Reviewer #1 (Public Review):

In this interesting manuscript, Nasser et al explore long-term patterns of behavior and individuality in C. elegans following early-life nutritional stress. Using a rigorous, highly quantitative, high-throughput approach, they track patterns of motor behavior in many individual nematodes from L1 to young adulthood. Interestingly, they find that early-life food deprivation leads to decreased activity in young larvae and adults, but that activity between these times, during L2-L4, is largely unaffected. Further, they show that this "buffering" of stress requires dopamine signaling, as L2-L4 activity is significantly reduced by early-life starvation in cat-2 mutants. The paper also provides evidence that serotonin signaling has a role in modulating sensitivity to stress in L1 larvae and adults, but the size of these effects is modest. To evaluate patterns of individuality, the authors use principal components analysis to find that three temporal patterns of activity account for much of the variation in the data. While the paper refers to these as "individuality types," it may be more reasonable to think of these as "dimensions of individuality." Further, they provide evidence that stress may alter the strength and/or features of these dimensions. Though the circuit mechanisms underlying individuality and stress-induced changes in behavior remain unknown, this paper lays an important foundation for evaluating these questions. As the authors note, the behaviors studied here represent only a small fraction of the behavioral repertoire of this system. As such, the findings here are an interesting and very promising entry point for a deeper understanding of behavioral individuality, particularly because of the cellular/synaptic-level analysis that is possible in this system. This paper should be of interest to those studying C. elegans behavior and also more generally to those interested in behavioral plasticity and individuality.

Reviewer #2 (Public Review):

This paper set out to understand the impact of early life stress on the behavior and individuality of animals, and how that impact might be amplified or masked by neuromodulation. To do so, the authors built on a previously established assay (Stern et al 2017) to measure the roaming fraction and speed of individuals. This technique allowed the authors to assess the effects of early life starvation on behavior across the entire developmental trajectory of the individual. By combining this with strains with mutant neuromodulatory systems, this enabled the authors to produce a rich dataset ripe for analysis to analyze the complicated interactions between behavior, starvation intensity, developmental time, individuality, and neuromodulatory systems.

The richness of this dataset - 2 behavioral measures continuous across 5 developmental stages, 3 different neuromodulatory conditions (with the dopamine system subject to decomposition by receptor types) and 4 different levels of starvation, with ~50-500 individuals in each condition-underlies the strength of this paper. This dataset enabled the authors to convincingly demonstrate that starvation triggers a behavioral effect in L1 and adult animals that is largely masked in intermediate stages, and that this effect becomes larger with increased severity of starvation. Furthermore, they convincingly show that the masking of the effect of starvation in L2-L4 animals depends on dopaminergic systems. The richness of the dataset also allowed a careful analysis of individuality, though only neuromodulatory mutants convincingly manipulated individuality, recapitulating earlier research. Nonetheless, a few caveats exist on some of their findings and conclusions:

1. Lack of quantitative analysis for effects within developmental stages. In making the argument for buffered effects of starvation on behavior during periods of larval development, the authors make claims regarding the temporal structure of behavior within specific stages. However, no formal analysis is performed and and the traces are provided without confidence intervals, making it difficult to judge the significance of potential deviations between starvation conditions.

2. Incorrect inferences from differences in significance demonstrating significant differences. The authors claim that there is an increase in PC1 inter-individual variation in tph-1 individuals, however the difference in significance is not evidence of a significant difference between conditions (see Nieuwenhuis et al. 2011). This undermines claims about an interaction of starvation, neuromodulators, and individuality.

3. Sensitivity of analysis to baseline effects and assumptions of additive/proportional effects. The neuromodulatory and stress conditions in this paper have a mixture of effects on baseline activity and differences from baseline. The authors normalize to the roaming fraction without starvation, making the reasonable assumption that the effect due to starvation is proportional to baseline, rather than an additive effect. This confound is most visible in the adult subpanel of figure 5d, where an ~2-3 fold difference in relative roaming due to starvation is clearly noted, however, this is from a baseline roaming fraction in tph-1 animals that are ~2 fold higher, suggesting that the effect could plausibly be comparable in absolute terms.

Unavoidably, any such assumptions on the expected interaction between multiple effects will be a gross simplification in complicated nonlinear systems, and the data are largely shown with sufficient clarity to allow the reader to make their own conclusions. However, some of the interpretations in the paper lean heavily on an assumption that the data support a direct interpretation (e.g. "neuronal mechanisms actively buffer behavioral alterations at specific development times") rather than an indirect interpretation (e.g. that serotonin reduces baseline roaming fraction which makes a fixed sized effect more noticeable). Parsing the differences requires either more detailed mechanistic study or careful characterization of the effect of different baselines on the sensitivity of behavior to perturbation-barring that it's worth noting that many of these interactions may be due to differences in biological and experimental sensitivity to change under different conditions, rather than a direct interaction of stress and neuromodulatory processes or evidence of differing neuromodulatory activity at different stages of development.

Reviewer #3 (Public Review):

In this study, Nasser et al. aim to understand how early-life experience affects 1) developmental behavior trajectory and 2) individuality. They use early life starvation and longitudinal recording of C. elegans locomotion across development as a model to address these questions. They focus on one specific behavioral response (roaming vs. dwelling) and demonstrate that early life (right after embryo hatching) starvation reduces roaming in the first larval (L1) and adult stages. However, roaming/dwelling behavior during mid-larval stages (L2 through L4) is buffered from early life starvation. Using dopamine and serotonin biosynthesis null mutant animals, they demonstrated that dopamine is important for the buffering/protection of behavioral responses to starvation in mid-larval stages, while in contrast, serotonin contributes to early-life starvation's effects on reduced roaming in the L1 and adult stages. While the technique and analysis approaches used are mostly solid and support many of the conclusions made in the manuscript for part 1), there are some technical limitations (e.g., whether the method has sufficient resolution to analyze the behaviors of younger animals) and confounding factors (e.g., size of the animal) that the authors do not yet sufficient address, and can affect interpretation of the results. Additionally, much of the study is descriptive and lacks deep mechanistic insight. Furthermore, the focus on a single behavioral parameter (dwelling vs. roaming) limits the broad applicability of the study's conclusions. Lastly, the manuscript does not provide clear presentation or analysis to address part 2), the question of how early life experience affect individuality.

Reviewer #1 (Public Review):

The DNA damage checkpoint is a cellular signalling pathway that responds to DNA damage and replication stress. This manuscript by Ho et al. systematically investigates an aspect of the checkpoint response in budding yeast that has been previously understudied, namely which proteins change subcellular and how these changed depend on the checkpoint kinases Mec1 and Rad53. By nice detective work the authors find a new mode of activation of Rad53, which is Mec1-independent, but rather depends on factors of so called retrograde signalling. Currently, we view checkpoint signalling as hierarchical, with Mec1 and Tel1 activating Rad53, despite both Mec1 and Rad53 having independent targets. This manuscript challenges that view by finding a Mec1 (and Tel1) independent mode of activation. It is very clear from survival and mass spectrometry data that in the absence of Mec1 this activation pathway and Rtg3 has a key role in activating Rad53. In the current form of the manuscript, it remains however difficult to assess what is the contribution of these factors on Rad53 activation in an otherwise WT background.

Reviewer #2 (Public Review):

Using an approach that combines synthetic genetic array (SGA) analysis with high-throughput microscopic analysis of the GFP-tagged yeast ORF collection in the budding yeast, Saccharomyces cerevisiae, this study has examined the contribution of the critical checkpoint kinases Mec1 and Rad53 to the subcellular relocalization of 322 candidate proteins in response to HU- and MMS-induced replication stress. Previous studies have established that Mec1 is required for Rad53 activation during replication stress and that Mec1 also serves checkpoint functions independent of Rad53. Unexpectedly, this study identifies groups of proteins whose stress-induced relocalization is dependent on Rad53 but not Mec1. This data indicates that Rad53 mediates some replication stress responses in a non-canonical manner that is independent of Mec1.

The authors confirm their initial observations from the screening approach by focusing on the Rad53-dependent and Mec1-independent focus formation of GFP-Rad54. Moreover, using mass-spec analysis the authors demonstrate that some Rad53 phosphorylation sites known to be critical for Rad53 activation, including a consensus Mec1 phosphorylation site, are phosphorylated after replication stress even in the absence of Mec1. Motivated by this finding the authors screen for potential kinase and phosphatase pathways that may regulate Rad53 function during MMS-induced replication stress. Top hits identified include members of the retrograde signaling pathway, which is confirmed by conventional genetic assays while mass spec analysis supports the involvement of Rtg3 in mediating Rad53 phosphorylation during replication stress in the absence of Mec1.

Overall this is a solid study reporting unexpected new findings that significantly advance our view of the global replication checkpoint response. The data are generally of high quality, well presented and quantified, and overall support the authors' claims. The mass spec approach used here to identify Rad53 phosphorylation sites offers an unbiased alternative to the simpler and more widely employed gel-shift method to monitor Rad53 activation. The hits identified in the various screens presented here provide a platform for potential follow-up studies by the community. The main drawback is that it remains unclear how Rtg3 promotes Rad53 activtation. However, this could be considered to be beyond the scope of this study.

Reviewer #3 (Public Review):

The work by Ho et al describes the identification of Mec1/Tel1 independent activation of Rad53 after MMS treatment, which could lead to changes of GFP fusion signals for several dozens of proteins and this was partly dependent on Rtg3. Starting from an unbiased, targeted screen, the authors identified proteins whose GFP fusion signals changed intensity in rad53∆ but not in mec1∆ cells using live cell imaging, including Rad54. Using Rad54 as a readout for the subsequent experiments, a second screen amongst kinases/phosphatases and their regulators found that rtg2-3 mutants reduced Rad54-GFP intensity. Mass spectrometry data identified Rad53 phosphorylate sites in mec1∆ tel1∆ cells, consistent with the cell biological data described above. Overall, the work was well done and supported the main conclusions. The concept of Mec1/Tel1-independent and Rtg3-dependent Rad53 activation connects checkpoint signaling with the retrograde pathway.

Reviewer #1 (Public Review):

In this paper, Reato, Steinfeld et al. investigate a question that has long puzzled neuroscientists: what features of ongoing brain activity predict trial-to-trial variability in responding to the same sensory stimuli? They record spiking activity in the auditory cortex of head-fixed mice as the animals performed a tone frequency discrimination task. They then measure both overall activity and the synchronization between neurons, and link this 'baseline state' (after removing slow drifts) of cortex to decision accuracy. They find that cortical state fluctuations only affect subsequent evoked responses and choice behavior after errors. This indicates that it's important to take into account the behavioral context when examining the effects of neural state on behavior.

Strengths of this work are the clear and beautiful presentation of the figures, and the careful consideration of the temporal properties of behavioral and neural signals. Indeed, slowly drifting signals are tricky as many authors have recently addressed (e.g. Ashwood, Gupta, Harris). The authors are well aware of the difficulties in correlating different signals with temporal and cross-correlation (such as in their 'epoch hypothesis'). To disentangle such slow trends from more short-lived state fluctuations, they remove the impact of the past 10 trials and continue their analyses with so-called 'innovations' (a term that is unusual, and may more simply be replaced with 'residuals').

I do wonder if this throws out the baby with the bathwater. If the concern is statistical confound, the 'session permutation' method (Harris) may be better suited. If the concern is that short-term state fluctuations are more behaviorally relevant (and obscured by slow drifts), then why are the results with raw signals in the supplement (Suppfig 8) so similar?

While the authors are correct that go-nogo tasks have drawbacks in dissociating sensitivity from response bias, they only cursorily review the literature on 2AFC tasks and cortical state. In particular, it would be good to discuss how the specific method - spikes, EEG (Waschke), widefield (Jacobs) and algorithm for quantifying synchronization may affect outcomes. How do these population-based measures of cortical state relate to those described extensively with slightly different signals, notably LFP or EEG in humans (e.g. work by Saskia Haegens, Niko Busch, reviewed in https://doi.org/10.1016/j.tics.2020.05.004)? This review also points out the importance of moving beyond simple measures of accuracy and using SDT, which would be an interesting improvement for this paper too.

Reviewer #2 (Public Review):

The relationship between measures of brain state, behavioral state, and performance has long been speculated to be relatively simple - with arousal and engagement reflecting EEG desynchronization and improved performance associated with increases in engagement and attention. The present study demonstrates that the outcome of the previous trial, specifically a miss, allows these associations to be seen - while a correct response appears less likely to do so. This is an interesting advance in our understanding of the relationship between brain state, behavioral state, and performance.

While the study is well done, the results are likely to be specific to their trial structure and states exhibited by the mice. To examine the full range of arousal states, it needs to be demonstrated that animals are varying between near-sleep (e.g. drowsiness) and high-alertness such as in rapid running. The fact that the trials occurred rapidly means that the physiological and neural variables associated with each trial will overlap with upcoming trials - it takes a mouse more than a few seconds to relax from a previous miss or hit, for example. Spreading the rapidity of the trials out would allow for a broader range of states to be examined, and perhaps less cross-talk between adjacent trials. The interpretation of the results, therefore, must be taken in light of the trial structure and the states exhibited by the mice.

Reviewer #2 (Public Review):

The manuscript by Mohebi et al. examines a critical open question regarding the interaction of cholinergic interneurons of the striatum and transmitter release from dopaminergic axons in behaving animals. Activation of cholinergic interneurons in the striatum can evoke dopamine release in brain slices and in vivo as measured with voltammetry. However, it remains an open question in what context and to what extent this acetylcholine-mediated dopamine occurs in behaving animals. Here, the authors argue that CIN activity triggers dopamine release in the nucleus accumbens which encodes the motivation to obtain a reward through increasing "ramps" of dopamine release. Their data suggest that the ramps are not reflected in the firing of dopaminergic neurons. Rather, they provide compelling evidence that the ramps of dopamine release correlate with ramps in cholinergic interneuron activity as measured with GCaMP6. What's more, the authors show that ACh-mediated dopamine release has no paired-pulse depression, a striking result that differs from all prior ex vivo brain slice data. The manuscript is extremely well written and the data are of very high quality. Overall, this study represents an important step forward in our understanding of how ACh-mediated dopamine release regulates behavior, and more broadly how axons can generate behaviors independently from somatic activity.

Major comments<br /> 1. The complete absence of any short-term plasticity in CIN-mediated dopamine release is a striking result that is important for the field. The authors should strengthen this result with additional quantitative analysis demonstrating the lack of STP. They have analyzed paired-pulse ratios, but they should analyze this for stimuli at the higher frequencies (4 Hz, etc) that are more physiologically relevant. For example, Fig 1e shows a CIN-evoked DA release at many optically-stimulated frequencies. The authors should quantify short-term plasticity by generating fits of the single stimulus signal and comparing the mathematical sum predicted from 4 stim DA signals at different frequencies to the recorded data. A similar analysis has been done with Ca signals (Koester and Sakmann, 2000).

2. The authors show that optical activation of CINs results in DA release as measured by dLight. To clearly establish that these signals are generated by DA release driven by nicotinic receptors (and not a partial effect of some unknown artifact), it would be useful to show that the optical CIN-evoked dLight signals shown in Fig. 1 are inhibited by nicotinic receptor antagonists such as DHbE. This control experiment would significantly strengthen the result shown here.

3. Similarly, the authors show clear correlations between CIN activity and DA release during behavior. The authors should consider determining whether CINs play a causal role in triggering DA release during behavior. For example, does infusion of DHbE in the NAc prevent the light-mediated DA release during behavior? As an alternative hypothesis, some groups have been suggesting that CIN activity has almost no direct influence over DA. Therefore, testing whether a causal relationship exists between CINs and DA release would be an important experiment in addressing these two opposing viewpoints.

4. The ramps that are described in this manuscript are an order of magnitude faster (increasing over 100s of milliseconds) than ramps described in other studies that occur over seconds. In fact, the two signals may be completely different functionally. Discussion of this topic would be helpful.

Public Review:

Barreat and Katzourakis analyze the evolutionary history of eukaryotic viruses (and related mobile elements) in the Bamfordvirae kingdom, and discuss potential scenarios regarding the origin of different viral taxa in this group. This version of their manuscript includes a larger number of sequences to better represent diversity in these viral groups, and explored new evolutionary scenarios, including a "virophage-first" hypothesis now presented as the one best supported by phylogenetic analyses. The authors also present compelling analyses suggesting that the "nuclear escape" hypothesis in which these different viral groups separately "escaped" from nuclear (integrated) elements is not consistent with the current genomic and phylogenetic information available.

This work is thus an important step in our collective understanding of the ancient evolutionary history of eukaryotic viruses, and more generally of the constraints and main drivers of virus evolution.

Reviewer #1 (Public Review):

Owen D et al. investigated the protein partners and molecular functions of ZMYM2, a transcriptional repressor with key roles in cell identity and mutated in several human diseases, in human U2OS cells using mass spectrometry, siRNA knockdown, ChIP-seq and RNA-seq. They tried to identify chromatin bound complexes containing ZMYM2 and identified known and novel protein partners, including ADNP and the newly described partner TRIM28. Focusing mainly on these two proteins, they show that ZMYM2 physically interacts with ADNP or TRIM28, and co-occupies an overlapping set of genomic regions with ADNP and TRIM28. By generating a large set of knockdown and RNA-seq experiments, they show that ZMYM2 co-regulates a large number of genes with ADNP and TRIM28 in U2OS cells. Interestingly, ZMYM2-TRIM28 do not appear to repress genes directly at promoters, but the authors find that ZMYM2/TRIM28 repress LTR elements and suggest that this leads to gene deregulation at distance by affecting the chromatin environment within TADs.

A strength of the study is that, compared to previous studies of ZMYM2 protein partners, it investigates binding partners of ZMYM2 using the RIME method on chromatin. The RIME method makes it possible to identify low-affinity protein-protein interactions and proteins interactions occurring at chromatin, therefore revealing partners most relevant for gene regulation at chromatin. This allowed the identification of novel ZMYM2 partners not identified before, such as TRIM28.

The authors present solid interaction data with appropriate controls and generated an impressive amount of datasets (ChIP-seq for TRIM28 and ADNP, RNA-seq in ZMYM2, ADNP and TRIM28 knockdown cells) that are important to understand the molecular functions of ZMYM2. These datasets were generated with replicates and will be very useful for the scientific community. This study provides important novel insights into the molecular roles of ZMYM2 in human U2OS cells.

The authors could have been more precise in the manuscript title and abstract to emphasize that these findings apply to human cells, as indeed there is no demonstration yet that the findings presented here can be transposed to mouse cells.

The manuscript's main conceptual advance is that the authors propose a novel model of gene regulation whereby transcriptional repressors of transposable elements could regulate genes at distance by modulating the local chromatin environment within TADs. Additional experiments would be needed to strengthen this model. For example the authors could have performed TRIM28 ChIP in ZMYM2-kd cells to test if ZMYM2 favors the recruitment of TRIM28 to its genomic targets, as well as ChIP-seq of repressive chromatin marks (such as H3K9me3) in ZMYM2-kd cells to investigate if the loss of ZMYM2 leads to reduced H3K9me3 in ERVs and over large regions surrounding the ERVs.

Reviewer #2 (Public Review):

In this study the authors investigate functional associations made by transcription factor ZMYM2 with chromatin regulators, and the impact of perturbing these complexes on the transcriptome of the U2OS cell line. They focus on validating two novel chromatin-templated interactions: with TRIM28/KAP1 and with ADNP, concluding that via these distinct chromatin regulators, ZMYM2 contributes to transcriptional control of LTR and SINE retrotransposons, respectively.

Strengths and weakness of the study:

- The co-localization of ZMYM2 with ADNP and TRIM28 is validated through RIME, ChIP-seq and co-IP. (Notably, since both RIME and ChIP-seq rely on crosslinking, and the co-IP with TRIM28 required crosslinking due to being SUMO-dependent, only the ZMYM2-ADNP co-IP experiment demonstrates an interaction in the absence of crosslinking).

- It is good that uniquely-mapped reads are used in the ChIP-seq analysis given the interest in repetitive elements. Likewise, though the RT-qPCR data in Fig5 should be complemented by analysis of the RNA-seq data that the authors already have, it seems that the primers are carefully designed such that a single retrotransposon copy is amplified.

- The top-scoring interactors are highly-abundant nuclear proteins: for example, data from the contaminant repository for affinity purification mass-spec data (https://reprint-apms.org/) show that TRIM28 is identified in 466 / 716 AP-MS experiments with a mean spectral count of 16. While this does not indicate that the ZMYM2-TRIM28 interaction is not 'true', it would have been helpful to further dissect the interaction to strengthen this conclusion. For example, it would be nice to see the co-IP (fig 3A) repeated from the cells expressing the ZMYM2 mutant that is no longer competent to bind SUMO (used in the ChIP-seq data of Fig 2). Alternatively - if the model is that ZMYM2 recruits SUMOylated TRIM28 - with well-characterized TRIM28 mutants that lack SUMOylation.

- The transcriptional response using bulk RNA-seq in ZMYM2-depleted cells is rather gene-centric despite the title of the paper being about TE transcription. In fact the only panels about TE transcription are the RT-qPCR data in Fig 5D,F. I may be missing something (and there aren't many details given about the RNA-seq experiments) but why not look at TE transcription in an unbiased way with the transcriptomic data at hand? I appreciate potential hazards of multi-mapping etc but it would be interesting to see at least some subfamily analysis (e.g. using the TEtranscripts tool). On a similar point, why not show some RNA-seq in the genome browser snapshots of the epigenomics - together with a RepeatMasker annotation track of TEs...

While the results broadly support the authors' conclusions, I have the overall impression that the central claim of TE transcriptional regulation by ZMYM2 could be strengthened a lot with some fairly straightforward additional experiments and analyses.

Reviewer #3 (Public Review):

ZMYM2 is a transcriptional repressor known to bind to the post-translational modification SUMO2/3. It has been implicated in the silencing of genes and transposons in a variety of contexts, but lacking sequence-specific DNA binding, little is known about how it is targeted to specific regions. At least two reports indicate association with TRIM28 targets (Tsusaka 2020 Epigenetics & Chromatin, Graham-Paquin 2022 bioRxiv) but no physical association with TRIM28 targets had been observed. Tsusaka 2020 theorizes an indirect, potentially SUMO-independent, interaction via ATF7IP and SETDB1.

Here, Owen and colleagues show that a subset of ZMYM2-binding sites in U2OS cells are clearly TRIM28 sites, and further find that hundreds of genes are silenced by both ZMYM2 and TRIM28. They next demonstrate that ZMYM2 homes to chromatin, and interacts with TRIM28, in a SUMOylation-dependent manner, suggesting that ZMYM2 is recognizing SUMOylation on TRIM28 itself. ZMYM2 separately homes to SINE elements bound by the ChAHP complex, in an apparently SUMOylation independent manner. Although this is not the first report to show physical interaction between ZMYM2 and ChAHP, it is the first to show that ZMYM2 homes to ChAHP-binding sites and functions as a corepressor at these sites.

The mode by which ZMYM2 and TRIM28 coregulate genic targets remains somewhat unclear. TRIM28/ZMYM2 bind to LTR elements, loss of these proteins results in upregulation of genes distal to (but in the same TAD as) these binding sites.

Overall, the manuscript is well-written, convincing, and fills a significant hole in our understanding of ZMYM2's mechanistic function.

Reviewer #1 (Public Review):

In the manuscript there is not much comparison between the crystal and cryoEM structures provided, and on inspection they appear to be very similar. The crystal structures also reveal parts of the CC domains in Las1, which is not present in the cryoEM structures. It is interesting the CC domains in Sc and Cj are quite different as illustrated in Figure 4B. They also seem to be somewhat disconnected from the rest of the complex (more so for Cj), even though that's not apparent in Figures 2-4. Despite this, it would be very useful to show the cryoEM densities when describing the catalytic site and C-terminal domain interactions, for example, as this can be very useful to increase confidence in the model and proposed mechanisms.

The description of the complex as a butterfly is engaging, and from a certain angle it can be made to look as such; this was also described previously in (Pillon et al., 2019, NSMB) for the same complex from a different organism (Ct). However, it is a bit misleading, because the complex is actually C2 symmetric. Under this symmetry, the 'body' would consist of two 'heads' one pointing up, one down facing towards the back, and one wing would have its back toward the viewer, the other the front. The structures presented here in Sc and Cj seem quite similar to the previous structure of the same complex in Ct, though the latter was only solved with cryoEM, and was also lacking the structure of the CC domain in Las1.

For the model suggested in Figure 8, perhaps in the 'weak activity' state, the LCT in Las1 could still be connected to Grc3, via the LCT, rather than disconnected as shown. This could facilitate faster assembly of the 'high activity' state. The complex is described as 'compact and stable', but from the structure and this image, it appears more dynamic, which would serve its purpose and the illustrated model better. The two copies of HEPN appear to have more connective area, meaning they are indeed more likely to remain assembled in the 'weak activity' state. On the other hand, HEPN in one protein appears to have less binding surface with PNK in Grc3, and even less so with the CTD (both PNK and CTD being from the other associated protein), meaning these bindings could release easily to form the 'weak activity' state.

There is also the potential to speculate that the GCT is bound to HEPN near the catalytic area in the 'weak activity' state. The reduced activity when the GCT residues are replaced by Alanine could then be explained by the complex not being able to assemble as quickly upon binding of the substrate, as it could if the GCT remained bound, rather than by a conformational change that it induces upon binding. The conformational change is also likely to be influenced by the combined binding of PNK and CTD in the assembled state, which also contact HEPN, rather than by GCT alone.

When comparing the structure of the HEPN domain in the lone Las1 protein to the structure of Las1-HEPN in the Las1-Grc3 complex, it is mentioned that 'large conformational changes are observed'. These could be described a bit better. The conformational change is ~3-4Å C-alpha RMSD across all ~150 residues in the domain (~90 residues forming a stable core that only changes by ~1Å). There is also a shift in the associated HEPN domain in Las1B domain compared to the bound HEPN in the Las1-Grc3 complex, as shown in Figure 7D: ~1Å shift and ~12degrees rotation. This does point to the conformation of HEPN changing upon complex formation, as does the relative positions of the HEPN domains in Las1A and Las1B. The conformational change and relative shift could indeed by key for the catalysis of the substrate as mentioned.

Overall, the structures presented should be very useful in further study of this system, even though the exact dynamics and how the substrate is bound are aspects that are perhaps not fully clear yet. The addition of the structures of the CC domain in two different organisms and the Las1 HEPN domain (not in complex with Grc3) as new structural information should allow for increasing our understanding of the overall complex and its mechanism.

Reviewer #2 (Public Review):

In this manuscript, Chen et al. determined the structural basis for pre-RNA processing by Las1-Grc3 endoribonuclease and polynucleotide kinase complexes from S. cerevisiae (Sc) and C. jadinii (Cj). Using a robust set of biochemical assays, the authors identify that the sc- and CjLas1-Grc3 complexes can cleave the ITS2 sequence in two specific locations, including a novel C2' location. The authors then determined X-ray crystallography and cryo-EM structures of the ScLas1-Grc3 and CjLas1-Grc3 complexes, providing structural insight that is complimentary to previously reported Las1-Grc3 structures from C. thermophilum (Pillon et al., 2019, NSMB). The authors further explore the importance of multiple Las1 and Grc3 domains and interaction interfaces for RNA binding, RNA cleavage activity, and Las1-Grc3 complex formation. Finally, evidence is presented that suggests Las1 undergoes a conformational change upon Grc3 binding that stabilizes the Las1 HEPN active site, providing a possible rationale for the stimulation of Las1 cleavage by Grc3.

Several of the conclusions in this manuscript are supported by the data provided, particularly the identification and validation of the second cleavage site in the ITS2. However, several aspects of the structural analysis and complimentary biochemical assays would need to be addressed to fully support the conclusions drawn by the authors.

• There is a lack of clarity regarding the number of replicates performed for the biochemical experiments throughout the manuscript. This information is critical for establishing the rigor of these biochemical experiments.

• The authors conclude that Rat1-Rai1 can degrade the phosphorylated P1 and P2 products of ITS2 (lines 160-162, Figure 1H). However, the data in Fig. 1H shows complete degradation of 5'Phos-P2 and 5'Phos-P4 of ITS2, while the P1 and 5'Phos-P3 fragments remain in-tact. Additional clarification for this discrepancy should be provided.

• The authors determined X-ray crystal structures of the ScLas1-Grc3 (PDB:7Y18) and CjLas1-Grc3 (PDB:7Y17) complexes, which represents the bulk of the manuscript. However, there are major concerns with the structural models for ScLas1-Grc3 (PDB:7Y18) and CjLas1-Grc3 (PDB:7Y17). These structures have extremely high clashscores (>100) as well as a significant number of RSRZ outliers, sidechain rotamer outliers, bond angle outliers, and bond length outliers. Moreover, both structures have extensive regions that have been modeled without corresponding electron density, and other regions where the model clearly does not fit the experimental density. These concerns make it difficult to determine whether the structural data fully support several of the conclusions in the manuscript. A more careful and thorough reevaluation of the models is important for providing confidence in these structural conclusions.

• The presentation of the cryo-EM datasets is underdeveloped in the results section drawing and the contribution of these structures towards supporting the main conclusions of the manuscript are unclear. An in-depth comparison of the structures generated from X-ray crystallography and cryo-EM would have greatly strengthened the structural conclusions made for the ScLas1-Grc3 and CjLas1-Grc3 complexes.

• The authors conclude that truncation of the CC-domain contributes to Las1 IRS2 binding and cleavage (lines 220-222, Fig. 4C). However, these assays show that internal deletion of the CC-domain alone has minimal effect on cleavage (Fig 4C, sample 3). The loss in ITS2 cleavage activity is only seen when truncating the LCT and LCT+CC-domain (Fig 4C, sample 2 and 4, respectively). Consistently, the authors later show that Las1 is unable to interact with Grc3 when the LCT domain is deleted (Fig. 6 and Fig. 6-figure supplement 2). These data indicate the LCT plays a critical role in Las1-Grc3 complex formation and subsequent Las1 cleavage activity. However, it is unclear how this data supports the stated conclusion that the CC-domain is important for LasI cleavage.

• The authors conclude that the HEPN domains undergo a conformational change upon Grc3 binding, which is important for stabilization of the Las1 active site and Grc3-mediated activation of Las1. This conclusion is based on structural comparison of the HEPN domains from the CjLas1-Grc3 complex (PDB:7Y17) and the structure of the isolated HEPN domain dimer (PDB:7Y16). However, it is also possible that the conformational changes observed in the HEPN domain are due to truncation of the Las1 CC and CGT domains. A rationale for excluding this possibility would have strengthened this section of the manuscript.

Reviewer #1 (Public Review):

Membrane receptor guanylyl cyclases are important for many physiological processes but their structures in full-length and their mechanism are poorly understood. Caveney et al. determined the cryo-EM structure of a highly engineered GC-C in a complex with endogenous HSP90 and CDC37. The structural work is solid and the structural information will be useful for the membrane receptor guanylyl cyclases field and the HSP90 field. However, a detailed characterization of the protein sample is lacking. Moreover, the physiological significance of this structure is not fully exploited by supporting experiments and the mechanistic insight is currently limited.

1. The characterization of the protein sample is lacking. SDS-PAGE would be useful to identify potential proteolysis, leading to the dissociation of GC dimer. Further size-exclusion chromatography would be helpful to estimate the molecular weight of the complex and to determine if only GC-C monomer is purified.

2. The orientation distribution of the particles is not homogenous in Fig. S1D. It would be helpful to present the 3DFSC curve to evaluate the effect of preferred orientation on the reconstruction.

3. Description of protein expression details is lacking. Did the author use transient transfection, stable cell line or virus-mediated transduction?

4. HSP90 binds ATP and is often co-purified with endogenous ATP/ADP. Is there ATP or ADP present in the sample/cryo-EM maps? Is the conformation of NBD similar to ATP-bound HSP90? The author needs to include the description/figures about the nucleotide state of HSP90.

5. The catalytic domains of GC have to be dimerized to perform cyclase function. The presence of only one GC-PK monomer in the cryo-EM structure indicates the structure does not represent an active state of GC. These results suggest the GC expressed in this way is not functional. The authors need to explain why most of the GC protein is trapped in this inactive form.

6. The GC-C construct used here is a highly engineered "artificial" construct, which has not been fully characterized in this work. Does this construct have similar activity as the activated wt GC-C? Does the protein (this engineered construct) expressed in CHO cells show activity?

7. Are the residues on the interface between GC and HSP conserved in other members of membrane receptor guanylyl cyclases? Would mutations on this interface affect the activity of GC?

8. The authors propose that targeting HSP90 would tune the activity of GC. Is there any experimental data supporting this idea?

9. The model in Fig. S3 is largely speculative due to the lack of supporting functional data. In addition, it would be better to change the title to "structure of the protein kinase domain of guanylyl cyclase receptor in complex with HSP90 and cdc37" because the mechanistic insight is limited.

Reviewer #2 (Public Review):

Caveney et al have overexpressed an engineered construct of the human membrane receptor guanyl cyclase GC-C in hamster cells and co-purified it with the endogenous HSP90 and CDC37. They have then determined the structure of the resultant complex by single particle cryoEM reconstruction at sufficient resolution to dock existing structures of HSP90 and CDC37, plus an AlphaFold model of the pseudo-kinase domain of the guanylyl cyclase. The novelty of the work stems from the observation that the pseudo-kinase domain of GC-C associates with CDC37 and HSP90 similarly to how the bona fide protein kinases CDK4, CRAF and BRAF have been previously shown to interact.

The experimentation is limited to the cryoEM analysis, and is lacking additional studies that would give deeper insight into the oligomeric nature - if any - of the GC-C when bound to HSP90-CDC37 as compared to the free protein. This is relevant, as the dimerization domain downstream of the pseudokinase, is evident in the maps - albeit not well resolved - and it is not clear whether it is still able to mediate dimerization with a second free or HSP90-CDC37-bound GC-C. It would also be good to see some experimentation that asks whether association with HSP90-CDC37 inhibits the guanyl cyclase activity. It is clear from previous work that HSP90-CDC37 silence the kinase activity of their bound client kinases, but in this case the catalytic guanyl cyclase is not directly associated with the chaperone complex and may still be able to function.

Although the sequence alignment presented in SuppFig 2 shows that GC-C conserves the classic DFG motif that plays a critical role in the regulation of most kinases, the numbering of the sequence is absent, making it very difficult to relate this to the structural detail shown in Fig 2B. This needs to be clarified, as the interaction of CDC37-Trp31 with the DFG motifs and downstream activation loops in CRAF and BRAF have been proposed as important features of the selectivity of these kinases for the HSP90-CDC37 system, and it would be good to be able to see clearly how much of this is also conserved in the GC-C pseudokinase domain interaction. For example, is the much shorter activation segment (DFG -> APE) ordered in the complex or disordered?

It was not easy to follow what was in the sample used for cryoEM. The cloning of the guanylyl cyclase (GC) component is described in the methods and they have shown some illustrations in fig 1 but a proper numbered figure of the domain organisation clearly showing domain boundaries and linker segments is really needed for a reader not familiar with the structure of GCs, especially since they have replaced the ECD with a leucine zipper in their construct. It is important to show a domain figure of what this construct looks like as well, as from the illustrations in fig 1 for examples its hard to see what's PK, DD, GC domains. It would also be helpful to see in the supplementary a gel of complex they put on the grids, to make it clearer what exactly the sample is and to reassure that the GC-C domains that are not resolved in the cryoEM are nonetheless present in the sample.

Overall there is only minimal proposal of mechanism or biological function based on the structure. The speculation in the Discussion of two fates - PP5 dephosphorylation or E3 ligase recruitment, is not supported by any experimentation, which is reasonable for speculation, but is also not underpinned by reference to any previously published work suggesting that these additional processes may be important. In the absence of any work by the authors can they put these speculations more in context with previously published work that supports the importance of these processes specifically for GC regulation?

Reviewer #3 (Public Review):

A detailed understanding of how membrane receptor guanylyl cyclases (mGC) are regulated has been hampered by the absence of structural information on the cytoplasmic regions of these signaling proteins. The study by Caveney et al. reports the 3.9Å cryo-EM structure of the human mGC cyclase, GC-C, bound to the Hsp90-Cdc37 chaperone complex. This structure represents a first view of the intracellular functional domains of any mGC and answers without doubt that Hsp90-Cdc37 recognizes mGCs via their pseudokinase (PK) domain. This is the primary breakthrough of this study. Additionally, the new structural data reveals that the manner in which Hsp90-Cdc37 recognizes the GC-C PK domain C-lobe is akin to how kinase domains of soluble kinases docks to the chaperone complex. This is the second major finding of this study, which provides a concrete framework to understand, more broadly, how Hsp90-Cdc37 recruits a large number of other diverse client proteins containing kinase or pseudokinase domains. Finally, the Hsp90-Cdc37-GC-C structure offer clues as to how GC-C may be regulated by phosphorylation and/or ubiquitinylation by serving as a platform for recruitment of PP5 and/or E3 ligases.

Comments:

1. The authors used an interesting approach to obtain the GC-C-Hsp90-Cdc37 complex. Flag-tagged human GC-C was overexpressed in CHO cells with the expectation of co-purifying endogenous hamster homologs of Hsp90 and Cdc37. There are several points worth noting:<br /> a. It is not clear from the data presented (Figure 1C, Suppl Fig 1A) or the Methods the percentage of particles in the cryo-EM specimen that represent the GC-C-Hsp90-Cdc37 complex. Presumably, some fraction of GC-C isolated will not be associated with Hsp90-Cdc37. If a very large portion of GC-C is associated with Hsp90-Cdc37, it would be good to explain why this is to be expected. Are 2D/3D classes corresponding to the activated GC-C dimer found? If not, why?<br /> b. Figure 1A suggests that GC-C is phosphorylated before recruitment of Hsp90-Cdc37. What is the phosphorylation status of the GC-C specimen that was imaged by cryo-EM?<br /> c. The resolution of the cryo-EM map (3.9 Å) is too low for unambiguous identification of proteins. Please provide more precise justification for the claim that the densities observed do in fact correspond to hamster Hsp90 and Cdc37.<br /> d. The authors state that human GC-C pulls down hamster Hsp90-cdc37 but soluble kinases cannot, despite the high sequence identity between human and hamster Hsp90-cdc37. Is this because GC-C recognition is more promiscuous? Can this difference be understood in light of the new structural information presented?

2. A large portion of the enforced GC-C dimer was not visible in the cryo-EM maps. It is not easy to learn from Figure 1 exactly which parts of the GC-C construct was sufficiently ordered and observed structurally. Please improve Figure 1.

3. On page 4, the authors claim that they are able to orient the GC-C-Hsp90-Cdc37 complex "as it would sit on a membrane" and referred to Figure 1B. It is not clear what is implied here. Does Hsp90-Cdc37 binding constrain the complex to face the inner leaflet of the membrane in a specific orientation as shown in Figure 1B? If true, this could potentially have important functional implications. Please illustrate how this was deduced based on the information available.

4. Also on page 4, it is stated that it is sterically unlikely an additional Hsp90-Cdc37 complex is associated with the other copy of GC-C in the leucine zippered dimer. It is not obvious to the reader how this may be the case. An additional figure could help make this more clear. Additional biochemical evidence will also help. The absence of GC-C-Hsp90-Cdc37 dimers in cryo-EM micrographs can also support the argument.

