, I am equally unsure that a single polarization would form rostrally and then split and re-coalesce as it moves caudally, as is currently depicted by 7B.

Multiple groups have recently shown the influence of geometric confinement on neuroectoderm and its ability to polarize and form a singular central lumen (Karzbrun 2021, Knight 2018), or the inverse situation of a lack of confinement resulting in the presence of multiple lumens. The tapering of the diameter of the tail and its shared perimeter and curvature with the polarization bears a striking resemblance to this controlled confinement. An interesting quantification to depict would include the number of lumens versus the transverse section diameter and CS stage to see if there is any correlation between embryo size and the number of multiple polarizations. Anecdotally, the fusion of multiple polarizations/lumens tends to occur often in these human organoid-type platforms, while splitting to multiple lumens as the tissues mature does not. Other supplements to Figure 7 could include 3D renderings of lumens of interest as depicted in Catala 2021, especially if it demonstrates the re-coalescence as seen in 7B.

The non-pathologic presence of multiple polarizations in human tails compared to the rodent pathogenic counterpart is interesting given that rodents obviously maintain this appendage while it is lost in humans.

3) Of potential interest is the process of junctional neurulation describing the mechanistic joining of the primary and secondary neural tube, which has recently been explored in chick embryos and demonstrated to have relevance to human disease (Dady 2014, Eibach 2017, Kim 2021). While it is clear this paper's goal does not center on the relationship between primary and secondary neurulation, such a mechanism may be relevant to the authors' interpretation of their observations of lumen coalescence. I wonder if the embryos studied provide any evidence to support junctional neurulation.

Reviewer #2 (Public Review):

Summary:<br /> This study utilizes a large series of neurulation human embryos to address several questions about the similarities and differences between human neurulation and model systems such as the chicken and rodent.

Strengths:<br /> The number of specimens utilized for the analysis provides robustness to the findings.

Weaknesses:<br /> It is not clear how the gestational age of the specimens was determined or how that can be known with certainty. There is no information given in the methods on this. With this in mind, bunching the samples at 2-day intervals in Figure 1J will lead to inaccuracies in assessing the rate of somite formation. This is pointed out as a major difference between specimens and organoids in the abstract but a similar result in the results section. The data supporting either of these statements is not convincing.

Whenever possible, give the numbers of specimens that had the described findings. For example, in Figure 2C - how many embryos were examined with the massive rounded end at CS13? Apoptosis in Figures 3 and 4?

For Figure 2I-K, it would be informative to superimpose the individual data points on the box plots distinguishing males from females, as in Figure 1I.

Is it possible to quantitate apoptosis and proliferation data?

The Tunel staining in Figure 3 is difficult to make out.

Additional improvements to the presentation of figures, writing, and quantization of results are suggested.

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.

eLife assessment

This study uses specific and robust genetic approaches to assess mechanisms of kainic acid-induced neurogenesis. This is a fundamental study that bridges several complementary methods and is a convincing use of existing approaches to explore roles for sonic hedgehog in activity-dependent and aging-associated hippocampal neurogenesis.

Reviewer #1 (Public Review):

Summary: Seizure stimuli has long been recognized to exhibit potent effects on adult neurogenesis, from depletion of the NSC pool to promoting aberrant migration of adult-born neurons. However, the identity and source of extrinsic signals is still incompletely understood. The work by Noguchi et al., demonstrates that Shh from mossy cells is a major source of Shh signaling after KA-mediated acute seizures. This work is interesting because mossy cells undergo hyperactivation during seizures, so this study provides a mechanistic link between mossy cell neuronal activity control of neurogenesis through Shh signaling. Weaknesses are that only male mice were analyzed in the seizure induction experiments and several control groups are missing for seizure induction, tamoxifen induction, and the DREADD experiment.

Strengths:

1. The study uses rigorous and specific genetic approaches (e.g., GliLacZ/+ mice; ShhEGFP-Cre/+ mice; mossy cell selective conditional Shh knockout using Crlr-Cre mice) to demonstrate Shh signaling is activated by seizures in mossy cells and contributes to aberrant neurogenesis.

2. Use of DREADDs (Crlr-Cre; hM3Dq) to show mossy cells control adult neurogenesis through Shh in an activity-dependent manner.

3. Demonstration that Shh deletion in mossy cells leads to reduction of the NSC pool uses stringent methods and analysis, including BrdU pulse-chase and co-labeling with NSC markers.

Weaknesses:

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?

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.

3. Several control groups are missing:<br /> -For seizure induction: missing vehicle (instead of no KA treatment).<br /> -For TAM induction: missing corn oil only to check leakiness and specificity of transgene.<br /> -For DREADD experiment: missing vehicle (to control for hM3 non-specific effects)

Reviewer #2 (Public Review):

Summary:<br /> The mechanisms by which seizures induce neurogenesis has remained unclear. Prior work from the authors demonstrated Mossy cell expressed Shh, that altered Shh expression follows epileptic seizures, and that Shh is a neural mitogen. Here authors show that Shh from mossy cells, which are well positioned between the pyramidal and granule cell layers, are a major source of signaling after seizures, contributing to seizure-induced neurogenesis. Moreover, they find that Mossy cell-sourced Shh is required for self-renewal of NSCs even outside of the context of seizures.

SVZ Gli1 expression was detected in NSCs and Gli1 reporter activity follows kainate-induced seizures. Heterozygous Shh mice show reduced seizure induced Shh signaling and reduced neurogenesis. After localizing Shh production to Mossy cells, authors removed Shh from Mossy cells and found reduced neurogenesis. By activating mossy cells through chemogenetic DREADD, they found that the effect of mossy cells on SVZ neurogenesis is activity-dependent, that Shh signaling activity is upregulated in NSCs by mossy cell neuronal activity, and that the induction of neurogenesis by mossy cell neuronal activity is compromised in the absence of Shh from mossy cells. In a series of experiments incorporating AAV DREADD, they find that mossy cell activity can contribute to neurogenesis in contralateral DG, and that seizure induced Shh may be transported along mossy axons. To examine long-term effects, they study mice several weeks after seizure, and find that suggesting that NSCs are less likely to return to their stem cell state after seizure-induced proliferation in the absence of Shh from mossy cells, and that Shh from mossy cells contributes to persistence of the NSC state during aging.

Strengths:<br /> The results are compelling and impactful, and the study is extremely well done. The various genetic lines in the study ensure robust results. Adequate consideration of statistics, methods of quantification, and avoidance of artifact is given.

Weaknesses:<br /> None identified.

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).

Reviewer #2 (Public Review):

Joshi et al. investigated the use of dantrolene, an RyR stabilizing drug, in improving contractile function and slowing pathological progression of pressure-overload heart failure. In a guinea pig model, they found that dantrolene treatment reduced cytosolic Ca2+ levels, improved contractility, reduced the incidence of arrhythmias, reduced fibrosis, and slowed the progression of heart failure. Importantly, delaying treatment until 3 weeks after aortic banding (when heart failure was already established) also resulted in improvements in function and decreased arrhythmogenesis. While some of the mechanistic details remain to be worked out, the data suggest that improving intracellular Ca2+ handling can break the vicious cycle of sympathetic activation, ROS production, and further deterioration of cardiac function.

The functional ECG and echo data are convincing, and very clearly demonstrate the positive effects of dantrolene in heart failure. This is important because dantrolene is already FDA-approved to treat malignant hyperthermia and muscle spasms, so repurposing this drug as a heart failure therapeutic might have a straightforward path to clinical implementation. This also highlights the non-specific nature of dantrolene to interact with RyR1, and therefore, potential side effects. However, this does not detract from the main proof-of-concept demonstrated here.