5. Some comments on Figure 2:<br /> a. NTD and CTD are mislabeled in Figure 2A.<br /> b. The authors should show cryo-EM density to support their modeling of GC-C in Figures 2B and C.

6. The authors claim that Hsp90-Cdc37 clients are more similar structurally near the cdc37 interface. Please illustrate this with additional figures. Suppl. Figure 2 is inadequate for this purpose. The authors can also consider adding a more detailed discussion comparing the interactions between the pseudokinase/kinase C-lobe and Cdc37 in known structures. Is shape/charge complementarity a universal feature of cdc37-dependent kinase/pseudokinase recruitment? It would be interesting to also consider if it would be possible to predict which of the ~60 human pseudokinases are possible Hsp90-Cdc37 clients. New structural findings from this study and publicly available AI-predicted protein structures could help.

Reviewer #1 (Public Review):

This manuscript conducts a classic QTL analysis to identify the molecular basis of natural variation in disease resistance. This identifies a pair of glycosyltransferases that contribute to steroidal glycoalkaloid production. Specifically altering the final hexose structure of the compound. This is somewhat similar to the work in tomatine showing that the specific hexose structure mediates the final potential bioactivity. Using the resulting transgenic complementation lines that show that the gene leads to a strong resistance phenotype to one isolate of Alternaria solani and the Colorado potato beetle. This is solid work showing the identification of a new gene and compound influencing plant biotic interactions. While the experiments are solid, the introduction, discussion and associated claims don't accurately reflect my reading of what is known and said in the current literature.

The sentence on line 53-54 is misleading. It provides only three citations on specific links between specialized metabolism and disease resistance. However, there are actually at least 40 on specific links of camalexin and indolic phytoalexins to disease resistance. Similarly there are dozens of uncited papers on benzoxazinoids, indolic glucosinolates, aliphatic glucosinolates and tomatine to both non-host and host based resistance mechanisms. This even goes as far as showing how the pathogens resist an array of these compounds. The choices in the introduction make it appear that little is known about specialized metabolism to disease resistance but I would suggest that this is not an allusion supported by the literature. I would agree that given the breadth of specialized metabolism we have a lot of knowledge about a set of them but that there are hundreds to thousands of untested compounds but to indicate that little is known is unfair to the specialized metabolism community. This is especially true as the introduction and discussion give no image of the large body of literature on specialized metabolism to insect interactions even though this is a major component of this manuscript.

I would also agree that specialized metabolism is not a conscious target of breeding programs but the work on benzoxazinoids in maize and glucosinolates in the Brassica's has shown that these compounds have been influenced by breeding programs. Similarly work on de novo domestication of multiple crops is focused on the adjustment of specialized metabolism in these crops.

I would disagree with the hint on line 49-50 and again on lines 236-239 that specialized metabolism may have less pleiotropy. This is not supported by recent work on benzoxazinoids and glucosinolates showing that they have numerous regulatory links to the plant and can be highly pleiotropic. Even the earliest avenicin work in oat showed that the deficient lines had altered root development.

My main message from the above three paragraphs is to point out that there are a number of places in the manuscript where the current state of the specialized metabolite literature is not accurately portrayed. To properly place the manuscript in the broader context, I would suggest a more even handed introduction and discussion that takes into account the current state of the specialized metabolism literature.

Is it accurate to say complete resistance to A. solani if only a single isolate of the pathogen is used? Is there evidence that I am unaware of that there are no isolates of this pathogen with saponin resistance? There are pathogens with natural tomatine resistance and this is a common feature of plant pathogens that they have genetic variation in the resistance to specialized metabolism. For example, it should be noted that Botrytis BO5.10 is a tomatine sensitive isolate and the van Kan and Hahn groups have published on isolates that are resistant to saponins. I would suggest caveating across the manuscript that this is a single isolate and that it is possible that there may be isolates with natural resistance to the steroidal glycoalkaloid?

In Figure 4b, is the infection site about 3.5 mm in size such that 3.5 mm means absolutely no infection? If not, that would mean there is some outgrowth by Alternaria and the resistance isn't complete.

Reviewer #2 (Public Review):

The study focuses on a mechanism of pest/pathogen resistance identified in Solanum commersonii, which appears to offer dominant resistance to Alternaria solani through the activity of specific glycosyltransferases which facilitate the production of tetraose glycoalkaloids in leaf tissue. The authors demonstrated that these glycoalkaloids are suppressive to the growth of multiple pathogenic ascomycetes and furthermore, that transgenic plants expressing these glycosyltransferases in susceptibleS. commersonii clones demonstrate improved resistance to a specific strain of A. solani and a genotype of Colorado Potato Beetle. The study design is straightforward, yet thorough, and does a good job demonstrating the importance of these genes in resistance. While the research findings are significant there are statements throughout the manuscript that overstate both the novelty and utility of the findings.

Title: While the protection is impressive, the title suggests that these glycoalkaloids provide protection against all fungi and insects, which is both unlikely and essentially impossible to prove. This should be changed to something more measured. This is especially true given that only a single fungus and insect were tested against transgenic plants, but would be an overstatement even with more robust evaluation.

Throughout the paper: A single isolate of A. solani and a single genotype of CPB were used in this study. While this is in line with the typical limitations of such a study, the authors need to be careful about claiming broad resistance to either of the species. Variability in fungicide tolerance and detoxification activity have been noted in both fungi and CPB, so more specific language should be used throughout (such as L213 and L221).

Reviewer #1 (Public Review):

In this article, Cacioppo et al., report on a previously unappreciated mechanism of the regulation of Aurora Kinase A (AURKA) protein levels that is orchestrated via coordinated action of alternative polyadenylation of AURKA mRNA and hsa-let-7a miRNA. Moreover, it is proposed that this mechanism may play a major role in neoplasia. In support of their model, the authors demonstrate that short-to-long 3'UTR AURKA mRNA isoform ratio is elevated in triple negative breast cancer patients where it correlates with poor prognosis. The authors further generated reporters suitable for single cell live imaging that express different 3'UTR variants, which revealed highly variable ratios of short and long 3'UTR AURKA isoforms across different cell lines. This was followed by actinomycin D chase and nascent chain immunoprecipitation assays in U2OS osteosarcoma cells to demonstrate that while short and long 3'UTR AURKA isoforms have comparable stability, short 3'UTR AURKA isoforms appear to exhibit higher ribosome association which is indicative of higher translation activity. Furthermore, using an additional reporter assay which takes advantage of trimethoprim-based stabilization of highly unstable E. Coli dihydrofolate reductase mutants Cacioppo et al., provide evidence that in contrast to the short 3'UTR AURKA mRNA isoform which appears to be constitutively translated throughout the cell cycle, long 3'UTR AURKA mRNA isoform is preferentially translated in the G2 phase. Further evidence is provided that suppression of long 3'UTR AURKA mRNA isoform is at least in part mediated by hsa-let-7a miRNA. Finally, the authors provide evidence that disrupting the expression of long 3'UTR AURKA mRNA isoform using CRISPR-based strategy, leads to overexpression of AURKA driven by the short 3'UTR isoform which is paralleled by an increase in cancer-related phenotypes.

Strengths: Overall it was thought that this study is of potentially broad interest inasmuch as it delineates a hitherto unappreciated mechanisms of regulation of AURKA protein levels, whereby AURKA is emerging as one of the major factors in neoplasia, including resistance to anti-cancer treatments. In general, it was thought that the author's conclusions were sufficiently supported by provided data. It was also thought that this study incorporates innovative methodology including single-cell expression sensors coupled with live cell microscopy and an assay to study translation in different phases of cell cycle without need for cell synchronization.

Weaknesses: Several relatively minor issues were observed regarding methodology and data interpretation. Namely, some inconsistencies between the models and/or cell lines that were used throughout the manuscript were noted. For instance, key experiments were performed almost exclusively in U2OS osteosarcoma cells, whereby triple negative breast cancer patient data were used to set the scientific foundation of the study. Considering potential differences in alternative polyadenylation between cell and tissue types, it was thought that investigation across the broader compendium of cell lines may be required for generalization of findings observed in U2OS cells. It was also found that the precise mechanisms underpinning the role of hsa-let-7a miRNA in regulation of AURKA protein levels remain largely obscure.

Reviewer #2 (Public Review):

Cacioppo et al describe a mechanism of translation regulation of Aurora A, which is dependent on alternative polyadenylation. They suggest that altered expression of the resulting isoforms in cancers is at least partly responsible for elevated Aurora A levels, which in turn is known to indicate poor prognosis.

The authors exploit publicly available databases and patient data to highlight the correlation of increased abundance of the SHORT isoform (relative to the LONG one) and poor patient survival in TNBC, as well as breast and lung cancer.

In their thorough mechanistic study they use a number of reporters to assess the impact of alternative polyadenylation on mRNA stability and translation efficiency and explore whether this process accounts for cell-cycle-regulated expression of Aurora A. These reporters are carefully controlled and well explained. I particularly commend the authors for the clear graphical presentations of the reporters (eg fig 2A, fig 3D, fig 4A). Rigorous control experiments are performed to make sure that the reporters work and "report" what they are meant to do, and to show that previous findings can be reproduced in experiments based on the reporters (eg higher protein expression from the short 3' UTR APA isoform of CDC6 mRNA, targeting of MZF1 3'UTR by hsa-let-7a).

They show that translation of the longer isoform is subject to suppression by hsa-let-7a, while the shorter isoform is not. They attribute cell-cycle regulated expression of Aurora A at least in part to the suppression of translation of the LONG isoform in G1 and S.<br /> In Figure 6 they address whether the APA-based regulatory mechanism alters Aurora A levels sufficiently to confer features associated with oncogenic transformation and overexpression of Aurora A. These data nicely tie together the observations in databases and the mechanistic part of the study.

The logic is clear and the conclusions are well supported by the data.

The authors state themselves that the impact of translation regulation on Aurora A levels in the cell cycle is an important but unanswered question. The evidence that suppression of translation of the LONG transcript contributes to the cell-cycle regulation of Aurora A is convincing, but the extent could be explored further. I wonder whether published genome-wide studies (eg PMCID 4548207, PMC3959127) have relevant data on the translation rate of Aurora A in the cell cycle.

In the paper this question is addressed in cells enriched in G1/S (Fig 6) and using the reporters (Fig 5). Having generated the ΔdPAS mutants, Aurora A levels could be easily assessed in each cell-cycle phase. The best way to do this would be sorting followed by immunoblotting.

The fact that Aurora A levels are reduced by a 6h treatment with 0.1 mg/ml CHX (Fig 6D) is interpreted as "AURKA expression in G1/S was reduced in the mutated cell lines when treated with CHX, indicating that translation of the short isoform is active in this phase" It is rather expected that using a translation inhibitor will stop the accumulation of a protein and so this experiment does not add much. A better approach to address the effect of the mutations on translation would be to add a proteasome inhibitor and follow accumulation of Aurora A, preferably not only in G1/S but also in other cell-cycle phases. Accumulation of the protein in this experiment would better reflect translation rates.

Reviewer #3 (Public Review):

Summary:

This manuscript sheds light on the cell cycle-dependent post-transcriptional regulation of the oncogenic kinase AURKA. AURKA mRNA is subjected to alternative polyadenylation (APA), resulting in a short and a long 3'UTR isoform. While the ratio long/short isoform is important for AURKA expression and might impact cancer development, it is not unclear how this is regulated throughout the cell cycle. Translation and decay rate of the long isoform only are targeted by let-7a miRNA and in a cell-cycle dependent manner. In contrast, the short isoform is translated highly and constantly throughout interphase. Finally, depletion of the long isoform led to an increase in proliferation and migration rates of cells. In Triple Negative Breast Cancer, where AURKA is typically overexpressed, the short isoform is predominant and its expression correlates with faster relapse times of patients, suggesting that this mechanism might play an important role in this cancer.

Originality and novelty:

The originality of this work is to show the cooperation between APA and miRNA-targeting in controlling gene expression dynamics of AURKA during cell cycle. To investigate this mechanism, the authors have developed an interesting transient single-cell and biochemical assay to rapidly study mRNA-specific gene expression in a way that measures post-transcriptional events. This manuscript puts an emphasis on the cell cycle dependent expression control of AURKA at the translation level. However, the magnitude of the changes in mRNA levels throughout the cell cycle is even greater than that of the changes in translation. Therefore, it remains unclear whether translation really is that important in controlling AURKA expression during the cell cycle. Moreover, (i) AURKA regulation by miRNA is already known (Fadaka et al., Oncotarget 2020, Zhang et al., Arch Med Sci 2020, Yuan et al., Technol Cancer Res Treat 2019, Ma et al., Oncotarget 2015), (ii) the concept of cooperation between APA and translation already is not new (Sandberg et al., Science 2008, Mayr and Bartel, Cell 2009, Masamha et al. Nature 2015), and (iii) previous transcriptome-wide studies already suggested a cell-cycle dependent control of AURKA at the translation level (Tanenbaun et al., eLife 2015, translation efficiency ratio G2/G1 = 1.59) as well as the mRNA level (Krenning et al., eLife 2022). The impact of this manuscript could be increased by investigating (i) the mechanism of cell cycle-dependent regulation by let7a expression (i.e is there changes in let7a expression or activity during the cell cycle in this model) and (ii) the origin of AURKA APA dysregulation in cancer (could it be modulated by CFIm25? (Masamha et al. Nature 2015, Tamaddon et al. Sci Rep 2020)).

Reviewer #1 (Public Review):

In this manuscript, the authors aimed to compare, from testis tissues at different ages from mice in vivo and after culture, multiple aspects of Leydig cells. These aspects included mRNA levels, proliferation, apoptosis, steroid levels, protein levels, etc. A lot of work was put into this manuscript in terms of experiments, systems, and approaches. However, as written the manuscript is incredibly difficult to follow. The Introduction and Results sections contain rather loosely organized lists of information that were altogether confusing. At the end of reading these sections, it was unclear what advance was provided by this work. The technical aspects of this work may be of interest to labs working on the specific topics of in vitro spermatogenesis for fertility preservation but fail to appeal to a broader readership. This may be best exemplified by the statements at the end of both the Abstract and Discussion which state that more work needs to be done to improve this system.

Reviewer #2 (Public Review):

Preserving and restoring the fertility of prepubertal patients undergoing gonadotoxic treatments involves freezing testicular fragments and waking them up in a culture in the context of medically assisted procreation. This implies that spermatogenesis must be fully reproduced ex vivo. The parameters of this type of culture must be validated using non-human models. In this article, the authors make an extensive study of the quality of the organotypic culture of neonatal mouse testes, paying particular attention to the differentiation and endocrine function of Leydig cells. They show that fetal Leydig cells present at the start of culture fail to complete the differentiation process into adult Leydig cells, which has an impact on the nature of the steroids produced and even on the signaling of these hormones.

The authors make an extensive study of the different populations of Leydig cells which are supposed to succeed each other during the first month of life of the mouse to end up with a population of adult and fully functional cells. The authors combine quantitative in situ studies with more global analyzes (RT-QtPCR Western blot, hormonal assays), which range from gene to hormone. This study is well written and illustrated, the description of the methods is honest, the analyses systematic, and are accompanied by multiple relevant control conditions.

Since the aim of the study was to study Leydig cell differentiation in neonatal mouse testis cultures, the study is well conceived, the results answer the initial question and are not over-interpreted.

My main concern is to understand why the authors have undertaken so much work when they mention RNA extractions and western blot, that the necrotic central part had to be carefully removed. There is no information on how this parameter was considered for immunohistochemistry and steroid measurements. The authors describe the initial material as a quarter testis, but they don't mention the resulting size of the fragment. A brief review of the literature shows that if often the culture medium is crucial for the quality of the culture (and in particular the supplementations as discussed by the authors here), the size of the fragments is also a determining factor, especially for long cultures. The main limitation of the study is therefore that the authors cannot exclude that central necrosis can have harmful effects on the survival and/or the growth and/or the differentiation of the testis in culture. In this sense, the general interpretation that the authors make of their work is correct, the culture conditions are not optimized.

Organotypic culture is currently trying to cross the doors of academic research laboratories to become a clinical tool, but it requires many adjustments and many quality controls. This study shows a perfect example of the pitfall often associated with this approach. The road is still long, but every piece of information is useful.

Reviewer #3 (Public Review):

Moutard, Laura, et al. investigated the gene expression and functional aspects of Leydig cells in a cryopreservation/long-term culture system. The authors found that critical genetic markers for Leydig cells were diminished when compared to the in-vivo testis. The testis also showed less androgen production and androgen responsiveness. Although they did not produce normal testosterone concentrations in basal media conditions, the cultured testis still remained highly responsive to gonadotrophin exposure, exhibiting a large increase in androgen production. Even after the hCG-dependent increase in testosterone, genetic markers of Leydig cells remained low, which means there is still a missing factor in the culture media that facilitates proper Leydig cell differentiation. Optimizing this testis culture protocol to help maintain proper Leydig cell differentiation could be useful for future human testis biopsy cultures, which will help preserve fertility and child cancer patients.

Methods: In line 226, there is mention that the central necrotic area was carefully removed before RNA extraction. This is particularly problematic for the inference of these results, especially for the RT-qPCR data. Was the central necrotic area consistent between all samples and variables (16 and 30FT)? How big was the area? This makes the in-vivo testis not a proper control for all comparisons. Leydig cells are not evenly distributed throughout the testis. A lot of Leydig cells can be found toward the center of the gonad, so the results might be driven by the loss of this region of the testis.

What did the morphology of the testis look like after culturing for 16 and 30 days? These images will help confirm that the culturing method is like the Nature paper Sato et al. 2011 and also give a sense of how big the necrotic region was and how it varied with culturing time.

There are multiple comparisons being made. Bonferroni corrections on p-value should be done.

Results: In the discussion, it is mentioned that IGF1 may be a missing factor in the media that could help Leydig cell differentiation. Have the authors tried this experiment? Improving this existing culturing method will be highly valuable.

Add p-values and SEM for qPCR data. This was done for hormones, should be the same way for other results.

Regarding all RT-qPCR data-There is a switch between 3bHSD and Actb/Gapdh as housekeeping genes. There does not seem to be as some have 3bHSD and others do not. Why do Igf1 and Dhh not use 3bHSD for housekeeping? If this is the method to be used, then 3bHSD should be used as housekeeping for the protein data, instead of ACTB. Also, based on Figure 1B and Figure 2A (Hsd3b1) there does not seem to be a strong correlation between Leydig cell # and the gene expression of Hsd3b1. If Hsd3b1 is to be used as a housekeeper and a proxy for Leydig cell number a correlation between these two measurements is necessary. If there is no correlation a housekeeping gene that is stable among all samples should be used. Sorting Leydig cells and then conducting qPCR would be optimal for these experiments.

Figure 2A (CYP17a1): It is surprising that the CYP17a1 gene and protein expression is very different between D30FT and 36.5dpp, however, the immunostaining looks identical between all groups. Why is this? A lower magnification image of the testis might make it easier to see the differences in Cyp17a1 expression. Leydig cells commonly have autofluorescence and need a background quencher (TrueBlack) to visualize the true signal in Leydig cells. This might reveal the true differences in Cyp17a1.

Figure 3D: there are large differences in estradiol concentration in the testis. Could it be that the testis is becoming more female-like? Leydig and Sertoli cells with more granulosa and theca cell features? Were any female markers investigated?

Figure 3D and Figure 5A: It is hard to imagine that intratesticular estradiol is maintained for 16-30 days without sufficient CYP19 activity or substrate (testosterone). 6.5 dpp was the last day with abundant CYP19 expression, so is most of the estrogen synthesized on this first day and it sticks around? Are there differences in estradiol metabolizing enzymes? Is there an alternative mechanism for E production?

Reviewer #1 (Public Review):

In this study the authors sought to address the issue of whether the Steller's sea cow -- a massive extinct sirenian ("sea cow") species that differs from its living relatives (manatees and dugongs) not only in body mass but also in having inhabited cold climates in the northern Pacific -- had hemoglobin adaptations that enhanced the species' thermoregulatory capacities relative to those of the extant species, which are restricted to relatively warm waters. To do so, the authors synthesized recombinant hemoglobin proteins of all the major sea cow lineages and used these data to assess differences in O2 binding, Hb solubility, responses to allosteric effectors, and thermal sensitivity. The work presented is very innovative and in my opinion convincingly demonstrates that the Steller's sea cow had remarkable hemoglobin adaptations that allowed for an extreme range extension into cool waters despite several physiological constraints that are inherent to the sirenian (and paenungulate, afrotherian, etc.) clade. I did not detect any obvious weaknesses of the paper, whereas the use of ancient DNA to resurrect 'extinct' hemoglobins, and the various analyses of these extinct hemoglobins alongside those of extant relatives is very exciting and are major strengths of the paper that make this study a very important advance for our understanding of Steller's sea cow's paleophysiology, as well as our understanding of the potential for extreme hemoglobin phenotypes that have not been documented among living species. Moving forward, these methods can be used to study aspects of the paleophysiology of other recently extinct mammals. I applaud the authors on an excellent and innovative study that significantly augments our understanding of the Steller's sea cow.

Reviewer #2 (Public Review):

This manuscript is an impressive "resurrection" of physiology regarding an enigmatic though unfortunately extinct species, and their potential adaptation to cold-water environments. I am largely convinced of their findings, which I feel are very straightforward and thorough.

One place where the authors perhaps fell a bit short was regarding some conclusions associated with maternal/fetal oxygen delivery. The sirenian versions of fetal & embryonic hemoglobin genes have been identified and assessed to some degree in previously published work the same research group. I feel the manuscript would have benefited from actual analysis of the fetal & embryonic hemoglobin (epsilon, gamma, zeta) to strengthen their assertions.

Reviewer #3 (Public Review):

Signore et al. the synthesized and functionally characterized the recombinant adult hemoglobin (Hb) proteins of extant, extinct, and ancestral sirenians to explore the putative role of Hb in helping Steller's sea cows adapt to life in extremely cold waters. The functional comparisons show that the Hb of the subarctic Steller's sea cows differs in multiple biochemical properties relative to the Hbs of the two extant sirenians in the study, the Florida manatee, and the dugong and also from the Hb inferred for the common ancestor of Steller's sea cow and dugong. Specifically, the Steller's sea cow shows reduced oxygen binding affinity, reduced sensitivity to the allosteric co-factors DPG, Cl-, and H+, increased solubility, and reduced thermal sensitivity. DPG plays an important role in regulating Hb oxygen affinity in mammals, and the lack of sensitivity to it is unique to the Hb of Steller's sea cow. Sequence comparisons show that the Hb of the Steller's sea cow differs at 11 amino acids from that of its sister group, the dugong, one of which is intriguing because it occurs in a position that is invariable among mammals at a site that is critical for DPG binding, a change from Lys to Ans in position 82 of the mature β/δ globin chain. To test the significance of this change, the authors use site directed mutagenesis to insert back a Lys in the Steller's sea cow Hb background (β/δ82Asn→Lys) and test its biochemical properties. The functional assays with the β/δ82Asn→Lys mutant indicate that reverting this position to its ancestral state drastically altered the biochemical properties of the Steller's sea cow Hb, making it functionally similar to the Hbs of manatee, dugong, and the Hb inferred for the common ancestor of Steller's sea cow and dugong.

The study's strength lies in comparing the different recombinant Hbs in an explicit evolutionary framework. The conclusions are supported by the analyses, and the results are relevant in the fields of evolutionary biology, physiology, and biochemistry because they suggest that a single amino acid substitution in a protein can have profound biochemical consequences that impact whole organism physiology.

Reviewer #1 (Public Review):

This study utilizes scRNA-seq to generate a detailed map of transcriptional changes that occur in asynchronously replicating the Trypanosoma brucei insect (PCF) and mammalian (BSF) stages. The analyses were performed on both fresh and cryo-preserved parasites, and transcriptional changes in PCF compared to existing proteomic datasets at the same stage. This is the first study to comprehensively map cell cycle-related transcriptional changes in T. brucei BSF and to undertake a side-by-side analysis of the two major parasite developmental stages. The study identified >1,500 transcripts that exhibit dynamic changes during the cell cycle across the two stages, substantially increasing the number of cell cycle-regulated (CCR) genes compared to previous analyses. Analysis of the data revealed common as well as stage-specific CCR transcripts and identified transcripts with known/suspected functions in cell cycle regulation as well as hypothetical proteins. The findings also support and quantify previous observations suggesting that most transcript changes (83-86% of CCR transcripts) are not reflected by similar changes in corresponding proteins, and where there is a correlation, protein expression levels expectedly lag behind transcripts. Overall, the study provides the most comprehensive transcriptome atlas of the T. brucei cell cycle undertaken to date, highlighting a large number of genes and cellular processes that are linked to cell cycle progression, while further confirming the importance of post-transcriptional regulatory processes in these divergent eukaryotes. The work represents a significant technical advance, particularly in the validation of the use of cryo-preserved parasites for single-cell RNS-seq, and nicely integrates results from previous proteomics and gene-knockout studies.

Reviewer #2 (Public Review):

Parasitic African trypanosomes are agents of devastating diseases in humans and animals. Currently, no vaccines exist, with control of human disease being realized thru vector suppression and elimination of infected hosts while animal diseases remain rampant on the continent. The molecular aspects of the multiple developmental stages the parasite undergoes thru its mammal and tsetse hosts, and the unique aspects of parasite gene expression regulation and host evasion mechanisms have been extensively investigated. Recent applications of single-cell transcriptomics (scRNA) to these approaches have expanded knowledge gained from total RNA and revealed new insights.

In this paper, Briggs et al., set out to determine the cell cycle-related genes (CCR) of T. brucei, which follows the typical eukaryotic progression through G1, S, G2, and M phases followed by cytokinesis, although trypanosomes are unusual in that both nuclear and mitochondrial genome replication and segregation are orchestrated during cell division. while many regulators remain unidentified, are absent, or have been replaced by trypanosomatid-specific factors. For these studies, they apply scRNA methodology using asynchronous mixed populations of cultured 'monomorphic' slender mammalian (BSF) and insect stage (PCF) cells and then determine their cell cycle phases computationally. Of interest, performing similar analysis with fresh and cryopreserved cells made minimal difference to the outcome, thus enabling future investigations with preserved cells.

The study identified 1,550 genes with dynamic transcript level changes reflective of the cell cycle, 1,151 of which had not been previously identified by bulk analysis. These revealed a common set of highly conserved CCR genes as well as unique gene transcript levels expressed thru the cell cycle for BSF and PCF cells. Expression patterns of the G1 and S phase genes are highly comparable between BSF and PCF forms, whereas, after the S phase, the timing of gene expression for the S-G2 transition is far less synchronized. Comparison between transcript expression patterns and previously published protein abundance changes identified a relative delay in peak levels for transcript and protein for at least 50% of the genes that could be compared. Collectively, this foundational analysis generates transcript atlases for BSF and PCF cell cycles, which can be further mined for downstream functional investigations.

Reviewer #3 (Public Review):

In this article, Briggs et al. used scRNAseq to get high-resolution cell cycle-regulated transcriptomes of both replicative forms of Trypanosoma brucei (PCF and BSF) without prior synchronization. Briggs et al. also demonstrated that performing the scRNAseq library immediately after thawing cryopreserved samples did not show significant differences. The authors used computational reconstruction of the cell cycle to get the dynamic expression patterns of cycling genes in both life cycle forms. They identified a core cycling transcriptome highly conserved between forms. However, some slight differences were found between them, e.g.: a switch in gene expression associated with the S-G2 transition is much more discrete in PCFs than BSFs. Moreover, as proteomics data across the cell cycle is not available for BSFs, the authors tagged the top most significant genes with transcripts peaking in G1, S, and G2/M phases with a fluorescent epitope. After comparing the transcript expression patterns with protein abundance, the authors found that the majority of genes with periodic cycling transcript and protein levels exhibited a relative delay between peak transcript and protein expression, which was expected. In summary, this work provides a valuable public tool for further investigation into gene expression dynamics throughout the cell cycle in T. brucei.

Reviewer #1 (Public Review):

The nuclear receptor Nurr1 is a target of interest in neurodegenerative diseases like Parkinson's and Alzheimer's, but its mechanism of activation on NBRE-containing promoters and potential druggability is unknown. A heterodimer of Nurr1 with RXRa can be activated by a subset of ligands that bind to the RXRa ligand binding domain (LBD). Here, the authors provide evidence that transcriptional activation occurs through ligand-induced dissociation of the heterodimer, leading to an active Nurr1 monomer.

NMR spectroscopy and other biophysical, biochemical, and cell-based assays provide a strong foundation for the work. The manuscript is well-written and easy to follow, and for the most part, it thoughtfully addresses experimental results and data interpretation with reasonable caveats. However, a reliance on simple correlative analyses, including some with rather modest correlations (R2 values {less than or equal to} 0.5), may fail to account for some potentially interesting outlier ligands and oversimplify conclusions. Despite this possible oversimplification, this manuscript provides solid evidence of their discovery of an interesting mechanism by which a subset of RXRɑ ligands leads to transcriptional activation of Nurr1 at NBRE promoters--this is an exciting finding that could be potentially relevant in the development of neuroprotective therapies.

Reviewer #2 (Public Review):

Nurr1 is a nuclear receptor and is important for mammalian brain development and homeostasis. Dysfunctional Nurr1 transcriptional activities are implicated in neurodegenerative diseases like Parkinson's. This exquisite ligand-dependent and specific transcriptional reprogramming make nuclear receptors ideal drug targets. However, the design of Nurr1-selective ligands has been confounded by the fact that Nurr1's ligand binding pocket appears to collapse in x-ray crystal structures. Interestingly, RXRalpha-targeted ligands, Nurr1's obligate heterodimer binding partner, show differential effects on Nurr1's transcriptional activities. In this study, the authors aimed to address how RXRalpha ligands lead to Nurr1 transcriptional activation. By combining biochemical approaches, NMR spectroscopy, and transcriptional reporter gene assays in neuronal cells, the authors convincingly show that these select RXRalpha ligands elicit an allosteric effect that reduces Nurr1 binding affinity. They further show that monomeric Nurr1 is a highly effective enhancer of the promoter that is repressed in the presence of RXRalpha. Overall, this is a well-presented and robust study as presented and the conclusions are supported by their evidence. This study should have a profound impact on the field as it provides a clear structural mechanism for ligand-dependent Nurr1 activation in neuronal cells.

Reviewer #3 (Public Review):

Nurr1 is an orphan nuclear receptor that may be a significant target for the treatment of neurodegenerative disorders. Targeting Nurr1 with small molecule ligands has been challenging, but there has been some progress in the identification of synthetic ligands that appear to increase Nurr1 activity. Nurr1 functions as a monomer, but may also heterodimerize with RXR. Heterodimerization appears to repress Nurr1 transcriptional activation via NBRE-driven reporters. Importantly, small molecule ligands that appear to selectively activate the Nurr1/RXR heterodimer complex (and not the Nurr1 or RXR homodimers, individually) have been identified. Exactly how these ligands function in this manner is unclear.

Here, the authors demonstrate that Nurr-1/RXR agonists actually function by perturbing the heterodimer formation providing Nurr1 monomers that are much more active in driving transcription. The authors demonstrate this with a range of biochemical, biophysical, and cell-based methodologies. Cotransfection assays examining the activity of Nurr1 on an NBRE reporter illustrate that RXRalpha is a repressor of Nurr1 transcriptional activity and that this is mediated by the RXR LBD. Using this experimental model as well as RXR coactivator interaction assays (biochemical) and RXR/DR1 reporter cotransfection assays, the authors examined multiple classes of RXR ligands (RXR agonists, modulators, antagonists, and Nurr1/RXRa selective agonists) to compare their activities. The Nurr1/RXR heterodimer agonists were quite effective at inducing transcription in the Nurr1/RXR assay but relatively ineffective in the RXR - coactivator binding assay or the RXR cotransfection assay. Using the array of ligands, the authors show that the Nurr1/RXR activity does not correlate to the ability of compounds to induce RXR to recruit a coactivator or activate RXR-mediated transcription. This suggests that Nurr1/RXR heterodimer agonists may not be mediating transcriptional activation via the "standard" mechanism. One weakness here is that some compounds used in the Nurr1/RXR transcription assay are not included in the other assays and may not have been included in the correlation studies. Assessment of RXR/Nurr1 dimerization in the presence of the ligands was assessed by ITC and demonstrated a correlation between the weakening of heterodimer formation and Nurr1/transcriptional activity suggesting that modulation of dimerization may be a mechanism by which the Nurr1/RXR heterodimer specific ligands function. NMR and analytical SEC data support this hypothesis as well. With regard to the physiological significance of these observations, no studies were completed on actual Nurr1 target genes addressing this type of mechanism offering limitations on the applicability of the hypothesis. However, the mechanism proposed is strongly supported by the data and offers a novel paradigm for the development of drugs targeting this receptor and possibly other nuclear receptors as well.

Reviewer #1 (Public Review):

In this manuscript, the authors describe a novel HA20-causing missense mutation, p.(Leu236Pro), in three patients from one family with periodic fevers, GI symptoms, urogenital ulcers, arthritis, and pustular rash. The patients had elevated levels of multiple proinflammatory cytokines, including IL-1b, IL-6, and TNFa. Patients had reduced A20 expression levels, and in silico analysis suggested that the p.Leu236Pro mutation destabilized the A20 protein. Using transfection assays, the authors determined that steady state protein expression of mutant A20 protein was lower, and that the half-life of the mutant protein was shorter. Treatment with MG132 increased the half life of mutant A20, suggesting that the mutant protein underwent degradation through the proteasome. Further experiments in the transfection system revealed that mutant A20 failed to suppress TNFα-induced NF-κB activity.

This paper will be of great interest to the field. HA20 is a novel disease (first described in 2016), and although the effects of frameshift/truncating mutations are quite evident, there is quite a lot of debate about the potential effects of missense mutations. It is not really clear which missense mutations cause disease and why, and clinicians who treat this disease are frequently faced with the dilemma of evaluating a patient with a rare missense variant of unknown significance. Thus, a paper that can explain the potential mechanisms by which missense mutations cause disease is highly relevant -- and this is an area of active investigation by several groups.

The strengths of this study include the thorough functional assessment of this novel mutation: the authors have collected quite a lot of data to show the effects of their mutation on protein stability and function. Another strength is the comparison with other similar mutations in the OTU and other domains. However, the data are not currently sufficient to support the conclusions of the authors about the effects of their mutation on protein folding. Similarly, the data do not sufficiently support the generalizability of this mechanism to other mutations in the OTU domain.

Reviewer #2 (Public Review):

The authors identified a novel TNFAIP3 variation Leu236Pro located in the A20 OUT domain and demonstrated its pathogenicity. Proinflammatory cytokines were substantially elevated in the patients. In vitro study showed decreased stability of the Leu236Pro A20 protein and Leu236Pro mutant failed to suppress TNF induced NF-κB activity. Review of previously reported TNFAIP3 missense variations revealed that only 3/7 are pathogenic. Truncating A20 mutations are easy to determine the pathogenicity, while missense TNFAIP3 variants require more functional studies to determine the pathogenicity. The results of this study can help interpretation of TNFAIP3 missense variations.

Reviewer #3 (Public Review):

The authors described the one family showing autoinflammatory phenotypes with L236P variant of TNFAIP3 gene. The variant has not been reported on and they evaluated the function of this variant using in vitro and in silico methods. I think this is well-written manuscript and I agree with their interpretation about the pathogenicity of this variant, but the new finding is poor. The variant information was only a new finding.

I recommend the revision of the following points.

In Table 2, T647P seemed to be pathogenic which was evaluated with in vitro assay by Kadowaki.

Two other missense variants, V377I (Niwano, Rheumatology 2022) and T602S (Jiang W, Cellular Immunol 2022) were recently reported. These should be included in the discussion.

Reviewer #1 (Public Review):

Yamanaka et al.'s research investigates into the impact of volatile organic compounds (VOCs), particularly diacetyl, on gene expression changes. By inhibiting histone acetylase (HDACs) enzymes, the authors were able to observe changes in the transcriptome of various models, including cell lines, flies, and mice. The study reveals that HDAC inhibitors not only reduce cancer cell proliferation but also provide relief from neurodegeneration in fly Huntington's disease models. Although the findings are intriguing, the research falls short in providing a thorough analysis of the underlying mechanisms.

HDAC inhibitors have been previously shown to induce gene expression changes as well as control cell division and demonstrated to work on disease models. The authors demonstrate diacetyl as a prominent HDAC inhibitor. Though the demonstration of diacetyl is novel, several similar molecules have been used before.

Reviewer #2 (Public Review):

Sachiko et al. study presents strong evidence that implicates environmental volatile odorants, particularly diacetyl, in an alternate role as an inhibitors HDAC proteins and gene expression. HDACs are histone deacetylases that generally have repressive role in gene expression. In this paper the authors test the hypothesis that diacetyl, which is a compound emitted by rotting food sources, can diffuse through blood-brain-barrier and cell membranes to directly modulate HDAC activity to alter gene expression in a neural activity independent manner. This work is significant because the authors also link modulation of HDAC activity by diacetyl exposure to transcriptional and cellular responses to present it as a potential therapeutic agent for neurological diseases, such as inhibition of neuroblastoma and neurodegeneration.

The authors first demonstrate that exposure to diacetyl, and some other odorants, inhibits deacetylation activity of specific HDAC proteins using in vitro assays, and increases acetylation of specific histones in cultured cells. Consistent with a role for diacetyl in HDAC inhibition, the authors find dose dependent alterations in gene expression in different fly and mice tissues in response to diacetyl exposure. In flies they first identify a decrease in the expression of chemosensory receptors in olfactory neurons after exposure to diacetyl. Subsequently, they also observe large gene expression changes in the lungs, brain, and airways in mice. In flies, some of the gene expression changes in response to diacetyl are partially reversable and show an overlap with genes that alter expression in response to treatment with other HDAC inhibitors. Given the use of HDAC inhibitors as chemotherapy agents and treatment methods for cancers and neurodegenerative diseases, the authors hypothesize that diacetyl as an HDAC inhibitor can also serve similar functions. Indeed, they find that exposure of mice to diacetyl leads to a decrease in the brain expression of many genes normally upregulated in neuroblastomas, and selectively inhibited proliferation of cell lines which are driven from neuroblastomas. To test the potential for diacetyl in treatment of neurodegenerative diseases, the authors use the fly Huntington's disease model, utilizing the overexpression of Huntingtin protein with expanded poly-Q repeats in the photoreceptor rhabdomeres which leads to their degeneration. Exposing these flies to diacetyl significantly decreases the loss of rhabdomeres, suggesting a potential for diacetyl as a therapeutic agent for neurodegeneration.

The findings are very intriguing and highlight environmental chemicals as potent agents which can alter gene expression independent of their action through chemosensory receptors.

Reviewer #1 (Public Review):

Asthma is a syndromic disease with multiple subtypes with different pathogenetic paths to a final wheezing phenotype. This limits the insights gleaned from genetic investigations of asthma. One of the most important phenotypes is early life onset wheezing, which persists. Here, the authors use data from multiple birth cohorts and by coupling latent class analysis of clinical phenotypic data with GWAS discovery, identify a novel locus close to annexin 1 (ANXA1) associated exclusively with early-onset persistent wheeze. The methodology is a major strength of the work and highlights the importance of acquiring and analysing phenotypic over simple use of doctor labels for complex diseases.