The guinea pig model employed here is also a strength, as the guinea pig has intracellular Ca2+ handling and ionic currents that are much more similar to human (vs. a murine model, for example).

One weakness is the exclusion of female animals from the study. The authors report more heterogeneity in the progression of HF in the female guinea pig model, however it will be very important to determine effects of dantrolene in the female heart, as there are considerable known sex differences in intracellular Ca2+ handling and contractility. Therefore, it is possible that dantrolene could have sex-dependent effects.

Reviewer #1 (Public Review):

The current study tests the hypothesis that inhibition of ryanodine receptor 2 (RyR2) in failing arrhythmogenic hearts reduces sarcoplasmic Ca leak, ventricular arrhythmias and improves contractile function. A guinea pig model of nonischemic heart failure (HF) was used and randomized to receive dantrolene (DS) or placebo in early or chronic HF. The authors show that DS treatment prevented ventricular arrhythmias and sudden cardiac death by decreasing dispersion of repolarization. The authors conclude that inhibition of RyR2 hyperactivity with DS mitigates the vicious cycle of sarcoplasmic Ca leak-induced increases in diastolic Ca and reactive oxygen species-mediated RyR2 oxidation. Moreover, the consequent increase in sarcoplasmic Ca2+ load improves contractile function.

In general, the study is well designed and the findings are likely to be of interest to the field.

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.

eLife assessment

The study's results offer a fundamental insight into how ACC1-mediated fatty-acid synthesis affects the survival and pathogenicity of iNKT cells in allergic asthma. The inclusion of mouse models, involving genetic adjustments and reconstitution experiments, along with the disparities found in iNKT cells between allergic asthma patients and control subjects in human studies, adds compelling evidence that substantiates these findings.

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.

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.

eLife assessment

The reviewers believe that this study provides valuable insights into understanding bone fragility in T2D patients through the use of human samples, laying the groundwork for future research. The employed methods were solid, demonstrating the feasibility of studying human samples. However, reviewers identified some minor weaknesses in the form of a limited number of subjects and a relatively small set of genes included in the analysis.

Reviewer #1 (Public Review):

Summary:<br /> Leanza et al. investigated the regulation of Wnt signaling factors in the bone tissue obtained from individuals with or without type 2 diabetes. They showed that typical canonical Wnt ligands and downstream factors (Wnt10b, LEF1) are down-regulated, while Wnt5a and sclerostin mRNA are unregulated in diabetic bone tissue. Further, Wnt5a and sclerostin associated with the content of AGEs and SOST mRNA levels also correlated with glycemic control and disease duration.

Strengths:<br /> - A strength of the study is the investigation of Wnt signaling in bone tissue from humans with type 2 diabetes. Most studies measure only serum levels of Wnt inhibitors, but this study takes it further and looks into bone specifically.<br /> - The measurement of AGEs and its correlation to the Wnt signaling molecules is interesting and important. The correlation of sclerostin and Wnt5a with AGEs and disease duration suggests that inhibited Wnt signaling is paralleled by higher AGE levels and potentially weaker bone.<br /> - The methodology in terms of obtaining the bone samples and the rigorous evaluation of RNA integrity is great and provides a solid basis for further analyses.

Weaknesses:<br /> - A weakness may include the rather limited number of samples. Especially for some sub-analyses (e.g. RNA analyses), only a subset of samples was used.<br /> - How was the sample size determined? It seems like more samples might have been necessary to obtain significant results for methods with a higher standard deviation (e.g. histomorphometry).<br /> - Why is the number of samples different for the mRNA measurements? In most cases, there were 9, but in some 8 and in some 10?

Overall, this study validates findings from the group that reported similar findings in 2020. This validates their methodology and shows that alterations in Wnt signaling are reproducible in human bone tissue.

Reviewer #2 (Public Review):

Summary:<br /> This study reports the levels of expression of selected genes implicated in Wnt signaling in trabecular bone from femur heads obtained after surgery from post-menopausal women with (15 women) or without (21 women) type 2 diabetes. They found higher expression levels of SOST and WNT5A, and lower expression levels of LEF-1 and WNT10B in tissues from subjects with T2D, correlating with glycemia and advanced glycation products. No significant differences in bone density were observed. Overall, this is a cross-sectional, observational study measuring a limited set of genes found to vary with glycemia in postmenopausal women undergoing hip surgery.

Strengths:<br /> The study demonstrates the feasibility of measuring gene expression in post-surgical trabecular bone samples, and finds differences associated with glycemia despite a relatively small number of subjects. It can form the basis for further research on the causes and consequences of changes in elements of the WNT signaling pathway in bone biology and disease.

Weaknesses:<br /> The small number of targeted genes does not provide a comprehensive view of the transcriptional landscape within which the effects are observed. The gene expression changes are not associated with cellular or physiological properties of the tissue, raising questions about the biological significance of the observations.

Reviewer #3 (Public Review):

Summary:<br /> The manuscript by Leanza and colleagues explores the regulation of Wnt signaling and its association with advanced glycation end products (AGEs) accumulation in postmenopausal women with type 2 diabetes (T2D). The paper provides valuable insights into the potential mechanisms underlying bone fragility in individuals with T2D. Overall, the manuscript is well-structured, and the methodology is sound. I would suggest some minor revisions to improve clarity.

Strengths:<br /> The study addresses an important and clinically relevant question concerning the mechanisms underlying bone fragility in postmenopausal women with T2D.

The study's methodology appears sound, and the inclusion of postmenopausal women with and without T2D undergoing hip arthroplasty adds to the clinical relevance of the findings. Additionally, measuring gene expression and AGEs in bone samples provides direct insights into the study's objectives.

The manuscript presents data clearly, and the results are well-organized.

Weaknesses:<br /> Title. The title could be more specific to better reflect the content of the study. Also, the abstract should concisely summarize the study's main findings, providing some figures.

Introduction: the introduction would benefit from the addition of a clearer, more focused statement of the research questions or hypotheses guiding this study.

Methods: more information is needed on the hystomorphometry analysis. Surgical samples from 8 T2D and 9 non-diabetic subjects were used for histomorphometry analysis. How did these subjects compare with the other subjects in the T2D and control groups? Were they representative? How were they selected?

eLife assessment

This study investigated the regulatory role of Mecp2 in quiescence exit during cell cycle progression. The study is significant since it provided fundamental insights into the mechanism controlling the cell cycle process. The evidence is convincing since the authors have presented experimental data from in vitro cell culture and in vivo injury-induced liver regeneration to support their conclusion.

Reviewer #1 (Public Review):

In the study described in the manuscript, the authors identified Mecp2, a methyl-CpG binding protein, as a key regulator involved in the transcriptional shift during the exit of quiescent cells into the cell cycle. Their data show that Mecp2 levels were remarkably reduced during the priming/initiation stage of partial hepatectomy-induced liver regeneration and that altered Mecp2 expression affected the quiescence exit. Additionally, the authors identified Nedd4 E3 ligase that is required for the downregulation of Mecp2 during quiescence exit. This is an interesting study with well-presented data that supports the authors' conclusions regarding the role of Mecp2 in transcription regulation during the G0/G1 transition. However, the significance of the study is limited by a lack of mechanistic insights into the function of Mecp2 in the process. This weakness can be addressed by identifying the signaling pathway(s) that trigger Mecp2 degradation during the quiescence exit.

Reviewer #2 (Public Review):

In the manuscript by Yang et al titled "Mecp2 fine-tunes quiescent exit by targeting nuclear receptors", the authors found that Mecp, a well-known protein because of its crucial role in neurological disorders, has a cell cycle-dependent ability to negatively regulate quiescent exit by transcriptional activation of metabolic genes while repressing proliferation-related genes. Conceptually, this is an interesting study with very well-executed experiments and controls.