The authors went on to demonstrate a putative mechanism such that the risk allele (T) may confer a reduction in ANXA1 expression. Altered ANXA1 expression was additionally recapitulated in a murine model of house dust mite (HDM)-induced allergic airway disease. In this model, ANXA1 increased, rather than decreased, which may be attributable to its role in resolving inflammation. ANXA1-deficient mice had a more severe phenotype. This strengthens the evidence for causality in the novel link between ANXA1 and asthma and opens the door for further investigations. While novel for this link, the finding is well supported by prior knowledge about ANXA1-related pathways and inflammation. ANXA1 is known to participate in phospholipase A2-dependent reduction of inflammatory mediator production. Glucocorticoids increase ANXA1 levels. ANXA1 deficiency leads to airway hyperreactivity in mice. Overall, ANXA1 appears to be suitable as a therapeutic target and this may spur further investigations into the pathway.

Reviewer #2 (Public Review):

Granell et al. investigated genetic factors underlying wheezing from birth to young adulthood using a robust data-driven approach with the aim of understanding the genetic architecture of different wheezing phenotypes. The association of 8.1 million single nucleotide polymorphisms (SNPs) with wheeze phenotypes derived from birth to 18 years of age was evaluated in 9,568 subjects from five independent cohorts from the United Kingdom. This meta-genome-wide association study (GWAS) revealed the suggestive association of 134 independent SNPs with at least one wheezing subtype. Among these, 85 genetic variants were found to be potentially causative. Indeed, some of these were located nearby well-known asthma loci (e.g., the 17q21 chromosome band), although ANXA1 was revealed for the first time to play an important role in early-onset persistent wheezing. This was strongly supported by functional evidence. One of the top ANXA1 SNPs associated with wheezing was found to be potentially involved in the regulation of the transcription of this gene due to its location at the promoter region. This polymorphism (rs75260654) had been previously evidenced to regulate the ANXA1 expression in immune cells, as well as in pulmonary cells through its association as an eQTL. Protein-protein network analyses revealed the interaction of ANXA1 with proteins involved in asthma pathophysiology and regulation of the inflammatory response. Additionally, the authors conducted a murine model, finding increased anxa1 levels after a challenge with house dust mite allergens. Mice deficient in anxa1 showed decreased lung function, increased eosinophilia, and Th2 cell levels after allergen stimulation. These results suggest the dysregulation of the immune response in the lungs, eosinophilia, and Th2-driven exacerbations in response to allergens as a result of decreased levels of anxa1. This coincides with evidence of lower plasmatic ANXA1 levels in patients with uncontrolled asthma, suggesting this locus is a very promising candidate as a target of novel therapeutic strategies.

Limitations of this piece of work that need to be acknowledged: (1) the manual and visual inspection of Locus Zoom plots for the refinement of association signals and identification of functional elements does not seem to be objective enough; (2) the sample size is limited, although the statistical power was improved by the assessment of very accurate disease sub-phenotype; (3) association signals with moderate significance levels but with strong functional evidence were found; (4) no direct replication of the findings in independent populations including diverse ancestry groups was described. Nonetheless, the robustness and consistency of the findings supported by different analytical and experimental layers is the major strength of this study.

The authors successfully achieved the aims of the study, strongly supported by the results presented. This study not only provides an exciting novel locus for wheezing with potential implications in the development of alternative therapeutic strategies but also opens the path for better-powered research of asthma genetics, focused on accurate disease phenotypes derived by innovative data-driven approaches that might speed up the process to disentangle the missing heritability of asthma, making use of still useful GWAS approaches.

Reviewer #3 (Public Review):

Genome-wide association studies on asthma have been challenging, due to the accuracy of phenotyping and potential gene-environment interactions. Thus, the authors aimed to identify genetic loci associated with subtypes of childhood wheezing. One main strength of this investigation is that the data availability of wheeze from birth to adolescence among multiple birth cohorts allowed the sub-phenotyping on a large scale and high statistical power. The study is properly designed and the conclusions are well-supported. Understanding the heterogeneity in subtypes of childhood wheezing is of great clinical interest and may help inform future directions in disease prediction and prevention.

Reviewer #1 (Public Review):

In their study, Osorio-Valeriano and colleagues seek to understand how bacterial-specific polymerizing proteins called bactofilins contribute to morphogenesis. They do this primarily in the stalked budding bacterium Hyphomonas neptunium, with supporting work in a spiral-shaped bacterium, Rhodospirillum rubrum. Overall the study incorporates bacterial genetics and physiology, imaging, and biochemistry to explore the function of bactofilins and cell wall hydrolases that are frequently encoded together within an operon. They demonstrate an important, but not essential, function for BacA in morphogenesis of H. neptunium. Using biochemistry and imaging, they show that BacA can polymerize and that its localization in cells is dynamic and cell-cycle regulated. The authors then focus on lmdC, which encodes a putative M23 endopeptidase upstream of bacA in H. neptunium, and find that is essential for viability. The purified LmdC C-terminal domain could cleave E. coli peptidoglycan in vitro suggesting that it is a DD-endopeptidase. LmdC interacts directly with BacA in vitro and co-localizes with BacA in cells. To expand their observations, the authors then explore a related endopeptidase/bactofilin pair in R. rubrum; those observations support a function for LmdC and BacA in R. rubrum morphogenesis as well.

An overall strength of this study is the breadth and completeness of approaches used to assess bactofilin and endopeptidase function in cells and in vitro. The authors establish a clear function for BacA in morphogenesis in two bacterial systems, and demonstrate a physical relationship between BacA and the cell wall hydrolase LmdC that may be broadly conserved. The eventual model the authors favor for BacA regulation of morphogenesis in H. neptunium is that it serves as a diffusion barrier and limits movement of morphogenetic machinery like the elongasome into the elongating stalk and/or bud. However, there is no data presented here to address that model and the role of LmdC in H. neptunium morphogenesis remains unclear.

The data presented illuminate aspects of bacterial morphogenesis and the physical and functional relationship between polymerizing proteins and cell wall enzymes in bacteria, a recurring theme in bacterial cell biology with a variety of underlying mechanisms. Bactofilins in particular are relatively recently discovered and any new insights into their functions and mechanisms of action are valuable. The findings presented here are likely to interest those studying bacterial morphogenesis, peptidoglycan, and cytoskeletal function.

Reviewer #2 (Public Review):

This is an excellent study. It starts with the identification of two bactofilins in H. neptunium, a demonstration of their important role for the determination of cell shape and discovery of an associated endopeptidase to provide a convincing model for how these two classes of proteins interact to control cell shape. This model is backed up by a quantitative characterisation of their properties using high-resolution imaging and image analysis methods.

Overall, all evidence is very convincing and I do not have many recommendations on how to improve the manuscript.

In my opinion, there are only two issues that I have with the paper:

1. The single particle dynamics of BacA is presented as analysed and I would like to give some suggestions how to maybe extract even more information from the already acquired data:

1.1. Presentation: Figure 5A is only showing projections of single particle time-lapse movies. To convince the reader that it was indeed possible to detect single molecules it would be helpful if the authors present individual snapshots and intensity traces. In case of single molecules these will show step wise bleaching.

1.2. Analysis: Figure 5B and Supplement Figure 1 are showing the single particle tracking results, revealing that there are two populations of BacA-YFP in the cell. However, this data does not show if individual BacA particles transition between these two populations or not. A more detailed analysis of the existing data, where one can try to identify confinement events in single particle trajectories could be very revealing and help to understand the behaviour of BacA in more detail.

2. The title of Fig. 3 says that BacA and BacD copolymerise, however, the data presented to confirm this conclusion is actually rather weak. First, the Alphafold prediction does not show the co-polymer, and second, the in vitro polymerisation experiments were only done with BacA in the absence of BacD. Accordingly, the only evidence that supports this is their colocalization in fluorescence microscopy. I suggest either weakening the statement or changing the title adds more evidence.

Finally, did the authors think about biochemical experiments to study the interaction between the cytoplasmic part of LmdC and the bactofilins? These could further support their model.

Reviewer #1 (Public Review):

The manuscript provides analyses on a very complete dataset on weight and length growth, as well as several physiological markers related to growth, in bonobos. Moreover, there is a good overview of the presence of adolescent growth spurts in non-human primates, by reviewing published data, in comparison to their own dataset. They discuss the need to consider scaling laws when interpreting and comparing growth curves of different species and variables.

The manuscript is very well written, the sample is large, and the methods are well explained. It seems they have analyzed a very complete dataset. Also, the discussion and the references supporting the findings are complete.

The main weakness of this manuscript is that they do not provide a direct comparison with previous analyzed datasets in other species, using their own method (in part maybe because there is not available data, but just published figures).

On the other side, conclusions are well supported by the results, and the previous published datasets are discussed in the manuscript, although not in detail.

Reviewer #2 (Public Review):

This work sheds new light on the growth trajectory of Bonobo and contributes heavily to the discussion of the exclusivity of certain aspects of growth in modern humans. These results are also interesting as long as they are based on the study of the largest sample ever considered in the study of the growth of this species by including morphometric measurements as well as endocrinological factors.

The authors approach the study of the presence of growth spurs (GS) in Bonobo on the basis that GS are exclusive to the growth in modern humans. This idea is fairly widespread, however studies on non-human primates have shown an acceleration of growth during adolescence in several species, these works are recalled, presented and discussed by the authors. The originality of this work lies in highlighting the importance of scaling in studies of growth trajectories. The absence of GS in Bonobo but also in other primate species may result from not considering the conjunction of weight and height in the analysis of growth, because the pronounced changes in the speed of the height are in relation to the speed of changes in weight and this is modified according to the size/age. The authors apply scaling corrections to their results and the GS become evident (or more obvious) in Bonobo. Thus, the exclusivity of GS in growth in modern humans may in fact result only by the application of analytical approach not very appropriate in non-human primates.

Reviewer #1 (Public Review):

For many years it has been understood that transposable elements (TEs) are an important source of natural variation. This is because, in addition to simple knockouts of genes, TEs carry regulatory sequences that can, and sometimes do, affect the expression of genes near the TEs. However, because TEs can be difficult to map to reference genomes, they have generally not been used for trait mapping. Instead, single nucleotide polymorphisms are widely used because they are easy to detect when using short reads. However, improvements in sequencing technology, as well as an increased appreciation of the importance of TEs to both linked to favorable alleles and are more likely to be causing the changes that make those alleles beneficial in a given environment. Further, because TE activity can occur after bottlenecks, they can provide polymorphisms in the absence of variation in point mutations.

In this manuscript, the authors carefully examine insertion polymorphisms in rice and demonstrate linkage to differences in expression. To do this, they used expression quantitative trait locus (eQTL) GWAS using TIPs as genetic markers to examine variation in 208 rice accessions. Because they chose to focus on genes that were expressed in at least 10% of the accessions, presumably because more rare variants would end up lacking statistical power. This is an understandable decision, but it says that recent insertions, such as the MITE elements detailed in a previous paper, would not be included. Importantly, although TIPs associated with differentially expressed genes are far less common than SNPs' traditional eQTLs, there were a significant number of eQTLs that showed linkage to TIPs but not to QTL.

The authors then show that of the eQTLs associated with both TIPs and SNPs, TIPs are more tightly linked to the eQTL, and are more likely to be associated with a reduction in expression, with variation in the effects of various TEs families supporting that hypothesis. Here and throughout, however, the distance of the TEs could be an important variable. It is also worth noting the relative numbers in order to assess the claim in the title of the paper. The total number of eQTL-TIPs is ten-fold less than the number of eQTL-SNPs, and, of the eQTLs that have both, there are a significant number of eQTL-TIPs that are not more tightly linked to the expression differences than the eQTL.

The authors show that eQTL-TIPs are more likely to be in the promoter-proximal region, but this may be due to insertion bias, which is well documented in DNA-type elements. Here and throughout the authors are careful to state that the data is consistent with the hypothesis that TEs are the cause of the change, but do not claim that the data demonstrate that they are.

Throughout the rest of the manuscript, the authors systematically build the case for a causal role for TEs by showing, for instance, that eQTL-TIPs show much stronger evidence for selection, with increased expression being more likely to be selected than decreased expression. The authors provide examples of genes most likely to have been affected by TE insertions.

Overall, the authors build a convincing case for TEs being an important source of regulatory information. I don't have any issues with the analysis, but I am concerned about the sweeping claims made in the title. Once you get rid of eQTLs that could be altered by either SNPs or TIPs and include only those insertions that show strong evidence of selection, the number of genes is reduced to only 30. And even in those cases, the observed linkage is just that, not definitive evidence for the involvement of TEs. Although clearly beyond the scope of this analysis, transgenic constructs with the TEs present or removed, or even segregating families, would have been far more convincing.

The fact that many of the eQTL-TIPs were relatively old is interesting because it suggests that selection in domesticated rice was on pre-existing variation rather than new insertions. This may strengthen the argument because those older insertions are less likely to be purged due to negative effects on gene expression. Given that the sequence of these TEs is likely to have diverged from others in the same family, it would have been interesting to see if selection in favor of a regulatory function had caused these particular insertions to move away from more typical examples of the family.

Reviewer #2 (Public Review):

In this manuscript, Castanera et al. investigated how transposable elements (TEs) altered gene expression in rice and how these changes were selected during the domestication of rice. Using GWAS, the authors found many TE polymorphisms in the proximity of genes to be correlated to distinct gene expression patterns between O. sativa ssp. japonica and O. sativa ssp. indica and between two different growing conditions (wet and drought). Thereby, the authors found some evidence of positive selection on some TE polymorphisms that could have contributed to the evolution of the different rice subspecies. These findings are underlined by some examples, which illustrate how changes in the expression of some specific genes could have been advantageous under different conditions. In this work, the authors manage to show that TEs should not be ignored when investigating the domestication of rise as they could have played an important role in contributing to the genetic diversity that was selected. However, this study stops short of identifying causations as the used method, GWAS, can only identify promising correlations. Nevertheless, this study contributes interesting insights into the role TEs played during the evolution of rice and will be of interest to a broader audience interested in the role TEs played during the evolution of plants in general.

Reviewer #1 (Public Review):

With this work, the authors address a central question regarding the potential consequences of post-translational modifications for the pathogenesis of neurodegenerative diseases. Phosphorylation and mislocalization of the RNA binding protein TDP43 are characteristic of ~50% of frontotemporal lobar degeneration (FTLD), as well as >95% of amyotrophic lateral sclerosis (ALS). To determine if acetylation is a primary, disease-driving event, they generated a TDP-43 mutant harboring an acetylation-mimicking mutation (K145Q). Animals carrying the acetylation-mimic mutation (K145Q) displayed key pathological features of disease, including more cytoplasmic TDP43 and impaired TDP43 splicing activity, together with behavioral phenotypes reminiscent of FTLD.

This is a well-written and well-illustrated manuscript, with clear and convincing findings. The observations are significant and emphasize the importance of post-translational modifications to TDP-43 function and disease phenotypes. In addition, the TDP43(K145Q) mice may prove to be a valuable model for studying TDP-43-related mechanisms of neurodegeneration and therapeutic strategies.

However, as it stands it is challenging to determine if any or all of the phenotypes are a direct consequence of interrupted RNA binding by TDP-43, rather than acetylation per se. Furthermore, all the results are obtained using an acetylation-mimic mutation that may simply be disrupting a key residue involved in RNA binding by TDP43, instead of mirroring acetylation itself, which in theory is a reversible modification. Lastly, it remains unknown why TDP43(K145Q) mice developed features of FTLD, but not ALS, despite the fact that TDP-43 acetylation was found in ALS tissue and not FTLD.

Reviewer #2 (Public Review):

This paper extends prior work demonstrating the importance of K145 acetylation of TDP-43 as a post-translational modification that impacts its RNA-binding capacity and may contribute to pathology in FTLD-ALS. The main strengths of this paper are the generation of a novel mouse model, using CRISPR gene editing, in which an acetylation-mimetic mutation (K to Q) is introduced at position 145. Behavioral, biochemical, and genetic analyses indicate that these mice display phenotypes relevant to TDP-43-associated disease and will be a valuable contribution to the field. While most of the data are rigorous and clearly presented, several weaknesses should be addressed to strengthen the manuscript and further characterize the phenotype of mutant mice.

Reviewer #3 (Public Review):

Numerous experimental models are phenotyped in this manuscript including mouse neurons, iPSC-derived human neurons, knock-in mice, and knock-in iPSCs. Expression of acetylation-mimic or acetylation-null TDP-43 protein is achieved either with overexpression or CRISPR-Cas9-based knock-in. A complex phenotype is observed including loss of TDP-43 function (reduced autoregulation, increased cryptic splicing) and a gain of TDP-43 (increased insoluble TDP-43 protein). These correlate with downstream neurobehavioral changes which are most consistent with a cortical/hippocampal phenotype without a motor phenotype. Post-translational modifications of disease-associated proteins are thought to contribute to neurodegenerative disease pathogenesis, and this study succeeds in demonstrating that TDP-43 acetylation results in downstream molecular and behavioral phenotypes.

There are numerous additional strengths. TDP-43 acetylation is a post-translational modification that is known to be associated with TDP-43 inclusions that are characteristic of human diseases. An important strength is the rigorous use of multiple different experimental models (rodent cells, iPSC-derived neurons, mice, overexpression, knock-in) with overall consistent results. Moreover, multiple orthogonal endpoints are presented including histology/cytology/immunostaining, biochemistry, molecular biology, and neurobehavioral assays. As TDP-43 acetylation is known to block RNA binding, these novel cellular and mouse models represent interesting albeit complex tools to study the functional consequences of a partial loss of function. As TDP-43 regulates its own expression (i.e. autoregulation), the complexity lies at least in part due to the loss of RNA binding leading to a functional loss of TDP-43 function which includes the increased expression of the TARDBP transcript and TDP-43 protein.

Conceptually, there is a disconnect in that the mouse model exhibits primarily a cortical/hippocampal phenotype more akin to frontotemporal lobar degeneration with TDP-43 inclusions (FTLD-TDP), while TDP-43 acetylation is only seen in ALS tissues and not in FTLD-TDP tissues because most of the pathologic protein in the latter is N-terminally truncated (i.e. the acetylation site is not present). That being said, there is no mouse model which completely and faithfully recapitulates the human disease, and this mouse model avoids overt overexpression (increased TDP-43 protein expression stemming from altered autoregulation) and avoids the use of synthetic/artificial mutation (such as mutation of the TDP-43 nuclear localization signal).

In terms of the CNS phenotype, it is difficult to interpret the reduced density of NeuN-positive neurons in the mouse model as a neurodegenerative phenotype. The reduction in NeuN density but not overall cellular density is only suggestive of neurodegeneration (as opposed to, for example, a developmental phenotype) without more rigorous stereological approaches that take into account potential volumetric changes. Indeed, the absence of astrocytosis and microgliosis argues against neurodegeneration.

Some of the loss of function measures (CFTR construct splicing, shift in SORT1 protein) are subtle, although RNA sequencing clearly shows many splicing aberrations including cryptic splicing events which overall supports that a loss of TDP-43 function is observed.

Finally, there are multiple instances where multiple measurements are made on a few biological replicates. ANOVA or t-tests are not appropriate in these instances (lack of independence).

Reviewer #3 (Public Review):

The current manuscript describes the expression of multiple Natriuretic peptides and their receptor during the early embryo development in the amphibian Xenopus laevis. This signaling pathway is well known to control a broad range of physiological processes but its role in embryogenesis has not been studied before. Thus, the study presents some important novel findings. After defining the combination of ligands and receptors expressed during embryogenesis, they used loss of function experiment to test the requirement of this signaling pathway to the development of neural crest cells.

The loss of function experiments are well controlled as they use both chemical inhibitors and Morpholino that block the translation of the protein. They also rescue the phenotypes by using either mRNA from the human protein (receptor), or purified peptides (Ligands).

The results clearly show that loss of either Npr1 or Npr3 affects the development of both neural crest and placodes, while Npr2 had no visible effect. Similarly, they found that the loss of the ligands Nppa and Nppc affected neural crest and placode development while Nppb had no effect. Again, the loss of function was achieved with both Morpholino KD and inhibitors. In general, the loss of neural crest and placodal marker are associated with an expansion of neural marker (Sox2) and a corresponding decrease of epidermal marker (Keratin).

For Npr3 the author show that the loss of the protein is associated with an increase in cell death and decrease in cell proliferation which match some previous work on the role of the receptor in other cell type. It is unclear how much this can account for the striking difference in patterning observed and experiment to test this have not been performed.<br /> Overall, this work is important for the field as it shows novel genes that are critical for craniofacial and sensory development. It is likely that mutations in any genes involved in this pathway could result in birth defect which could be corrected pharmacologically.

Reviewer #1 (Public Review):

This manuscript reports the unique finding that specific ligands and receptors in the natriuretic peptide signaling pathway act during early embryogenesis to discriminate between neural crest (NC) and cranial placode (CP) fates. This is a significant finding for two reasons: 1) the developmental role of this pathway has not been studied in any detail; and 2) how cells located in the border between the neural ectoderm and non-neural ectoderm decide on NC versus CP fates is of broad interest and being actively pursued by a number of laboratories. The authors present logical and experimentally convincing support for their conclusions. They report the expression patterns by in situ hybridization and qPCR of the various ligands and receptors of the natriuretic peptide signaling pathway, clearly demonstrating that several of these molecules are expressed in the right place at the right time to influence NC and/or CP formation. They establish that Npr3 is a target of Pax3 and Zic1, two transcription factors previously shown to be required for NC and CP formation, further illustrating that it is part of the appropriate regulatory network. Next, the authors use morpholino knock down of Npr3 to show that the resulting embryos have deficient expression of two NC genes and two CP genes. The controls used for the knock-down are the correct ones and were confirmed by treatment with a high-affinity and selective Npr3 antagonist. The function of Npr3 was further explored by discriminating between its known two functions - clearance of natriuretic peptides and inhibition of adenylyl cyclase - by expressing either WT or mutant versions of human NPR3 in Npr3 morphant embryos. That WT rescued both NC and CP genes but the mutant version only rescued NC genes leads to the appropriate conclusion that Npr3 regulates NC and CP fates via different mechanisms. This conclusion was confirmed by treating Npr3 morphants with a specific adenylyl cyclase inhibitor, which restored CP gene expression, and treating CP promoting explants with an adenylyl cyclase activator, which repressed CP gene expression. Using similar knock-down approaches the authors convincingly demonstrate that Npr2 does not participate in NC/CP formation, but Npr1 does; again, the knock-down results were confirmed by treating embryos with a specific Npr1 antagonist. Finally, the authors complete the story by determining by equally well-controlled knock-down experiments which of the three natriuretic peptides participate in this process. In short, the many different experiments strongly support the conclusions, and the experiments are well controlled and include large numbers of embryos to provide exceptional rigor.

Reviewer #2 (Public Review):

This study reports a novel role of the natriuretic receptors Npr3 and Npr1 in the formation of neural crest (NC) and cranial placode (CP) progenitor populations in frog embryos. The authors discovered this receptor family in a screen for genes activated during NC development. They show the relevant expression of these receptors and the corresponding ligands in the NC and CP populations. Knockdown and rescue experiments combined with pharmacological drug treatment demonstrated that Npr3 clearance activity is required for NC progenitor formation. Surprisingly, adenylyl cyclase inhibition was required for cGMP production and the effect on CP development. The authors conclude that the two second messengers downstream participate in the segregation of the NC and CP progenitors in embryonic development.

The significance of this study is in the demonstration of two distinct developmental programs that are separately controlled by different activities of the same receptor. The study is well designed and executed with proper controls. Nevertheless, the data suggesting that Npr3 regulates NC and CP fates via different mechanisms are limited and need further support, such as the analysis of additional markers for CP progenitors, to be unambiguously interpreted. The work is likely to impact two different areas: early embryonic development and natriuretic peptide signaling.

Reviewer #1 (Public Review):

Rapan et al. analyzed the cytoarchitectonic of the prefrontal cortex based on observer-independent analysis, confirming previous parcellations based on cyto-, myelo-, and immunoarchitectonic approaches, but also defining novel subdivisions of areas 10, 9, 8B, and 46 and identified the receptor density "fingerprint" of each area and subdivision. Furthermore, they analyzed the functional connectivity of the prefrontal cortex with caudal frontal, cingulate, parietal, and occipital areas to identify specific features for the various prefrontal subdivisions. Altogether, this study corroborates previous parcellations of the prefrontal cortex, adds new cortical subdivisions, and provides a neurochemical description of the prefrontal areas useful for comparative considerations and for guiding functional and clinical studies.

Strengths:<br /> - This study provides a detailed cytoarchitectonic map of the prefrontal cortex enriched with receptor density and functional connectivity data.<br /> - The authors shared the data via repositories and applied their map to a macaque MRI atlas to further facilitate data sharing.

Weaknesses:<br /> - The temporal cortex should be included in the functional connectivity analysis as it is known from anatomical studies that most prefrontal areas display rich connectivity with temporal areas. The aim of creating a comprehensive view of the frontal cortex makes the manuscript data-rich but cursory in discussing the relevant anatomical and functional literature.

Reviewer #2 (Public Review):

Rapan and colleagues did perform an impressive multi-modal parcellation of the macaque frontal cortex. In addition to qualitative cytoarchitectonic and resting-state functional fMRI data analyses, the authors based their parcellation on quantitative receptor density analysis of 14 receptors. Compared with the classic Walker map of the macaque frontal cortex, the authors produced a more refined map. Those results should be discussed in light of previous work on the same topic (Petrides et al. 2012 Cortex; Reveley et al. 2017 Cerebral Cortex; Saleem and Logothetis 2012).

Reviewer #3 (Public Review):

The function of a brain area is defined by its interaction with other regions. Accordingly, two areas communicate via axons and dendrites, but the language is plurimodal along the neurotransmitter-receptor dimension. Consequently, reading its neurochemical constituents is the most advanced way to characterize the brain into functional territories.

Along this theoretical line of research, Rapan et al. produced an exceptional report on the structure of the macaque frontal lobes based on cytoarchitectural division complemented with functional connectivity and neurochemical data. Results are lavishly illustrated. They report 35 cytoarchitectural areas in the prefrontal lobe with precise, different connectivity and neurotransmitter profiles together with practical anatomical landmarks. All data is openly available to the community and will constitute a cornerstone for future neuroscientific research in the macaque frontal lobes.

I congratulate the authors for this already extraordinary work.

Reviewer #1 (Public Review):

The authors have approached the study of the mechanism of maturation of retroviruses lattice, where Gag polyprotein is the main component. The Gag polyprotein is common to all retroviruses and makes up most of the observed lattice underlying the virion membrane. Within the lattice, 95% of the monomers are Gag, and 5% are Gag-Pol, which has the 6 domains of Gag followed by protease, reverse transcriptase and integrase domains (coming from Pol) embedded within the same polyprotein. For the maturation and infectivity of HIV retrovirus, the Gag proteins within the immature lattice must be cleaved by the protease formed from a dimer of Gag-Pol. Importantly, the lattice covers only 1/3 to 2/3 of the available space on the membrane. The incompleteness of the lattice results in a periphery of Gag monomers with unfulfilled intermolecular contacts. Recently, the structure of the immature lattice has been partially resolved using sub-tomogram averaging cryotomography (cryET) and it has been shown that the incompleteness of the lattice provides more accessible targets for the protease (Tan A. et al. 2021). Based on these, the authors have wondered: does the incompleteness of the lattice allow for dynamic rearrangements that ensure that protease domains embedded within the lattice can find one another to dimerize and activate? To answer this, they started from experimental cryoET data and used reaction-diffusion simulations of assembled Gag lattices with varying energies and kinetic rates to test how lattice structure and stability can support the dimerization of the Gag-Pols. They found that although they represent only 5% of the monomers that assemble into the lattice, the stochastic assembly ensure that at least a pair of them are adjacent within the lattice. They next showed that if the molecules are distant from one another, they would need to detach, diffuse, and reattach stochastically at the site of another Gag-Pol molecule.

I consider the work very interesting, which could contribute to a very important aspect of retroviruses maturation such as their infectivity. However, the observations made by the authors do not necessarily answer their initial question which seemed to be focused on studying the possible role of the incompleteness of the lattice on the protease activation rather than the mechanism of Pol activation itself. Maybe this is only a nuance to be polished in the writing.

The weakness of the work comes from both the fact their entire study has been done by computational methods and the exclusion in their computational approaches of well-known cellular components with a role in retrovirus maturation, which might obey to the fact of keeping their models into the simplest possible since handling atomistic models is already a heavy task. Maybe complementary molecular or structural studies would strengthen their results.

Reviewer #2 (Public Review):

Immature lattice assembly remains an arcane topic, and these simulations provide high resolution data such as assembly kinetics and large-scale lattice rearrangement. Further, the authors extend their model to compare directly with experiments, e.g. SNAP-HALO dimerization, which provides a basis to interpret their conclusions. The manuscript is difficult to read, as it is a technical manuscript that overuses jargon; overall, it seems written for a specialized audience. Additionally, there are several aspects of the model design that remain opaque, such as the implicit lipid method and the suppression of multi-site nucleation. Further, analyses such as time auto-correlation and mean first passage time are not given much context by the authors. Altogether, it is the opinion of this reviewer that several revisions to the manuscript should be incorporated to improve clarity and strengthen the significance of the authors' efforts.

Reviewer #3 (Public Review):

The manuscript concerns the cleavage of the Gag polyprotein lattice from the HIV virion membrane, a key stage in HIV lifecycle, and one that is required for HIV to become infectious. Since cleavage requires homodimerization between the small fraction (5%) of such Gag polyproteins that carry a protease domain, referred to as Gag-Pol, this raises questions regarding how such homodimerization can take place, and whether it can happen on the required timescales, given that Gag-Pol is typically embedded in a lattice that is observed to form one large connected component.

The authors address these questions in silico, using particle-based reaction diffusion simulations. Such simulations are rigid-body and "structure-resolved" meaning that they rigidly incorporate the geometry of the polyproteins, and their various binding interfaces, based on existing structural data. Other aspects of the simulations are also in-line with available data, including copy numbers, lattice curvature, and dissociation rates. This focused approach is a strength of the work and allows the authors to make credible claims that their simulations have relevance to HIV (as does their commitment to comparison with HALO-SNAP-based measurements of dimerization kinetics as well as iPALM experiments that characterize lattice dynamics).

A central part of the model is that it allows for the "possibility of imperfect alignment of molecules in the lattice", presumably due to the incompatibility of regular hexagonal tiling and surfaces with non-zero Gaussian curvature, such as a sphere. This is implemented via the ad-hoc imposition of a free-energy penalty when complete hexamers are formed, implying that hexamers are less stable than six ideal bonds. By varying this strain penalty, the authors can change the stability of the lattice independently of individual binding affinities, allowing its use as an effective fitting parameter when comparing to HALO-SNAP data. In the latter case, agreement between simulation and experiment can only be found at moderate levels of lattice stability.

However, such energetic penalties are present whenever the polyprotein structure must undergo deformations which, on surfaces with nonzero Gaussian curvature, should be the case for partial tilings as well as complete ones (where all six interfaces form bonds). This, therefore, appears to be a weakness of the work. An elastic implementation of polyprotein structure, for example, would permit strain to accumulate (and therefore stresses to propagate) throughout the lattice naturally, irrespective of whether complete hexamers were formed, and might reasonably be expected to impact the likelihood of different lattice structures. Whilst it is not clear how or whether this would lead to qualitatively or quantitatively different results, it is nevertheless worth remarking upon since the authors high-level claim is that lattice structure is an important determinant of the mean-first-passage times to dimerization.

Overall, I find this to be a valuable study, carried out in a solid and comprehensive manner. The primary impact of the work appears to be twofold: the unification of different experimental measurements under a single model, and the further identification of the salient parts of that model that most impact biological function. The results advance the understanding of one of the steps of the HIV lifecycle, via a better description of the mechanisms underpinning Gag-Pol dimerization. Notably, the authors stop short of drawing parallels to many related concepts and models in statistical physics, such as those concerning percolation and diffusion limited aggregation as well as the notions of dislocations and defects in crystalline matter on curved surfaces. These might reasonably have provided a basis for better understanding and quantification of the authors' simulations, as well as improving the scope for extensions and conceptual clarity.

Reviewer #1 (Public Review):

The paper by Mohebi, Collins, and Berke describes the interactions between cholinergic interneurons and dopamine (DA) release in the core of the nucleus accumbens (NAc) in rats. The cholinergic triggering of DA release has been a debated issue in recent years, and this study provides data supporting cholinergic-dependent DA release.

The authors first show that optogenetic activation of cholinergic interneurons (CINs) induces DA release in the NAc, increasing with pulse width, frequency, and train pulse duration. They next show using simultaneous imaging of CIN calcium activity and DA release using RdLight that both are correlated in their response to sensory stimuli and entry to reward port in freely moving rats. They show that while CIN activity and DA release show ramping activity before entry to the center and food ports, such ramping is not seen in the spiking activity of DA cells. lastly, the authors show that blocking nicotinic receptors in the NAc by injection of DHBE impairs task performance, with similar (albeit weaker) effects as the DA antagonist flupenthixol. The uncoupling between DA release and DA cell firing, under certain conditions, has been shown by the authors in a previous paper (Mohebi et al, 2019). Here, the authors add the CINs calcium activity during the same task, showing that the dynamics of CIN activity resemble that of DA release. The results presented show correlations between CIN activity and DA release during behavior, however, the role of CINs in controlling DA release is not tested directly. The data presented in the paper are clear and it is well written. However, there are a few issues that need to be addressed, including some key experiments that could directly test the functional role of CIN-induced DA release.

Reviewer #3 (Public Review):

This report by Mohebi et al. provides new answers to old questions by showing that the activity of striatal cholinergic interneurons (CINs) escalates progressively during specific reward-related behaviors and that this correlates with previously observed ramps in dopamine (DA) release in the nucleus accumbens core. The report is strong and provides evidence for the authors' hypothesis that DA ramps are independent of DA neuron activity, but are instead the result of CIN activity and corresponding acetylcholine (ACh) release. The authors further demonstrate that the fidelity of CIN activation and consequent driving of DA release is even more robust in vivo than observed ex vivo slice preparations, which is fundamental for understanding the role of ACh-DA interactions in behavior. The findings complement the authors' previous evidence ventral tegmental area (VTA) DA neuron firing patterns do not show a ramping pattern; the previously reported VTA data are appropriately included here (in Fig. 3) to illustrate the absence of VTA firing during the time-locked increases in CIN activity and DA release. The present studies stop short of showing a direct link between CIN activity and DA release, however, which would require examining DA release during behavior in the presence of an antagonist of nicotinic ACh receptors. The authors also extend the understanding of the regulation of DA release by acetylcholine (ACh) by showing that optical activation of CINs in vivo promotes DA release responses that do not attenuate with repetitive stimulation. This contrasts with previous results in ex vivo striatal slices in which ACh-evoked DA release has been found to decline progressively from rundown and/or receptor desensitization. The authors propose that in vivo, AChE may be more effective in curtailing local ACh levels than in slices because of the slightly lower temperature typically used for slice studies, as well as the use of superfusion that might facilitate some AChE washout (AChE inhibitors are still effective in slices, of course). Overall, the report not only provides evidence for the cellular substrate for DA ramps but also shows the robustness of ACh-driven DA release in vivo. A few points to strengthen the report are listed below.

1) The authors give a few details about how CINs were activated at the beginning of the results, but say only that DA dynamics were monitored using fiber photometry. Given that the methods are at the end, a brief summary should be given here to indicate whether this means direct monitoring of DA or indirect via GCaMP, for example. It would be helpful to note the sensor used in the abstract, as well. In this light, as it were, RdLight1 should be described upon the first mention.

2) The authors show that infusion of DHbE in the NAc likelihood of decisions to approach the center port, as did antagonism of DA receptors. This supports the authors' argument that ramping of CIN activity and consequent ACh release underlies observed ramps in DA release. However, to show a causal interaction requires testing whether the observed DA ramps are absent after DHbE infusion in the NAc, under the same conditions that attenuated behavior.

3) In Fig. 3, the y-axis title for the upper panels should specify VTA, not simply "rate". This is stated in the legend, but should also be specified in the figure panel.

4) A recent preprint in BioRxiv by AC Krok, NX Tritsch et al. shows a related correlation between ACh and DA release in vivo in a reward task, as well as differences in other conditions. This report shows also that cortical input to CINs indeed plays a role, as suggested in the concluding sections of the present report. Consideration of the data in the preprint in the context of the present results could be valuable for the field.

Reviewer #1 (Public Review):

The authors compared the neural mechanisms of calling song in five Xenopus species. Two (X. laevis and X. petersii) were previously shown to produce fictive calls. This paper developed the techniques to evoke fictive calls for three additional species: X. cliivi, X. amieti, and X. tropicalis. The authors compared fast and low components of the calls and determined that the fast components in all species required bilateral coordination in the parabrachial nucleus (PBN), but the slow components were produced in the nucleus ambiguous (presumably with bilateral control, but that was not tested.

The abstract does not adequately summarize the content of the paper. There is no mention of stimulation, or bilateral connectivity, which is a large part of the paper. The names of all five species should appear in the abstract, not just X. laevis.

The conclusion that the "fast and slow CPGs identified in male X. laevis are conserved across species." is contradicted by the last paragraph, which states, "Fast trill-like CPGs are likely present only in fast clickers..." This inherent contradiction needs to be resolved.

The abstract also over-emphasizes the testosterone results. It states, "the development of fast CPGs [central pattern generators] depends on testosterone in a species-specific manner: testosterone facilitates the development of fast CPGs in a species with a courtship call containing fast clicks, but not in a species with a courtship call made entirely of slow clicks." The use of the word "development" implies embryology. Here, adults were treated and looked at 13 weeks later. There is no data presented about development. The effects of T could be simply to upregulate certain receptors of a circuit that was already present.

The concluding sentence of the abstract is, "The results suggest that species-specific calls of the genus Xenopus have evolved by utilizing conserved fast or slow CPGs that are broadly tuned to generate fast or slow trains of clicks, the development of which appear to be regulated by a strategic expression of testosterone receptors in the brain of each species." However, testosterone treatment was only applied to X. laevis females. The conclusion is based on plasma levels of testosterone in X. tropicalis. The conclusion that there is differential expression of testosterone receptors in the brain of each species is completely speculative and not supported by the data presented here.

Reviewer #2 (Public Review):

This study by Yamaguchi and Peltier provides a detailed investigation of the brainstem CPG functional organization that rules vocal behaviors in several Xenopus species, from an evolutionary perspective. The main conclusion of the paper reveals that vocal CPGs, located in the brainstem, generating fast and slow clicks in Xenopus male courtship calls are conserved across various Xenopus species. But the development of the fast CPG depends on testosterone only in species producing fast-click courtship calls.

Reviewer #1 (Public Review):

By the in vitro DNA damage response (DDR) assay with a defined DNA substrate using Xenopus extracts and in vitro binding assays with purified proteins, the authors nicely showed the role of APE1 (APEX1) in ATRIP recruitment for DDR activation, particularly a non-enzymatic (structural) role of APE1 in the binding to both ssDNAs and ATRIP. The results described in the paper are very convincing to support the authors' claim. However, these studies lack the quantification with proper statistics (and/or mentioning the reproducibility of the results). And, given the important discovery of APE1 in the DDR activation in vitro, it would be nice to demonstrate the role of APE1(APEX1) in ATR activation in vivo using siRNA-mediated knockdown of mammalian cells or yeast cells.