Since the mutation of MeCP2 was identified as the cause of Rett syndrome, the previous reports have been focused on the exhaustive biochemical and functional characterization of this protein. In this study, the authors show that MeCP2 expression is cell-cycle related, and acute reduction of Mecp2 is essential for efficient quiescence exit in cells. They also identified a novel E3 ligase Nedd4 contributes to Mecp2 degradation during G0 exit. These findings are the first description of MeCP2 protein expression during the cell cycle. The variation in MeCP2 levels at different stages of the cell cycle phases should be taken into consideration when examining MeCP2-related disordered disease.

Reviewer #1 (Public Review):

Summary:<br /> The authors developed a deep learning method called H3-OPT, which combines the strength of AF2 and PLM to reach better prediction accuracy of antibody CDR-H3 loops than AF2 and IgFold. These improvements will have an impact on antibody structure prediction and design.

Strengths:<br /> The training data are carefully selected and clustered, the network design is simple and effective.

The improvements include smaller average Ca RMSD, backbone RMSD, side chain RMSD, more accurate surface residues and/or SASA, and more accurate H3 loop-antigen contacts.

The performance is validated from multiple angles.

Weaknesses:<br /> There are very limited prediction-then-validation cases, basically just one case.

Reviewer #2 (Public Review):

This work provides a new tool (H3-Opt) for the prediction of antibody and nanobody structures, based on the combination of AlphaFold2 and a pre-trained protein language model, with a focus on predicting the challenging CDR-H3 loops with enhanced accuracy than previously developed approaches. This task is of high value for the development of new therapeutic antibodies. The paper provides an external validation consisting of 131 sequences, with further analysis of the results by segregating the test sets into three subsets of varying difficulty and comparison with other available methods. Furthermore, the approach was validated by comparing three experimentally solved 3D structures of anti-VEGF nanobodies with the H3-Opt predictions

Strengths:<br /> The experimental design to train and validate the new approach has been clearly described, including the dataset compilation and its representative sampling into training, validation and test sets, and structure preparation. The results of the in silico validation are quite convincing and support the authors' conclusions.

The datasets used to train and validate the tool and the code are made available by the authors, which ensures transparency and reproducibility, and allows future benchmarking exercises with incoming new tools.

Compared to AlphaFold2, the authors' optimization seems to produce better results for the most challenging subsets of the test set.

Weaknesses:<br /> The scope of the binding affinity prediction using molecular dynamics is not that clearly justified in the paper.

Some parts of the manuscript should be clarified, particularly the ones that relate to the experimental validation of the predictions made by the reported method. It is not absolutely clear whether the experimental validation is truly a prospective validation. Since the methodological aspects of the experimental determination are not provided here, it seems that this may not be the case. This is a key aspect of the manuscript that should be described more clearly.

Some Figures would benefit from a more clear presentation.

Reviewer #3 (Public Review):

Summary:<br /> The manuscript introduces a new computational framework for choosing 'the best method' according to the case for getting the best possible structural prediction for the CDR-H3 loop. The authors show their strategy improves on average the accuracy of the predictions on datasets of increasing difficulty in comparison to several state-of-the-art methods. They also show the benefits of improving the structural predictions of the CDR-H3 in the evaluation of different properties that may be relevant for drug discovery and therapeutic design.

Strengths:<br /> The authors introduce a novel framework, which can be easily adapted and improved. The authors use a well-defined dataset to test their new method. A modest average accuracy gain is obtained in comparison to other state-of-the art methods for the same task while avoiding testing different prediction approaches.

Weaknesses:<br /> The accuracy gain is mainly ascribed to easy cases, while the accuracy and precision for moderate to challenging cases are comparable to other PLM methods (see Fig. 4b and Extended Data Fig. 2). That raises the question: how likely is it to be in a moderate or challenging scenario? For example, it is not clear whether the comparison to the solved X-ray structures of anti-VEGF nanobodies represents an easy or challenging case for H3-OPT. The mutant nanobodies seem not to provide any further validation as the single mutations are very far away from the CDR-H3 loop and they do not disrupt the structure in any way. Indeed, RMSD values follow the same trend in H3-OPT and IgFold predictions (Fig. 4c). A more challenging test and interesting application could be solving the structure of a designed or mutated CDR-H3 loop.

The proposed method lacks a confidence score or a warning to help guide the users in moderate to challenging cases.

The fact that AF2 outperforms H3-OPT in some particular cases (e.g. Fig. 2c and Extended Data Fig. 3) raises the question: is there still room for improvements? It is not clear how sensible is H3-OPT to the defined parameters. In the same line, bench-marking against other available prediction algorithms, such as OmegaFold, could shed light on the actual accuracy limit.

eLife assessment

This work presents H3-OPT, a deep learning method that effectively combines existing techniques for the prediction of antibody structure. This work is important because the method can aid the design of antibodies, which are key tools in many research and industrial applications. The experiments for validation are solid, although several points remain partially unclear, such as (1) which examples constitute proper validation, (2) what the relevance of the molecular dynamics calculations as performed is, (3) the statistics for some of the comparisons, and (4) the lack of comparison with other existing methods.

eLife assessment

The strength of this important study is that it provides compelling evidence in several biological models, including Xenopus embryos, that Wnt3a increases macropinocytosis and that PMA increases this cellular response. This novel link between Wnt, focal adhesions, lysosomes, and macropinocytosis will be very interesting for cell and tumor biologists. In future work, it will be good to identify the underlying mechanism, i.e., the molecular node whereby this interaction occurs.

eLife assessment

Drosophila is a powerful model organism for understanding the molecular and neural regulation of sleep. However, methodological limitations exist that would appear to limit the relevance of work done in the fly to our understanding of mammalian sleep. In this important work, the authors provide physiological, behavioral, and molecular evidence for the existence of two potential sleep stages in Drosophila. The experiments are generally well conducted and the authors' interpretations of their results are solid overall. Although technically innovative and conceptually provocative, there are aspects of the approaches used and results obtained that leave the central conclusions open to interpretation.

eLife assessment

This behavioral modeling study investigates how humans make decisions on the difficulty of perceptual categorization tasks. The study finds that such judgments are best described by an evidence-accumulation model that includes a dynamic comparison of difficulty-related evidence, which terminates when the difference in evidence between two tasks reaches a predetermined bound – a valuable finding for research in perceptual decision-making. The paper provides compelling behavioral evidence for the proposed model through: 1) quantitative model selection/validation procedures, and 2) qualitative analyses of the relation between the optimal model of the task and the human data (and the proposed model).

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.

eLife assessment

This study provides valuable insights into the role of two under-researched sperm-specific proteins (Cylicin 1 and Cylicin 2). The authors provide convincing evidence that they have an essential role in sperm head structure during spermatogenesis, and that their loss leads to subfertility or infertility, with a dose-dependent phenotype. Importantly, the authors identify infertile males with mutations in both Cylicin1 and Cylicin2. Thus, the findings from the mouse models might be applicable to understanding human male infertility with similar structural defects.

Reviewer #1 (Public Review):

Mice and humans have two Cylicin genes (X-linked Cylicin 1 and the autosomal Cylicin 2) that encode cytoskeletal proteins. Cylicins are localized in the acrosomal region of round spermatids, yet they resemble a calyx component within the perinuclear theca of mature sperm nuclei. The function of Cylicins during this developmental stage of spermiogenesis (tail formation and head elongation/shaping) was not known. In this study, using CRISPR/Cas genome editing, the authors generated Cylc1-and Cylc2-knockout mouse lines to study the loss-of-function of each Cylicin or all together.

The major strengths of the study are the rigorous and comparative phenotypic analyses of all the combinatorial genotypes from the cross between the two mouse lines (Cylc1-/y, Cylc2-/-, Cylc1-/y Cylc2+/- and Cylc1-/y Cylc2-/-) at the levels of male fertility, cellular, and subcellular levels to support the conclusion of the study. While spermatogenesis appeared undisturbed, with germ cells of all types detected in the testis, low sperm counts in epididymis were observed. Mice were subfertile or infertile in a dose-dependent manner where fewer functional alleles had more severe phenotypes; the loss of Cylc2 was less tolerated than the loss of Cylc1. Thus, loss of Cylc1, and to an even greater extent, loss of Cylc2, leads to sperm structure anomalies and decreased sperm motility. Particularly, the sperm head and sperm head-neck region are affected, with calyx not forming in the absence of Cylicins, the acrosomal region being attached more loosely, and the sperm head itself appearing structurally rounder and shorter. Furthermore, manchette, which disassembles during spermiogenesis, persists in mature sperm of mice missing Cylc2. It is interesting that the study identifies a human male that has mutations in both CYLC1 and CYLC2 genes and suffers from infertility, with similar motility and sperm structure defects compared to the mouse models. CYLC1 in the sperm from the infertile patient sperm is absent, providing evidence that in both rodents and primates, Cylicins are essential for male fertility. Evolutionary analysis of two genes adds an interesting point. The authors show that the reason for the loss of Cylc2 being more severe is due to the higher conservation of Cylc2 compared to Cylc1 in rodents and primates.

Overall, the work highlights the relevance and importance of Cylicins in male infertility and advances our understanding of perinuclear theca formation during spermiogenesis.

Reviewer #2 (Public Review):

The work presented in this manuscript focuses on the role of Cylicins in spermiogenesis and the consequences of their absence on infertility. The manuscript is presented in two parts: the first part studies the absence of Cylicins from KO mouse models and shows in mice that both isoforms of Cylicins are necessary for normal spermiogenesis. The evaluation of double heterozygotes is particularly useful for the second part which looks at the presence of mutations in these genes in a cohort of infertile men. A patient with two hemizygous/heterozygous mutations in the CYLC1 and 2 genes, respectively, was identified for the first time and the results obtained with the KO models support the hypothesis of the pathogenicity of the mutations.

In general, the experiments are perfectly performed and the results are clear. Numerous techniques in the state of the art in male reproduction are used to obtain high-quality phenotyping of the mouse models.

The discovery of two concomitant mutations in an infertile patient is very interesting and the work carried out on mice allows supporting that an absence of CYLC1 and a heterozygous mutation of CYLC2 could lead to a phenotype of complete infertility. However, as the mutation on CYLC2 is not identified as pathogenic, the pathogenicity of this mutation remains in question (the authors note this point in the discussion). It would be interesting to see if the mutated amino acid is conserved between different species. In mice, the authors have shown the importance of these proteins on the morphology of the acrosome. What about in humans?

Reviewer #3 (Public Review):

The authors tried to study the role of the cylicin gene in sperm formation and male fertility. They used the Crispr/cas 9 to knockout two mouse cylicin genes, cylicin 1 and cylicin 2. They used comprehensive methods to phenotype the mouse models and discovered that the two genes, particularly cylicin 2 are essential for sperm calyx formation. They further compared the evolution of the two genes. Finally, they identified mutations of the genes in a patient. The major strengths are the high quality of data presented, and the conclusion is supported by their findings from the animal models and patients. The major weakness is that the study is rather descriptive without molecular mechanism studies, limiting its impact on the field.

Joint Public Review:

In this manuscript, Karl et al. explore 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. The manuscript demonstrates that FGF4, FGF8, and FGF9 exhibit distinct binding modes towards FGFRs. It is also proposed that FGF8 exhibits "biased ligand" characteristics that is manifested via binding and activation FGFR1 mediated by unproven and speculative "structural differences in the FGF-FGFR1 dimers, which impact the interactions of the FGFR1 trans membrane helices, leading to differential recruitment and activation of the downstream signaling adapter FRS2".

eLife assessment

This important study provides an example of integrating computational and experimental approaches that lead to new insights into the energy landscape of a model kinase. Compelling use of molecular dynamics simulations and NMR spectroscopy provide a conformational description of active and excited states of the kinase; one of which has not been captured in previously solved crystal structures. Overall, this comprehensive study expands our understanding of the architecture and allosteric features of the conserved bilobal kinase domain structure.

Reviewer #1 (Public Review):

Summary:<br /> The authors use insights into the dynamics of the PKA kinase domain, obtained by NMR experiments, to inform MD simulations that generate an energy landscape of PKA kinase domain conformational dynamics.

Strengths:<br /> The authors integrate strong experimental data through the use of state-of-the-art MD studies and derive detailed insights into allosteric communication in PKA kinase. Comparison of wt kinase with a mutant (F100A) shows clear differences in the allosteric regulation of the two proteins. These differences can be rationalized by NMR and MD results.

Weaknesses:<br /> The very detailed insights gained by the authors into allosteric regulation require very specialized techniques in this study. This poses a challenge to communicate the methods, the results, and the meaning of the results to a broader audience. In some places, the authors overcome this challenge better than in others.

Reviewer #2 (Public Review):

Summary:<br /> In this study, Olivieri & Wang et.al. probe the role of the conserved alphaC-beta4 loop in the allosteric regulation of the PKA catalytic subunit. The authors employ a combination of NMR-restrained molecular dynamics simulations and mutational analysis to uncover the conformational transitions between distinct excited states and identify a pivotal role for the alphaC-beta4 loop in facilitating these conformational transitions. These studies support previous models proposing the alphaC-beta4 loop as a critical element in kinase conformational regulation. Overall, this is a timely and fitting study.

Strengths:<br /> 1. Exciting application of NMR and MD to explore hidden conformation states of kinases.<br /> 2. Novel mechanistic insights into the role of the alphaC-beta4 loop in PKA.

Weaknesses:<br /> 1. While the alphaC-beta4 loop is a conserved feature of protein kinases, the residues within this loop vary across various kinase families and groups, enabling group and family-specific control of activity through cis and trans acting elements. F102 in PKA interacts with co-conserved residues in the C-tail, which has been proposed to function as a cis regulatory element. The authors should elaborate on the conformational changes in the C-tail, particularly in the arginine that packs against F102, in the results and discussion. This would further extend the impact and scope of the manuscript, which is currently confined to PKA.<br /> 2. The MD data and conformational states would be a valuable resource for the community and should be shared via some open-source repositories.<br /> 3. The authors state that ES1 and ES2 states are novel and not observed in previous crystal structures. The authors should quantify this through comparisons with PKA inactive states and with other AGC kinases.<br /> 4. Based on the results, can the authors speculate on the impact of oncogenic mutations in the alphaC-beta4 loop mutations in PKA?

Reviewer #3 (Public Review):

Summary:<br /> Combining several MD simulation techniques (NMR-constrained replica-exchange metadynamics, Markov State Model, and unbiased MD) the authors identified the aC-beta4 loop of PKA kinase as a switch crucially involved in PKA nucleotide/substrate binding cooperatively. They identified a previously unreported excited conformational state of PKA (ES2), this switch controls and characterized ES2 energetics with respect to the ground state. Based on translating the simulations into chemical shits and NMR characterizing of PKA WT and an aC-beta4 mutant, the author made a convincing case in arguing that the simulation-suggested excited state is indeed an excited state observed by NMR, thus giving the excited state conformational details.

Strengths:<br /> This work incorporates extensive simulation works, new NMR data, and in vitro biochemical analysis. It stands out in its comprehensiveness, and I think it made a great case.