Reviewer #2 (Public Review):

ATM and Rad3-related (ATR) interact with ATRIP and plays a central role in DNA damage response. Previous studies have established the idea that ATR is recruited to RPA-covered ssDNA via ATRIP-RPA interaction. In this paper, the authors propose a new RPA-independent mechanism for ATR recruitment.

Reviewer #3 (Public Review):

In this manuscript, the authors explore the mechanism of ATRIP recruitment to single-stranded DNA (ssDNA), which is important for ATR activation and the subsequent control of DNA repair and cell cycle progression. Using Xenopus egg extracts, in vitro interaction assays, and ssDNA constructs, the authors found that AP endonuclease 1 (APE1) plays a role in the recruitment of ATRIP to ssDNA independently of RPA. Moreover, APE1 domains are characterized for ssDNA, ATRIP, and RPA interaction, determining that the nuclease activities of APE1 are not required for this new mode of ATRIP recruitment. Overall, the work presented makes a compelling case for a novel role for APE1 in ATRIP recruitment that seems crucial for ATR activation (at least in the Xenopus system). The results are likely to have an important impact on our understanding of the determinants for activation of ATR signaling and cellular responses to DNA damage and replication stress. It remains unclear whether the findings will be extended to other organisms and be relevant for different types of DNA lesions. Also, there are several points of concern in the manuscript that require further clarification, especially regarding some of the quantitative analyses presented and the claimed importance of the RPA-independent mode of ATRIP recruitment for ATR activation.

Reviewer #1 (Public Review):

In their study, Aman et al. utilized single cell transcriptome analysis to investigate wild-type and mutant zebrafish skin tissues during the post-embryonic growth period. They identified new epidermal cell types, such as ameloblasts, and shed light on the effects of TH on skin morphogenesis. Additionally, they revealed the important role of the hypodermis in supporting pigment cells and adult stripe formation. Overall, I find their figures to be of high quality, their analyses to be appropriate and compelling, and their major claims to be well-supported by additional experiments. Therefore, this study will be an important contribution to the field of vertebrate skin research. Although I have no major concerns, I would like to offer a few minor comments for the authors to consider.

1) The discovery of ameloblasts in the zebrafish skin is a fascinating finding that could potentially provide a new research model for understanding the development and regeneration of vertebrate teeth. It would be beneficial if the authors could provide further elaboration on this aspect and discuss how the zebrafish scale model could be utilized by researchers to better understand the morphogenesis of vertebrate teeth and/or hair.

2) While the overexpression-rescue experiments (i.e., fgf20a and pdafaa) provide crucial evidence to support the author's conclusions, it is important to note that overexpression driven by the heat-shock promoter is not spatially regulated. Therefore, it should be acknowledged that the rescue effects may not be cell-autonomous, as suggested in the current version.

3) Figure 7D. The authors used the ET37:EGFP lines to visualize hypodermis. Based on the absence of EGFP signal in the deep dermis of bnc2 mutants, the authors concluded that the hypodermis may be missing, suggesting the importance of the hypodermis in pigment cell formation. However, since the EGFP evidence is indirect, it is crucial to confirm the absence of the hypodermis structure with histology.

4) As the dataset is expected to be a valuable asset to the field, please provide Excel tables summarizing the key genes and their corresponding expression levels for each major cluster that has been identified.

Reviewer #2 (Public Review):

The authors used single cell transcriptome analysis of zebrafish skin cells and characterized various types of cells that are involved in scale formation and stripe patterning. The methods employed in this study is highly powerful to provide mechanistic explanation of these fundamental biological issues and will be a good example for many researchers studying other biological issues. Furthermore, the results characterizing differences in gene expression patterns among various types of cells will be informative for other researchers in the field.

For scale formation, it is known that mineralized tissues may significantly differ in rayfins and lobefins since sox9, col2a1, and col10a1 are all expressed in osteoblasts, in addition to chondrocytes, in zebrafish and gar (Eames et al., 2012, BMC Evol. Biol.). Furthermore, in mammals, Col10 is expressed in chondrocytes in mature cartilage that undergoes ossification. Thus, unlike the authors argue, col10a1 expression is not apparently relevant to the elasticity of scales.

The authors also state that the expression of dlx4a, msx2a, and runx2b characterize cells homologous to mammalian ameloblasts. However, dlx4, runx2, and msx2 are all duplicated in zebrafish, and the function of duplicated genes in teleost fishes may differ from that of single ancestral gene. Moreover, none of Dlx4, Msx2, and Runx2 is expressed specifically by ameloblasts in mammals. Indeed, both Msx2 and Runx2 are expressed in osteoblasts, while the expression of Dlx4 in ameloblasts is not reported. These results, together with the expression of an enamel gene, enam, in dermal cells (SFC), do not appear to support the homology of the surface tissue of mammalian teeth and zebrafish scales.

Reviewer #3 (Public Review):

This work describes transcriptome profiling of dissected skin of zebrafish at post-embryonic stages, at a time when adult structures and patterns are forming. The authors have used the state-of-the-art combinatorial indexing RNA-seq approach to generate single cell (nucleus) resolution. The data appears robust and is coherent across the four different genotypes used by the authors.

The authors present the data in a logical and accessible manner, with appropriate reference to the anatomy. They include helpful images of the biology and schematics to illustrate their interpretations.

The datasets are then interrogated to define cell and signalling relationships between skin compartments in six diverse contexts. The hypotheses generated from the datasets are then tested experimentally. Overall, the experiments are appropriate and rigorously performed. They ask very interesting questions of interactions in the skin and identify novel and specific mechanisms. They validate these well.

The authors use their datasets to define lineage relationships in the dermal scales and also in the epidermis. They show that circumferential pre-scale forming cells are precursors of focal scale forming cells while there appeared a more discontinuous relationship between lineages in the epidermis.

The authors present transcriptome evidence for enamel deposition function in epidermal subdomains. This is convincingly confirmed with an ameloblastin in situ. They further demonstrate distinct expression of SCPP and collagen genes in the SFC regions.

The authors then demonstrate that Eda and TH signalling to the basal epidermal cells generates FGF and PDGF ligands to signal to surrounding mesenchyme, regulating SFC differentiation and dermal stratification respectively.

Finally they exploit RNA-seq data performed in parallel in the bnc2 mutants to identify the hypodermal cells as critical regulators of pigment patterning and define the signalling systems used.

Whilst these six interactions in the skin are disparate, the stories are unified by use of the sci-RNA-seq data to define interactions. Overall, it's an assembly of work which identifies novel and interesting cell interactions and cross-talk mechanisms. There are some aspects that require clarification:

With respect to the discontinuous relationship noted in Figure 2I in the epidermis, the authors did not make mention of the fact that there are in fact two independent sources of periderm in the zebrafish. The first periderm derives from the EVL, is segregated a gastrulation, and gradually replaced from the basal epidermis during post-embryonic stages. Could this residual EVL-derived periderm have reduced sensitivity of the trajectory mapping from basal to periderm? The authors should comment whether their transcriptome dataset likely had residual EVL-derived periderm and if this might have impacted their trajectory continuity interpretation.

The authors ask if dermal SFCs express proteins associated with cartilage formation and use Col10a1 orthologues as markers (Fig 3B, I). I wonder if these are the best transcripts to answer this question as this has also been described to label osteoblasts in certain contexts in the fish and the authors might want to refer to Li et al 2009 or Avaron et al 2005. Were other markers of cartilage formation present such as collagen2 genes? These may be more definitive. The authors might want to reinterrogate their datasets for true cartilage markers or reframe their question.

Finally, of interest, were there any clear clusters on the UMAP plots (Fig 1 Supp3A) of unassigned identity? Even comment on these and how they were dealt with would be of significant interest to the field, as it is highly unlikely all cell types in the skin have been defined. This dataset promises to be a critical reference for defining these in the future.

Minor clarification:

Fig 2E top. The authors interpret that fate-mapped SFCs at the posterior margin are progressively displaced towards the scale focus. This is confusing as the margin SFC in Fig 2E seems to show them staying largely at the margin. Please clarify if this is what you meant.

Reviewer #3 (Public Review):

This paper addresses an apparent contradiction related to the interaction between spontaneous neural activity and neural plasticity during circuit development. It is well established that spontaneous activity contains instructive information for developmental downstream circuit refinement, for instance for the formation of retinotopic projections in the visual system. These developmental cues are contained in activity correlations, and thus can be picked up by Hebbian mechanisms. However, previous work has shown that informative correlations in spontaneous activity can be found on slow time scales (100s of milliseconds). Here it is shown that in this case correlations on fast time scales arise simultaneously from the integration of unrefined inputs and that these likely interfere with developmental plasticity. The paper shows that such fast, "parasitic" correlations can appear during retinal wave activity, and provides evidence that NMDA receptors can suppress them to avoid their influence during developmental plasticity.

This work is based on detailed biophysical models of thalamic relay neurons, which were fit to data from in-vitro whole-cell recordings. A genetic algorithm was used to fit these models, which provides a family of suitable models instead of a point estimate of good parameters. This approach is a real strength as it shows that the effects generalise well to many plausible models, and do not depend on specific parameter choices. The model neurons are then placed in simulated networks (without or with anatomically informed recurrent connections) and driven by retinal wave activity recorded from the mouse. Together the simulation and analysis show under which conditions fast, undesirable correlations do and do not appear. Specifically, the key model ingredient this work identifies for the suppression of fast correlations is the presence of NMDA receptors on the recipient synapses of the relay neurons.

An open question is how the parasitic correlations are actually suppressed by NMDA receptors. Is it correct that a stronger NMDAR contribution to the transmitted activity simply low-pass filters the incoming spike trains, and that fast correlations are smoothed out as a result? So are developing circuits tuned to slower activity? This could also explain why AMPA receptors subunits with slower kinetics are expressed during development in many circuits.

Taken together, I think this paper presents a very interesting set of results. The issue with parasitic correlations is quite obvious in retrospect, and clearly, a problem developing circuits will generally face. Additionally, the presence of NMDA receptors is often linked to plasticity and is seen as less important in shaping postsynaptic integration. Although no developmental plasticity has been modelled, would it be possible to predict the possible effects of experimental manipulations?

Reviewer #1 (Public Review):

The authors address an important and understudied problem: how precise temporal properties of synaptic transmission might impact the kinds of neuronal correlations that instruct development. The methods used to characterize and simulate retino-thalamo-cortical development are carefully carried out and yield convincing results. Based on these simulations, the authors argue that features such as slow NMDA receptor-mediated currents are able to prevent aberrant development which might otherwise result from rapid timescale correlations that lack meaningful information about visual topography.

Reviewer #2 (Public Review):

The paper starts with the premise that given the broad immature connectivity between the retina and thalamus during development, locally homogeneous synaptic currents should generate precise spike correlations (on a millisecond timescale) which are not seen in development and could be bad for developmental refinements and "network diversity". Rather, the correlations during development are over much longer timescales. The authors propose that two main factors, the dominance of NMDA (over AMPA) currents and the absence of recurrent connections prevents these precise correlations and preserves diversity.

The paper consists of three parts: (I) develop a biophysical model for a thalamic neuron, (II) use the model to determine which factors govern precise correlations, and then (III) simulate a cortical network and demonstrate loss of network diversity when precise correlations are used. While all parts are interesting, there are several claims in each (and the links between them) that are not fully justified.

What is commending about the paper is that it is one of few theoretical/modeling papers that focuses on neural circuit development and it manages to link experimental results to principles of circuit function. The authors apply quite a few modeling approaches ranging from single-neuron models (including building a database of thalamic neurons based on experimental data) and network models. Some of the claims regarding the timescales of correlations (long in development) are unjustified because the authors use a fixed-timescales kernel to compute these correlations and mainly investigate their amplitude or level, not their timescales. It is also not clear how important is the heterogeneity among thalamic neurons. Are the effects on the correlations the result of NMDA currents or the neuronal diversity from their database? Are precise correlations generated because of the diverse/heterogeneous neurons, or because of the levels of convergence? What happens to homogeneous neurons? The authors also propose that precise correlations impair network diversity but never show this impairment directly beyond a diversity of excitatory-to-excitatory connection strengths. If the authors were to clarify these issues then the paper could be a valuable contribution to the field of developmental systems and computational neuroscience.

Reviewer #1 (Public Review):

T2D in youth has been reported to reduce bone mass due to impaired bone anabolism, but the underlying mechanisms are not fully understood. The authors study the relationship between T2DM (Type 2 Diabetes Mellitus) and "skeletal fragility." Specifically, they look at glucose metabolism defects in osteoblasts during T2DM and their impacts on osteoblast activity. The results are novel as they elucidate the effects of low-dose STZ models of T2DM on osteoblast function and the function of osteoblasts from those mice in terms of glycolysis, glucose uptake, and function. Additionally, it covers recovery of glucose metabolic effects through overexpression of Hif1a or Pfkfb3 (targeted to osteoblasts) and metformin treatment. The role of Hif1a and Pfkfb3 in osteoblasts with regard to the rescue of T2DM bone effects is critical to the novelty of the paper and may benefit from being included and emphasized in the title and/or abstract. The study of osteoblasts and their glucose metabolism has been studied but not extensively at the mechanism level. The approach of using a mouse model is good for youth-onset T2D. It would be helpful if the author could include a bit more in the abstract about the critical role of Hif1a and Pfkfb3 in osteoblasts in recovery from T2DM treatment's bone effects in vivo.

Reviewer #1 (Public Review):

In their manuscript, Wang et al. investigate the changes occurring at the CNS borders upon neonatal bacterial meningitis. Both the dural meninges and the leptomeninges display changes. Using single nuc RNAseq and imaging approaches, they show that fibroblasts, endothelial cells and macrophages get inflamed, with an increase vascular leakage. Mechanistically, TLR4 KO but not CCR2 KO or liposome treatment (to deplete leptomeningeal macrophages) was able to rescue the vascular impairment. This is an interesting study that provides useful datasets for the community. However, we recommend several additions regarding data analysis (definitions, single cell, imaging) as well as additional studies (bacterial load, protein validation).

Reviewer #2 (Public Review):

In a neonatal model of bacterial meningitis induced by s.c. injection of E. coli, transcriptional changes were found across all major cell types including endothelial cells, fibroblasts and macrophages. Among macrophages, they describe 2 resident subsets and 2 inflammatory subsets. By immunohistochemistry of arachnoid and dura flatmounts, they show vascular changes upon infection, including clustering of CLDN5 and PECAM1, and disorganized capillary morphology, which was dependent on Tlr4 signaling but independent of arachnoid macrophages.

The manuscript would benefit from rewriting, it is not written in a concise manner and the rationale for experiments, time points for analyses and their conclusions are not clear. The model of s.c. bacterial infection is not well introduced and overall changes in the periphery, survival curves or bacterial counts (in the KO models) in the meninges/brain are not mentioned.

Reviewer #1 (Public Review):

This work puts forward a comprehensive characterisation of colorectal cancer (CCCRC), by classifying it into 4 subtypes with distinct TME features. It uses 10 public databases: 8 microarray datasets for the training of molecular classification and 2 RNAseq for validation (CRC-RNAseq) to identify the 4 subtypes using unsupervised machine learning (consensus clustering). These 4 subtypes were found to be somewhat distinct in terms of immune response and the possibilities for effective treatments. They found that one subtype may be more sensitive to chemotherapy, two to WNT pathway inhibitor SB216763 and Hedgehog pathway inhibitor vismodegib, and one to ICB treatment. They show an association with patient outcome in terms of PFS, validated in the validation cohort. They used histology to correspond the subtypes to known pathological types, as well as investigating their T cell makeup. They also investigated the genetic tumour evolution that may occur between the subtypes. A single-sample gene classifier was put forward as a way of identifying the class of cancer.

The evidence for the main results of the work is convincing, but a few areas need to be clarified and extended.

In the determination of the 4 subtypes (C1-C4) the methodology is clear, and the definition of the training and validation data are clear and well presented. The techniques used are well suited to the problem. The performance of the classification as a predictor of prognosis is presented as KM curves of PFS and OS for the training and validation sets. The training data shows a significant log-rank p-value in both PFS and OS. The validation data shows a significant effect in PFS.

What follows is quite an exhaustive process of finding differences between the cohorts using a multitude of techniques and datasets, including genomics, epigenetics, transcriptomics, and proteomics. These sections are mainly descriptive and do add understanding to the classification, especially with regard to the T-cell populations that are invasive.

Improvements could be made to the latter sections of the main paper. The basis for the potential clinical responses of the subtypes is arrived at via a "pre-clinical model" based on 81 genes. It would benefit from clarification on what genes were used in model training and details of the final model. Similarly the description of the "Single-sample gene classifier" could be enhanced similarly with a better description of which genes are in the final classifier.

Reviewer #2 (Public Review):

This study aimed to classify colorectal cancer (CRC) samples based on the expression of genes in selected gene lists, where the gene lists were chosen to represent aspects of the tumour microenvironment, tumour-associated immune cells, and tumour cells. The resulting clusters were then used to define a classifier, followed by a detailed description of molecular features of the tumours and tumour microenvironments assigned to each cluster. The authors claim this study is more "holistic" than previous work on CRC clustering/classifiers because they aimed to explicitly include additional components of the tumour microenvironment in both the clustering/classifier definition and in the subsequent description of molecular characteristics.

The CCCRC clustering and the resulting classifier presented in this paper are derived from published RNAseq studies. The multi-omics aspect of the work is restricted to smaller sample numbers for which both transcriptomic and another omics dataset were available in public resources and comprises a description or correlative analysis of each omics data type within each of the assigned CCCRC subtypes.

By applying solid computational methods to a compendium of published RNAseq datasets (n~1500 tumours), they found that tumour samples from colorectal cancers clustered into 4 subtypes ("CCCRC" subtypes) on the basis of 61 pre-defined gene expression signatures. These subtypes correlated with but did not correspond to, the previously described Consensus Molecular Subtypes (CMS) of colorectal tumours.

Other types of molecular data were available for some tumours, obtained from the same published resources: whole-slide images, mutations, tumour proteomics, and/or scRNAseq. The authors reanalysed these datasets using standard methods and drew correlations with the CCCRC subtypes they had assigned in this work. To (semi-)quantify immune infiltration characteristics from whole-slide images (WSI), they additionally performed automated segmentation in addition to review by pathologists, which in combination produced a convincing WSI-derived dataset.

In combination with existing CRC classifications, this study could facilitate future biomarker discoveries. This appears to be the authors' main claim, and the data and methods broadly support this claim.

Some aspects of the work need to be clarified:

This work relies on the definition of 4 clusters of CRC tumours based on consensus clustering of the 61 gene lists, which in turn depends on the choice of clustering method and the choice of gene lists. Sufficient detail is provided about the gene lists and resulting clusters, but this paper does not show how robust the 4 clusters are to these choices; for example, the "Energy" gene list appears to be a relatively strong component of clusters C2 and C3.

The authors examined whether their CCCRC classification showed differential disease progression in available retrospective cohorts of people treated with anti-PDL1 therapy. The authors presented this work as "significance of CCCRC in guiding the clinical treatment of colorectal cancer", but the data presented in this section cannot support clinical treatment decisions, which would require prospective studies and clinical trial designs. However, this section is potentially useful for generating hypotheses about potential biomarkers related to the CCCRC subtypes, and might, in the future with additional evidence, contribute to the design of a trial. The authors point out that additional experimental evidence would be required.

Other prognostic or predictive clinicopathological variables for colorectal cancer are not discussed in detail in the present work but are important for further work on the prognostic and predictive value of CRC molecular subtypes and biomarker derivation. Discrepancies in treatment response have previously been observed in separate CRC trials of biologically targeted agents with different chemotherapy backbones and other authors have suggested that treatment interactions with the tumour microenvironment might in part explain these discrepancies (e.g. Aderka (2019) PMID:31044725, and others).

Reviewer #3 (Public Review):

In their study: Comprehensive characterization of tumor microenvironment in colorectal cancer via histopathology-molecular analysis, Wu et al., aim to examine the contribution of the tumour microenvironment (TME) on biological and clinical heterogeneity in colorectal cancer (CRC).

To achieve this the authors use a vast array of publicly available datasets across a variety of biological modalities (transcriptomic, epigenetic, mutational). Using thoughtfully curated genesets the authors classify CRC into 4 holistic comprehensive characterised CRC (CCCRC) subtypes which comprise immune, stromal, and tumour features of CRC biology.

The authors investigate the association of their novel CCCRC subtypes with current "gold standard" classification schemes.

The authors' integration of deep learning methods for HE classification and subsequent association with "Tumor level" CCCRC subtypes is a refreshing addition to the study. Comment on the degree of heterogeneity observed in HE samples and correlation to the heterogeneity of CCCRC subtypes would be a welcomed addition. It is likely publicly available datasets from such platforms as 10X Genomic Visium would be available for this type of analysis.

Whilst one of the main outcomes of the study is the addition of another classification scheme to the field of colorectal cancer, the CCCRC scheme represents a holistic perspective on CRC classification.

The authors provide a welcomed graphical overview of the complex narrative of the study in Figure 7.

The authors focus on the classification of inter-patient heterogeneity and its associated predictive and prognostic utility. There appears to be a significant degree of overlap between immunosuppressive and immune excluded, and proliferative and immuno-modulatory signatures in Figure 1A. One of the major limitations of patient response to treatment is intra-patient heterogeneity, it would be nice for the authors to comment briefly on the degree of intra-patient heterogeneity of the CCCRC subtypes.

Overall the authors succeed in providing a holistic deep characterisation of CRC from the perspective of a variety of biological modalities. The authors provide a novel classification scheme for the field of CRC which demonstrates prognostic and predictive utility, which would benefit from further validation from external datasets. The authors demonstrate a pathway for integration and interpretation of complex high-dimensional data into clinically translatable currency such as the H&E.

Reviewer #1 (Public Review):

This paper investigates the metabolic basis of a node, posterior cingulate cortex (PCC), in the default node network (DMN). They employed sophisticated MRI-PET methods to measure both BOLD and CMRglc changes (both magnitude and dynamics) during attention-demanding and working memory tasks. They found uncoupling of BOLD and CMRglc in PCC with these different tasks. The implications of these findings are poorly interpreted, with a conclusion that is purely based on other work independent of this study. Various suggestions could allow them to place some speculations in line with a stronger interpretation of their results.

This is one of several papers in recent years investigating the metabolic underpinnings of activated (or task-positive) and deactivated (or task-negative) cortical areas in the human brain. In this study, they used BOLD fMRI and glucose PET scan to examine the metabolic distinction of the default node network (DMN), which is known to be deactivated during attention-demanding tasks, with different types of cognitively demanding tasks. Unlike the BOLD response in posteromedial DMN which is consistently negative, they found that CMRglc of the posteromedial DMN (a task-negative network) is dependent on the metabolic demands of adjacent task-positive networks like the dorsal attention network (DAN) and frontoparietal network (FPN). With attention-demanding tasks (like Tetris) the BOLD and CMRglc are both downregulated in DMN (specifically the posterior cingulate cortex, PCC, a task-negative node of DMN), but working memory induces CMRglc increase in PCC and which is decoupled from the negative BOLD response in PCC.

1. These complicated results are the main findings, and to provide a biological basis to these data they rather surprisingly, but without their own experimental evidence, conclude that the negative BOLD and negative CMRglc in PCC during attention-demanding tasks is due to decreased glutamate signaling (which was not measured in this study) and the negative BOLD and positive CMRglc in PCC during working memory is due to increased GABAergic activity (which was not measured in this study). It is rather surprising that without measurement, a conclusion is made which would at best be considered a hypothesis to be tested. Thus, independent of these hypothesized mechanisms, they need to summarize their results based on their own measurements in this study (see 3 for a hint).

2. It is mentioned that the FDG-PET scans allow quantitative CMRglc, both in terms of units of glucose use but also with high time resolution. Based on the method described, it isn't clear how this is possible. Important details of either prior work or their own work have been excluded that show how the time course of CMRglc (regardless of whether it's absolute or relative) can be compared with the BOLD time course. Furthermore, it is extremely difficult to conceive that quantitative CMRglc can be estimated without additional measurements (e.g., blood samples, etc). Significant methodological details have to be provided, which even should make their way to results given the importance of their BOLD-CMRglc coupling and decoupling in the same region.

3. It is surmised that the glutamatergic/GABAergic involvement of these metabolic differences in PCC is from another study, but what mechanism causes the BOLD signal to decrease in both stimuli? This is where the authors have to divulge the biophysical basis of the BOLD response. At the most basic level, the BOLD signal change (dS) can be positive or negative depending on the degree of coupling with changed blood flow (dCBF) and oxidative metabolism (dCMRO2) from resting condition. Unfortunately, neither CBF nor CMRO2 was measured in this study. In the absence of these additional measurements, the authors should at least discuss the basis of the BOLD response with regard to CBF and CMRO2. If we assume that both attention-demanding and working memory tasks decreased BOLD response in PCC in the same way, we have identical dCBF/dCMRO2 in PCC with both tasks, i.e., their results seem to suggest an alteration in aerobic glycolysis with different tasks. With attention-demanding tasks, CMRglc decreases similarly to CMRO2 decreases in PCC, whereas with working memory tasks, CMRglc increases differently from CMRO2 decreases. This suggests PCC may the oxygen to glucose index (OGI=CMRO2/CMRglc) would rise in PCC attention-demanding tasks, but fall in PCC with working memory tasks. This is obviously an implication rather than a conclusion as CBF or CMRO2 were not measured.

4. Given the missing attention that gives rise to the BOLD contrast mechanism, it is almost necessary to discuss the biophysical basis of BOLD contrast and specifically how metabolic changes have been linked to both increases and decreases in neuronal activity in the past. Although this type of work has largely been conducted in animal models, it seems that this topic needs to be discussed as well.

Reviewer #2 (Public Review):

This paper provides an important and insightful investigation into patterns of activations that emerge in external task states. The authors use state-of-the-art methods and novel analytic approaches to establish that deactivations in the default mode network during external tasks are driven by activity in brain regions that are important in the current tasks (such as the visual or dorsal attention networks). It will be important in the future to understand whether this is a symmetrical phenomenon by studying this behaviour in states that maximize activity within the default mode network and also drive reductions in networks that are not relevant to these situations.

Reviewer #3 (Public Review):

The authors report a study where, using multiple datasets with [18F]FDG PET bolus + continuous infusion ("functional PET") and BOLD fMRI data, they re-evaluate the metabolic and hemodynamic properties of the default mode network (DMN) in a task-evoked context, with a focus on posteromedial DMN due to its relevance for across-network integration.<br /> They show how posterior DMN is differently engaged depending on the chosen task: while visual and motor tasks lead to BOLD deactivations and glucose metabolic decrease, specifically in the dorsal posterior cingulate cortex (PCC) area, working memory tasks produce BOLD deactivations but metabolic increases, specifically in ventral PCC, as shown in their previous paper (Stiernman et al. 2021, https://doi.org/10.1073/pnas.2021913118). This aims to solve the controversies elicited by findings of both increased and decreased glucose consumption in the presence of BOLD deactivation in the DMN.

Additionally, they show how task-evoked glucose metabolism in posterior DMN seems to be shaped by that of the corresponding task-positive networks, with a positive link with dorsal attention and a negative link with frontoparietal network metabolism. This is explored using a type of directional connectivity analysis called "metabolic connectivity mapping", drawn from their previous work (Riedl et al. 2016, https://doi.org/10.1073/pnas.1513752113; Hahn et al. 2020, https://doi.org/10.7554/eLife.52443). They go on to speculate that concomitant BOLD deactivation and reductions in glucose expense might relate to decreased glutamatergic signaling, while BOLD deactivations accompanied by increased glucose consumption might depend on increased GABAergic neuronal activity.

This is a relevant topic because it not only shows how the DMN is flexibly engaged in different tasks but also allows us to better understand the complex relationships between BOLD fMRI and [18F]FDG PET signals, which are still not fully characterized to this day. Of course, while in resting state the situation is further complicated by the more uncertain physiological meaning of the resting BOLD signal, task-evoked states are expected to provide a more interpretable intermodal link between metabolism and hemodynamics, due to the known major changes in blood flow, blood volume, and glucose metabolism - which underlie BOLD and [18F]FDG signal changes - in response to neural activation. However, even in task states, there is not always a strong association between the two responses, as previously shown by the authors themselves (Rischka et al. 2018, https://doi.org/10.1016/j.neuroimage.2018.06.079). This is something I think the authors should stress out a little more, as they have previously done (Rischka et al. 2018, https://doi.org/10.1016/j.neuroimage.2018.06.079), both in the introduction and in reference to Figure 1, which shows clear differences between BOLD and [18F]FDG activations/deactivations (e.g., widespread negative responses in the cerebellum for [18F]FDG).

Overall, the analyses reported in the manuscript are simple and seem mostly sound, drawing from well-established methods in PET and fMRI activation studies, with additional approaches previously developed by some of the authors themselves (e.g., "metabolic connectivity mapping", Riedl et al. 2016, https://doi.org/10.1073/pnas.1513752113). Moreover, a clear strength of the paper is the high number of subjects, at least from a PET perspective, i.e., n = 50 for the Tetris task, plus group averages of previously published data for working memory (Stiernman et al. 2021, https://doi.org/10.1073/pnas.2021913118) and motor tasks (Hahn et al. 2018, https://doi.org/10.1007/s00429-017-1558-0).

The conclusions are in line with the results, and, though a little speculative, are potentially relevant for further exploration aimed at characterizing the neurotransmitter pathways underlying positive and negative BOLD and [18F]FDG responses. Moreover, the language is sufficiently clear to allow a proper understanding of the aims and the results, as well as the details of the analyses. As a side note, the title should probably be adjusted to "Task-evoked metabolic demands of the posteromedial default mode network are shaped by dorsal attention and frontoparietal control networks", to emphasize that the findings do not necessarily generalize to the resting state.

In conclusion, I am overall quite positive about this manuscript, which seems to nicely position itself within the existing literature, making some additional contributions.

Reviewer #1 (Public Review):

The authors assessed the association between exposures and obesity by environment-wide and epigenome-wide association studies. The strength of this study is that exposures, body mass index, and waist-hip ratio were measured three times from adolescence to early adulthood, and the associations were repeatedly evaluated. A weakness of this study is that a loose significance threshold was used for the epigenome-wide association study and only a small number of study subjects were measured in early adulthood. Since this is an observational study, the confounding effect should be considered when interpreting the exposures associated with obesity reported in this study.

Reviewer #2 (Public Review):

Since this study is a long-term cohort study in children and adolescents, it is advisable to decide whether to highlight differences by age group or to show consistent effect after exposure. In particular, obesity and related diseases are closely related to socio-economic environmental factors, and its impact might be different according to age (group) at exposure.

The part described in comparison with previous studies is a good attempt. However, some results are consistent with those of previous studies and some are not. This may be related to the time difference in socio-economic environmental factors rather than simply the difference between the West and China (Hong Kong). According to modernization/urbanization, changes in living environment, changes in family relationships, and changes in the care environment can also be factors especially in children.

In studying the effect of environment on gene expression, it can be thought that the influence of genes and the degree of expression might be different depending on the age of the subject (newborn, infant, infant, adolescent, adult) duration of exposure and these still need to be elucidated.

Reviewer #1 (Public Review):

This manuscript presents an exciting set of experiments on the mechanisms through which PSD proteins induce actin bundle formation. The study builds on a previous observation from the Zhang laboratory that phase condensates of six PSD proteins lead to the formation of actin bundles. Here, deep mechanistic analyses determine the necessity of upper vs. lower level PSD proteins for actin bundle formation, identify the domains and interactions of these proteins that are necessary and sufficient to induce actin bundles, and provide a first assessment in neurons of potential roles of the newly discovered mechanisms. The authors find that a patch of arginines in the Homer EVH1 domain plays a central role. Strikingly, no adaptors are needed for PSD condensates to induce actin bundles. This work is important for the understanding of roles and mechanisms of interactions between postsynaptic receptor scaffolds and cytoskeletal elements in dendritic spines. The mechanisms that are uncovered are likely mediators of structural and functional synaptic plasticity.

Overall, the data are rigorously acquired and convincing, the presentation of the findings is logical and clear, and the manuscript is well-written. In my view, a few adjustments in data presentation (quantitative assessment of in vitro experiments, statistical analyses) and additional analyses of existing data (on the localization and roles of transfected Homer proteins in neurons) will improve the paper, but new experiments are not necessary.

Reviewer #2 (Public Review):

In the manuscript, Chen and colleagues reconstituted the minimal system that indicates the coupling of PSD condensates with actin polymerization. While the functional connection between the assembly and dynamics of PSD and actin was known, the molecular mechanism remained elusive. Using a series of elegant biochemical reconstitutions and in-vitro assays complemented with analysis in living cells and primary neurons, the authors characterized whether PSD condensates of Homer-1, Shank-3 and SAPAP/GKAP are sufficient to induce F-actin bundling. Furthermore, they dissected the positively-charged Arg patch within EVH1 domain of Homer to be crucial for the F-actin bundling. Postsynaptic CaMKII and a short isoform of Homer, Homer1a, can both attenuate this process, suggesting various mechanisms neurons can regulate this process. Overall, the topic is timely, the study is well-designed, and the assays are clearly executed. However, several aspects need to be experimentally addressed, including some important controls:

1. It is well established that molecular crowding plays a crucial role in F-actin bundling. For example, in the reconstitution assays in Fig.1, the authors use 10 µM of each component of PSD (total of 60 µM), to which 5 µM actin is added. Yet, in their control assays (Supp. Fig. 1), only 10 µM of each protein was checked with the same amount of actin. A control is missing where the total protein crowding would be preserved, for example, by adding BSA or protein to mimic non-specific protein crowding.<br /> 2. Is the F-bunding observed under these physiological ratios of PSD proteins and actin? For instance, a recent quantitative study (PMID: 34168338) suggests actin:Homer-1 is 200:1 or 100:1, which is in stark difference from the 1:2 molar ratio used in the study. The protein concentrations (molar ratios) need to match the physiological.<br /> 3. In the cell migration assays, it is somewhat unclear to what extent the interaction is direct. For instance, co-sedimentation at ultra-speed (100,000 g) was used to suggest a direct binding of EVH1-GNC4 fusions (Homer1, Enah) with F-actin. The control that needs to be included is a protein known not to bind to F-actin incubated under the same conditions (salt concentration, duration of incubation) and spun down at 100,000xg. This is important to exclude that the tested proteins non-specifically entangle into F-actin without specifically binding to it, particularly at such high speed.<br /> 4. The imaging assay in hippocampal neurons uses an increased spine head size as a proxy for F-actin bundling. However, one needs to be careful as the baseline includes soluble mCherry, which is both much smaller in size and does not specifically enrich the spines. The image of Homer 1 R3E shows overall lower localization at the spines. Thus, one cannot exclude that the spine enlargement upon overexpression of Homer 1 wt and R3E+EN is not primarily driven by their overall enrichment in the PSD phase. A suitable control for this assay would be mCherry-tagged PSD95, which would localize to the spines yet is not directly involved in F-actin bundling.

Reviewer #1 (Public Review):

This study presents a valuable comparison of fibre orientation estimates from three different modalities: diffusion MRI, scattered light imaging, and x-ray scattering. The comparison is interesting as each modality is sensitive to different aspects of tissue microstructure - water anisotropy, micron-scale structural coherence, and myelin lamella respectively. Where scattered light and x-ray imaging can be only applied ex vivo, diffusion MRI has in vivo applications but suffers from being an indirect estimate of the microstructure of interest. By acquiring all modalities in both a vervet monkey and human brain sample, the authors provide quantitative, pixel/voxel-wise comparisons of fibre orientation estimates within the same tissue samples. The authors show convincing agreement in fibre orientations from all three methods, giving confidence in the fidelity of the methods for neuroanatomical investigations. Differences are also observed: SLI is shown to have less reliable estimates of fibre inclination, and the CSD analysis presented overestimates the number of crossing fibre populations when compared to the microscopy methods, particularly in single fibre regions such as the corpus callosum, a known artefact in some diffusion analyses.

In the current PDF, it is very difficult to see fibre orientations in figures due to low resolution, limiting the reader's ability to assess the results. Higher-resolution images would provide more information and easier comparisons.

The methods are generally clear though some additional information is needed: 1) to specify the resolution that the orientations are compared in each figure and how data was up-/down-sampled for these comparisons respectively. For example, each SAXS pixel contains many SLI pixels. It is currently unclear whether the mean SLI orientation from a neighbourhood is equivalent to the SLI compared, or whether a comparison was made for each SLI pixel. Similarly, for the dMRI-microscopy comparisons. 2) I also could not follow why two SLI methods are presented in the methods: SLI scatterometry relating to Figure 2, and angular SLI relating to all other results. Further clarification is needed. 3) Since the quality of the data co-registration can strongly impact pixel/voxel-wise comparisons, quantification of the registration accuracy or overlays demonstrating the quality of the co-registration would be valuable.

A primary weakness of the work as a diffusion MRI validation study is that though diffusion MRI supports many different models to extract fibre orientations with different outputs, here only a single model is compared to the microscopy data, which may affect the generalisability of the results. Further, it only compares the primary orientations from the diffusion MRI and does not consider each fibre population's magnitude (density of fibres) or the orientation dispersion, both of which can influence downstream analyses.

The paper could be strengthened by a more detailed discussion on the differences between the imaging modalities - e.g. in terms of imaging resolution, signal-generating mechanisms, and sensitivity to specific aspects of the tissue microstructure - and how these differences may limit their application to specific neuroanatomical investigations, or ability to validate one another. For example, the microscopy sections are 80 microns thick whilst the diffusion voxel is 200 microns. I expect this could contribute to the difference in the number of fibre populations per voxel.

The hypothesis that dMRI signal contributions from extra-axonal water result in additional fibre populations could be investigated by running CSD on both low and high-b-value data (for example using the openly available MGH dataset, Fan 2016) where fewer secondary fibre populations should be observed at high b-value.

Reviewer #2 (Public Review):

This work is a cross-validation of an x-ray tomography technique (SAXS) and an optical microscopy technique (SLI) for imaging axonal orientations ex vivo. These innovative methods were introduced in recent papers by the authors, who have teamed up here to compare them side-by-side on the same tissue samples for the first time. The two methods are both label-free (do not require staining) and they are quite complementary. SAXS can provide full 3D orientation measurements on intact tissue, but it operates at a mesoscopic resolution and requires access to a synchrotron. SLI can measure the orientations of multiple fascicles per voxel at a microscopic resolution and relies on more widely accessible equipment, but its accuracy suffers for fiber orientations perpendicular to the imaging plane and it requires tissue to be sectioned before it is imaged. Therefore it makes a lot of sense to explore the complementary strengths of these two techniques, and to use one to "fill in the blanks" of the other. The paper also compares the orientation measurements obtained with SAXS and SLI to those obtained with diffusion MRI. The latter provides only indirect measurements based on water diffusion, at a mesoscopic resolution somewhat lower than that of SAXS, but has the benefit of being feasible in vivo.

A limitation of this study is that conclusions on the comparison between SAXS and SLI are drawn from only 2 sections of a partial monkey brain sample and 2 sections of a partial human brain sample. Conclusions on diffusion MRI are drawn only on the 2 human sample sections. This is particularly an issue for the comparison to diffusion MRI, as the diffusion MRI voxels are wider than the section thickness, hence one cannot preclude that any orientations detected with diffusion MRI but not with SAXS and SLI come from the portion of the voxel that is missing from the corresponding SAXS/SLI section.