Weaknesses:<br /> The manuscript is somewhat difficult to read even for kinase experts, and even harder for the layman. The difficulty partially arises from mixing technical description of the simulations with structural interpretation of the results, which is more intuitive, and partially arises from the assumption that readers are familiar with kinase architecture and its key elements (the aC helix, the APE motif etc).

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).

eLife assessment

This study presents a valuable finding on the relationship between a high protein diet and resistance exercise on fat accumulation and glucose homeostasis. The evidence supporting the claims of the authors is solid, although the inclusion of mechanistic insight would have strengthened the study. The work will be of interest to dieticians, diabetologists, and exercise biologists working to understand the link between dietary protein, insulin resistance, and physical activity.

Reviewer #1 (Public Review):

Summary:<br /> The study conducted on mice establishes a noteworthy connection between dietary protein intake and resistance exercise impact on metabolic health and muscle development. In sedentary mice, a diet rich in protein resulted in excessive fat accumulation and compromised blood sugar regulation in comparison to a diet low in protein. Intriguingly, when mice followed the high protein diet alongside progressive resistance training, they exhibited protection against surplus fat gain, though blood glucose regulation remained impaired. The research also revealed that resistance training notably enhanced muscle hypertrophy induced by exercise, particularly in mice on the high protein diet. Although the maximum strength achieved was similar across diets, this highlights the potential synergy between high protein consumption and resistance exercise in promoting skeletal muscle growth.

Strengths:<br /> The study possesses several significant strengths. Firstly, it combines controlled dietary manipulations with resistance exercise, providing a comprehensive understanding of their combined effects on metabolic health and muscle growth. The use of mouse models, while not directly translatable to humans, offers a controlled experimental environment, enabling precise measurements and observations. Moreover, the study reveals nuanced outcomes such as the differential impact of high protein intake on adiposity and muscle hypertrophy. The emphasis on both positive and negative findings lends balance to the conclusions, enhancing the overall credibility of the study. Additionally, the clear delineation of diet-exercise interactions contributes to the broader understanding of dietary and exercise recommendations for metabolic health and muscle development.

Weaknesses:<br /> Certain limitations warrant consideration. Firstly, the study's exclusive reliance on mice might limit the generalizability of the findings to humans due to inherent physiological differences. Additionally, the absence of direct investigation into the underlying molecular mechanisms responsible for the observed outcomes leaves room for speculation. Moreover, the research's concentration on male and young mice raises questions about the applicability of these findings to female and older subjects. Lastly, the study's duration and the specific resistance exercise protocol utilized might not fully reflect long-term human scenarios, underscoring the need for further research in more diverse populations and over extended timeframes.

Reviewer #2 (Public Review):

Summary: In this manuscript, Trautman et al. set out to test the hypothesis that increased intake of dietary protein is deleterious to health when uncoupled from resistance training.

Strengths: The experimental design is well crafted and the experiments provide useful information supporting the hypothesis. The authors take into account the limitations of their study in the discussion, and guide the reader through their results and the interpretation in a fair and measured way, without overstating claims.

Weaknesses: As acknowledged by the authors in the discussion section, this study only features a small sample of male mice from a single strain. Thus the results may not hold when female mice and diverse genetic backgrounds are analyzed. The lack of repeated measures of physiological parameters is also a limitation of the study. Measurements of body weight, body composition, food (calorie) consumption, and locomotor/strength assays could have been provided throughout the study and compared to a baseline value for each animal.

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)

Reviewer #2 (Public Review):

The authors sought to define the molecular structure of autoinhibited Kinesin-1, which is the major kinesin providing plus-end directed transport on microtubules. The paper reports a structural model of full-length kinesin-1 which builds on the known folded conformation of kinesin-1 and describes its autoinhibitory mechanism using cryo-EM, alphafold structural predictions, cross-linking, and mass spectrometry. The authors study the conformation of dimeric Kinesin Heavy Chain (KHC) and tetrameric KHC bound to the Kinesin Light Chains (KLCs), where KLC stabilizes the autoinhibited conformation. The combination of these various approaches leads to an integrated molecular model of autoinhibited Kinesin-1. Until now, there was some debate over the role of the small coiled-coil 3 (a and b) and where the hinge region of Kinesin-1. The authors resolve this question and present data indicating the hinge is between cc3a and cc3b.

In some places the absence of crosslinks is reported as a lack of interaction, however, it could also be that there are no residues that can be crosslinked in this region. Some crosslinks also are too long to satisfy the model, so it is possible, while most crosslinks occur when Kinesin-1 is inhibited, that a small number of crosslinks arise from when Kinesin-1 adopts another conformation. The structural data are supported by single-molecule motility assays with various mutants of Kinesin-1, which greatly help characterising the domains functionally.

Overall there are some interesting novel data on the autoinhibitory mechanism of Kinesin-1, with well performed and analyzed data with KLC and TRAP. The topic and paper will be of interest to many.

eLife assessment

This paper will be of significant interest to the research community working on cytoplasmic transport and microtubule motors, offering important insights into the structural arrangement of autoinhibited Kinesin-1. The paper reports a structural model of full-length kinesin-1 describing its autoinhibitory mechanism using cryo-EM, Alphafold structural predictions, cross-linking, and mass spectrometry. The data are of high quality and together offer a compelling model for how Kinesin-1 is autoinhibited, indicating that auto-inhibition does not rely on the IAK motif alone but on a more extensive intramolecular interface.

Reviewer #1 (Public Review):

Using a combination of structural biology methods, this report aims to describe the auto-inhibited architecture of kinesin 1 either as homodimers or hetero-tetramers. Hence, the multiple contacts between the protein domains and their folding pattern are addressed using cross-linking mass spectrometry (XL-MS), negative stain electron microscopy and Alpha Fold-based structure prediction. Based on the existing literature, the key domains and amino acids responsible for kinesin-1 inhibited state were not clearly deciphered. The synergetic use of different methods now seems to describe in detail the molecular cues that could induce kinesin-1 refolding and opening. Multiple interactions between the different domains seem to induce the folded conformation.

The combination of methodologies is an efficient way to unravel details that could not be addressed previously. The paper is well written. The methods for generating the electron microscopy data and its relevance and quality, for instance, are much better described after revision. In addition, the conclusions are now more convincing because similar investigations are carried out for all isoforms (KIF5B and FIF5C) in parallel.

This article raises the potential strength and power of deep learning structure prediction methods combined simultaneously with other structural biology methods to answer specific questions. In the present context, this study will certainly be helpful in revealing and understanding the activation mechanism of kinesin motor proteins.

Reviewer #2 (Public Review):

Summary:<br /> In eukaryotes, sterols are crucial for signaling and regulating membrane fluidity, however, the mechanism governing cholesterol production and transport across the cell membrane in bacteria remains enigmatic. The manuscript by Zhai et al. sheds light on this topic by uncovering three potential cholesterol transport proteins. Through comprehensive bioinformatics analysis, the authors identified three genes bstA, bstB, and bstC encoding proteins which share homology with transporters, periplasmic binding proteins, and periplasmic components superfamily, respectively. Furthermore, the authors confirmed the specific interaction between these three proteins and C-4 methylated sterols and determined the structures of BstB and BstC. Combining these structural insights with molecular dynamics simulation, they postulated several plausible substrate binding sites within each protein.

Strengths:<br /> The authors have identified 3 proteins that seem likely to be involved in sterol transport between the inner and outer membrane. The structures are of high quality, and the sterol binding experiments support a role for these proteins in sterol transport.