The stated aim of the paper is to provide a framework for combining the complementary benefits of SAXS and SLI, rather than simply presenting the results of a cross-validation study. This is a significant and ambitious aim. However, in order for this to serve as a framework, there would have to be clear prescriptions for how researchers interested in obtaining ground-truth measurements of axonal orientations would do so by using these two methods in tandem. This is not adequately developed in the paper in its present form. For example, the results show reasonable agreement between SAXS and SLI orientations when fibers lie within the SLI imaging plane and decreasing agreement for fibers with increasing through-plane inclination. How would the two methods be combined in voxels where they disagree? Would one use SLI orientations in voxels with fewer through-plane fibers and SAXS orientations in voxels with more through-plane fibers? How would voxels be assigned to each category? How would the orientation vectors from the two modalities be composed and how would the resolution difference between the two be handled? When the through-plane measurement of SLI is unreliable, is its in-plane measurement still reliable? That is if there were one mainly in-plane and one mainly through-plane fiber population, would the orientation of the former still be measured correctly by SLI? There is also considerable agreement reported here between through-plane orientations obtained with SAXS and diffusion MRI. Would this mean that diffusion MRI itself could be used to supplement SLI with through-plane orientations? Any clear set of prescriptions along these lines would represent a framework for imaging orientations by combining modalities. This, however, would require detailed steps for how to perform the combination and use the multi- vs. uni-modal framework to reconstruct connectional anatomy.

A key advantage of SAXS is that it can be performed on intact samples, i.e., before any nonlinear distortions of the tissue are introduced by sectioning. Thus it can provide an undistorted reference, with contrast on axonal orientations that would be absent in, say, a structural MRI of comparable resolution. This contrast could be used to drive registration of the distorted SLI sections to an undistorted SAXS volume, and therefore is a key way in which the two techniques can complement each other. Here, however, this is not explored, as SAXS is performed after sectioning. It is not clear if this is the authors' prescription for how a combined SAXS/SLI framework would be implemented, or if it was done specifically for this study. First, it would seem that SAXS on the intact sample would be lower maintenance, requiring less setup time and hence potentially less overall beamtime than performing SAXS on each section separately. This would make it more practical for routine deployment beyond a few sections. Second, because the SAXS data are now nonlinearly distorted, they cannot be affinely aligned to the MRI volumes. While, in principle, performing both SAXS and SLI on the sections may facilitate the comparison between the two, having to unmount, rehydrate, and remount the sections in between may negate this advantage, as now there is no guarantee that SAXS and SLI can be affinely registered to each other. Here all these registration steps are performed affinely, so it is unclear to which extent the computed errors between modalities are characterizing the inherent limitations of the respective contrasts, or limitations of the registration technique. Some of the alignment is performed manually, for example, specific regions of the images are realigned by hand, and the slice of the diffusion MRI volume that is aligned to the SAXS/SLI sections is chosen by hand. Again, for this to serve as a framework that can be deployed on whole samples, there would have to be clear prescriptions for how to perform these steps robustly, how to ensure that the MRI can be acquired in a coordinate frame parallel to the sections, etc.

Finally, the paper puts forth a general conclusion that diffusion MRI overestimates the number of fiber populations per voxel, on the basis of small ODF peaks appearing perpendicular to the main ODF peaks. Of all conclusions in the paper, this is the least convincingly supported by evidence. First, these small perpendicular peaks are a known artifact, which would be typically eliminated by ignoring ODF peaks below a certain amplitude, a common practice in diffusion tractography algorithms. The authors refrain from using an amplitude threshold, with the rationale that it may also remove true diffusion orientations. However, they apply a threshold when they detect SLI peaks (a rather stringent 8% of the maximum). Second, the explanation that these artifactual peaks may appear due to vessel walls is not convincing. Vasculature is sparse. A single vessel wall will not impact the diffusion signal in the same way as a bundle of parallel axons. In an axon bundle, water molecule displacements are restricted in all directions except parallel to the axons. A single vessel wall in a voxel will not have the same effect on displacements (which are much smaller than the size of the voxel). From Figure 5, it looks like there would be at most 1-2 of these vessels in a diffusion MRI voxel, and they would not be in all voxels. This cannot explain the widespread appearance of these small artifactual peaks. Third, many ODF reconstruction methods have parameters that can be adjusted to make these artifactual peaks more or less prominent. The default parameters may be optimal for in vivo but not ex vivo data, due to the effects of fixation. In light of these concerns, I would caution against making such a general statement about all diffusion MRI in the human brain, especially on the basis of a single diffusion reconstruction method applied to a single location in one brain.

Reviewer #1 (Public Review):

The study tackles the topic of male harm (sexual selection favoring male reproductive strategies that incur a reduction of female fitness) from an interesting angle. The authors put emphasis on using wild-collected populations and studying them within their normal thermal range of reproductive conditions. Where previous studies have used temperature variation as a proxy for stressful environmental change, this approach should instead clarify what can be the role of male harm on female fitness in natural conditions. A minor caveat regarding this point is the fact the polygamy treatment also has a heavily male-biased sex ratio (3:1). The authors argue that this sex ratio is within the range of normal variation in that species, but it is likely that the average is still (1:1) in natural populations and using a male-biased sex ratio could magnify the intensity of male harm. This does not undermine the conclusions regarding the temperature sensitivity of sexual conflict but should be acknowledged.

The authors find that varying temperature within a range found in natural conditions affects the reproductive interactions between males and females, particularly through male-harm mechanisms. Male harm, measured as a reduction in lifetime reproductive success (LRS) from monogamy to polygamy settings is present at 20C, stronger at 24, and absent or undetectable at 28C. Female senescence is always faster in the polygamy mating systems as compared to monogamy, but the effect appears strongest at 20C. Mating behaviors of males and females in these different settings are used to attempt to uncover underlying mechanisms of the sensitivity of male harm to temperature.<br /> A weakness of the manuscript in its current form is the lack of clarity about the experimental design, which makes understanding the results a long and involved procedure, even for someone who is familiar with the field. If the authors consider revising the manuscript, I suggest giving a better overview of the experimental design(s) earlier in the manuscript, perhaps supported by a diagram or flowchart. I also suggest structuring the results better to aid the reader (e.g., make clearer distinctions between results that come from the different experiments). Finally, some additional figures and statistical tests corrected for multiple testing would help get a better feel of some aspects of the dataset.

I believe that the conclusions are generally justified and the results overall convincing. Overall, this is an impressive study with a lot of dimensions to it. Its complexity is a challenge and may require additional effort from the authors to make it easier to access. The core of the question is answered by LRS measures, but the authors have also provided a wealth of behavioral data as well as other fitness components. The manuscript could be greatly improved by putting more effort into linking the different metrics together to track down potential mechanisms for the observed variation in male-harm-induced reduction in female LRS. The discussion would also benefit from considering the female side of the sexual conflict coevolution arms race.

Reviewer #2 (Public Review):

Londoño-Nieto et al. investigated the influence of temperature on the form and intensity of sexual conflict in Drosophila melanogaster. They aimed to test the effect of naturally occurring temperature fluctuations on a wild population of Drosophila while disentangling pre- and post-copulatory episodes of sexual conflict. To this end, they exposed females to males under monogamy or polyandry, hence manipulating the degree of male harm experienced by females. The effect of temperature was explored by exposing these groups to 20, 24, or 28{degree sign}C. They found that female fitness suffered from male harm most at 24{degree sign}C and less at the other two temperatures. Interestingly, pre- and postcopulatory episodes of sexual conflict were affected differently by temperature. Overall, these data suggest that the relationship between sexual conflict and temperature can be strong and complex. Hence, these results can have important implications for the impact of sexual conflict on population viability, especially in light of the climate crisis.

This paper tackles a highly relevant question using an established model organism for sexual conflict and contains a rich dataset obtained using a series of carefully planned experiments and analysed in an appropriate way. Importantly, the authors used biologically meaningful temperatures and mating treatments, which increases the relevance of the data. The main conclusions are well supported by the data. Nevertheless, the devil is in the detail, and given the way the authors frame their study (i.e. testing a natural population under naturally occurring temperature fluctuations) and their results (i.e. sexual conflict is buffered by temperature effects in the wild) there are some limitations to be considered:

1) The authors frame their study as addressing the question of how sexual conflict reacts to naturally occurring temperature fluctuations in the wild. Nevertheless, the population used in this experiment had been kept for nearly 3 years in the laboratory prior to the experiment. Importantly, the authors ensured that the laboratory population maintained genetic diversity, by regularly crossing wild lines into it. Nevertheless, this population remained for some time in the laboratory under standardized conditions. The applied temperature fluctuations are in a biologically meaningful range (though only during the reproductive season), but it remains unclear if the applied fluctuations were in a standardized way (i.e. pre-programmed) or included random fluctuations (i.e. a more natural setting). This laboratory setup has certainly clear advantages, for example, it enables the exclusion of any effects other than the temperature on sexual conflict. Nevertheless, how these will then ultimately play out in the wild could be a different story.

2) The authors highlight clearly that temperature fluctuations in the wild might play an important part in how sexual conflict plays out in natural populations. This very interesting and highly relevant point might lead the reader to assume that this is what was actually tested in the experiment. Nevertheless, in the experiments, different constant temperatures were applied to the flies, while only the stock population was kept at a fluctuating temperature regime. Hence, the influence of fluctuations during episodes of sexual conflict remains untested. While the present data show that sexual conflict can be modulated by temperature, the effect of naturally occurring fluctuations on the net cost of sexual conflict to a population remains unclear.

3) The authors conclude that the effect of sexual conflict can be buffered by temperature in the wild. In general, I agree with this, although a more conservative way of framing this would be to say that temperature modulates or moderates sexual conflict instead of buffers it. If there really is a buffering effect of temperature in the wild remains to be tested, I believe. This will depend on how actual changes in temperature affect this dynamic (see point 2). In addition, I think another interesting open question is what the mechanism behind the observed differences might be. Are male and female interests really more aligned at different temperatures (i.e. males plastically reduce harm)? This would really buffer the harm of sexual conflict at those temperatures. Nevertheless, alternatively, males might not be perfectly adapted to manipulate the female optimally at lower or higher temperatures. This would mean that if the temperatures change, males might evolve to increase the manipulation of females, and hence the scope for sexual conflict might not change in the end under this scenario. Nevertheless, as the authors themselves state: 'An intriguing possibility is thus that SFPs are more effective at lowering female re-mating rates at warm temperatures, thereby buffering these costs.' Therefore, a temperature-dependent increase in the effectiveness of male manipulation might counterintuitively reduce sexual conflict in this species.

4) In the end the authors argue that the climate crisis might have 'unexpected positive consequences via its effect on male harm'. Sexual conflict is indeed widespread, but it takes many different forms (as has been nicely described in the introduction of this paper). Because the studied system seems to be quite a specific example, it is questionable how far spread this phenomenon is in nature. In addition, it remains unclear how male harm will evolve in response to the climate crisis (see point 3). Finally, the relative fitness of females increased in the present experiment, as the tested range was within the reproductive optimum of the species. Nevertheless, the relative importance of the positive effect of sexual conflict on fitness outside of optimal temperatures seems questionable.

Nonetheless, I believe these results to be of exceeding interest to the scientific community and of importance to the field. It opens up many potential research directions and adds further data to the fascinating field of sexual conflict, SFPs, and male harm in Drosophila.

Reviewer #3 (Public Review):

In this paper, the authors explore the effects of the environment, specifically temperature, on male harm to females. Male harm is the phenomenon where males reduce female fitness in polyandrous systems, where a single female may mate with multiple males. The selection of males to increase their reproductive success in male-male competition can lead to genetic conflict that increases male fitness at the expense of female fitness. Typically, male harm has been studied in single environments under optimal conditions. However, there is an increasing focus on the effect of the environment on fitness costs of male harm to females, as a way to better understand the effect of male harm on population fitness in more realistic ecological contexts. In this paper, the authors add to these studies by exploring the effect of temperature on male harm and female fitness, using the fruit fly Drosophila melanogaster, as a model system. They find that temperature affects the impact of male harm on female fitness, with male harm having the greatest effect at 24˚C relative to 20˚C and 28˚C. The authors then go on to disentangle how temperature affects the various components of male harm that impact female fitness (e.g. harassment, ejaculate toxicity). The paper demonstrates that male harm depends on ecological context, which has implications for understanding its impact on population fitness under realistic ecological scenarios, particularly with respect to climate change.

The strength of the paper is that it demonstrates that male harm (presented as differences in female life reproductive success between monogamous and polyandrous matings) changes with temperature. The authors dissect this general observation by showing that different aspects of pre-copulatory reproductive behavior, for example, male-male aggression, copulation rate, and female rejection rate, also change with temperature. Further, they demonstrate that correlates for male ejaculate quality also change with temperature, suggesting that temperature also affects post-copulatory mechanisms of male harm.

The weakness of the paper is that the method and results section are difficult to follow, which negatively impacts the interpretation of the data. The experiments are complex and need to be for what the authors are studying. Nevertheless, the paper is written in a way that makes it challenging for the reader to fully understand how precisely the experiments were conducted. Further, the authors do not explain clearly how some of the experiments relate to the phenomenon ostensibly being assayed. For example, a more detailed explanation of why mating duration and remating latency are assays for ejaculate quality in the context of sperm competition would be very helpful in interpreting the data. Further, a clearer explanation of the statistical analyses conducted

Reviewer #1 (Public Review):

The authors generated a detailed single-cell RNAseq dataset for the microfilariae stage of the human nematode parasite Brugia malayi. This is an impressive and important achievement, given that it is difficult to obtain sufficient material from human parasites and the microfilariae are protected by a chitin sheath. The authors collected microfilariae from jirds and carefully worked out a protocol of digestion, dissociation and filtering, to obtain single-cell material for sequencing.

The single-cell resource was complemented with a dataset derived from FACS-sorted large secretory cells, allowing the identification of several specific proteins expressed in this unique microfilarial cell-type important for immune evasion.

The authors also generated new data for secretory cells of Caenorhabditis elegans and concluded that there is limited similarity between the composition of Brugia and C. elegans secretory cell types.

In a further set of experiments, the authors analysed gene expression changes in dissociated Brugia cells to the commonly used anthelminthic drug ivermectin. This revealed specific gene expression changes across various cell types, providing new insights into how the drug effects the parasite.

Finally, the authors developed a method to keep dissociated Brugia cells alive in culture for two days. This method will aid cellular studies of this parasite.

The authors may want to explore the new resource in more detail to reach more specific biological conclusions. For example, the authors mention that the large secretory cells are critical to parasite survival and immune evasion. With a more complete list of genes expressed in these cells the authors could try to reach more specific conclusions or predictions. Are there newly identified secreted factors that could contribute to immune evasion? It would be important to read in more detail about such proteins (including an analysis of the sequences and phylogenies), especially if the authors could identify new candidates as potential vaccine or diagnostic targets. Likewise, can the data be used to understand in more detail the mechanism of immune evasion or ivermectin action?

The authors searched for known secreted proteins, including antigens, vaccine targets, and diagnostic markers and mapped the expression of these to the single-cell atlas. It is not clear from the paper how comprehensive previous studies to identify secretory proteins were. With the new resource in hand, the authors could look at all secreted proteins (with a signal peptide) expressed in the ES and other cells. The paper would benefit from a more comprehensive overview of the classes of secretory proteins and their expression.

The authors show that an abundance of C2H2 transcription factors is localizing almost exclusively to the secretory cells. It would be useful to see a classification of these proteins and phylogenetic analysis relating them to C2H2 from C. elegans and other animals.

In general, a more detailed bioinformatic analysis of secretory products and more discussions of potential functions (e.g. serpins etc.) would make the paper more interesting and could stimulate more mechanistic thinking.

Reviewer #2 (Public Review):

The overall objective of this paper is to characterize the cells that are responsible for producing the secretions of the parasitic larvae, Brugia malayi. This parasite is a human pathogen that is one of three responsible for lymphatic filariasis/elephantiasis a disease that threatens half of the world's population. The specific focus of this work is protein secretions made by the parasites. In general, it is well-known that parasitic worms can manipulate and evade host immune immunity via secreted products. Studies have focused on the activities of these secretions and specific molecules. What is lacking is a detailed description of the identity and anatomical location of the cells that produce them. This is especially important as these cells are the target of different classes of anthelminthic drugs. This knowledge could allow new strategies to target these pathogens and to better understand the mechanism of actions.

To better understand this important topic, this manuscript describes a method to dissociate cells of the pre-larval stage (microfilariae) of the human parasitic filarial nematode, Brugia malayi. This method is then used to create an atlas of cells based on the expression profiles of individual dissociated cells. Cells are grouped into clusters with similar patterns of expression using single-cell mRNA sequencing analysis pipelines and the clusters are defined by using a combination of known functionalities based on the well-established, free living, soil nematode, C. elegans, and different functional classifications based on genes of interest. These include known antigens as well as targets of 3 classes of anthelmintic molecules. Using the scRNA-seq data, clear hypotheses can be made about ion channel and structural protein composition, the putative targets of the anthelminthics. Finally, it is proposed that the dissociated cells can be cultured which can facilitate future studies since cell lines or primary cultures of cells from filarial worms are not available.

This paper represents a huge undertaking on an important and understudied area. The authors have taken on a major challenge to gain novel insights, and to provide data and protocols for the field to use. The data are well-presented and support the conclusions of the work. The authors have broadly achieved their goals and the data generated and methodology will be important for the community.

Reviewer #3 (Public Review):

Henthorn and coworkers obtain a single cell atlas of the parasite nematode Brugia malayi to search for excretory secretory products. These are involved in therapeutic responses but it is unknown what are the cell types that express them. In fact this seems as an ideal question to be addressed with single cell transcriptomics. The authors analyse their dataset, coming to the conclusion that many of these ES products are expressed broadly throughout the parasite, including secretory and non secretory types. This would be a nice conclusion if supported by the data. Then they go on to compare responses to exposure of ivermectin at the single cell level.

I must praise the attempt of using single cell transcriptomics to examine this question. These relatively novel methods have been so far used to collect information of cell types, but have immense potential for the investigation of important questions in neglected diseases like this. Fundamental knowledge about the biology of Brugia malayi and the tissue and cell types present are key to understanding their pathogenesis and advancing new therapeutic options. The authors start this research project with the right model and right technique.

My major concern is the quality of their single cell data. The authors perform no FACS or other methods to clear their suspension from cellular debris. This arises from all cell types, and then gets encapsulated with single cells in the droplet-based single cell transcriptomic process. Then, all cell barcodes receive genes from a single cell but also from a collection of cellular debris particles (arising from all other cell types). This, and only this, can in principle explain one of the major findings in the abstract: secreted antigens are expressed broadly in many cell types. This same caveat might explain their finding of pan neuronal markers broadly expressed - conceptually very similar to what the authors hold for secreted antigens, but that the authors only mention briefly and do not explain.

Reviewer #1 (Public Review):

The manuscript Role of cytoneme-like structures and extracellular vesicles in Trichomonas vaginalis parasite: parasite communication by Salas N et al is an interesting manuscript with novel findings, clear strategies, and fine design of experiments. Despite the quality of the manuscript, it must be improved in order to deliver the best message in the area of cellular biology and molecular parasitology.

Reviewer #2 (Public Review):

The manuscript is rigorous and clearly written; the experiments are well described, and the conclusions are consistent with the experimental results. Particularly interesting are the data demonstrating the role of cytoneme-like structures. The microscopy images supporting the experimental data are clear and fascinating.<br /> The work is, in my opinion, well conducted.

Reviewer #3 (Public Review):

In this manuscript, the authors (Salas et al.) have investigated the communication strategies among various strains or species of Trichomonas vaginalis. T. vaginalis is a parasite that is responsible for non-viral sexually transmitted infections, worldwide. The authors have demonstrated that highly adherent parasite uses cytoneme-like membrane structures and extracellular vesicles (EVs) to communicate with poorly adherent isolates and mount a stronger response to hosts.

The major strength of this work is the use of state-of-the microscopic techniques to analyze cytonemes and EVs. However, the weakness is the experiments shown in the manuscript are more descriptive than mechanistic. The significance of this work is high because it demonstrates the presence of a unique communication strategy in Trichomonas vaginalis. Trichomonas uses cytoneme-like elongated membrane structures and extracellular vesicles to interact with each other and induce a robust pathogenic response in host cells.

The authors have used state-of-the-art cell biology techniques to conduct the study and the data analysis is solid.

Overall, the experiments are solid and the authors were able to accomplish their objectives of demonstrating parasite communication in T. vaginalis.

Reviewer #1 (Public Review):

The authors of this study exerted a variety of laboratory experiment methods and in silico analysis of expression data, and showed the differentiated aspects of the protein functions of the product of the duplicated genes eS27 and eS27L as well as their redundant aspects. These proteins are components of the cellular machinery for translation, namely 'readout' of the genome, in eukaryotes. This study provides a valuable test case of examining why seemingly redundant genes that underwent gene duplication during evolution have been retained in the genomes of many present-day organisms.

Reviewer #2 (Public Review):

In this manuscripts, the authors investigated differential role of two closely related proteins, S27 and S27L , which are one of the subunits of ribosome. Ribosomes containing each protein associate with a distinct set of mRNAs, suggesting that ribosomes in the cells play distinct roles depending on which subtype of S27 subunits they contain. The authors also performed functional analyses using mutant mice, and demonstrated that functions of S27-containing ribosome can be rescued by S27L-containing ribosome and vice versa. These findings provide new experimental insights into the origin of family genes fixed during the course of evolution.

Reviewer #3 (Public Review):

A current topic in the translational control field revolves around the idea that "the ribosome" is not a singular monolith machine, but rather that there are a variety of ribosomes, some with specialized functions. The presence of evolutionarily conserved ribosomal protein gene paralogs provides a platform for testing this idea. Presumably, if a paralog is required to translate a specific mRNA or class of mRNAs in a cell or organ type specific manner, it's loss should generate an observable phenotype. In this study, Xu and colleagues exploit the evolutionarily conserved eS27 and eS27L proteins to probe this hypothesis. Technically, the work is on the cutting edge of the field. Advanced genetic engineering techniques were used to generate mice lacking either paralogous gene, to create reciprocal swaps of each coding sequence into the other locus, and even to create genetically homogenous mice. The authors also use state of the art molecular biology methods, e.g. paralog-specific ribosome profiling, to search for differences in the mRNAs translated by ribosomes containing either of the two homologs.

Some phylogenetic evidence was presented suggesting that the paralogs first appeared during a gene duplication event in vertebrates: however, only and bird and one amphibian are represented. It is recommended that this analysis go deeper, parsing the amphibians and fish more finely. Although not identifying evidence for specialized ribosomes, they did find that it is essential that at least two copies of eS27 or eS27L are retained. Interestingly, the embryonic lethality of truncation alleles of either of the two paralogs result manifested at different stages of development, pointing to some kind of functional differences during development. The finding that eS27L containing ribosomes are more prevalent in lactating mammary gland and liver is an interesting observation, and that such ribosomes are preferentially associated with mRNAs involved in the cell cycle. From this the authors conclude that the data support subfunctionalization model of eukaryotic ribosomal protein S27 evolution rather than a specialized ribosome model. I also note that this is the most comprehensive and technologically advanced study of its kind in the translational control field and that it represents a significant contribution to the field of evolutionary biology.

Reviewer #1 (Public Review):

Tunneling nanotubes, contrary to exosomes, directly connect remote cells and have been shown to allow the transfer of material between cells, including cellular organelles and RNAs. However, whether sorting mechanisms exist that allow to specifically transfer subspecies of RNAs, especially of mRNA, has not been shown, and the transcriptional consequences of RNA transfer have not been addressed yet.

Using cocultures (or mix or single cultures as controls) of human MCF7 breast cancer cell line, and immortalized mouse embryo fibroblasts (MEFs), followed by separation of human and mouse cells by cell sorting, the authors performed deep sequencing of the human mRNAs detected in mouse cells. An accurate analysis of the transferred material shows that all donor cell mRNAs transfer in a manner that correlates with their expression level, with less than 1% of total mRNA being transferred in acceptor cells. These results show that the process of RNA transfer is nonselective and that the consequences on the cells receiving the RNAs should depend on the phenotype of the sending cells. These results are complemented by the last part of the manuscript where the authors convincingly show that the coculture of the two cell lines results in significant transcriptomic changes in acceptor MEF cells that could become CAF-like cells.

Reviewer #2 (Public Review):

In this manuscript, the authors characterize the extent of RNA transfer between cells in culture, with an emphasis on trying to identify RNAs that are transferred through tunneling nanotubes (TNTs). They use an in vitro human-mouse cell co-culture model, consisting of mouse embryonic fibroblasts and human MCF7 breast cancer cells. They take advantage of the CD326 cell surface molecule, which is specifically expressed on MCF7 cells, to separate the two cell populations using magnetic beads conjugated to anti-CD326 antibodies, followed by deep sequencing to identify human RNAs present in mouse cells. They identify many 'transferred' RNAs. Further analysis of sequencing data together with experiments using synthetic reporters indicate that RNA transfer is non-selective, that the amount of transfer strongly correlates with the level of expression in donor cells, and does not appear to require specific RNA motifs. The authors also note that co-culture with MCF7 cells leads to significant changes in the MEF transcriptome.

The experiments are overall carefully designed, and the data are clearly and quite carefully presented to point out limitations in interpretation and to distinguish speculations from experimental conclusions. It should however be kept in mind that it is unclear to what extent these limitations influence the conclusions reached. For example, the identification of transferred RNAs relies on the purity of the isolated cell populations and, while the authors provide some supporting evidence for this, nevertheless potential caveats remain. For instance, the isolated MEF samples used for analysis appear to lack single MCF7 cells, but still contain components, labeled as 'double stained' and 'unstained' cells, which are uncharacterized. The authors present some arguments as to why these would not contribute to 'transferred' reads, but given the low level of detectable transferred RNAs, and the unclear origin of these components, whether they influence the results could be debatable. Furthermore, the small number of replicates (2 replicates for the genome-wide studies and 1 replicate for most of the subsequent experiments) minimizes the confidence in the conclusions. In this context, it is also notable that the profile of transferred RNAs between the two replicates of co-cultured samples appears quite different by PCA analysis. It is thus conceivable that there might be specificity in the RNA 'transferome', influenced by unknown experimental variables, which is though masked when averaging those samples in subsequent analyses.

While the manuscript emphasizes the role of TNTs in RNA transfer, the actual involvement of TNTs relies solely on the observation that potential TNTs form between co-cultured cells. Other means of transfer, such as through engulfment or phagocytosis of cell fragments, could still possibly contribute. Furthermore, the dependence of mRNA transfer on direct cell-to-cell contact is demonstrated for 5 RNAs and extrapolated to transcriptome-wide RNA transfer, an assumption which might, or might not, be valid.

Finally, the results on gene expression changes induced by co-culture (Figures 7, 8) are of unclear relevance. As the authors point out, it is uncertain whether RNA transfer or other paracrine or adhesion-mediated signaling events, underlie these changes. It is therefore not easy to see how these results relate to the rest of the presented work. Furthermore, while the authors expand on the potential significance of changes observed in genes related to cancer-associated fibroblasts or to immunity-related genes, these remain speculative and untested.

Overall, the manuscript presents evidence indicating that RNA is transferred non-selectively in co-cultured cells, under specific conditions and between the cell types tested. The impact of the work is reduced by the lack of mechanistic understanding underlying this transfer and the uncertainty of whether this phenomenon has any subsequent physiological relevance.

Reviewer #1 (Public Review):

Animals respond to their environment in a state-dependent manner. One of the best examples of this is the dramatic changes in behaviours in the female after mating. In flies, this includes an overall increase in food consumption, a well-documented increase in protein appetite, increased salt appetite, increased egglaying behaviour, and reduced sexual receptivity.

In this study, the authors argue that sugar is a macronutrient that should be essential to support the increased metabolic needs of the fly and the lipid demand of the eggs. They isolate sugar (instead of providing it in a choice assay) and document that indeed mated flies have an increased appetite for sugars.

They then go on to demonstrate that this increase is not need-based, but is anticipatory in nature and that it is not changes in sensitivity of the sugar-sensing neurons, but central brain circuitry that drives this behvioural change. Finally, they work out the circuitry demonstrating that it diverges from the well-described three-layer mating circuit (SPSN>SAG>pC1) that is active in virgins but inhibited by sex-peptide in mated females. They use EM datasets to identify the pCd2>Lgr3+ neurons as downstream of pC1 and develop genetic tools to monitor and manipulate neuronal activity in these neurons to show that the Lgr3+ neurons are active in the mated state because they receive inhibitory inputs from the pCd2s.

As LG3 neurons are known to be activated by the DILPs, which mediate satiety, their model proposes the state of mating (as signalled by central brain circuitry) is essentially a state of additional hunger.

Reviewer #2 (Public Review):

This manuscript by Laturney et al. has found a previously uncharacterized neural link between female mating status and upregulation of sugar intake in the common fruit fly, Drosophila melanogaster. Although mated female flies have been known to increase both yeast and salt intake compared to virgin females, changes in sugar intake have not been previously described. Using quantitative monitoring of food intake, functional calcium imaging, connectome tracing, and neuronal manipulations, authors convincingly demonstrated that the Sex Peptide sensory neurons (SPSN) and their downstream neural circuit control the activity of female-specific Lgr3 neurons in a mating-dependent manner. In virgin females, the SPSN circuit (including its output pCd-2 neurons) is active, which is predicted to inhibit hunger-promoting Lgr3 neurons. After mating, the SPSN circuit becomes silent, which should disinhibit Lgr3 neurons. Indeed, they found that optogenetic silencing of pC2-d neurons promoted sucrose consumption. The newly characterized pCd-2 neurons are sexually dimorphic, consistent with their role in female-specific post-mating modulation of sucrose consumption.

Aside from the novelty of the mating-dependent changes in sugar intake, an exciting discovery of the current study is that separate circuits control different aspects of post-mating behavioral changes (increased egg-laying, mating rejection, increased sugar consumption). This finding illustrates a general neural mechanism by which a single "internal state" exerts its influences on multiple behaviors via branches of circuits from a hub for the given state (pC1 for the female mating status), which is a powerful mechanistic model for other internal states.

The high-quality data based on elegant yet rigorous experiments deserve praise as a textbook example. They presented multiple independent lines of evidence to demonstrate the function of each component of the SPSN circuit over the sucrose consumption Lgr3 neurons, which convincingly proves that the pCd-2a/b neurons transmit information of mating status to a hunger-controlling hub. Experiments have been exceptionally rigorous. Genetic manipulations were performed with multiple controls. They used multiple split GAL4 lines to target specific classes of neurons to eliminate the neuronal off-target effect. They also used multiple types of feeding assays to clarify the feeding phenotype induced by mating. Overall, the scientific rigor of this work sets a standard for researchers in the field to follow.

That the activity levels of pCd-2 neurons and their downstream Lgr3 neurons are indeed influenced by mating has not been directly tested. Since multiple previous publications consistently demonstrated that the SPSN-SAG-pC1 axis is suppressed by the Sex Peptide, the authors' conclusion that pCd-2 neurons are suppressed after mating (for example, see line 319) is very likely correct. However, what the authors showed was that silencing of the SPSN circuit "can" increase sucrose consumption in virgin females. To what extent mating suppresses pCd-2 neurons (and disinhibits Lgr3 neurons) remains uncharacterized. The inhibition exerted by the Sex Peptide is likely partial, which might not be precisely recapitulated by the optogenetic silencing. Mated female flies show an increased preference for protein and salt. The authors' finding that they also increase sugar consumption after mating indicates that mating causes a substantial change in female feeding patterns. The current work elevates the value of Drosophila as a neurogenetic model to understand how the nervous system achieves the complex tasks of nutritional homeostasis after mating, which dramatically alters the energy allocation in many species (including mammals). Data presented in this work will advance our understanding of how females coordinate feeding priorities in a face of changing nutritional demands after mating, which is one of the fundamental questions in neuroscience.

Reviewer #3 (Public Review):

Mating changes an animal's behavior. In Drosophila, mated females have higher energy needs, suggesting that their consumption of caloric foods may be altered. While previous studies have examined post-mating changes in the consumption of specific nutrients such as salt and protein, it was not known whether the intake of sugar, their primary energy source, is also changed. This study describes a post-mating increase in sugar intake and identifies the neural circuit that mediates this change. By using precise genetic manipulations, behavioral assays, and new connectome datasets, the authors provide high-quality data to support their claims.

This study reveals several new insights into the regulation of behavior after mating: 1) Female flies increase sugar intake after mating, and this is an "anticipatory" change rather than a homeostatic change resulting from energy depletion. 2) The post-mating change in sugar intake is mediated by the sex peptide circuit, SPSNs-SAG-pC1, which is known to regulate other post-mating changes. 3) The authors identify a new downstream target of pC1, the pCd-2 neurons, which regulate feeding. pCd-2 neurons do not affect egg-laying, and neurons downstream of pC1 that regulate egg-laying or receptivity after mating do not affect sugar intake. Thus, the SPSN-SAG-pC1 circuit that regulates post-mating behaviors diverges downstream of pC1 into multiple branches regulating different behaviors. 4) The authors identify cells downstream of pCd-2, median bundle cells expressing Lgr3, the receptor for Dilp8. These cells are inhibited by pCd-2, suggesting that they are active in mated females, and promote sugar consumption. Because previous studies showed that Dilp8 and Lgr3 are expressed more highly in fed flies and suppress feeding, the present study suggests that Lgr3+ cells integrate hunger and mating signals to regulate feeding. This is an interesting circuit motif that could extend to mammals. In future studies, it will be interesting to test how hunger and mating signals are integrated within these cells (e.g. do they function redundantly, additively, etc).

Reviewer #1 (Public Review):

The human genetic variant Dantu increases the surface tension of red blood cells making it hard for malaria parasites to invade. This was shown beautifully by Kariuki et al in 2020 (doi.org/10.1038/s41586-020-2726-6) by analysing blood from children using in vitro assays with cultured malaria parasites. Now Kariuki et al show that parasite growth is indeed restricted in vivo by infecting Dantu adults under controlled conditions with cryopreserved Plasmodium falciparum sporozoites and analysing parasite growth by qPCR. The authors compare parasite growth, peak parasitaemia and if / when treatment was sought for malaria symptoms between non-Dantu (111) and Dantu heterozygous (27) and homozygous (3) participants. Dantu either completely prevented malaria parasite detection in the blood (for 21 days) or slowed down parasite growth considerably.

The authors present compelling in vivo evidence that Dantu conveys protection by preventing malaria parasites from establishing a blood-stage infection. Because the effect on parasite growth is crystal clear the link to uncomplicated malaria follows - no/less parasites leads to less participants experiencing malaria symptoms and seeking treatment. It should however be noted that the paper does not show that Dantu reduces symptomatology at identical parasite densities to non-Dantu. Its protective effect seems to be purely parasitological.

Given that all volunteers were exposed to malaria prior to being experimentally infected (in various transmission settings ranging from low to high) the authors state that they adjusted for factors like schizont antibody concentration in their multi-variate analysis. More details on the assumptions and which dependent / independent variables were included would benefit interpretation. It would be also good to see if Dantu individuals were spread homogeneously across all transmission settings - if e.g. they all had history of intense malaria exposure and thus strong pre-existing anti-malaria immunity this might account in part for reduced parasite growth when compared to non-Dantu from lower transmission settings. Being able to de-convolute the effect of pre-existing immunity from Dantu would strengthen the paper.

The authors also presents data on other red cell polymorphisms known to modulate malaria infection and improve outcome: G6PD, blood group O, alpha thalassaemia and ATP2B4. However, no statistically significant differences between non-carriers and hetero/homozygous individuals were observed. This is probably because these mutations exert their effect not directly on parasite growth but modulate disease symptoms when parasite burden is high - which cannot be investigated in controlled human malaria infection settings as ethical considerations mandate treatment of all volunteers at parasite densities >500 parasites/ ul or any parasitaemia with symptoms. Controlled infections need to be complemented with other methods to understand the protective impact of genetic polymorphisms.

Reviewer #2 (Public Review):

The large genetic association studies conducted in East Africa have shown that the Dantu blood group provides substantial protection against severe malaria. The proposed mechanism of protection is reduced red cell invasion resulting in reduced parasite multiplication. This hypothesis was tested in adult Kenyan volunteers infected with P. falciparum under careful monitoring. The strength of the study is that the CHMI model using a single parasite strain has few confounders and it provides a very clear answer. The data reported on the other "protective" genetic polymorphisms is also fascinating. The hypothesis that Dantu reduces merozoite invasion has some support from previous laboratory studies, but it would be useful to confirm, once invasion is successful, that intraerythrocytic growth is unimpaired (e.g. count merozoites per schizont, measure asexual cycle length etc).

Reviewer #1 (Public Review):

In this manuscript the authors describe a new method for perturbing chromatin in living cells by delivering a local temperature gradient. Employing this approach, the authors uncover interesting behaviors that underscore the variability in the mechanical response of subnuclear domains and structures. The combination of a new experimental tool that should be accessible to many users and new insights are compelling, although there is the need for some controls and a broader discussion of prior work.

Strengths:<br /> 1. There is a need for non-invasive methods for probing the mechanical properties of chromatin, and nuclei and the approach developed by the authors has strong potential to be of broad utility.<br /> 2. By and large the authors provide a reasonable characterization of the technical aspects of the method, for example how local temperatures rise and the propagation of the temperature gradient relative to the rastering of the IR laser.<br /> 3. The findings that different chromatin compartments respond in distinct manners, in ways perhaps that were not intuited previously (for example, the highest level of deformation for "medium dense" chromatin domains regions), is provocative and raises new ideas about how the chromatin polymer and diffusible nuclear constituent molecules in different domains together contribute to the mechanical response.<br /> 4. The method provides insights into the viscoelastic properties of different chromatin domains, particularly different time scales of behavior, that have been challenging to access with existing approaches.<br /> 5. The authors provide new measurements of the behavior of nucleoli, which leads to insights that will impact our view of the mechanical behavior of such organelles.

Weaknesses:<br /> 1. Direct or indirect effects of the temperature gradient on the integrity of the DNA needs to be addressed, as this could influence the response particularly given the observation that there is a ~15% of the response that is not reversible (see next point).<br /> 2. The authors do not probe the basis for the irreversibility of the chromatin response, which seems to perhaps differ between different chromatin regions. The underlying factors that underlie this need to be further explored.<br /> 3. The authors need to acknowledge the time scales of behaviors that can be revealed using the approach and how this influences their observations. For example, they observe the creep behavior on the 1 second timescale, which is an order of magnitude below observations of the behavior of whole nuclei (~15 seconds) for nuclei from mammalian to yeast that has been suggested to reflect chromatin flow.<br /> 4. There are numerous studies important for the premise and interpretation of this study that need to be considered/cited.

Reviewer #2 (Public Review):

In this manuscript, Seelbinder et al, introduce a novel, elegant approach to study the organization of cell nuclei, which complements currently existing technology. The authors employ localized temperature gradients to move chromatin inside the nucleus noninvasively, and they study flow fields and deformations of different nuclear compartments in different experimental settings. The study is timely and should be of broad interest to a wide readership, in particular since the method can also be applied to study mechanical relationships of subcellular compartments in other cellular and extracellular systems.