Weaknesses:<br /> While the author's model is very plausible, direct evidence for a role of BstABC in transport, or that the 3 proteins function together in a single pathway, is limited.

eLife assessment

This is a valuable contribution to our understanding of how some bacteria can transport sterols from the cytoplasm to the outer membrane. Though much remains to be tested and explored, the data and analyses presented here provide solid evidence for the genetic and physical interaction of BstA/B/C with bacterially-produced sterols. The manuscript will be of interest to scientists focusing on the characterization of novel bacterial proteins and those studying lipid transport and acquisition in bacterial pathogens.

Reviewer #1 (Public Review):

Summary<br /> This article by Zhai et al, investigates sterol transport in bacteria. Synthesis of sterols is rare in bacteria but occurs in some, such as M capsulatus where the sterols are found primarily in the outer membrane. In a previous paper the authors discovered an operon consisting of five genes, with two of these genes encoding demethylases involved in sterol demethylation. In this manuscript, the authors set out to investigate the functions of the other three genes in the operon. Interestingly, through a bioinformatic analysis, they show that they are an inner membrane transporter of the RND family, a periplasmic binding protein, and an outer membrane-associated protein, all potentially involved with lipid transport, so providing a means of transporting the lipids to the outer membrane. These proteins are then extensively investigated through lipid pulldowns, binding analysis on all three, and X-ray crystallography and docking of the latter two.

Strengths<br /> The lipid pulldowns and associated MST binding analysis are convincing, clearly showing that sterols are able to bind to these proteins. The structures of BstB and BstC are high resolution with excellent maps that allow docking studies to be carried out. These structures are distinct from sterol-binding proteins in eukaryotes.

Weaknesses<br /> While the docking and molecular dynamics studies are consistent with the binding of sterols to BstB and BstC, this is not backed up particularly well. The MST results of mutants in the binding pocket of BstB have relatively little effect, and while I agree with the authors this may be because of the extensive hydrophobic interactions that the ligand makes with the protein, it is difficult to make any firm conclusions about binding.

The authors also discuss the possibility of a secondary binding site in BstB based on a slight cavity in domain B next to a flexible loop. This is not backed up in any way and seems unlikely.

Reviewer #3 (Public Review):

Summary:<br /> The work in this manuscript builds on prior efforts by this team to understand how sterols are biosynthesized and utilized in bacteria. The study reports a new function for three genes encoded near sterol biosynthesis enzymes, suggesting the resulting proteins function as a sterol transport system. Biochemical and structural characterization of the two soluble components of the pathway establishes that both proteins can bind sterols, with a preference for 4-methylated derivatives. High-resolution x-ray structures of the apoproteins reveal hydrophobic cavities of the appropriate size to accommodate these substrates. Docking and molecular dynamics simulations confirm this observation and provide specific insights into residues involved in substrate binding.

Strengths:<br /> The manuscript is comprehensive and well-written. The annotation of a new function in a set of proteins related to bacterial sterol usage is exciting and likely to enable further study of this phenomenon - which is currently not well understood. The work also has implications for improving our understanding of lipid usage in general among bacterial organisms.

Weaknesses:<br /> The authors might consider moving some of the bioinformatics figures to the main text, given how much space is devoted to this topic in the results section.

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.

eLife assessment

This valuable study informs whether diminishing BDNF expression or alterations in the activity of BDNF-containing neurons in the paraventricular nucleus of the hypothalamus contributes to metabolic alterations in individuals with reduced RAI1 function, including those afflicted with Smith-Magenis syndrome (SMS). The evidence supporting the conclusions is compelling in that RAI1 deficits in BDNF-containing neurons partly contribute, with prominent effects on glycemic control and modest effects on feeding and body weight regulation. This study would be of interest to neuroscientists and medical biologists working on metabolic disorders such as obesity and diabetes, as the findings in this study further links SMS-associated obesity with reduced Bdnf gene expression in the PVH and shed light on the role of the Rai1 gene in the PVH Bdnf neurons and offer a basis for future therapeutic strategies for managing obesity in SMS.

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 AKT cascades, 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 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. 2-supple 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.

The CRISPR-mediated knockdown of the Rai1 gene appears to be highly effective, and 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 an AKT pathway activator, the specific biological processes, and neurons responsible for this effect remain unclear. Elucidating these aspects in future studies would be significant when considering potential applications to human SMS cases.

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.

Reviewer #3 (Public Review):

Summary:<br /> Smith-Magenis syndrome (SMS) is associated with obesity and is caused by deletion or mutations in one cope 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 by providing three lines of evidence. First, the authors conducted proteomic analysis of hypothalamic extracts from WT and SMS (Rai1 +/-) mice and showed that several signaling cascades downstream of BDNF (e.g., PI3K-AKT and mTOR) were down regulated in SMS mice. Second, the authors found that deletion of both copies of the Rai1 gene in all BDNF-expressing cells or BDNF-expressing neurons in the PVH led to obesity, although the phenotype is more subtle than that observed in SMS mice. Third, they found that Rai1 deletion reduced excitability of PVH BDNF neurons.

Strengths:<br /> The study provides additional evidence linking BDNF deficiency to hyperphagia and obesity associated with SMS. Furthermore, the study shows that deletion of only one copy of the Rai1 gene in all BDNF-expressing cells did not cause obesity. This result indicates that BDNF deficiency only has a minor contribution to the metabolic symptoms associated with SMS patients who lose one copy of the RAI1 gene. The discovery that Rai1 is important for excitability of PVH BDNF neurons is interesting.

Weaknesses:<br /> The main mechanism underlying SMS-associated obesity remains to be identified. This limitation is discussed in this revised manuscript. The authors also address my previous concerns in this revised manuscript.

Reviewer #1 (Public Review):

Chen and colleagues investigated ZC3H11A as a potential cause of high myopia (HM) in humans through the analysis of exome sequencing in 1,015 adolescents and experiments involving Zc3h11a knock-out mice. The authors showed four possibly pathogenic missense variants in four adolescents with HM. After that, the authors presented the phenotypic features of Zc3h11a knock-out mice, the result of RNA-sequencing, and a comparison of mRNA and protein levels of the functional candidates between wild-type and Zc3h11a knock-out mice. Based on their observations, the authors concluded that ZC3H11A protein contributes to the early onset of myopia.

The strengths of this manuscript include: (1) successful identification of characteristic ophthalmic phenotypes in Zc3h11a knock-out mice, (2) demonstration of biological features related to myopia, such as PI3K-AKT and NF-kB pathways, and (3) inclusion of supporting human genetic data in individuals with HM. On the other hand, the weaknesses of this paper appear to be: (1) the lack of robust evidence from their genomic analysis, and (2) insufficient evidence to support phenotypic similarity between humans with ZC3H11A mutations and Zc3h11a knock-out mice. Given that the biological mechanisms of high myopia are not fully understood, the identification of a novel gene is valuable. As described in the manuscript, it is worth noting that the previous study using myopic mouse model has implicated the role of ZC3H11A in the etiology of myopia (Fan et al. Plos Genet 2012).

Specific comments:<br /> 1. I am concerned about the certainty of similarity in phenotypes between individuals with ZC3H11A mutation and Zc3h11a knock-out mice. A crucial point would be that there are no statistical differences in axial lengths (ALs) between wild-type and Zc3h11a knock-out mice at 8W and 10W, even though ALs in the individuals with ZC3H11A mutation were long. I would also like to note that the phenotypic information of these individuals is not available in the manuscript, although the authors indicated the suppressed b-wave amplitude in Zc3h11a knock-out mice. Considering that the authors described that "Detailed ophthalmic examinations were performed (lines: 321-323)", the detailed clinical features of these individuals should be included in the manuscript.

2. The term "pathogenic variant" should be used cautiously. Please clarify the pathogenicity of the reported variants in accordance with the ACMG guideline.