The non-invasive manipulation of cell organelles in intact cells has been a challenge for decades. The new technique introduced in this study contributes to closing this important gap, enabling experiments to better understand spatial and mechanical relationships between different cell compartments. This study is a very nice example of how concepts and approaches from physics can be exploited to better understand biology.

Reviewer #3 (Public Review):

Seelbinder et al present local heating of the cell nucleus in live cells as a perturbation of the nucleus, which they use to interrogate mechanical properties of the nucleus. The authors use their recently developed technique of generating local heat gradients (Mittasch et al, 2018) and apply it to the cell nucleus, where they then measure the displacements/strains of chromatin as a function of distance from the heat source. They show that during the heat perturbation the nuclear area and shape remain unchanged. They measure spatially resolved strains across the nucleus and find that different parts of the nucleus exhibit different mechanical behavior. Their analysis reveals that chromatin shows both elastic and viscous properties at the timescales of seconds, with heterochromatin showing solid-like properties. In addition, they find that the nucleolus shows high resistance to the heat-induced deformation at the seconds' timescale.

Conceptually, this is an interesting and thought-provoking work allowing for new ways to perturb the cell nucleus and study its internal mechanics.

Reviewer #1 (Public Review):

In this work, authors seek to understand how the polycomb complex may coordinate gene expression changes that occur during sequential stages of neuronal maturation. The main strengths are 1) choice of cerebellar granule neurons which mature over a protracted period during normal cerebellar development and constitute a relatively homogeneous population of neurons, 2) use of a genetic in vivo mouse model where a histone demethylase is knocked out, combined with an in vitro culture model of maturing cerebellar granule neurons in which a histone methyltransferase is inhibited, 3) use of CUT & TAG in neuronal cultures to investigate how changes in the H3K27me3 repressor chromatin modification at promoters correlate with gene expression and chromatin accessibility changes. The authors propose a bidirectional effect of the same chromatin repressor modification that is responsible, at least in part, for the timely loss of expression of early genes and the appearance of genes expressed later in maturation. This is the major impact of the work for those interested in cerebellar development. A weakness in the work lies in its narrow focus, which is on promoter regions almost exclusively.

The work is primarily bioinformatics driven and lacks physiological significance of the gene expression changes, or how the culture timing correlates with temporal regulation and chromatin changes in vivo. However, the results do support the proposal that polycomb-associated enzymatic activities play sequential roles during successive stages of cerebellar maturation.

Reviewer #2 (Public Review):

Ramesh, Liu et al. investigated the dynamics of the histone H3 lysine 27 trimethyl mark (H3K27me3) in the cerebellum during postnatal development. They profile the mark and measure gene expression at three time points (P7, P14, P60) to show that there is a global increase in the amounts of H3K27me3 genome-wide, but a generalized loss of the mark at promoters. This loss is associated with neuronal genes that become expressed in the mature cerebellum. Through conditional knockout and transcription factor analysis, they implicate the autism-associated lysine demethylase gene KDM6B in the removal of H3K27me3 at genes that become active postnatally and show that the ZIC transcription factors are candidates to mediate some of these effects. They then use pharmacologic inhibition of KDM6B and the PRC2 component, EZH2, in a granule neuron culture system to further dissect the function of these enzymes in H3K27me3 dynamics.

The authors employ multiple genomic methods to carry out rigorously controlled experiments and their conclusions are well supported by the data. The study provides fundamental insights into the dynamics of H3K27me3 during the postnatal development of circuits in the brain. In particular, the findings that substantial changes in the H3K27me3 mark continue through the later steps of cerebellar maturation (P14 to P60) and that the autism-associated gene KDM6B is involved in this process, will be of significant interest to the field.

The study has some limitations with regard to scope and mechanism. For example, given the importance of enhancers in the regulation of gene expression, the omission of any analysis of H3K27me3 at defined enhancer elements is a limitation of the study. In addition, while the observations supporting the role of ZIC proteins in the removal of H3K27me3 during gene activation are interesting, the lack of direct mechanistic analysis investigating this biology limits the strength of the conclusions that can be made about the direct function of these factors in H3K27me3 dynamics.

Reviewer #1 (Public Review):

The authors have studied the effect of temperature on the interspecific interaction strength of coastal marine fish communities, using eDNA samples. Their introduction describes the state of the art concerning the dynamics of interspecific interactions in ecological communities. This introduction is well written and highly information dense, summarizing all that the reader needs to know to further understand their study setup and execution.

The authors hypothesize that water temperature changes could have an effect on the interspecific interaction strength between marine fishes, and they studied this with a two year long, bi-weekly eDNA sampling campaign at 11 study sites in Japan with different temperature gradients. These 550 water samples were analysed for fish biodiversity through eDNA-metabarcoding using MiFish primers. By using the most abundant fish species as an internal spike in and quantifying the copy numbers from this species by qPCR, the authors were able estimate DNA copy numbers for the total dataset. From the 50 most frequently detected fish species in these samples they showed that temperature affected the interspecific interaction strength between some species. Their work provides a highly relevant approach to perform species-interaction strength analysis based on eDNA biodiversity assessments, and as such provides a research framework to study marine community dynamics by eDNA, which is highly relevant in the study of ecosystem dynamics. The models and analytical methods used are clearly described and made available, enabling application of these methods by anyone interested in applying it to their own site and species group of interest.

Strengths: The authors have a study setup that is suitable to measure the effects of temperature of the eDNA diversity, and have taken a large number of samples and all appropriate controls to be able to accurately measure and describe these dynamics. The applied internal spike in to enable relative eDNA copy number quantification is convincing.

Weaknesses: The authors aim to study the relationship between species interaction strength and ecosystem complexity, and how temperature will influence this. However, there is only limited ecological context discussed explaining their results, and a link with climate change scenario's is also limited. A further discussion of this would have strengthened the manuscript.

The authors were able to find a correlation between water temperature and interaction strengths observed. However, since water temperature is dependent on many environmental variables that are either directly or indirectly influencing ecosystem dynamics, it is hard to prove a direct correlation between the observed changes in community dynamics and the temperature alone.

Reviewer #2 (Public Review):

In this work Ushio et al. combine environmental DNA metabarcoding with novel statistical approaches to demonstrate how fish communities respond to changing sea temperatures over a seasonal cycle. These findings are important due to the need for new techniques that can better measure community stability under climate change. The eDNA metabarcoding dataset of 550 water samples over two years is, I feel, of sufficient scale to provide power to detect fine-scale ecological interactions, the experiments are well controlled, and the statistical analysis is thorough.

The major strengths of the manuscript are: (1) the magnitude of the dataset, which provides densely replicated sampling that can overcome some of the noise associated with eDNA metabarcoding data and scale up the number of data points to make unique inferences; (2) the novel method of transforming the metabarcode reads using endogenous qPCR "spike-in" data from a common reference species to obtain estimates of DNA concentration across other species; and (3) the statistical analysis of time-series and network data and translating it into interaction strengths between species provides a cross-disciplinary dimension to the work.

I feel like this kind of study showcases the power of eDNA metabarcoding to answer some really interesting questions that were previously unobtainable due to the complexities and cost of such an exercise. Notwithstanding the problems associated with PCR primer bias and PCR stochasticity, the qPCR "spike-in" method is easy to implement and will likely become a standardised technique in the field. Further studies will examine and improve on it.

Overall I found the manuscript to be clear and easy to follow for the most part. I did not identify any serious weaknesses or concerns with the study, although I am not able to comment on the more complex statistical procedures such as the "unified information-theoretic causality" method devised by the authors. The section on limitations of the study is important and acknowledges some issues with interpretation that need to be explained. The methods, while brief in parts, are clear. The code used to generate the results has been made available via a GitHub repository. The figures are clear and attractive.

Reviewer #1 (Public Review):

The authors use a combination of structural and MD simulation approaches to characterize phospholipid interactions with the pentameric ligand-gated ion channel, GLIC. By analyzing the MD simulation data using clusters of closed and open states derived previously, the authors also seek to compare lipid interactions between putative functional states. The ultimate goal of this work is to understand how lipids shape the structure and function of this channel.

The strengths of this article include the following:

1) The MD simulation data provide extensive sampling of lipid interactions in GLIC, and these interactions were characterized in putative closed and open states of the channel. The extensive sampling permits confident delineation of 5-6 phospholipid interaction sites per subunit. The agreement in phospholipid binding poses between structures and the all-atom MD simulations supports the utility of MD simulations to examine lipid interactions.

2) The study presents phospholipid binding sites/poses that agree with functionally-important lipid binding sites in other pLGICs, supporting the notion that these sites are conserved. For example, the authors identify interactions of POPC at an outer leaflet intersubunit site that is specific for the open state. This result is quite interesting as phospholipids or drugs that positively modulate other pLGICs are known to occupy this site. Also, the effect of mutating W217 in the inner leaflet intersubunit site suggests that this residue, which is highly conserved in pLGICs, is an important determinant of the strength of phospholipid interactions at this site. This residue has been shown to interact with phospholipids in other pLGICs and forms the binding site of potentiating neurosteroids in the GABA(A) receptor.

Weaknesses of this article include the following:

1) The authors describe in detail state-dependent lipid interactions from the MD simulations; however, the functional significance of these findings is unclear. GLIC function appears to be insensitive to lipids, although this understanding is based on experiments where GLIC proteoliposomes were fused to oocyte membranes, which may not be optimal to control the lipid environment. Without functional studies of GLIC in model membranes, the lipid dependence of GLIC function is not definitively known. Therefore, it is difficult to interpret the meaning of these state-dependent lipid interactions in GLIC.

2) It is unlikely that the bound phospholipids in the GLIC structures, which are co-purified from e. coli membranes, are POPC. Rather, these are most like PE or PG lipids. While it is difficult to accommodate mixed phospholipid membranes in all-atom MD simulations, the choice of POPC for this model, while practically convenient, seems suboptimal, especially since it is not known if PE or PG lipids modulate GLIC function. Nevertheless, it is striking that the overall binding poses of POPC from the simulations agree with those identified in the structures. It is possible that the identity of the phospholipid headgroup will have more of an impact on the strength of interactions with GLIC rather than the interaction poses (see next point).

3) The all-atom MD simulations provide limited insight into the strength of the POPC interactions at each site, which is important to interpret the significance of these interactions. It is unlikely that the system has equilibrated within the 1.7 microseconds of simulation for each replicate preventing a meaningful assessment of the lipid interaction times. Although the authors report exchange of up to 4 POPC interacting at certain residues in M4, this may not represent binding/unbinding events (depending on how binding/interaction is defined), since the 4 Å cutoff distance for lipid interactions is relatively small. This may instead be a result of small movements of POPC in and out of this cutoff. The ability to assess interaction times may have been strengthened if the authors performed a single extended replicate up to, for example, 10-20 microseconds instead of extending multiple replicates to 1.7 microseconds.

Reviewer #2 (Public Review):

The authors convincingly show multiple inner and outer leaflet non-protein (lipid) densities in a cryo-EM closed state structure of GLIC, a prokaryotic homologue of canonical pentameric ligand-gated ion channels, and observe lipids in similar sites during extensive simulations at both resting and activating pH. The simulations not only corroborate structural observations, but also suggest the existence of a state-dependent lipid intersubunit site only occupied in the open state. These important findings will be of considerable interest to the ion channel community and provide new hypotheses about lipid interactions in conjunction with channel gating.

Reviewer #1 (Public Review):

In principle a very interesting story, in which the authors attempt to shed light on an intriguing and poorly understood phenomenon; the link between damage repair and cell cycle re-entry once a cell has suffered from DNA damage. The issue is highly relevant to our understanding of how genome stability is maintained or compromised when our genome is damaged. The authors present the intriguing conclusion that this is based on a timer, implying that the outcome of a damaging insult is somewhat of a lottery; if a cell can fix the damage within the allocated time provided by the "timer" it will maintain stability, if not then stability is compromised. If this conclusion can be supported by solid data, the paper would make a very important contribution to the field.

However, the story in its present form suffers from a number of major gaps that will need to be addressed before we can conclude that MASTL is the "timer" that is proposed here. The primary concern being that altered MASTL regulation seems to be doing much more than simply acting as a timer in control of recovery after DNA damage. There is data presented to suggest that MASTL directly controls checkpoint activation, which is very different from acting as a timer. The authors conclude on page 8 "E6AP promoted DNA damage checkpoint signaling by counteracting MASTL", but in the abstract the conclusion is "E6AP depletion promoted cell cycle recovery from the DNA damage checkpoint, in a MASTL-dependent manner". These 2 conclusions are definitely not in alignment. Do E6AP/MASTL control checkpoint signaling or do they control recovery, which is it?<br /> Also, there is data presented that suggest that MASTL does more than just controlling mitotic entry after DNA damage, while the conclusions of the paper are entirely based on the assumption that MASTL merely acts as a driver of mitotic entry, with E6AP in control of its levels. This issue will need to be resolved.

Finally, the authors have shown some very compelling data on the phosphorylation of E6AP by ATM/ATR, and its role in the DNA damage response. But the time resolution of these effects in relation to arrest and recovery have not been addressed.

Reviewer #2 (Public Review):

This is an interesting study from Admin Peng's laboratory that builds on previous work by the PI implicating Greatwall Kinase (the mammalian gene is called MASTL) in checkpoint recovery.

The main claims of this study are:

1) Greatwall stability is regulated by the E6-AP ubiquitin ligase and this is inhibited following DNA damage in an ATM dependent manner.<br /> 2) Greatwall directly interacts with E6-AP and this interaction is suppressed by ATM dependent phosphorylation of E6-AP on S218<br /> 3) E6-AP mediates Greatwall stability directly via ubiqitylation<br /> 4) E6-AP knock out cells show reduced ATM/ATR activation and quicker checkpoint recovery following ETO and HU treatment<br /> 5) Greatwall mediated checkpoint recovery via increased phosphorylation of Cdk substrates

In my opinion, there are several interesting findings presented here but the overall model for a role of the E6-AP -Greatwall axis is not fully supported by the current data and will require further work. Moreover, there are a number of technical issues making it difficult to assess and interpret the presented data.

Major points:

1) The notion that Greatwall is indeed required for checkpoint recovery hinges on two experiments shown in Figures 5A and B where Greatwall depletion blocks the accumulation of HELA cells in mitosis following recovery from ETO treatment and in G2/M following release from HU. An alternative possibility to the direct involvement of Greatwall in checkpoint recovery could be that Greatwall in HeLA cells is required for S-phase progression (as for example Charrasse et al. suggested). A simple control would be to monitor the accumulation of mitotic cells by microscopy or FACS following Greatwall depletion without any further checkpoint activation.

2) The changes in protein levels of Greatwall and the effects of E6-AP on Greatwall stability are rather subtle and depend mostly on a qualitative assessment of western blots. Where quantifications have been made (Figures 2D and 4F) the loading control and the starting conditions for Greatwall (0 timepoints in the right panel) appear saturated making precise quantification impossible. I would argue that the authors should at least quantify the immuno-blots that led them to conclude on changes in Greatwall levels and make sure that the exposure times used are in the dynamic range of the camera (or film). A more precise experiment would be to use the exogenously expressed CFP-Greatwall that is described in Figure 6 and measure the acute changes in protein levels using quantitative fluorescence microscopy in live cells. This is, in my opinion, a lot more trustworthy than quantitative immuno-blots.<br /> I also note here that most experiments linking Greatwall levels to E6-AP were done using siRNA, while the E6-AP ko cells would be a more reliable background for these experiments, especially with reconstituted controls.

3) This study has no data linking the effects of Greatwall to its canonical target PP2A:B55. The model shown in Figure 9 is therefore highly speculative. The possibility that Greatwall could act independently of PP2A:B55 should at least be considered in the discussion given the lack of experimental evidence.

4) The major effect of E6-AP depletion on the checkpoint appears to be a striking reduction in ATM/ATR activation, suggesting that this ubiquitin ligase is involved in checkpoint activation rather than recovery. It is not clear if this phenotype is dependent on Greatwall. If so it would be hard to reconcile with the default model that E6-AP acts via the destabilisation of Greatwall. In the permanent absence of E6-AP, increased Greatwall levels should inactivate B55:PP2A. How would this lead to a decrease in ATM/ATR activation? This is unlikely, and indeed Figure 5E shows that the reduction of MASTL in parallel to E6-AP does not result in elevated levels of ATR/ATM activation. Conversely, the S215A E6-AP mutant does have a strong rescue impact on ATR/ATM (Figure 8D).

5) In summary, I do not think that the presented experiments clearly dissect the involvement of E6-AP and Greatwall in checkpoint activation and recovery. E6-AP depletion has a strong effect on checkpoint activation while Greatwall depletion is likely to have various checkpoint-independent effects on cell cycle progression.

Reviewer #3 (Public Review):

In this manuscript, Li et al. describe the contribution of the ATM-E6AP-MASTL pathway in recovery from DNA damage. Different types of DNA damage trigger an increase in protein levels of mitotic kinase MASTL, also called Greatwall, caused by increased protein stability. The authors identify E3 ligase E6AP to regulate MASTL protein levels. Depletion or knockout of E6AP increases MASTL protein levels, whereas overexpression of E6AP leads to lower MASTL levels. E6AP and MASTL were suggested to interact in conditions without damage and this interaction is abrogated after DNA damage. E6AP was shown to be phosphorylated upon DNA damage on Ser218 and a phosphomimicking mutant does not interact with MASTL. Stabilization of MASTL was hypothesized to be important for recovery of the cell cycle/mitosis after DNA damage.

The identification of this novel pathway involving ATM and E6AP in MASTL regulation in the DNA damage response is interesting. However, is surprising that authors state that not a lot is known about DNA damage recovery while Greatwall and MASTL have been described to be involved in DNA damage (checkpoint) recovery. In addition, PP2A, a phosphatase downstream of MASTL is a known mediator of checkpoint recovery, in addition to other proteins like Plk1 and Claspin. Although some of the publications regarding these known mediators of DNA damage recovery are mentioned, the discussion regarding the relationship to the data in this manuscript are very limited.

The regulation of MASTL stability by E6AP is novel, although the data regarding this regulation and the interaction are not entirely convincing. In addition, several experiments presented in this paper suggest that E6AP is (additionally) involved in checkpoint signalling/activation, whereas the activation of the G2 DNA damage checkpoint was described to be independent of MASTL. Has E6AP multiple functions in the DNA damage response or is ATM-E6AP-MASTL regulation not as straightforward as presented here?

Altogether, in my opinion, not all conclusions of the manuscript are fully supported by the data.

Reviewer #1 (Public Review):

In this report, the authors use what they describe as a novel phenotypic survival screening method to uncover ATP-dependent kinases that may show synthetic lethality (when inhibited) with BRCA2 loss. Interestingly, they find that inhibiting ROCK kinases in BRCA2 deficient cells (but not BRCA1 deficient cells), triggers synthetic lethality. They further show that the synthetic lethality is independent of acute replication stress and is preceded by enhanced M-phase defects (anaphase bridges and abnormal mitotic figures). These data, therefore, suggest a new pathway (ROCK kinases) that may be targeted to induce synthetic lethality in BRCA2 deficient cells.

Reviewer #2 (Public Review):

This paper describes a novel synthetic lethal interaction between BRCA2 loss and the cytokinesis regulators, including ROCK. The SL effects are restricted to short-term in vitro assays, and the underlying mechanisms remain largely elusive. The impact of the work in its current form is limited.

Strengths:<br /> - A novel synthetic lethal (SL) interaction, which appears independent from the -BRCA2 SL interaction that depends on replication fork stalling and DNA damage induction.<br /> - The SL interaction is validated in a panel of genetic models of BRCA2 deficiency.<br /> - The SL interaction can be induced using clinically approved agents.

Weaknesses<br /> - The evidence that this SL interaction is independent of replication defects is not solid.<br /> - The SL interaction is based on chemical inhibitors only, with 6 out of 9 ROCK inhibitors not demonstrating the SL interaction.<br /> - The mechanisms by which ROCKi specifically affects BRCA2-defective cells are elusive.<br /> - It remains unclear what the cause of the multiple mitotic defects is.

Combined, it remains unclear if the identified SL interaction is therapeutically meaningful. Clinical stage inhibitors are available, and various BRCA2-deficient cancer models have been described, allowing the authors to address this in long-term in vitro assays and in vivo assays. Also, the authors describe multiple phenotypic consequences, but the order of events and the reason why the effects are specific to BRCA2 remain largely unclear. Furthermore, the notion that the observed effects are independent of replication defects requires further substantiation.

Reviewer #3 (Public Review):

Martino et al. demonstrated that BRCA2-deficient cells (but not BRCA1-deficient cells) bear additional vulnerabilities (i.e., cytokinesis failure) outside S phase that could represent new synthetic lethality targets. Strengths of the study include the ability of the authors to recapitulate the cell death by ROCK inhibition by inhibiting another key cytokinesis enzyme, CITK. The claims are well supported by the data, and because the study indicates HR failure/replication stress is not the only possible way to achieve synthetic lethality in BRACA mutant cancers the study will be of broad interest to potential readers.

Reviewer #1 (Public Review):

The manuscript by Zheng et al. examined the disease-causing mechanisms of two missense mutations within the homeodomain (HD) of CRX protein. Both mutations were found in humans and can produce severe dominant retinopathy. The authors investigated the two CRX HD mutants via in vitro DNA-binding assay (Spec-seq), in vivo chromatin-binding assay (ChIP-seq), in vivo expression assay of downstream target genes (RNA-seq), and retinal histological and functional assays. They concluded that p.E80A increased the transactivation activity of CRX and resulted in precocious photoreceptor differentiation, whereas p.K88N significantly changed the binding specificity of CRX and led to defects in photoreceptor differentiation and maintenance. The authors performed a significant amount of analyses. The claims are sufficiently supported by the data. The results not only uncovered the underlying disease-causing mechanisms, but also can significantly improve our understanding of the interaction between HD-TF and DNA during development.

Minor concerns:<br /> 1. The E80A, K88N and R90W (previously reported by the same group) mutations are located very close to each other in the homeodomain (Figure 1A), but had distinct effects on the activity of CRX. Has the structure of the homeodomain (of CRX) been resolved? If so, could the authors discuss this phenomenon (mutations close to each other but have distinct effects) based on the HD-DNA structure? In addition, has this phenomenon been observed in other homeodomain TFs?<br /> 2. The authors should briefly summarize the effects/disease-causing-mechanisms of all the reported CRX mutations in the discussion part. The readers can then have a better overview of the topic.<br /> 3. CRX can also function as a pioneer factor (reported by the same group). Would these HD mutations distinctively affect chromatin accessibility (which then leads to ectopic binding on the genome)?<br /> 4. The discussion part can be shortened and simplified.

Reviewer #2 (Public Review):

Zheng et al., investigated the molecular and functional mechanisms of two homeodomain missense mutations causing human retinal photoreceptor degeneration diseases in photoreceptor development regulated by the CRX transcription factor. They analyzed the E80A mutation associated with dominant cone-rod dystrophy (CRD) and the K88N mutation associated with dominant Leber Congenital Amaurosis (LCA). The authors found that E80A CRX binds to the same target DNA sites as WT CRX, but the binding specificity of K88N CRX is altered from that of WT in an in vitro assay. They generated Crx(E80A) and Crx(K88N) KI mice and performed ChIP assay and observed that K88N CRX binds to novel genomic regions from the WT-binding sites, while E80A binds to the WT sites. In addition, using the KI mice, they found that E80A and K88N differently affect the expression of Crx target genes. This study is well executed with proper and solid methodologies, and the manuscript is clearly written. This study gives us the insights how single missense CRX mutations lead to different types of human retinal photoreceptor degeneration diseases.

While the study has strengths in principle, it has a couple of weaknesses. One is how well E80A KI mice function as a pathological model of dominant CRD, in which cones are mainly first affected, is not clearly shown in this study. More data investigating how cones are affected by performing histological, molecular, and physiological analyses will be helpful and useful. For example, in the Discussion, the authors describe that E80A associates with S-cone opsin promoter results is "data now shown". This data must be presented for the readers. In addition, more molecular insights as to how E80A affects cones will strengthen this study. Another point is that it will be very valuable if the authors could show how E80A and K88N differently affect the 3D structure of the CRX homeodomain. Even a simulation model would be valuable.

Reviewer #1 (Public Review):

Zhou et al. investigated the factors that regulate mitotic chromosome size scaling during the early embryo divisions in Xenopus laevis using imaging of intact whole embryos and of embryo extracts with different sources of nuclei. They find that chromosome volume decreases during embryogenesis, and scales with nuclear and spindle volume throughout a broad range of embryo stages (stages 3 to 9) and cell sizes. They show that extracts from stage 3 or stage 8 embryos demonstrate significant differences in chromosome length, mirroring changes to chromosome volume observed in vivo. Using extracts from eggs or stage 8 embryos, and nuclei from sperm or stage 8 embryos, the authors demonstrate that chromosome length is dictated by the chromosomes and not the maternal mitotic environment, and find that the major determining factor is the amount of condensin I loading on mitotic chromosomes, which they correlate to changes in DNA loop size and layering. Interestingly, they find that the prior state of nuclei prior to entry into mitosis dictates mitotic chromosome length. They attribute this phenomenon to the nuclear to-cytoplasmic ratio during the prior interphase and suggest that some factor is titrated on chromatin that sets condensin I loading in mitosis. Notably, they found that chromosome length does not scale with nuclear or spindle size in vitro. In another set of experiments, the authors found that artificially increasing the palmitoylation of importin resulted in decreased chromosome length. However, this scaling effect is not due to condensin I loading differences, but to some unidentified importin cargo that would get released as cell size decreases during development. Overall, the conclusions of this paper are well supported by data, but some aspects of data interpretation and analysis need to be clarified and extended. The approaches used here are quite impressive and creative and provide compelling evidence for factors that regulate chromosome scaling during development in a vertebrate organism.

Reviewer #2 (Public Review):

In this work from Zhou et al., the authors address mechanisms of mitotic chromosome size scaling during development. Their approach, which employs complementary use of in vivo (Xenopus embryos) and in vitro systems (Xenopus extracts), rendered investigation of this relationship experimentally tractable and allowed the authors to convincingly demonstrate that mitotic chromosome scaling is mediated by differential loading of maternal chromatin remodeling factors during interphase. The authors show that this scaling is dependent on an increasing nucleo-cytoplasmic (N/C) and that condensin I is titrated away from chromosomes as the N/C ratio is increased. Interestingly, the authors found that spindle and nuclei did not scale with changes in N/C ratio, suggesting that although mitotic chromosome scaling correlates with spindle and nuclei scaling, it is mechanistically distinct. Complementary Hi-C analyses of chromatin architectures of both larger condensin I-rich chromosomes and smaller condensin I-poor chromosomes support a condensin-based looping model to explain the inverse relationship between chromosome-associated condensin and chromosome length, however, this model seems somewhat contrived due to inherent limitations of the approach. A characterization of an independent importin-α-dependent mitotic chromosome scaling mechanism, though potentially interesting, is too premature to be included and a bit of a non sequitur in terms of the overarching narrative and major findings of the work. Though there is some room for improvement in terms of image analysis and measurements, the work is well-written, comprehensive in scope, and addresses a fundamental biological question. Furthermore, the authors' major conclusions and substantive claims are well-supported by the experimental results.

Reviewer #3 (Public Review):

In the work by Zhou, et.al., the authors pursue a mechanistic understanding of chromosome size scaling in development, a problem first noted in 1912 by Conklin and largely unstudied until very recently. Using the tools available in the Xenopus genus developmental biology system (cell extracts, related species of differing size, etc.), they nicely show that condensin I levels directly correlates with chromosome size. Further, importin levels decrease leading to axial shortening of chromosomes during development. The combined physical outcome is that Mitotic Chromatin looping changes, resulting in axial compression of chromosomes. This work represents a major step in the molecular understanding of how the genome is regulated through development and changing cell size, which also occurs in many other adult tissues and cancers. Further work to understand other contributing factors and understanding how loop structure changes the polymer dynamics of mitotic chromatin will be exciting in the future.

Peer review report

Title: Publication Patterns and Perceptions of Open Science in Indian Scholarly Community: Insights from a Survey

version: 2

Referee: Moumita Koley

Institution: Indian Institute of Science, Bangalore, India

email: moumitakoley@iisc.ac.in

ORCID iD: 0000-0003-2394-0663

General assessment

The author of the article provides a limited perspective on Publication Patterns and Perceptions of Open Science in the Indian Scholarly Community. This article sheds some light on open science practices, considering the scarcity of data on this topic. The main drawbacks, the survey conducted in the article is the only methodology used, and it is limited to a small group of researchers. Understanding publication patterns (Open Access publication and use of preprints) should be made using bibliometric studies. Another drawback of the article is that it primarily focuses on researchers from the agriculture field, which is over-represented and makes it misleading to claim that the study represents the entire Indian scholarly community. This is particularly problematic since the physical and chemical sciences dominate the Indian research community, and data from these fields are entirely absent in the article.

Essential revisions that are required to verify the manuscript

This study is at an early stage; more data points and representations of various fields are necessary to claim validity. Moreover, a mixed-method approach is more suitable.

Other suggestions to improve the manuscript

The introduction section mentions several preprint servers, but some are not operational. For example, ArabiXiv is not accepting new submissions, and IndiaRxiv has few submissions. Since there are limited responses from other South Asian countries, the author has chosen to focus on India. However, it is unclear if the percentages of career levels of professionals are representative of India alone.

One drawback of this article is the over-representation of researchers from the agriculture field. In the Indian ecosystem, agricultural research institutes are separate from the general university system and governed by different funding and governance systems. Therefore, the norms and practices can vary significantly.

In the STEM subjects, Chemical Sciences contributed the most publications in India from 2015-2019, followed by Physical Sciences. Biological Sciences had fewer publications during this period(the method used for this statement: a quick search in the Web of Science). However, this data does not represent the publication behaviour of the major constituents (Physical and Chemical Science) of the Indian academic community. Therefore, it is suggested to shift the narrative towards agricultural science.

The statement "patent and scholarly data website, India has produced 19,76,966 scholarly works till date" lacks a timeframe.

The APC section statements are unclear. As far as current knowledge goes, no study has shown a correlation between JIF and APC. The statement "Was it because of JIFs they must publish in Open Access when there is Green Route to Open Access (depositing in subject or institutional repositories)" is unclear. Moreover, while Indian national funding agencies have green OA mandates, they have not been enforced. Several studies indicate that Indian researchers' adoption of green OA is low, so authors have no obligation to publish OA.

The article concludes that advocacy is needed, but it is essential to understand the research assessment frameworks of Indian academia and funding agencies. Without recognition in assessment, researchers are unlikely to adopt Preprints. Preprint submission is becoming the norm in some disciplines, which may improve the situation.

Decision

Requires revisions: The manuscript contains objective errors or fundamental flaws that must be addressed and/or major revisions are suggested.

Reviewer #3 (Public Review):

International researchers from the International Agency for Research on Cancer and cancer screening program experts from six countries in Latina America (Argentina, Colombia), Asia (Sri Lanka, Bangladesh, Thailand), and Northern Africa (Morocco), provide detailed information on the impact of the COVID Pandemic on cancer screening and diagnostic services.

The authors examine countries that have had screening programs and a surveillance system/registry to see how the volume of screening, diagnostic procedures, and detection of precancers or cancers are impacted. The data are presented as case studies with an explanation of the program, the technologies, and then the impact. They describe no matter how low or high income the country, there was a considerable impact on the volume of screening.

Usually, the impact of the pandemic on cancer screening has been limited to Europe or North America and is usually not quantified. This information will be helpful for these countries to examine the impact on stage distribution and eventually mortality impact through modeling studies. The authors also comment on some interesting hypotheses such that the impact on recovery based on if one is detecting precancers (e.g. colon cancer/cervical cancer) vs. invasive cancers (breast cancer). Strategies that require less frequent screening,self-collection, where screening and treatment can be combined in fewer visits, or where some visits can occur via telehealth are valuable strategies or lessons learned that will allow for quicker recovery time after a pandemic.

The authors acknowledge the limitations and strengths of these case-based studies well.

It is beautiful storytelling with both qualitative and quantitative data.

Reviewer #1 (Public Review):

The impact of the COVID-19 pandemic on cancer screening, diagnosis, referrals, and management has been well documented in high-resourced countries; but such quantitative estimates are rarely available from low- and middle-income countries (LMIC). The authors chose two very high human development index (HDI) category LMICs (Argentina and Thailand), two high HDI category LMICs (Colombia and Sri Lanka), and two medium HDI category LMICs (Bangladesh and Morocco), and looked at available data for cervical, breast, and colorectal cancer screening. The authors demonstrate that the reduction in the test volumes during the pandemic (2020) versus the previous year (2019) was quite comparable to that observed in high-income countries. Additionally, some countries demonstrated resilient catch-up of programmatic performance within a short period of time after the disruptions.

Major strengths include the use of national-level data estimates from key focal points for the CancScreen-5 project, an international data repository of cancer screening programmatic data, the use of appropriately comparable monthly estimates in the pre-pandemic vs. pandemic year, and representation of illustrative case studies from six countries across the medium-to-very high HDI status among LMICs.

Weaknesses include inherent limitations of such real-world outcome/registry data, lack of data across the screening continuum, inability to explore granular-level country-specific factors affecting disruptions as well as catch-up of screening, and high variability of performance of screening tests (especially those with subjective interpretation such as VIA for cervical cancer or clinical breast exam) across the comparison periods such that screen positivity rates may have been affected in unpredictable ways.

The authors have achieved their aims since this descriptive epidemiology analysis provides key estimates from LMICs that have not been explored/evaluated in the literature.

This work will be useful for future studies conducted by health modellers on measuring the impact on late/advanced stage detection and excess case burden and mortality.

Reviewer #2 (Public Review):

The Covid-19 pandemic has had major adverse impacts on cancer screening globally. Despite this, most prior reports have not included observations from LMICs. This paper aims to address this important gap.

Because comparable data were not available across the countries reported here, comparisons would not be appropriate, so the authors chose a case study design, which was a prudent decision and a strength of the work.

The authors make use of data from IARC's CanScreen5 reporting system, which is completely appropriate. In addition, this aspect serves to demonstrate the usefulness of the CanScreen5 system, as it can be used to support this type of study. National data were not available in all countries.

The main findings in the paper describe the early impact of the Covid-19 pandemic on cancer screening participation for the screening programs reported on in the 6 countries that were selected.

I would anticipate that, having demonstrated that this type of case study focusing on cancer screening in LMICs is feasible, this would encourage others to conduct further studies among LMICs, which would be welcomed by the field.

Reviewer #1 (Public Review):

This paper is based on the premise that ketamine exerts antidepressant effects that are rapid by increasing glutamatergic transmission. However, the authors note that how this effect occurs is unclear because ketamine antagonizes the NMDA receptor, a glutamatergic receptor.<br /> Others have suggested a compensatory change in the glutamatergic transmission and the authors suggest how this might occur. The authors should clarify if prior studies suggested a mechanism different from theirs and if so, which might be correct.

There are also other mechanisms, such as the block of NMDA receptors on interneurons and the disinhibition of principal cells. It is important to clarify if this has already been addressed in the literature. Also, if their cultures are primarily glutamatergic neurons or they include interneurons and glia.

The authors show calcineurin is reduced after ketamine exposure and this increases AMPA receptor GluA1 phosphorylation. They also show that Calcium permeable AMPA receptors )CP-AMPARs) increase.

They also use suggest that the CP-AMPARs and other changes lead to enhanced synaptic plasticity, which could lead to antidepressant effects.

Although a lot of work is done in cultured hippocampal neurons, 14 days in vitro, they show effects in vivo that are consistent with the data from cultures. For example, ketamine increases GluA1 phosphorylation. Also, blocking CPAMPARs in vivo reduces anxiety/depressive behaviors such as the open field and tail suspension tests.

Overall the study appears to be done well and the presentation, writing, and references are good. There are important concerns regarding statistics, behavior, and pharmacology and several minor concerns.

Major concerns<br /> 1. Statistics.<br /> What was the stat test if the control was always 1?<br /> Often the control group is 1.00 with no SD but in other tests, the control group is 1.000 with an SD.<br /> e.g., line 145: "(CTRL) (CTRL, 1.000 and ketamine, 1.598 {plus minus} 0.543, p = 145 0.0039), but not GluA2 (CTRL, 1.000 and ketamine, 1.121 {plus minus} 0.464, p = 0.6498"

Line 188:<br /> Here the control group has a SD:<br /> Line 188 CTRL, 1.000 {plus minus} 0.106 and ketamine, 0.942 {plus minus} 0.051, p = 0.0170

2. Behavior.<br /> It is not clear that the open field and tail suspension tests measure antidepressant actions. Why were more standard tests such as forced swim or sucrose preference, novelty-suppressed feeding, etc not used?

3. Pharmacology.<br /> The conclusions rest on the specificity of drugs.<br /> Is 5 uM FK506 specific?<br /> 20 μM 1-naphthyl acetyl spermine (NASPM)?<br /> 10 mg/kg IEM-1460?

Reviewer #2 (Public Review):

The abstract and introduction framework asserts that ketamine's enhancement of excitatory synaptic drive in the hippocampus is presumed to underlie its rapid antidepressant effects. This is not the only, and perhaps not the primary effect mechanism suggested by prior experiments, also strongly implicating disinhibitory effects in the prefrontal cortex as necessary and sufficient to mediate antidepressant effects. Nevertheless, it is valuable to seek mechanistic motifs that provide multiple paths for explaining the seemingly counterintuitive effects where NMDAR blocker enhances excitatory transmission. These need not be conserved across brain regions and cell classes. The primary result of this study demonstrates that 1 hr-long ketamine application to cultured cells reduces calcineurin and GCaMP activity to elevate AMPA receptor subunit GluA1 phosphorylation and enhance the expression of Ca2+-permeable, GluA2-lacking (CP-)AMPARs. These observations are then evaluated in vivo, where calcineurin shows a similar response to ketamine and CP-AMPAR antagonist-abolished ketamine effects on behavior in the open field and tail suspension tests. One significant uncertainty this study helps resolve is whether GluA2-containing AMPARs are removed from synapses or whether GluA2-lacking AMPARs are inserted following ketamine administration. GCaMP imaging, FRET and glutamate uncaging assays provide a strong complement to biochemistry and in vivo data. There are several significant technical and conceptual limitations in this work, which substantially limit the extent of conclusions that can be drawn at this point.

1. The age of neurons in cell culture experiments was 14 days in vitro (DIV), representing developing cultures that are just starting to form synapses. How these effects carry over to more mature cultures or adult animals is unclear.

2. Phosphorylation analyses, forming the foundation of this work, are carried out 1 hr after ketamine treatment. This is prior to the observed clinical effects of ketamine and this point should be acknowledged. Whether and how long this effect lasts remains to be examined. If the goal is to highlight the earliest likely effects of ketamine that should precede potential clinical effects, this should be acknowledged, and in that case, the onset of effects should be clarified. At this point, the temporal features remain undersampled, with a single time-point.

3. A lower dose (50%) treatment was used to evaluate potential sex differences in ketamine effects, which is not sufficiently justified, except post hoc based on behavioral data. The discussion section does consider potential factors that can account for observed differences.

4. The 1-hr timeline to behavioral testing is fast, relative to clinical effects on behavior as well as behavioral effects measured in most studies using mouse models.

5. Tail suspension test is broadly acknowledged as an inadequate model of antidepressant effects.

6. There is no evidence from the in vivo experiments that effects in the hippocampus are due to direct actions of ketamine, as those reported for the cell culture studies. Intraperitoneal injections cannot be used to localize primary effects in vivo to the hippocampus, which would require local delivery.