3. The genetic analysis does not fully support the claim that ZC3H11A is causative for HM. While the authors showed the rare allele frequencies and high CADD scores (> 20) of the identified variants, these were insufficient to establish causality. A helpful way to assess the causality would be performing a segregation analysis. An alternative approach is to show significant association by performing a gene-level association test. Assessing the pathogenicity of the variants using various prediction software, such as SIFT, PolyPhen2, and REVEL may also provide additional supportive evidence.

4. As shown in Figure 2, significant differences in refraction were observed from 4 weeks to 10 weeks. Nevertheless, no differences were observed in AL, anterior/vitreous chamber depth, and lens depth. The author should experimentally clarify what factors contribute to the observed difference in refraction.

5. The gene names should be italicized throughout the manuscript.

6. Table 1: providing chromosomal positions and rs numbers (if available) would be helpful for readers.

7. Figure 5b, c, and d: the results of pathway analysis and GO enrichment analysis are difficult to interpret due to the small font size. It would be preferable to present these results in tables. Moreover, the authors should set a significant threshold in the enrichment analyses.

eLife assessment

This useful study reports an investigation of ZC3H11A as a cause of high myopia through the analysis of human data and experiments with genetic knockout of Zc3h11a in mice, providing a model of myopia. The evidence supporting the conclusions is currently incomplete. It could be strengthened by a more thorough genetic analysis, fuller presentation of human phenotypic data, and more explanation for the reasons why there was no increased axial length in mice with myopia. The work will be of interest to ophthalmologists and researchers working on myopia.

Reviewer #2 (Public Review):

Summary:<br /> Chong Chen and colleagues reported that mutations were identified in the ZC3H11A gene in four adolescents from 1015 high myopia subjects in their myopia cohort. They further generated Zc3h11a knockout mice utilizing the CRISPR/Cas9 technology. They analyzed the heterozygotes knockout mice compared to control littermates and found refractive error changes, electrophysiological differences, and retinal inflammation-related gene expression differences. They concluded that ZC3H11A may play a role in the early onset of myopia by regulating inflammatory responses.

Strengths:<br /> Data were shown from both clinical cohort and animal models.

Weaknesses:<br /> Their findings are interesting and important, however; they need to resolve several points to make the current conclusion.

1. They described the ZC3H11A gene as a pathogenic variant for high myopia. It should be classified as pathogenic according to the guidelines of the American College of Medical Genetics and Genomics (Richards et al., Genet Med 17(5):405-24, 2015). The modes of inheritance for the families need to be shown. They also described identifying the gene as a "new" candidate. It should be checked in databases such as gnomAD and ClinVar, and any previous publications and be declared as a novel variant.

2. The phenotypes of the heterozygote mice are weak overall. The het mice showed mild to moderate myopic refractive shifts from 4 to 10 weeks of age. However, this cannot be explained by other ocular biometrics such as anterior chamber depth or lens thickness. Some differences are found between het and WT littermates in axial length and vitreous chamber depth but disappear after 8 weeks old. Furthermore, the early differences are not enough to explain the refractive error changes. They mentioned that they did not use homozygotes because of the embryonic lethality. I would strongly suggest employing conditional knockout systems to analyze homozygotes. This will also be able to identify the causative tissues/cells because they assume bipolar cells are functional. The cells in the retinal pigment epithelium and choroid are also important to contribute to myopia development.

3. Their hypothesis regarding inflammatory gene changes and myopic development is not logical. Are the inflammatory responses evoked from bipolar cells? Did the mice show an accumulation of inflammatory cells in the inner retina? Visible retinal inflammation is not generally seen in either early-onset or high-myopia human subjects. Can this be seen in the actual subjects in the cohort? To me, this is difficult to adapt the retina-to-sclera signaling they mentioned in the discussion so far. Egr-1 may be examined as described.

Reviewer #3 (Public Review):

Chen et al have identified a new candidate gene for high myopia, ZC3H11A, and using a knock-out mouse model, have attempted to validate it as a myopia gene and explain a potential mechanism. They identified 4 heterozygous missense variants in highly myopic teenagers. These variants are in conserved regions of the protein, but the authors provide no evidence that these specific variants affect protein function. They then created a knock-out mouse. Heterozygotes show myopia at all ages examined but increased axial length only at very early ages. Unfortunately, the authors do not address this point or examine corneal structure in these animals. They show that the mice have decreased B-wave amplitude on electroretinogram (a sign of retinal dysfunction associated with bipolar cells), and decreased expression of a bipolar cell marker, PKC. They do not address, however, whether there are fewer bipolar cells, or simply decreased expression of the marker protein. On electron microscopy, there are morphologic differences in the outer nuclear layer (where bipolar, amacrine, and horizontal cell bodies reside). Transcriptome analysis identified over 700 differentially expressed genes. The authors chose to focus on the PI3K-AKT and NF-B signaling pathways and show changes in the expression of genes and proteins in those pathways, including PI3K, AKT, IB, NF-B, TGF-1, MMP-2, and IL-6, although there is very high variability between animals. They propose that myopia may develop in these animals either as a result of visual abnormality (decreased bipolar cell function in the retina) or by alteration of NF-B signaling. These data provide an interesting new candidate variant for the development of high myopia, and provide additional data that MMP2 and IL6 have a role in myopia development, but do not support the claim of the title that myopia is caused by an inflammatory reaction.

Reviewer #3 (Public Review):

Summary:<br /> In this study, the authors set out to address the question of how the SNARE protein Syntaxin 17 senses autophagosome maturation by being recruited to autophagosomal membranes only once autophagosome formation and sealing is complete. The authors discover that the C-terminal region of Syntaxin 17 is essential for its sensing mechanism that involves two transmembrane domains and a positively charged region. The authors discover that the lipid PI4P is highly enriched in mature autophagosomes and that electrostatic interaction with Syntaxin 17's positively charged region with PI4P drives recruitment specifically to mature autophagosomes. The temporal basis for PI4P enrichment and Syntaxin 17 recruitment to ensure that unsealed autophagosomes do not fuse with lysosomes is a very interesting and important discovery. Overall, the data are clear and convincing, with the study providing important mechanistic insights that will be of broad interest to the autophagy field, and also to cell biologists interested in phosphoinositide lipid biology. The author's discovery also provides an opportunity for future research in which Syntaxin 17's c-terminal region could be used to target factors of interest to mature autophagosomes.

Strengths:<br /> The study combines clear and convincing cell biology data with in vitro approaches to show how Syntaxin 17 is recruited to mature autophagosomes. The authors take a methodical approach to narrow down the critical regions within Syntaxin 17 required for recruitment and use a variety of biosensors to show that PI4P is enriched on mature autophagosomes.

Weaknesses:<br /> There are no major weaknesses, overall the work is highly convincing. It would have been beneficial if the authors could have shown whether altering PI4P levels would affect Syntaxin 17 recruitment. However, this is understandably a challenging experiment to undertake and the authors outlined their various attempts to tackle this question. In addition, clear statements within the figure legends on the number of independent experimental repeats that were conducted for experiments that were quantitated are not currently present in the manuscript.

eLife assessment

This paper addresses a fundamental issue in the field of autophagy: How is a protein responsible for autophagosome-lysosome fusion recruited to mature autophagosomes but not immature ones? The work succeeds in its ambition to provide a new conceptual advance. The evidence supporting the conclusions is convincing, with solid fluorescence microscopy, biochemical assays, and molecular dynamics simulations. This work will be of broad interest not only to cell biologists and biochemists studying autophagy but also those focusing on lipid/membrane biology.

Reviewer #1 (Public Review):

In this manuscript, the authors report a molecular mechanism for recruiting syntaixn 17 (Syn17) to the closed autophagosomes through the charge interaction between enriched PI4P and the C-terminal region of Syn17. How to precisely control the location and conformation of proteins is critical for maintaining autophagic flux. Particularly, the recruitment of Syn17 to autophagosomes remains unclear. In this paper, the author describes a simple lipid-protein interaction model beyond previous studies focusing on protein-protein interactions. This represents conceptual advances.

Reviewer #2 (Public Review):

Summary:<br /> Syntaxin17 (STX17) is a SNARE protein that is recruited to mature (i.e., closed) autophagosomes, but not to immature (i.e., unclosed) ones, and mediates the autophagosome-lysosome fusion. How STX17 recognizes the mature autophagosome is an unresolved interesting question in the autophagy field. Shinoda and colleagues set out to answer this question by focusing on the C-terminal domain of STX17 and found that PI4P is a strong candidate that causes the STX17 recruitment to the autophasome.

Strengths:<br /> The main findings are: 1) Rich positive charges in the C-terminal domain of STX17 are sufficient for the recruitment to the mature autophagosome; 2) Fluorescence charge sensors of different strengths suggest that autophagic membranes have negative charges and the charge increases as they mature; 3) Among a battery of fluorescence biosensors, only PI4P-binding biosensors distribute to the mature autophagosome; 4) STX17 bound to isolated autophagosomes is released by treatment with Sac1 phosphatase; 5) By dynamic molecular simulation, STX17 TM is shown to be inserted to a membrane containing PI4P but not to a membrane without it. These results indicate that PI4P is a strong candidate that STX17 binds to in the autophagosome.

Weaknesses:<br /> • It was not answered whether PI4P is crucial for the STX17 recruitment in cells because manipulation of the PI4P content in autophagic membranes was not successful for unknown reasons.<br /> • The molecular simulation study did not show whether PI4P is necessary for the STX17 TM insertion or whether other negatively charged lipids can play a similar role.<br /> • The question that the authors posed in the beginning, i.e., why is STX17 recruited to the mature (closed) autophagosome but not to immature autophagic membranes, was not answered. The authors speculate that the seemingly gradual increase of negative charges in autophagic membranes is caused by an increase in PI4P. However, this was not supported by the PI4P fluorescence biosensor experiment that showed their distribution to the mature autophagosome only. Here, there are at least two possibilities: 1) The increase of negative charges in immature autophagic membranes is derived from PI4P. However the fluorescence biosensors do not bind there for some reason; for example, they are not sensitive enough to recognize PI4P until it reaches a certain level, or simply, their binding does not occur in a quantitative manner. 2) The negative charge in immature membranes is not derived from PI4P, and PI4P is generated abundantly only after autophagosomes are closed. In either case, it is not easy to explain why STX17 is recruited to the mature autophagosome only. For the first scenario, it is not clear how the PI4P synthesis is regulated so that it reaches a sufficient level only after the membrane closure. In the second case, the mechanism that produces PI4P only after the autophagosome closure needs to be elucidated (so, in this case, the question of the temporal regulation issue remains the same).

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.

Reviewer #2 (Public Review):

Summary:

Recent advances in single-cell profiling of gene expression (RNA) permit the analysis of specialized cell types, an approach that has great value in the nervous system which is characterized by prodigious neuronal diversity. The novel data in this study focus primarily on genetic profiling to compare autonomic neurons from ganglia associated with the cranial parasympathetic outflow (sphenopalatine (also known as pteropalatine), the thoraco-lumbar sympathetic outflow (stellate, coeliac) and the sacral parasympathetic outflow (pelvic). Using statistical methods to reduce the dimensionality of the data and map gene expression, the authors provide interesting evidence that cranial parasympathetic and sacral sympathetic ganglia differ from each other and from sympathetic ganglia (Figures 1, S1 - S4). The authors interpret the mapping analysis as evidence that the cranial and sacral outflows differ so calling them both parasympathetic is unjustified. Based on anatomical localization of markers (Figure 2 ) (mainly transcription factors) the authors show a similarity between the sympathetic and pelvic ganglion. In Figure 3 they present evidence that some pelvic ganglionic neurons are dually innervated by sympathetic preganglionic neurons and sacral preganglionic neurons. These observations are interpreted to mean that the pelvic ganglion is not parasympathetic, but rather a modified sympathetic ganglion - hence the title of the manuscript.

Strengths:<br /> The extensive use of single-cell profiling in this work is both interesting and exciting. Although still in its early stages, it holds promise for a deepened understanding of autonomic development and function. As noted in the introduction, this study extends previous work by Professor Brunet and his associates.

Weaknesses:<br /> This work further documents differences between the cranial and sacral parasympathetic outflows that have been known since the time of Langley - 100 years ago. The approach taken by Brunet et al. has focused on late neonatal and early postnatal development, a time when autonomic function is still maturing. 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. How then do genetic programs specifying brainstem and spinal development differ and how can this account for kinship that Brunet documents between spinal and sacral ganglia? One feature that seems to set the pelvic ganglion apart is the mixture of 'sympathetic' and 'parasympthetic' ganglion cells and 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). 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? 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)). What then about neuropeptides, whose expression pattern is incompatible with the revised nomenclature proposed by Brunet et al.? Figure 1B indicates that VIP is expressed by sacral and cranial ganglion cells, but not thoracolumbar ganglion 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.

Reviewer #1 (Public Review):

In recent years, these investigators have been engaged in a debate regarding the classification of the sacral parasympathetic system as "sympathetic" rather than "parasympathetic," based on shared developmental ontogeny of spinal preganglionic neurons. In this current study, these investigators conducted single-cell RNAseq analyses of four groups of autonomic neurons: paravertebral sympathetic neurons (stellate and lumbar train ganglia), prevertebral sympathetic neurons (coeliac-mesenteric ganglia), rostral parasympathetic ganglia (sphenopalatine ganglia), and the caudal pelvic ganglia (containing traditionally recognized sacral "parasympathetic cholinergic neurons," which the investigators sought to challenge in terms of nomenclature). The authors argued that the pelvic ganglionic neurons shared the expression of more genes with sympathetic ganglia, as opposed to parasympathetic ganglia. Additionally, the pelvic neurons did not express a set of genes observed in the rostral parasympathetic sphenopalatine ganglia. Based on these findings, they claimed that the sacral autonomic system should be considered sympathetic rather than parasympathetic. However, these arguments face significant challenges.

Firstly, among the P1-4 clusters of pelvic neurons, the P3 cluster predominantly represents noradrenergic sympathetic neurons, known to be present in pelvic ganglia. These neurons share gene expression patterns typically found in sympathetic neurons and lack the key cholinergic features identified in the P1, P2, and P4 clusters. 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.

Secondly, as mentioned above, the P1, P2, and P4 clusters are cholinergic neurons, expressing ChAT (and VIP). The authors claimed that these neurons shared a large set of genes expressed in sympathetic neurons (class I genes shown in Figure 1B). A closer look at the expression showed that some genes are expressed at higher levels in sympathetic neurons and in P2 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. 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.

Thirdly, noradrenergic sympathetic neurons and cholinergic neurons, by virtue of expressing different neurotransmitters, could have distinct roles. It is true that some cholinergic neurons reside in the sympathetic train ganglia as well, such as those innervating the sweat gland and some vascular systems; in this sense, the pelvic ganglia share some features with sympathetic ganglia, except that the pelvic ganglia contain a much higher percentage of cholinergic neurons compared with sympathetic ganglia. 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. Thus, from the functionality point of view, it is not justified to claim that "pelvic organs receive no parasympathetic innervation".

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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