7. If (MNI)-caged L-glutamate was used at 1 μM concentration, as stated in methods, this is considerably below typical concentrations reported in the literature.

Reviewer #3 (Public Review):

Ketamine has been shown to be effective at producing a rapid-antidepressant effect at low doses, but the underlying molecular mechanism of this effect is still not clear. Previous studies have suggested that the effect of low-dose ketamine may occur by promoting neuronal plasticity in the hippocampus. However, this goes against the findings that ketamine acts as a noncompetitive NMDA receptor antagonist, which should prevent NMDAR-dependent plasticity. Furthermore, a therapeutic dose of ketamine has been shown to increase neuronal Ca2+ signaling, which again does not conform to its antagonistic action on NMDA receptors. In this paper, the authors provide evidence that therapeutic low-dose ketamine increases the expression of Ca2+-permeable AMPA receptors (CP-AMPARs) by increasing phosphorylation of GluA1 subunit of AMPARs and surface expression of GluA1-containing CP-AMPARs. They further provide evidence that this is likely mediated by a decrease in calcineurin activity and that blocking CP-AMPARs prevent the antidepressant effect of ketamine in mice. One interesting finding of this study is that the authors see heightened sensitivity of ketamine in female mice, both at the level of behavioral readout and for molecular correlates. This finding is interesting in light of the different pharmacokinetics of ketamine reported in females and that ketamine metabolites can bind estrogen receptors.

Based on their data and previous findings, the authors outline a plausible molecular signaling mechanism for the antidepressant effect of ketamine. Specifically, the authors propose that reduced neuronal activity, which could be triggered by ketamine-induced NMDAR antagonism, causes homeostatic plasticity to upregulate GluA1-containing CP-AMPARs. Their data would support this idea, as phosphorylation of GluA1 as well as increased surface expression and functional incorporation of CP-AMPARs at synapses have been shown before in models of homeostatic plasticity.

Overall, the study is well-done and the data presented support the main conclusions. One main question is whether the current finding provides a conceptual advancement in our understanding of the molecular signaling involved in ketamine's antidepressant effects. There are previous studies that showed an increase in CP-AMPARs in the nucleus accumbens and an increase in the expression of GluA1 in the hippocampus with low-dose ketamine. In addition, ketamine's antidepressant effect has been shown to require GluA1 phosphorylation. The main contribution of this paper might be that it provides the potential molecular signaling within the same preparation (i.e. hippocampal neurons) and provides a causal link of CP-AMPARs in mediating the behaviorally measured antidepressant effect of ketamine.

Another question is whether the behavioral effect of ketamine is due to molecular changes in the hippocampus as outlined in this paper. A more targeted inhibition of CP-AMPAR function could resolve this issue. With the systemic application of CP-AMPAR antagonist as done in this study, it would be hard to know the role of CP-AMPAR upregulation in the hippocampus in mediating ketamine's effect. Especially, considering that low-dose ketamine has been shown to upregulate CP-AMPARs in the nucleus accumbens. While it would have been nice to know the site of action, this does not alter the conclusion that CP-AMPARs are involved in mediating the antidepressant effect of ketamine on behavioral readouts.

Reviewer #1 (Public Review):

The essentiality of Rv1636 has previously been predicted in numerous genetic studies. Here, the authors provide evidence that Rv1636 is an essential protein in Mtb. The authors report that chromosomal deletion of the gene encoding Rv1636 is only possible when an additional copy of the wild type gene is provided at the L5 integration site in the chromosome. While this is a standard method of demonstrating gene/protein essentiality in this system, the manuscript only provides a PCR reaction with "no amplicon" as proof of a double crossover event in an engineered merodiploid strain (Fig 6C). The authors fail to provide definitive evidence for a double crossover mutation in the merodiploid using primers that amplify a double crossover-dependent amplicon or the authors should a provide a southern blot demonstrating evidence for a bona fide double crossover event. The authors suggest that silencing the gene encoding Rv1636 with a CRISPRi system decreases viability of Mtb when a silencing guide RNA is expressed following Atc addition and spot plated onto agar. These studies lack a "no Atc control" and it is unclear how Mtb colonies appear after 6-7 days in these studies given the slow growth of this bacterium.

A sub-point of the manuscript describes the genetic organization around the gene that encodes Rv1636 in various Mycobacterial spp. Figure 1 also highlights the putative transcriptional start sites for the gene encoding Rv1636. The putative transcriptional start site information is just a summary of work from other groups and this information adds little to the main goals of this manuscript.

Another sub-point of this manuscript is that Rv1636 may be secreted by Mtb in a SecA2 dependent manner. The authors demonstrate that Rv1636 is not present in the culture filtrate of Mtb lacking SecA2 (Fig 2). However, these data are difficult to interpret without a secreted protein "loading control" which is typical for these types of experiments. The authors also report the development of a luciferase-based detection method for quantifying protein secretion in Mtb and use this to support their conclusion. This is a new tool that could be useful in detecting secreted proteins in Mtb. However, this method is not rigorously validated in these studies and do not present controls for cell lysis for example. Additionally, the authors fuse a ~19 kDA luciferase subunit to the C-terminus of CFP10 as a reporter for Esx1-dependent secretion. It is known that this region of CFP10 is critical for interactions with secretory components of the Esx1 system fractionation and it unclear if the CFP10 fusion protein is actually secreted.

The authors explore the idea that Rv1636 may potentially function as a "sink" for cAMP and quantify the molar amounts cAMP, ATP, and Rv1636 in Mtb. These studies demonstrate that the molar amounts of Rv1636 exceeds the levels of cAMP (free or protein-bound) in the cytosol of the Mtb. The authors conclude that the excess of Rv1636 may potentially be a "sink" for unbound cAMP but do not test this idea experimentally in Mtb due to the very low levels of cAMP in this bacteria.

Instead, the authors continue exploring the idea that specific proteins can serve as a cAMP "sink" using M. smegmatis (Msm) since this bacterium produces more cAMP (~25x) in the cytosol compared to Mtb. The authors present data that over expression of Rv1636 in Msm increases the amount of protein-bound cAMP. It is presumed here that the protein-bound cAMP is bound to Rv1636. Alternatively, deleting the Rv1636 homolog in Msm (MSMEG_3811) results in an increase in the amount of "free cAMP". Again, it is presumed that deleting the cAMP binding protein MSMEG_3811 is responsible for the increase in the amount of "free cAMP" in the cell.

Lastly, the authors use two small molecule compounds that may bind Rv1636 and demonstrate some level of bacterial inhibition using a spot plating method. No evidence is provided to demonstrate that these compounds are specifically binding/inhibiting Rv1636. These studies are lacking rigorous demonstration of "on target" inhibition and add very little to the reliable conclusions in this paper.

Reviewer #2 (Public Review):

In this paper by Banerjee et al., the authors described the potential role of two universal stress proteins in M. smegmatis and M. tuberculosis in regulating intracellular free cAMP concentration, which was a unique observation. The experiments were logically designed to prove the expression and interactions; it would have been worthwhile to explore beyond to gain an insight into how the changing levels of free cAMP could modulate any key phenotypes in the bacteria such as virulence, antibiotic resistance, etc. in the content of knockout/knockdown and overexpression of MSMEG_3811 and Rv1636 in individual organisms. The preliminary data of natural inhibitor STOCKIN43384 impacting the survival of M. smegmatis was interesting, but authors need to prove the MOA by using knockdown and overexpression strains of Rv1636.

Reviewer #3 (Public Review):

This paper describes fundamental work which attempts to understand how universal stress proteins Rv1636/Msmeg3811 function as a sink allowing mycobacteria to use intra-bacterial cAMP. Because cAMP is a major second messenger, Rv1636 remains essential to mycobacteria. A compound that inhibits cAMP binding of Rv1636 also can effectively inhibit mycobacterial growth. The major strength of the manuscript is that the authors probed their hypothesis by different approaches. In general, the conclusions from the results are largely justified. However, I find the manuscript quite difficult to follow. Also, the results and functional analyses are inadequate as they rely on a limited set of experiments, thereby making the evidences less than compelling.

Reviewer #2 (Public Review):

The evolution and control of the three-part life history of holometabolous insects have been controversial issues for over a century. While the functioning of broad as a master gene controlling the pupal stage and of E93 as a master gene for the adult stage has been known for about a decade or more, chinmo has only recently been proposed as being the master gene responsible for maintaining the larval stage (Truman & Riddiford, 2022). While the former paper focused on the embryonic and early larval function of Chinmo, this paper explores its metamorphic effects and defines the roles of Broad and E93 in the phenotypes produced by manipulations of Chinmo expression.

Overall, the paper is well presented but in places, readers would be helped if the authors were more explicit about the logic and details of their manipulations. There are a couple of conceptual issues that the authors should address.

The role of Broad in larval tissues:<br /> One intriguing issue relates to the relationship of Chinmo to Broad and E93 in larval versus imaginal tissues prior to metamorphosis. The knock-down of chinmo in imaginal discs results in severe suppression of growth and the lack of metamorphic patterning genes such as cut and wingless. Normal growth and patterning are reestablished though, if broad is also knocked-down, supporting the notion that the effects of the lack of Chinmo are mediated through the premature expression of Broad.<br /> In the salivary glands, by contrast, chinmo knock-down suppresses growth, and this growth suppression is not reversed by simultaneous broad knockdown. They properly conclude that the role of Chinmo in supporting the growth of larval tissues does not involve Broad, but their data on the expression of salivary gland proteins suggest that Broad still plays some role in Chinmo function in salivary glands. Fig. 5E shows the levels of various salivary glue proteins in the glands of Chinmo knock-down larvae. The levels are reduced, as expected by the lack of salivary gland growth, but a significant finding is that they are there at all! The Costantino et al. (2008) paper shows that these genes are only induced in the mid-L3. Ecdysone, acting through Broad isoforms, is necessary for their appearance and these SGS genes can be induced in the L1 and L2 stages by ectopic expression of some Broad isoforms. Their low levels in Fig 5, would be due to the small size of the gland, but the gland's premature expression of Broad likely causes their induction. In larval cells, then, Chinmo may feed into two parallel pathways, one that does not involve broad and regulates growth and the other, utilizing Broad, regulating premetamorphic changes.<br /> It would be useful to look at early larval salivary gland proteins such as ng-1 to -3 that are expressed in salivary glands before the critical weight. Also, it would be interesting if the appearance of the SGS proteins after chinmo knock-down (Fig 5E) is abolished by simultaneous knock-down of broad.

Role of Chinmo and Broad in Hemimetabolous insects:<br /> In the conclusion of their comparative studies on the cockroach (line 342), the authors state that Broad exerts no role in the development of hemimetabolous insects. However, this conclusion is not consistent with the literature. The first study of broad knockdown in a hemimetabolous insect was in the milkweed bug Oncopeltus fasciatus by Erezyilmaz et al. (2006). Surprisingly to Erezyilmaz et al., broad knock-down in early-stage nymphs did not cause premature metamorphosis. However, Broad expression was essential for tissues of the wing pads and dorsal thorax to undergo morphogenetic growth (rather than simple isomorphic growth), and for stage-specific changes in coloration through the nymphal series (but not for the nymph to adult color change). A similar function for Broad on wing growth during the later nymphal stages was later shown in Blattella (Fernandez-Nicolas et al., 2022; Huang et al., 2013). The wing- and genital pads represent "imaginal" tissues in the nymph and the need for Broad in these tissues are the same as seen in imaginal discs as the latter shift from isomorphic growth to morphogenesis at the critical weight checkpoint in the L3.<br /> This would suggest that important roles for Broad and E93 are already established in the hemimetabolous insects with E93 controlling the shift from immature (nymphal) to adult phenotypes and Broad controlling the premetamorphic growth of imaginal tissues in early-stage nymphs. Chinmo might then be needed to keep both in check.

Reviewer #1 (Public Review):

This study demonstrates that Chinmo promotes larval development as part of the metamorphic gene network (MGN), in part by regulating Br-C expression in some tissues (exemplified in the wing disc) and in a Br-C independent manner in other tissues such as the salivary gland. I have included below the following comments on the submitted version of this manuscript:

1. The authors have shown experimentally that Chinmo regulates Br-C expression in the wing disc but not the larval salivary gland. Based on this, they posit that Chinmo promotes larval development in a Br-C-dependent manner in imaginal tissues and a Br-C-independent manner in other larval tissues. This generalization of Chinmo's role in development would be more compelling if the relationship between Chinmo and Br-C were explored in other examples of imaginal/larval tissues.

2. Chinmo, Br-C, and E93 have all been shown to be EcR-regulated in larval tissues, including the brain and wing disc (as in Zhou et al. 2006, Dev Cell; Narbonne-Reveau and Maurange 2019, PLOS Biology; Uyeharu et al. 2017, ). It would be interesting (and I believe relevant to this study) to know whether the roles of these factors in their respective developmental stages are EcR-dependent and whether their regulation by EcR (or lack thereof) depends on whether the tissue is larval or imaginal.

3. In the chinmo qPCR analysis shown in Fig1A, whether animals were sex-matched or controlled was not indicated. Since Chinmo has a published role in regulating sexual identity (Ma et al. 2014, Dev Cell; Grmai et al. 2018, PLOS Genetics), and since growth/body size is known to be a sexually dimorphic trait (Rideout et al. 2015, PLOS Genetics), it seems important to establish whether the requirement of Chinmo for larval development and/or growth. I recommend either 1) controlling for sex by repeating qPCRs in Fig 1A in either males or females, or 2) reporting male/female chinmo levels at each stage side-by-side.

4. In Fig2E, the authors show that salivary gland secretion (sgs) genes are repressed in salivary glands lacking chinmo. Sgs genes are expressed during late larval stages as the animal prepares to pupate. Thus, based on the proposed model where Chinmo promotes larval development and represses the larval-to-pupal transition, one might expect that larval salivary glands lacking chinmo would express higher than normal levels of sgs genes. This expectation directly opposes the observed result - it would be helpful to speculate on this in the interpretation of results.

Reviewer #2 (Public Review):

Like humans, Bengalese finches rely on auditory feedback to maintain the acoustic stability of their learned vocalizations, and deafening causes acoustic degradation of their songs. How disruptions to sensory input alter gene expression in brain regions important for singing and song learning remains relatively unexplored. The authors develop an innovative serial laser capture RNA-sequencing method, which allows them to conduct large-scale analyses of gene expression in spatially defined singing-related regions, as well as in surrounding non-singing-related regions. These methods are used to demonstrate that deafening preferentially alters gene expression in song-related regions relative to surrounding song-related areas, and that deafening reduces correlations in gene expression between connected song-related regions. The authors then compare their findings to a previous single-cell RNA sequencing dataset to determine the cell types whose gene expression is likely to be most strongly affected by deafening and song degradation. Finally, the authors repeat their measurements of gene expression changes in RA following unilateral lesion of LMAN and find that LMAN lesions have the largest effect on groups of genes whose expression was also strongly affected by deafening. The study is elegant and rigorous, and its conclusions are well-supported. This work reveals candidate genes that may play a role in stable vocal performance and whose changes in expression may contribute to the acoustic degradation of vocal performance following deafening.

Reviewer #1 (Public Review):

In this manuscript, the authors seek to define the transcriptional response to deafening in the songbird brain. They compare transcriptional changes in the song regions with changes in the non-singing-associated surrounds, compute a song degradation score against which they can compare gene expression, and they use single-cell sequencing data from these brain regions to map genes to cells. The study is impressively comprehensive for time points, replicates, brain regions, comparisons, and alternative strategies (e.g. the LMAN lesions). This dataset builds nicely upon studies that assessed gene expression changes upon singing and applies a broad and useful series of bioinformatics analyses to get the strongest evidence for function from the data.

I think this dataset will be of great interest to a broad range of researchers who study neuronal plasticity mechanisms.

Reviewer #3 (Public Review):

In this study, the authors probe the molecular changes that occur in a neural circuit for learned behavior that depends on sensory input to maintain stereotypy. Songbirds, as the Bengalese finches used here are, are premier systems in which to ask these questions because they produce a highly stereotyped song that emerges after sensory learning becomes integrated into the function of a sensorimotor neural circuit responsible for singing. By deafening a group of birds (who show a shift in their song structure) and comparing them to hearing birds, clues as to how plasticity in motor output may emerge from genomic changes that alter the function of cells within the various components of the neural circuit.

There are multiple strengths of the paper:<br /> 1. The results may have broad implications because the type of sensorimotor neural circuit (cortico-basal ganglia-thalamic-cortical loop) used for singing is generally necessary for learned behaviors.

2. The methods and analyses are generally rigorous, including the parsing of song elements, and the type of detailed RNA sequencing and analysis that demonstrates the power of a genomic view of neural plasticity as it relates to behavioral plasticity.

3. Because the authors assayed the pallial (cortical) areas, as well as the basal ganglia component, of the sensorimotor circuit they were able to creatively compare how different facets of the network contributed to a) unmodified brain properties, b) properties perturbed after the loss of the auditory input that is required to stabilize song structure. As a result, they have added to the known molecular profiles for each of these brain areas, the accounting of how they may be specialized in comparison to the surrounding non-song brain, and what changes occur after deafening. Utilizing some existing single-cell sequencing data, the authors present for the first time some insight into what cell types may be showing the most robust changes, and therefore which may be driving the shift in song structure. The analysis further pushes in new ways to suggest how the molecular properties of a given brain area may relate to those of directly-connected areas. Together, these findings provide valuable clues as to the specific cell types and signaling properties that may be central to the production of stabilized, learned behavior.

4. One of the cortical brain areas, LMAN, was lesioned in a subset of the hearing subjects because it projects to the area that showed the greatest molecular difference between deafened and hearing birds (RA). The idea was to compare how this affected molecular properties with properties after the loss of auditory input; because RA is the output motor area for the song, its properties may be most directly tied to song structure. Using unilateral lesions was a strong choice of experimental design that allowed for rigorous analysis of this idea, and was interpretable because birds do not have a direct inter-hemispheric callosum.

The foundation of the paper is solid, though the results shown raise several questions that are not fully addressed, and limit some of the power of the implications.

The biggest questions arise from the finding that RA shows the largest number of molecular changes after deafening. The analysis and interpretations do not fully incorporate what we know of this circuit, at least from another well-studied songbird, the zebra finch, from which the authors derive other types of information. For example, it is not yet clear if RA is most changed because it is most directly involved in song output or because it receives projections from two areas within the sensorimotor circuit (LMAN and HVC). How do we consider the fact that by adulthood, LMAN and HVC cells project onto the same RA neurons? Are those the cell types being identified here? Would HVC lesions be expected to have the same effect as LMAN lesions? Are the cell types showing the greatest change those that are most involved in song output (e.g. are they projecting to nXIIts)? How do these results relate to the findings of changes in RA after HVC and LMAN lesions reported decades ago? How do these findings compare to an earlier study that also performed sequencing on areas from the sensorimotor circuit in deafened juveniles? Further, RA also receives information from the auditory processing regions of the brain, via the immediate structure RA-cup. It is not yet explicitly addressed how some effects may be from the loss of this more direct access to auditory information, rather than from information and projections originating within the sensorimotor circuit, and reinforces the question of whether or not the number of inputs to a particular brain area is a driving factor in the general pattern of changed RNAs after perturbation.

Importantly, since the LMAN lesions did not create significant changes in the song structure, it is difficult to know how to interpret the meaning of these molecular changes in RA, alone and in combination with the comparison to the RA profiles from deafened birds. Of importance is the question of whether or which molecular profiles are thus signatures of behavioral plasticity or not.

Reviewer #2 (Public Review):

Neurons of the inferior olive exhibit strong subthreshold oscillations, and drive complex spiking through climbing fiber synapses onto Purkinje cells in the cerebellar cortex. This activity plays an essential role in coordinating motor control and the induction of cerebellar plasticity. In this study, the authors make use of optogenetic and electrophysiological approaches to examine the interplay between intrinsic oscillations and two important excitatory and inhibitory input populations to the inferior olive. The authors show that excitation is enhanced when it occurs in the rebound phase of the preceding inhibition. Using a computer model, the authors also show that enhanced excitation can effectively recruit larger populations of neurons, presumably through gap junctional coupling. The strengths of the study include the authors' ability to independently control both excitatory and inhibitory pathways, as well as the rigorous and systematic examination of input timing and amplitude and their effects on spike output. There were some weaknesses; high variability in cell resting potentials raised questions about how cell health impacted the findings, and there needed to be better documentation of recording conditions and parameters. There also needed to be a more extensive discussion about the nature of input timing and frequency under behaviorally relevant conditions. Given these relatively minor issues, the study provides new insight and depth into synaptic integration in the inferior olive and adds to our understanding of how input timing is translated into climbing fiber signals.

Reviewer #1 (Public Review):

The network of neurons of the inferior olive has long been suggested as a timing machine that controls the precise timing of movements, correcting movement and participating in the prediction of movement time. These timing capabilities have been attributed to the unique feature of the neurons to generate subthreshold voltage oscillations that can be used as a timing machine. In this study, the effect of the inhibitory and excitatory synaptic inputs on the oscillatory behavior was examined, demonstrating their different effects as well as the effects of combing the two inputs.

Reviewer #3 (Public Review):

This is an interesting paper but not entirely surprising. Given the known voltage dependency of intrinsic oscillations of IO neurons, the fact that a hyperpolarizing input from a GABAergic synapse or a depolarization from an excitatory input can phase shift an oscillation depending on the timing is not surprising. It could be predicted from what is already known about the underlying conductances of the oscillations in these cells. The authors, however, do provide some quantification for both the inputs and the effects they have on the oscillations. Whether or not this quantification can be extrapolated to in vivo conditions, however, remains to be seen. There are multiple technical issues that the authors need to address.

Reviewer #2 (Public Review):

The authors report a study comparing self-reported stable and unstable knees with total knee arthroplasty. Advanced imaging methods (dynamic fluoroscopy with model-image registration) and analysis of muscle activities were used to characterize the study subjects during three ambulatory activities (level gait, downhill walking, and stair descent).

The subject cohort all received one design of TKA in a similar time period. The unstable subgroup was >60% female, while the stable knee cohort was 70% male, which is a notable limitation. The measurement methods are state-of-the-art and expertly applied.

The results suggest there may be measurable differences in knee kinematics in subjects with unstable knees, but this was not strongly supported across groups. Rather it was highlighted in 3 individuals who self-reported instability during the test session. The muscle activity analysis supports there being differences between the stable and unstable knee groups.

Despite the limitations of a small subject cohort with only a single TKA design, the study highlights important methods that appear suitable to further study the factors contributing to clinical dissatisfaction with TKA as it relates to joint stability and function during ambulatory tasks.

Reviewer #1 (Public Review):

This manuscript seeks a greater understanding of joint movements in recipients of total knee replacements who have symptoms of unstable prosthetic joints. The authors describe the results of a carefully conducted retrospective analysis of joint movements after total knee replacement (TKA) using a recently developed method based on videofluoroscopy. Kinematic data supplemented by electromyography measurements of muscle activation through normal gait. These measurements were conducted while walking on flat ground, down an incline, or down stairs. The kinematics and EMG data provide convincing evidence of altered knee kinematics when symptoms of joint instability occurred that were accompanied by subject-specific changes in patterns of muscle activation. The manuscript raises interesting questions about how patients adapt muscle activation patterns to limit discomfort prior to TKA and to what degree these same defensive strategies influence joint stability post-operatively.

Reviewer #1 (Public Review):

Villalobos-Cantor et al. describe a chemical/genetic strategy to enable cell-type-specific labeling of nascent proteins in living tissues (called POPPi). O-propargyl-puromycin (OPP) is a commonly used compound to label nascent proteins in cells and tissue, however, its application is limited in vivo because it can not be targeted to individual cell types, tissues, or organs. Using Drosophila as a genetically tractable in vivo model organism, Villalobos-Cantor et al. incubate live tissue with a puromycin analog called phenylacetyl-OPP (PhAc-OPP) in combination with cell-type expression of Penicillin G acylase (PGA), which converts PhAc-OPP to OPP. As PGA is under the control of the Gal4/UAS system, a vast library of tissue-specific Gal4 lines can in theory be used to conduct labeling experiments in vivo.

The major strength of the methods and results is the demonstration that labeling can occur in specific cell types of the dissected brain - neurons and glia. For example, protein synthesis in individual dopamine neurons in the brain can be visualized and distinguished from neighboring cells, a remarkable achievement and striking image. These results in dissected brains nicely demonstrate that PhAc-OPP can penetrate into brain tissue, diffuse to internal locations, pass through the cell membrane, and become converted to OPP and label nascent proteins. A major weakness of the methods and results is the lack of exploration of POPPi in tissues other than the brain, as well as in non-dissected living animals. For example, the authors do not test if PhAc-OPP delivery can occur by feeding animals, or if PhAc-OPP can penetrate into various dissected tissues. Results from these experiments would be of great importance to others interested in applying this technique in non-brain tissues, and would properly support the authors' claims in the title and abstract that this is a general method (not only for the brain).

Assuming that PhAc-OPP can penetrate various dissected tissues, this method would have a significant impact on tissue-specific measurements of protein synthesis and could be a valuable new molecular reporter for gene function analysis (e.g. tissue-specific gene knockout + POPPi). If PhAc-OPP could be ingested by flies, perfuse through the body, and label nascent proteins in a cell-type specific manner, then POPPi could be incredibly useful for tissue-specific proteome profiling (i.e. mass spectrometry) in an in vivo living animal (non-dissected), similar to the BioID system.

Reviewer #2 (Public Review):

In this manuscript, Villalobos-Cantor et. al. described a new technique for cell-type specific in vivo labeling of nascent peptides, which they call POPPi. POPPi is based on sequence-independent incorporation of the puromycin analog OPP into an elongating peptide, which also simultaneously terminates the growing peptide. To achieve cell-type-specific labeling, the authors used an OPP derivative, PhAc-OPP, as the labeling substrate. PhAc-OPP contains a blocking group that prevents it from incorporating into the growing peptide, and the blocking group can be cleaved off by the enzyme PGA, which is expressed in the cell type of interest.

The authors validated POPPi in different cell types in the Drosophila brain and showed that this method could be used to image general translation or to biochemically enrich nascent peptides in a cell-type-specific manner. They also showed that with an optimized labeling protocol, it is possible to achieve efficient labeling with minimum effect on animal viability and health. The authors further used POPPi to provide independent support for a previously known phenomenon: age-dependent decline in general translation in the neurons. The results of this work are solid, and the main conclusions are well supported by the data presented. The manuscript is very well written with a clear logic flow and is very easy to read.

What is less clear is how generally useful POPPi will be to the community. The authors pointed out two major cell-type specific applications of POPPi, 1) imaging general translation and 2) biochemically purifying nascent peptides. For application #1, although POPPi might be a more desirable method in some cases, a combination of non-cell-type specific labeling using OPP, and marking the cell type of interest by a fluorescent protein might be simpler. Because labeling with OPP eliminates the enzymatic step that converts non-reactive PhAc-OPP to reactive OPP, the labeling kinetics can be improved, and the toxicity associated with PGA expression can be avoided. For application #2, a currently widely used strategy for a similar purpose is various types of ribosome profiling techniques. Ribosome profiling may be easier to perform than POPPi, and because proteins cannot be amplified, a very large quantity of starting materials will be needed if one wants to use POPPi to characterize cell-type specific nascent proteome. In fact, in this manuscript, the authors used western blots to detect candidate proteins and did not use mass spec to characterize the nascent proteome.

Reviewer #3 (Public Review):

In this manuscript, Villalobos-Cantor et al. have implemented the method for monitoring cellular proteome that their lab has established in cell culture models of Drosophila brains. The method uses a puromycin analog (O-propargyl-puromycin, OPP) that is locked by the addition of phenylacetyl group (PhAc-OPP) that can be unlocked by expression of Penicillin G acetylase (PGA) to tag the proteins translated in a specific cell type. When unlocked, OPP can get incorporated into the newly translating nascent peptide, and abort translation while allowing click chemistry addition of various tags, such as fluorophore-azide to visualize or biotin-azide to immunopurify polypeptides. The authors demonstrate the use of the method in adult drosophila brains expressing PGA in neurons or glia, showing that the addition of OPP is indeed PGA dependent and the proteins are only tagged in the cells that express PGA. The authors also show that when fluorophore azide is used to visualize the proteome and the samples are run on a gel, bands of various sizes can be observed to have incorporated OPP, arguing the method labels the proteome indiscriminately. The authors also optimized the protocol by titrating the amount of PhAc-OPP to use to minimize cellular stress. Also, they show that driving the expression of PGA with elav-Gal4 or repo-Gal4 is not toxic and does not cause phenotypes although Actin-Gal4 driven expression causes phenotypes. Finally the authors demonstrate the use of the technique to show that there is an age-induced decrease in total protein synthesis in the fly brain. This is a nice technique to implement in fly but the characterization of the technique is not complete in its current state. It is not clear what percentage of the nascent peptides are tagged, and whether the cells in the tissue are equally represented in the lysates for immunopurification.

Reviewer #1 (Public Review):

This project aimed to understand if decision making impairments commonly observed in older adults arise from working memory (WM) or reinforcement learning (RL) deficits. Evidence in the paper suggests it is the former; they observe poorer task accuracy in older adults that is accompanied by a faster memory decay in older adults using a novel hierarchical instantiation of a previously validated computational model. There were no similar changes in RL in this model. These results are extended using Magnetic Resonance Spectroscopy (MRS) to measure glutamate and GABA levels in striatum, prefrontal and parietal regions. They found that impairments in working memory were linked to reductions of glutamate in PFC, particularly in the older adult group.

The task employed is elegant and has been studied extensively in different populations and is well-validated (though here a hierarchical Bayesian extension is developed and validated). The results however may not be definitive in some respects; the paper did not replicate previously observed RL deficits. It therefore, remains possible that this is due to the sensitivity of the task to this RL component in ageing and future work is needed to fully bridge the gap in the literature.

Although the study is well-executed, there is an obvious limitation in the use of a cross-sectional design to address this question. The authors acknowledge this limitation in the discussion but could go further to highlight the potential confound of cohort effects on gaming, RL and WM tasks more generally. Without within-person change data, the evidence can only be suggestive of potential age-related decline. For this reason, it may be more appropriate to use the terminology "age-related differences' rather than "age-related declines" given the study design.

Reviewer #2 (Public Review):

In this study, Rmus and colleagues contribute to the important open question of whether reinforcement learning deficits observed in older adults are due to impairments in basic learning processes, or can be attributed to a decline in working memory function. The authors present cross-sectional behavioral data from a task designed to assess the role of working memory in reinforcement learning. And they use computational modeling in conjunction with MR spectroscopy to demonstrate a relationship between prefrontal glutamate and age-related impairments in learning specific to working memory decay. I found the overall story compelling, the data novel, and the analysis carefully executed. Below I outline some areas in which the claims of the manuscript could be strengthened.

1. I may have missed this, but does glutamate correlate with other model parameters? Or did the authors only focus on the WM parameters because of the age difference? In support of the specificity argument, it would be important to show that glutamate only predicts WM related parameters regardless of whether there was an age difference or not.<br /> 2. As it is somewhat common with these tasks, it seems like the model does not fully capture the performance deficit in OA (Fig. 2B), even when all the individual difference parameters in WM are allowed to vary. Can the authors say more about the discrepancy? This is an interesting datapoint which may give clues to mechanism.<br /> 3. Relatedly, it may not be possible with these data alone, but can authors discuss what the WM decay parameter captures? In particular for OA, the distinction between generating and maintaining a "task set" has been extensively written about. Older adults tend to have difficulty internally generating and flexibly deploying task sets, but somewhat paradoxically can perform better than YA in certain decision situations (e.g. when reward is dependent on previous choices, see Worthy et. Al. 2011). The task in this study necessarily pushes OA in a regime in which relying on familiar decision strategies is sub-optimal, and task sets must be continuously generated. Is there a type of intervention do authors expect would reverse the observed deficit in WM?<br /> 4. There is a wealth of evidence suggesting striatal DA loss in older adults, which served as the basis for many of the original investigations and hypotheses regarding a simple RL deficit in OA (e.g. work by Shu-Chen Li and others). While the authors do not directly measure DA in this study, it would be helpful to place the results in the context of that literature.<br /> 5. Finally, the main argument of the paper as I read it is that PFC glutamate mediates the performance deficits observed in RL because it reflects a compromised WM system. Sample size permitting, it would be helpful to see a formal test of this mediation relationship.

Reviewer #3 (Public Review):

Aging impacts many cognitive functions, and how these changes affect performance in different tasks is an important question. By testing 42 older and 36 younger healthy adults with a novel learning task and MR spectroscopy, Rmus et al addressed the important question whether age-related declines in learning are driven by WM, or by deficiencies of the RL system. The task varied the role of working memory in learning by asking participants to learn about either 3 or 6 stimulus response associations from feedback (set sizes 3 and 6). The paper combines a detailed computational account of participants behaviour and striatal and prefrontal/parietal MR spectroscopy in order to assess individual glutamate and GABA levels.

The authors report an effect of set-size on learning in both are groups, and show that participant age is associated with (1) worse accuracy, (2) a larger set size performance difference, and (3) a heightened sensitivity to reward. Computational modelling showed that working memory decay differed between age groups, but that reliance on WM to perform the task at hand was similar in both age groups (similarly differing between conditions in both groups). Turning to the MRS results, the paper shows that an aggregate measure of glutamate relates to aggregate task performance, that prefrontal glutamate specifically relates to WM decay observed in the task, and that age was negatively associated with glutamate levels.

While the paper is well worth reading and offers many interesting data points, the title's suggestion that "Age-related decline in prefrontal glutamate predicts failure to efficiently deploy working memory in working memory" is, in my opinion, not fully supported by the evidence. First, the authors don't report clear evidence for any age-related differences in WM reliance in the task overall. Second, the authors find that MFG glutamate relates significantly only to WM decay, not the parameter that captures WM deployment. Third, correlations don't imply predictive relations.

Another important open question relates to the relatively large age difference in the effect of set-size on performance. The authors write that working memory will contribute less to performance in higher set size conditions. Yet, age differences are largest in the set size 6 condition, suggesting that RL-dependent learning is most severely impaired in learning (set size 6 performance), rather than WM dependent learning (set size 3 performance). Finally, a statistically significant age difference in reward sensitivity seems to be hardly integrated into the authors' overall interpretation.

The issues laid out above set aside, the paper has the potential to make an important contribution to the literature on cognitive aging.

Reviewer #2 (Public Review):

The work from Nakajima-Takagi et al describes the phenotypes and study of a PCGF1 mutant mouse model. PCGF1 is a core component of the non-canonical PRC1.1 complex and specific functions of this complex in hematopoiesis. Using somatic inactivation models, the authors demonstrate that the acute deletion of PCGF1 from adult hematopoiesis leads to a progressive myeloid bias in the bone marrow and peripheral blood. This occurs at the expense of the HSPC compartment, with a reduction in all populations and of the lymphoid committed populations. The myeloid bias is cell intrinsic, as competitive transplant of the PGCF1 deficient bone marrow recapitulates the phenotype. The effect is not due to exhaustion or loss of self-renewal of the HSCs.<br /> To understand the basis for the myeloid bias, the authors first assessed transcriptome signatures and see a shift in gene expression programs related to myeloid development and targets of the key myeloid transcription factor C/EBPa. Further analysis demonstrated an increased expression of Cebp1 in the PCGF1-deficient LSK cells. Reducing the expression of Cebpa could modify the myeloid skewing of Pcgf1 deficient cells in culture. This de-repression of Cebpa correlates with changed local H2AK119ub1 levels in the HPSC populations.

Additional studies assessed how the loss of Pcgf1 changed the response to hemoablation, in this instance with a single dose of 5-FU. This study coupled with scRNA-seq suggested that PRC1.1 was important in regulating the GMP populations, potentially through a self-renewal program. This led to a focussed analysis of the GMPs, with evidence for altered Hoxa9 and b-catenin levels contributing to the altered GMP behaviours. Both have been implicated and demonstrated to have functional roles in these programs in other studies.

Finally, ageing of Pcgf1 deficient mice demonstrated that these mice were predisposed to developing T-ALL and MPN. The authors provide a characterisation of these moribund states and their phenotypes are consistent with the diagnosis.

Overall the work demonstrates a specific requirement for Pcgf1, and therefore PRC1.1, in the regulation of hematopoiesis. I think the authors largely achieved the aims and the results are supportive of the conclusions. The work shows myeloid bias, experimental evidence that this is due to a derepression of a myeloid lineage program in the HPSC and associated chromatin changes, and functions for Pcgf1 in both hematopoietic regeneration and malignancy. This suggests a unique role for non-canonical PRC1.1 compared to canonical PRC 1.

Strengths:<br /> - in vivo experiments and evidence;<br /> - multiple lines of evidence supporting the conclusion;<br /> - mechanistic studies provide direct evidence of the proposed mechanism.

Weaknesses:<br /> - can the authors demonstrate normal maturation of the myeloid lineages as this would be important to differentiate between myeloid bias and a block in myeloid differentiation? This is important to distinguish between.<br /> - include analysis of mature myeloid cells and FACS plots to allow assessment of maturation.

Reviewer #3 (Public Review):

The myeloid bias in hematopoietic stem and progenitor cells upon genetic inactivation of Pcgf1, a component of the PRC1 complex is convincingly demonstrated by a Pcgf1 conditional allele crossed with a tamoxifen-inducible Are, combined with transplantation. The overproduction of myeloid cells may be contributed to by the derepression of two PRC target genes Cebpa and Hoxa9 at the multipotent HSPC and lineage-committed GMP levels. The involvement of these two genes is demonstrated by decreased H2AK119ub1, elevated CEBPa expression, and increased CEBPa binding motifs in KO HSCs. Functional rescue by manipulating CEBPa levels on the background of Pcgf1 KO is attempted in vitro. The derepression of Hoxa9 is shown in Pcgf1 KO GMPs, which expanded in the KO mice. Finally, constitutive inactivation of Pcgf1 results in lethal myeloproliferation. Together, this paper demonstrates another HSPC regulator, whose loss of function leads to myeloid-biased hematopoiesis, which in extreme cases could end in myeloid transformation.

Reviewer #1 (Public Review):

This interesting manuscript by Nakajima-Takagi et al describes the roles of the PRC 1.1 member Pcgf1 in myeloid lineage commitment in hematopoiesis and in regulating myeloid differentiation and self-renewal during emergency myelopoiesis. The roles of Pcgf1 have been explored previously in the context of Runx1 depletion or in the context of myelofibrosis together with the JAK2V617F mutation, but this is the first report of the specific roles of Pcgf1 in HSCs and in myelopoiesis. The authors convincingly demonstrate that conditional deletion of Pcgf1 in hematopoietic cells causes a lineage switch in HSCs from lymphoid to myeloid fates and that a key mechanism for this lineage switch is regulation of the H2AK119ub1 chromatin mark, leading to de-repression of CEBPalpha, a key transcription factor that promotes myeloid cell fate. They also perform a single-cell RNAseq experiment and demonstrate an increase in the population of "self-renewing GMPs", and they attribute this increase to an upregulation in HoxA9 expression and beta-catenin activation. They also demonstrate that HoxA9 overexpression promotes beta-catenin activation, which has been observed in emergency myelopoiesis in other studies, though the mechanism for this is unclear. The authors also demonstrate that deletion of Pcgf1 in hematopoietic cells can also lead to deregulated myelopoiesis, leading to a lethal MPN in a subset of animals. They conclude that Pcgf1 plays a critical role to regulate emergency myelopoiesis, and to prevent the malignant transformation of myeloid progenitors.

Overall, the methods are highly rigorous and the results support the authors' conclusions. The only conclusion that would require further clarification is that Pcgf1 promotes emergency myelopoiesis. Emergency myelopoiesis typically starts with a proliferative burst of myeloid progenitors in response to a stress stimulus, followed by enhanced myeloid differentiation into mature functional myeloid cells. In this Pcgf1 KO mouse model, it is clear that there is an increase in the production of myeloid progenitors, and prolonged survival of myeloid progenitors in culture, but there is no demonstration that this results in the generation of mature functional myeloid cells. It appears that there may also be a differentiation block, likely due to the increase in "self-renewing progenitors", which is likely a consequence of HoxA9 upregulation, and possibly the beta-catenin activation in myeloid progenitors. Therefore, if there is also a differentiation block due to Pcgf1 deletion, the statement that emergency myelopoiesis is enhanced may be an oversimplification. What appears to occur is an expansion of a pool of self-renewing transformed or pre-transformed myeloid progenitors, and the relevance of this event to emergency myelopoiesis is not entirely clear. However, there is a clear significance of these findings and this new mouse model for studying the pathogenesis of myeloid malignancies, such as MPN, MDS, or AML, in which mutations in other components of PRC1.1 are frequently mutated, so this study is likely to have a significant impact in the field.

Reviewer #3 (Public Review):

In this study, Cunha et al. examined the role of different oxygen tensions (21%, 5%, and 1% O2) and HIF-1α stabilisation in regulating murine and human CD8+ T cell proliferation and function. The authors find that hypoxia (1% O2) and pharmacological PHD inhibition with FG-4592, enhance murine T cell activation but impair proliferation. Furthermore, adoptive cell transfer (ACT) therapy of CD8+ T cells from both conditions reduced tumour burden in a B16-OVA melanoma model. Short hypoxic conditioning (1% O2) of human CD8+ T cells for 1 day increased HIF-1α stabilisation, with increased activation, glycolysis, and mitochondrial function still observed following 6 days of normoxic cell culture. Short hypoxic conditioning of HER2 and CD19 CAR-T cells improved their activation and cytotoxicity in vitro, while HER2 CAR-T cell counts were increased in vivo, reducing tumour burden, and increasing survival when compared to 21% O2.

Strengths:<br /> The paper convincingly demonstrates that short hypoxic conditioning in a defined window improves CAR-T cell function through in vitro cytotoxicity assays and following adoptive transfer in a preclinical HER2+-SKOV3+ positive tumour model. Thus, the major conclusion of the paper is mostly well supported by the data and could represent a novel strategy to improve CAR-T cell immunotherapy for solid tumours in the future.

Weaknesses:<br /> The extent to which hypoxic conditioning-mediated improvement in CAR-T cell function is dependent on HIF-1a-driven metabolic reprogramming is unclear and other potential mechanisms are not explored. 5FG-4592 and VHL silencing in HER2 CAR-T cells did not phenocopy each other faithfully. In addition, neither approach was as effective as short hypoxic conditioning with 1% O2 in improving CAR-T cell function in vitro or in vivo. Although the authors suggest the temporal dynamics of HIF-1α stabilisation is the key point, this is not convincingly proven, and no metabolic characterisation of these CAR-T cells was performed. It is unclear how changes elicited during short hypoxic conditioning are maintained following continued normoxic cell culture. Hypoxia is known to rapidly regulate histone methylation and chromatin structure in a HIF-independent manner (PMID: 30872525; PMID: 30872526). Are similar epigenetic changes observed in T cells, and if so, could these epigenetic changes underlie improved T cell activation?<br /> Complications may also arise when comparing different oxygen tensions given recent data that suggests standard cell culture conditions can lead to local hypoxia through a combination (https://www.biorxiv.org/content/10.1101/2022.11.29.516437v1) of cellular respiration and poor O2 diffusion. Although it is unclear how this will impact suspension T cells it does beg the question as to whether HIF-1α stability following T cell activation is (at least in part) mediated by pericellular O2 limitations in cell culture over time, even in presumed hyperoxic (21% O2) conditions? Or if T cells subsequently cultured at 21% O2 following short hypoxic conditioning (1% O2) still experience local hypoxia during the 6-day culturing protocol? It would be important to assess this in future work and at least discuss these potential weaknesses.

Reviewer #1 (Public Review):

This study represents an important work in the field of (CAR)T-cell immunotherapy by analyzing the effect of different oxygen tension on the function and differentiation of T-cells (especially CD8+). Although it has been described that low oxygen levels can influence effector function/differentiation of T-cells, as nicely acknowledged by the authors in the introduction, a comprehensive analysis in the context of immunotherapy has been missing so far and this study adds significant findings that will be relevant for patient care in all fields applying (CAR)T-cell immunotherapy.

The strength of the evidence is generally solid although there are some discrepancies between the different ways to induce HIF-1α (i.e. low O2, pharmacological inhibition, shRNA knockdown) that need to be clearly stated and/or discussed.

1) The first section of the results determines the impact of low oxygen and pharmacological HIF-1α stabilization on CD8+ T-cell activation/differentiation. Low oxygen diminishes cell growth but induces T-cell activation and effector cytokines, while HIF-1a stabilization mimics the effects on activation without alterations in expansion. Unfortunately, it remains unclear why effects upon low O2 are more pronounced although pharmacological HIF-1a stabilization is more efficient.<br /> 2) As a next step, in vitro conditioned T-cells are transferred into a subcutaneous B16-OVA model. Although only the low O2 levels increase T-cell numbers in vivo after the transfer, the initial tumor burden was nicely decreased by both low O2 and HIF-1a stabilization. However, only the latter significantly improved survival and it remains unclear and uncommented why.<br /> 3) Next, the authors address whether pre-conditioning of human CART-cells to induce HIF-1α either by pharmacological stabilization or by silencing of VHL shows similar effects. Surprisingly, both ways of HIF-1a stabilization resulted in different effects concerning differential gene expression and cytotoxic capacity of CART-cells. Accordingly, pharmacologically pre-conditioned CART-cells did not have a significant impact on survival in an in vivo model, while the VHL-silenced ones did significantly improve animal survival. This discrepancy between the two modes of HIF-1a stabilization remains uncommented. Unfortunately, it also remains unclear why the pharmacological HIF-1a stabilization significantly improved the survival in animals of the B16-OVA model and not in the human CART-cell model.<br /> 4) After this, the researchers determine how the timing of hypoxic conditioning affects the (CAR)T-cells. Here it is convincingly shown that already a short period of hypoxic conditioning (1 day) with a subsequent expansion phase (additional 6 days) is sufficient to induce HIF-1a mediated alterations (e.g. metabolic changes, calcium flux, intracellular signaling). Although this section is coherent in itself, the switch between different times of hypoxic conditioning, expansion, and analysis is difficult to follow and might lead to confusion. The expression pattern of e.g. HIF-1a on day 1 and day 7 together with the nuclear amounts of NFAT and c-Myc might be misunderstood, like the other presented data as well.<br /> 5) Last, short-term hypoxic conditioning of CART cells is tested in a solid tumor mouse model. The previously identified conditioning protocol also increases CART-cell function against solid tumors (as shown by enhanced cytotoxicity, reduced tumor burden, and prolonged survival). Unfortunately, although both HER2-CART-cells and CD19-CART-cells are shown to have superior cytotoxicity in vitro after the pre-conditioning, only HER2-CART-cells are demonstrated to be superior upon low O2 conditioning in an in vivo adoptive transfer mouse model and CD19-CART-cells remain an open question.

Generally spoken, the limitations of the manuscript are:<br /> 1) The occurring discrepancies of determining effects caused by the different modes of Hif-1a stabilization which certainly are caused by the complex nature of Hif-1a regulatory network, and;<br /> 2) The limitation of detected effects primarily on CD8+ T cells while CART-cells products usually are a mixture of CD4+ and CD8+ ones.

Reviewer #2 (Public Review):

In this work, Cunha et al provide an insightful and exhaustive analysis of the role of hypoxia and HIF-1a for T cell activation and function. The work contributes to the field by showing that transient hypoxia occurring simultaneously with T cell stimulation (antigen recognition) induces an effector program in T cells that results in increased cytotoxicity in vivo and in mouse models. Importantly, the induction of this effector phenotype is not necessarily linked with an increase in proliferation in vitro, and in vitro differences are mostly observed upon antigen re-challenging.

The major strengths of the work are the use of different complementary methods to modulate HIF-1a (low oxygen conditions, inhibition of PDH by FG-4592, and deletion of VHL) and the combination of mouse and human models, especially addressing how to implement the findings to the production of CAR-T cells. Besides, the authors not only evaluate T cell function but also dive into the pathways driving the responses observed, which provides mechanistic insight.

While activation of HIF-1a through the different means mentioned before results in similar signatures in terms of T cell effector phenotype and animal response, there are some aspects that differ between the models. This is probably indicating that low levels of oxygen have other effects beyond the regulation of HIF, and that pharmacological modulation of HIF-1a might not be exactly equivalent to HIF-1a stabilization by real hypoxia.

The work is useful to better understand the discrepancies in the field, where it has been previously shown that hypoxia can have both a pro-inflammatory effect and an immunosuppressive effect on T cells. The answer proposed by the authors is that it´s a matter of timing, and not so much the magnitude of the HIF-1a response. Despite this being relatively easy to control ex vivo, the challenge occurs when considering the role of hypoxia in vivo, which probably lasts longer than the transient hypoxia needed for beneficial effects on T cells, causing T cell exhaustion.

From the translational perspective, the study suggests strategies to improve CAR-T cell therapy but also has some limitations. Despite an improvement of cytotoxicity and survival observed in mouse models upon adoptive cell transfer or injection of CAR-T cells with previously increased HIF1a levels, these approaches do not result in curation and survival is still quite low in all groups. Interestingly, improved survival with HER2 CARs exposed ex vivo to low oxygen conditions for 1 day is clear and more promising.

Reviewer #2 (Public Review):

In this manuscript, Niethamer et al. investigate the role of the transcription factor ATF3 in lung regeneration after H1N1 influenza. They focus on endothelial ATF3 which is present in a subset of lung capillaries in the adult mouse lung. Interestingly, they found that influenza infection upregulates endothelial ATF3 and that endothelial deletion of Atf3 results in impaired regeneration, leading to enlarged airspaces after viral infection. They further show that this effect may be due to an increase in apoptosis and a decrease in proliferation, suggesting that endothelial ATF3 is necessary for pulmonary vascular regeneration, as well as recovery of the alveolar architecture.<br /> Given the recent publications in the field describing lung endothelial heterogeneity, as well as its possible role in injury repair, this work is relevant to the community. It also supports the idea that epithelial-endothelial crosstalk is important for lung regeneration and proposes a potential candidate for this process.

Strengths:<br /> The authors identified and tested the role of endothelial Atf3 in lung regeneration using well-established techniques. They identified this transcription factor as a candidate using state-of-the-art scRNA-seq. They also carefully lineage traced ATF3 expressing cells using an inducible reporter before and after infection and then used a pan-endothelial driver Cdh5 to delete Atf3 specifically in the endothelium. Thus, the authors successfully show significant changes in the alveolar structure after infection in their mutant model.

Weaknesses:<br /> Although there is evidence that the author's claims have biological relevance, this paper would benefit from strengthening and/or clarifying some things:

• The scRNA-seq analysis is performed in two separate objects ("control lung" and "H1N1 infected lung 14dpi"). For these two sets of data to be comparable, the authors should have integrated the objects and analyzed them together. This is not only important for deciding the clusters' identities and making sure that the same clusters are compared between control and infected, but also necessary to compare gene expression.<br /> • ATF3 is not only present in Cap1_B, in the infected lung there seems like Cap1_A express less ATF3. The authors should comment on this difference.<br /> • It is unclear how the clusters Cap1_A and Cap1_B were decided. The manuscript would benefit from clarification.<br /> • It would be beneficial to see via immunofluorescence the morphological and spatial differences between ATF3-expressing and non-expressing endothelial cells since this transcription factor is expressed in multiple endothelial cell types.<br /> • The authors mention ATF3 is not endothelial-specific. Expression of ATF3 in other cell types should be evaluated via immunofluorescence.<br /> • The authors should have shown evidence of the deletion in their Atf3EC-KO mouse and addressed whether they had residual ATF3. If there is no antibody available, RNAscope could be used, or Western Blot or RT-PCR on sorted endothelial cells.<br /> • The authors only show the epithelium as evidence that the alveolar region is altered in their mutant after infection. The endothelium should have also been investigated, especially since their mutant is an endothelial-specific deletion. Within this, the different endothelial cells should have been assessed by a method other than RNAscope such as immunofluorescence, given that this method is unable to show morphology and there are antibodies available.<br /> • Bulk RNA-seq from endothelial cells is used in the manuscript. However, because ATF3 is not specific to Cap1_B cells or even capillaries alone, the downstream gene expression analysis of bulk RNA should be placed into the context of lung endothelial heterogeneity.<br /> • Although the authors mentioned that the infection with H1N1 influenza can have regional differences, they do not show how they picked regions for their analysis and quantification, and whether ATF3 upregulation was found in more severely affected regions. Furthermore, since they quantified via FACS, this heterogeneity in the infection itself could have affected their observations.

Reviewer #1 (Public Review):

Here the authors investigate the mechanisms by which pulmonary endothelial cells (EC) contribute to alveolar repair post-H1N1-mediated acute lung injury and the molecular basis for the heterogeneity of this response among different EC subpopulations. Using single-cell transcriptomic analysis they identify the CREB family factor Atf3 differentially enriched in CAP1B cells, a subpopulation of EC previously known for its proliferative behavior in response to alveolar injury. They report a crucial role for Atf3 in injury repair but not during homeostasis. Using a combination of lineage tracing and loss function approach and an influenza mouse model in vivo, they show that Atf3 inactivation in ECs results in the inability of CAP1B ECs to initiate a proliferative response to repair the vascular compartment and ultimately regenerate the lung. Notably, the decreased number of Atf3 lineage-labeled EC capillaries was shown to correlate with the alveolar regions that failed to repair the post-H1N1 injury. They conclude that Atf3 is an essential factor for repair damaged capillaries in alveolar injury.

The study is carefully designed and the results provide novel important information about a previously undisclosed role of Atf3 in the regeneration of the lung vascular component. The work has many strengths and is supported by impressively coherent data from the analysis of mouse genetic models, single-cell transcriptomic, and phenotypic characterization.

Reviewer #1 (Public Review):

This manuscript described the role of ALKBH5, an evolutionarily conserved mRNA m6A demethylase as a key regulator of axon regeneration. The authors screened the function of m6A regulators during axon regeneration and found that ALKBH5 limits regenerative growth associated with DRG neurons, by enhancing the stability of Lpin2 mRNA via erasing a single m6A modification in the 3'UTR. The major strength of the manuscript is the convincing importance of ALKDH5 as an attenuator to initially suppress the axon regeneration in the CNS and in the PNS proven by in vivo model system. These findings further suggest the potential use of ALKDH5 inhibitors to enhance neural regeneration upon physical injury.

Reviewer #3 (Public Review):

This is an elegant article that shows the reciprocal actions of Alkbh5 gene modulation and of a putative target, Lpin2. The work focuses on the DRG; it is important to note that the group also examines a retinal ganglion model where changes in Alkbh5 are not as prominent, and perhaps because of that the resulting effects of Alkbh5 modulation are not as pronounced. Thus, the effects of a broadly acting agent such as Alkbh5 might differ depending on the exact biology of the model. This doesn't diminish the finding at all, but the group nicely shows that the efficacy of Alkbh5 gene modulation might vary among different models.

A strength of the manuscript is the paper's use of reciprocal experimental designs to demonstrate effects. For instance, in Fig. 3 the authors show that Alkbh5 knockdown (KD) improves axonal regeneration and in Fig. 4 they show that Alkbh5 KD increases levels of methylated LPIN2, a transcript implicated in promoting axonal regeneration. Conversely, Figs. 5 and 6 also show that WT Alkbh5 over-expression inhibits axonal regeneration while an inactive Alkbh5 mutant has no effect. Alkbh5 KD is expected to increase levels of its target transcripts, and indeed, the group focuses on LPIN2 and shows that Alkbh5 KD increases LPIN2 adenosine methylation which is associated with a reciprocal decrease in total LPIN2 transcript (because m6A promotes degradation of the labeled transcripts). In Fig. 7 they go on to look at a specific target site of m6A on LPIN2. The hypothesis is that methylation of the target m6A site on LPIN2 will lead to a reduction in transcript levels; they show that mutating this target adenosine prevents the resulting effects of Alkbh5, implicating adenosine methylation in the modulation of LPIN2 levels. Finally, they show that over-expressing LPIN2 inhibits axonal regeneration while inhibiting LPIN2 increases regeneration. Thus, the experimental design includes many levels of reciprocal actions that are observed examining regeneration, adenosine methylation, and LPIN2 transcript levels. Taken together this approach is very convincing. The last figure examines the extent to which the KD approach extends to other models; the authors show that Alkbh5 is less active in a retinal ganglion model. The limited efficacy in the retinal ganglion is disappointing but serves to highlight the strength of the actions in the DRG model and provide a warning that the actions of Alkbh5 might vary significantly depending on the particular pathophysiology to which its gene modulation is being applied.

The manuscript does have some weaknesses, but the weaknesses are modest and do not change the overall interpretations of the manuscript. For instance, interpreting the quantitative efficacy in Fig. 1 and 2 depends on knowing the efficiency of uptake of the RNAi for Alkbh5 and subsequent virally transduce shAlkbh5, however, the authors do not show this efficiency. But such weaknesses are quite minor and do not change any of the conclusions.

Reviewer #1 (Public Review):

Baggett C., Murphy K. R., and Sengun E. et al. investigated cell senescence as the basis of pro-arrhythmogenic changes associated with myocardial infarction in the aged heart using the rabbit as a model, with validation of senescence markers on human heart specimens. The study is interesting and addresses a relevant biological and health issue. The authors demonstrate that aged rabbits are prone to arrhythmogenesis associated with higher mortality within 72 h after induction of myocardial infarction. Analysis of scar morphology determined that fibrosis is not sufficient to explain age-associated arrhythmogenesis. Instead, the authors show that senescence, assessed by -galactosidase activity, expression of regulators of the senescence-associated secretory phenotype, and H2AX, is increased in myofibroblasts compared to endothelial cells in infarcted aged rabbit hearts. Accordingly, H2AX was detected in αSMA+ cells in human-aged hearts. The authors tested the influence of myofibroblasts on cardiomyocyte electrophysiology by exposing cardiomyocytes in vitro to conditioned media from fibroblasts in which senescence was induced by treatment with etoposide. Such treatment did not affect action potential duration, leading the authors to conclude that senescent fibroblasts are unlikely to influence cardiomyocytes through paracrine signaling. Instead, the authors propose a possible yuxtacrine effect. To test this, they performed immunofluorescence to infer potential myofibroblast-cardiomyocyte coupling by the presence of connexin 43 in the cell-cell interphase and tested the potential electrophysiological effects of coupling using a computational model.

The analysis of peri-procedure mortality, arrhythmogenesis, and senescence in young and aged rabbits subjected to myocardial infarction is valuable, represents a significant amount of work, and the results support the conclusions drawn. Stronger evidence that senescent myofibroblasts couple with cardiomyocytes in the aged heart is needed to support the proposed model.

The authors conclude a propensity of myofibroblast senescence based on the finding that 80% of αSMA+ cells are also positive for H2AX. Showing the immunofluorescence results on hearts 2 weeks after MI would help to more convincingly illustrate the result. From these immunofluorescence experiments, it is also concluded that most of the persistent senescent cells in the scar correspond to myofibroblasts. The results presented show a continued increase in the proportion of H2AX+ cells in aged hearts up to 12 weeks after myocardial infarction. According to results in Figures 4F and G, these cells do not correspond to either myofibroblasts or endothelial cells. Given that H2AX+ cells are significantly increased in the aged heart, could the results presented suggest that a different cell type might be more important for the aged heart's response to MI? Providing some insight into the identity of these cells would be helpful to better understand the results presented. For example, cardiomyocyte senescence could contribute to arrhythmic phenotypes.

The results presented show that treatment of cardiomyocytes with conditioned media from, and co-cultured with, senescent myofibroblasts did not change action potential duration in cardiomyocytes. This led to the conclusion that paracrine signalling is unlikely to contribute to a pro-arrhythmogenic phenotype. It is possible that cardiomyocytes do couple with myofibroblasts in the in vitro system used. In which case, the results presented would not favor the proposed model. Another important possibility to be considered is that myofibroblasts might not have produced senescence-associated secretory phenotype-mediators at concentrations high enough to alter action potential duration in the conditions tested. Experimental evidence of the levels of selected mediators of the senescence-associated secretory phenotype in conditioned media would help assess a potential paracrine effect.

The evidence of coupling, i.e., the presence of connexin-43 in the interphase between αSMA+ and cardiomyocytes needs to be strengthened. Perhaps analyzing Z-stack 3D reconstructions would help to better define adjacent cells and more precisely reveal the localization of connexin-43.

Reviewer #2 (Public Review):

1) A detailed step-by-step approach to validation of some previously known outcomes.<br /> 2) Useful for more focus to be placed on data from the second half of the paper.<br /> 3) Some reflection on the media used to study paracrine effects is needed - more experiments here would be beneficial.<br /> 4) Path clamp experiments - how does bath solution alter the effect of any limited paracrine effect - we are removing cells from the treatment media and putting them in physiological solutions - an opportunity to recover?

Reviewer #1 (Public Review):

This manuscript describes the differences in the plasma proteome and metabolome in healthy Tanzanian and healthy Dutch adults. The inflammatory plasma proteome was measured using the Olink 92 Inflammation panel, while the plasma metabolome was analyzed using a mass spectrometry-based untargeted approach. The plasma metabolome was measured only in the Tanzanian cohort. This study aimed to link the pro-inflammatory proteome of Tanzanian and Dutch healthy individuals with environmental factors and dietary lifestyles.

The correlation between the plasma proteome and food-derived metabolome profiles can shed light on the development of non-communicable diseases. This observation stresses the importance of dietary transition and lifestyle changes in expressing inflammation-related molecules. Moreover, this study describes the inflammatory proteome profile in healthy Tanzanian individuals covering a cohort with limited studies. The molecular differences in circulating biomolecules between healthy individuals living in East Africa and individuals living in Western Europe and the correlations with intrinsic and environmental features are novel.

This study lacks a robust and solid validation of some of the differentially regulated circulating proteins and correlations between food-derived metabolites and proteins in a selected cohort. The discovery-driven approach in this manuscript highlights potential findings that need to be supported by a validation phase. According to this reviewer, the lack of such validation impacts the robustness of the results and the hypotheses generated. Due to that, the manuscript should incorporate validation experiments.

Reviewer #2 (Public Review):

This study assessed the inflammatory and metabolic profiles of a healthy sub-Saharan Africa (Tanzania) population versus a healthy population outside Africa (Dutch). Using plasma samples from these cohorts, an O-Link proteomics inflammatory panel and targeted metabolomics platforms were utilised. The study shows that 'healthy' Tanzanians display an enhanced pro-inflammatory phenotype versus Dutch volunteers. Specific pathways and metabolites identified included - increase activation of the Wnt/Beta catenin pathway, and the metabolites 4E-BP1 and FGF21. The study highlights some interesting findings regarding the impact of diet on inflammatory pathway activation.

Major Strengths & Weaknesses - This is an interesting study and approach that aims to address some challenging questions in underrepresented populations. The findings demonstrate the importance of diet and dietary interventions on metabolic health, as well as key inflammatory proteins. It does raise the question whether anti-inflammatory therapies need to be targeted to specific at-risk populations, more so than other populations.

Impact - The study demonstrates the importance of considering differences between populations and the inclusion of underrepresented populations in such studies. The data suggests that lifestyle changes in sub-Saharan Africa are potentially contributing to altered inflammatory and metabolic profiles. Thus, health initiatives advocating traditional diets may alleviate the NCD epidemic in sub-Saharan Africa.

Reviewer #1 (Public Review):

For PRLR, the question being asked is whether and how the intracellular domain (ICD) interacts with the cellular membrane or how the disordered ICD can relay and transmit information. The authors show that PI(4,5)P2 in the membrane localizes around the transmembrane domain (TMD) due to charge interactions and facilitates binding of the ICD to the membrane, even in the absence of the TMD. Furthermore, the ICD and PI(4,5)P2 form a co-structure with JAK2 which locks a disordered part of the ICD into an extended conformation, allowing for signal relay and, through multiple complex conformations, may enable switching signalling on and off.

Strengths:<br /> - NMR paired with MD is a powerful way to probe an interaction especially when peaks disappear and become difficult to probe by NMR.<br /> - Using NMR and MD to formulate hypotheses which are then tested by cell studies is quite informative. The combination of MD, NMR, and cell biology is a strength.<br /> - The authors are diligent in testing MD simulations on systems with and without PIP2.<br /> - The use of Pep1 and Pep2 to differentiate the KxK region that interacts with PIP2 is helpful.<br /> - The four utilized mutants help illustrate the co-dependence of the respective regions in the formation of the co-structure.

Weaknesses:

- In Figure 2G, there is a big change in CSP between 280 and 290, which the authors do not comment about.<br /> - The data in Figure 2 are summarized as indicating the formation of extended structure in the ICD upon binding. It is not clear to me what data show an extended structure.<br /> - No modelling or experiments were done with PIP3 despite conclusions and models which rely on the phosphorylation of PIP2 to PIP3. At the very least, these would be useful as negative controls.<br /> - Only R2 experiments were done when the authors mention investigating dynamics. R1 and -HetNOE dynamics would be useful for creating a complete picture.<br /> - Some of the exciting results are under-emphasized including Fig 3H and 3I.

Reviewer #2 (Public Review):

The authors combine NMR experiments, cell experiments, and molecular simulations to address the question of how lipid interactions of the prolactin receptor contribute to signalling. They assess the interactions of the disordered cytoplasmic tail of the receptor with phosphoinositides among others by chemical shift perturbations from NMR for different PIP2-containing membranes, by coarse-grained simulations, as well as site-directed mutagenesis and subsequent cell signalling experiments to monitor the activation of the mutants. A major result is that PIP2 interactions are functionally important, which so far has not been known for this receptor. Their results are likely relevant for other non-receptor tyrosine kinases.

The hypothesis that the protein complex is regulated by IDR-membrane interactions is very novel. A major strength is the close connection of and feedback between state-of-the-art experiments and simulations.

This is where I see weaknesses:<br /> 1. The motivation of focusing on LID1 is limited.<br /> 2. The data and analysis for the JAK2-PRLR complex appear somewhat superficial, and a connection between conformational states to their functional relevance is lacking. In fact, the majority of the simulation part of the paper is about suggesting different states of the PRLR-JAK2 complex but the states and their hypothesized functional relevance are not further taken up, e.g. by experiments, and yet presented as major results, e.g. in the abstract.<br /> 3. The connection between simulations and mutational study is not very direct.<br /> An open question is if the mutants can distinguish between the effects of PRLR-PIP2 interaction or PRLR-JAK2 interaction, even though this conclusion is still drawn from the data.<br /> 4. The conclusions drawn from the mutagenesis study (lines 547-555) are not directly supported by data. Only a partial correlation between PRLR membrane localisation and STAT5 activation is no reason to attribute the unexplained part of the STAT5 activation to PRLR-JAK2 interactions without further studies.<br /> 5. PIP2 is identified as an important regulator, with very solid support from the presented data. PIP3 is part of the model but not discussed before or as part of the results. The analysis could be similarly applied or the data directly relevant to the understanding of PIP3 plays a similar role, as interactions are likely primarily electrostatically driven.

Reviewer #3 (Public Review):

Araya-Secchi and coauthors present a very interesting study on the role of PIP2 lipids in the potential modulation of prolactin receptor signaling. The study is well-conducted and employs an integrated approach that combines NMR spectroscopy, modeling (primarily coarse-grain MD simulations), and cell biology. This combination of methods is crucial for gaining a deeper understanding of cell receptors, from their biophysical properties to their cellular functions.

The modelling work is mainly based on both coarse grain forcefield versions Martini2.2 and Martini3. These two versions of the forcefield may produce different results. Therefore, depending on the system being modeled, the results presented here should be considered in light of the limitations inherent to each version of the forcefield.

Reviewer #1 (Public Review):

The authors study single and pairs of MDCK cells adherent to an H-shaped geometry on a flat surface. In this pattern, the cells form strong peripheral stress fibers. To a lesser extent, these cells also exhibit stress fibers in the cell interior, which otherwise has a rather homogenous actin distribution. Using a combination of traction force microscopy, from which they infer the stress distribution by monolayer stress microscopy, and "contour analysis" the authors quantify the 'bulk' and the 'surface' stress in these cells. This analysis shows that single cells are mechanically polarized whereas pairs are not.

The authors then go on to optogenetically activate the actomyosin contractility of either one half of a single cell or one cell of a pair. Combining their stress measurements in these situations and using a finite element mechanical model, the authors convincingly show that the mechanical response in the non-activated part is active. By varying the aspect ratio of the adhesion patterns, they also find that the efficacy of active stress propagation depends on the mechanical and structural polarity of the cell. Furthermore, they provide evidence that their results on cell pairs generalize to tissues.

Strengths:

This study uses a nice combination of physical tools to address an important question in tissue mechanics. The data is compelling and fully supports the authors' conclusions.

Weaknesses:

There are no major weaknesses.

In summary, although the fact that mechanical stress propagation in tissues is an active process might not come as a surprise, the study makes substantial contributions to a quantitative contribution of this process. As such it is of fundamental significance in the field. It will be interesting to explore the consequences of this mechanism for mechanical stress propagation in the context of developmental processes. It will be also of great interest to study how this local process can be accounted for in large-scale theories.

Reviewer #2 (Public Review):

In A. Ruppel, et al, the authors study the mechanics of one cell, two cells, and cell monolayers upon a transient local activation of contractility. First, the authors characterize the tractions and stress maps (measured via Traction Force Microscopy and Monolayer Stress Microscopy, resp.) for one and two cells in the absence of contractility activation, and found a correlation between the principal stress direction and actin fiber orientation. Next, the authors use the theory of foams to infer, combining traction force data and cell geometry data, the mechanical parameters of cells like the line tension or the force of adherent fibers. Next, the authors activate contractility by means of optogenetic tools on one half of the system and quantify the response on both halves, concluding that the receiver half response is driven by active processes, increasing contractility for two cells, while fluidizing for one cell. Next, the authors estimate the level of active response in cell doublets by comparing the stress maps to numerical simulations of a thin elastic medium with anisotropic contractility. By varying aspect ratios of the H pattern, the authors find a correlation between the principal stress direction and the orientation of stress fibers and find that the previous active response is in general enhanced when the principal stress direction is perpendicular to the orientation of the fibers. Finally, these features are also found in a cell monolayer for a fixed confinement aspect ratio.

Overall, the manuscript contains a broad characterization of the steady state mechanics and the dynamical response to the activation of contractility for one cell, two cells, and cell monolayers.

Reviewer #1 (Public Review):

Overall, this manuscript by Liu et al. provides a largely convincing mechanism for both how Zfp467 regulates osteoblast differentiation and how PTH1R expression and function in osteoblast-lineage cells is regulated at the transcriptional level, finding that NF-kB (RelB/p50) regulates PTH1R expression downstream of Zfp467. PTH1R expression and activity in turn is enhanced in Zfp467-deficient osteoblasts. In turn, PTH signaling regulates Zfp467 expression through PKA activity. In particular, the new findings on mechanisms of regulating PTH1R expression and evidence that this in turn impacts osteoblast differentiation are felt to be of broad interest and importance. The approach used is felt to be largely sound. Areas of major concern are few and relate mostly to better fleshing out how the NF-kB pathway is impacted as a part of the molecular pathway implicated here and clarifying some confusion regarding uCT data that appears to be discussed but which this reviewer cannot locate in the figure.

Reviewer #2 (Public Review):

The authors hypothesized that PTH1R and ZFP467 could constitute a feedback loop that facilitates PTH-induced osteogenesis and that conditional deletion of Zfp467 in osteogenic precursors would lead to high bone mass. Using a number of methods, they have established a regulatory feedback mechanism of this transcription factor and the PTH receptor in osteoblastic precursors as well as showing that PrrxCre deletion of Zfp467 causes an increase in trabecular bone mass, while AdipoCre does not. Nevertheless, they have not established the actual mechanism of action of the transcription factor nor which gene it acts on in the osteoblast. They have mostly achieved their aims and the results partially support their conclusions. However, the work is descriptive and does not address the central issue of how ZFP467 acts. At present, its impact on the field is limited.

Reviewer #3 (Public Review):

In this paper the authors report a new pathway by which PTH, by activating PTH1R, increases bone mass. Specifically, they describe that PTH1R and the transcription factor Zfp467 are part of a feedback loop that promotes PTH-induced osteogenesis. By using in vivo mouse models, they indicate that deletion of Zfp467 in osteoblast progenitors increases bone mass and osteogenic differentiation whereas deletion of Zfp467 in adipocytes does not cause any bone phenotype, suggesting that deletion of Zfp467 in mesenchymal progenitors is important for bone mass. With a series of in vivo studies, they demonstrate that PTH suppresses Zfp467 expression via the cyclic AMP-PKA pathway and genetic deletion of Zfp467 causes increased PTH1R transcription by increasing nuclear translocation of p50 and activation of the P2 promoter, thus increasing the expression of PTH1R and the cellular responsiveness to PTH.

The strength of the paper are the use of genetically modified animal models, the analysis of both female and male mice and the logic flow of the in vitro data. The weaknesses of the paper are the wrong conclusion that the phenotype of the PrrxCre Zfp467 mice perfectly recapitulates one of the global Zfp467 KO mice, the lack of histomorphometric data showing increased osteoblastogenesis and the missing evidence that the forward feedback loop is relevant to the response to PTH in vivo. The analysis is therefore incomplete. Once those points are addressed, this paper would be of great interest in the bone field.

Reviewer #1 (Public Review):

In this study, the authors sought to develop a measure of Staphylococcus aureus intracellular virulence levels in the lab (the InToxSa assay) that more closely mimics the activity seen in vivo. They then used untargeted approaches (GWAS, homoplasy) on a set of 387 Australasian clinical isolates to identify genes with mutants associated with reduced intracellular toxicity. The authors identified several mutated genes which reduced virulence in the strains chosen for the study, demonstrating that their approach can be used to uncover virulence-related genes in S. aureus.

The study is clearly written, with high-quality figures. The development of the InToxSa assay is carefully described and logical. InToxSa was shown to potentially be more sensitive than the tryptophan blue test in detecting reduced intracellular cytotoxicity phenotype. They also showed evidence for agrA mutants and other transposon mutants with reduced inToxSa cytotoxicity having increased bacterial cell numbers cells compared to wild-type (Fig 2, Fig5GH), which is critical to the argument that bacteremia selects for intracellular persistence as a way to escape the immune system. There was an interesting and thoughtful use of random forest to choose the most appropriate parameters of the kinetic model.

The GWAS studies used publicly deposited genome data and clearly showed lineage effects of reduced intracellular survival of CC239 and CC22, confirming previous results. GWAS also confirmed the well-known pervasive association of agr mutants with reduced toxicity. Using a well-described homoplasy test for convergent evolution to extract more power, several other potential genes associated with enhanced intracellular toxicity were discovered or rediscovered, perhaps most significantly, the ausA gene, with biosynthesizes aureusimines (pyrazinone secondary metabolites) posited to have a role in the phagosomal escape.

There are two main 'weaknesses'. The first is the limited power that comes from only using measuring the phenotype of 387 strains. Whether this is because of the expense/ difficulty of the inToxSa is not discussed, leaving open the question of how much this assay could be scaled up in the future. The second is that the main output of the assay is actually reduced intracellular toxicity (PI uptake AUC), which is inferred to be strongly linked to increased intracellular persistence. The linkage between the phenotypes comes primarily from microscopic studies on a limited number of strains. It may be true of all cases but the possibility exists that for some of the strains, reduced cytotoxicity may be associated with intracellular elimination, which would presumably be a negative outcome for systemic infection.

Overall, the authors achieved their aims in terms of assay development and showing the utility of the pipeline for mutation discovery. This is a waypoint in the larger aim of understanding mutational pathways that lead to increased persistence of systemic S. aureus. Obviously, a lot more data is needed. The InToxSa intracellular screening method is interesting and could be reused/adapted by the community. This research should also spark more interest in the role of ausA and aureusimines in virulence and some of the other genes discovered through the untargeted approach.

Reviewer #2 (Public Review):

This manuscript introduces a novel assay in a 'phenomics' approach to address an important aspect of S. aureus pathogenesis. The authors set out to identify mutations that arise during clinical S. aureus infections that cause a decrease in intracellular host-cell toxicity and increase intracellular persistence. To do this, they use a 'phenomics' approach. For phenotype, they quantify HeLa cell toxicity for each strain in a panel of 387 clinical S. aureus isolates. This is done by measuring HeLa cell death induced by intracellular S. aureus via propidium-iodide uptake. The whole genomes of each of these 387 isolates had previously been sequences. They use the genomic data and phenotype data to carry out a genome-wide association study (GWAS) looking for genetic signatures that correlate with reduced HeLa cell cytotoxicity. As expected, mutations in agr were the strongest locus-level signal, but the study did identify one agr-independent mutation in ausA, which was able to be independently validated, showing that the assay is robust enough to find causal mutations. The analysis is thoughtful, the assay appears robust, and I think the discussion of conclusions and limitations is mostly valid. Thus, my concerns are focused on further understanding the practical utility of the approach and whether or not the HeLa cell model recapitulates what happens in professional phagocytes. For example, it is not clear to me that this system has the statistical power to find novel, biologically relevant rare mutations without first being very mindful in selecting strains that are extremely genetically similar. It is also not clear to me that the toxicity assay captures the important features of the intracellular persistence that occurs in vivo within professional phagocytic cells. Thus, given these practical limitations and a somewhat artificial model system, the impact on the field is likely to be moderate in nature. However, the analysis and approach taken could be re-purposed to any robust quantitative phenotype, and this will certainly be of great interest to others that study bacterial evolution in clinical contexts.

Reviewer #1 (Public Review):

In this paper, Krishnan et al. describe their findings on the genetic architecture of the heart mitochondrial proteome that influences cardiac hypertrophy. They analyzed common genetic variations contributing to mitochondrial and heart functions in a panel of inbred mouse strains called the Hybrid Mouse Diversity Panel (HMDP), by performing whole heart proteomics. The authors have published a number of papers on this panel, which appears to be a powerful system to study various genetic factors. They identified three trans-acting genetic loci, located on chromosome (chr) 7, chr13, and chr17, which control both mitochondrial proteins and heart hypertrophy. High-resolution regional mapping identified NDUFS4, LRPPRC, and COQ7 as the candidate genes for chr13, chr17, and chr7 loci, and variations of these genes were associated with heart mass in isoproterenol-induced heart failure and diet-induced obesity. Using co-expression protein networks using weighted gene co-expression network analysis (WGCNA), they show that the chr13 locus was highly enriched for complex-I proteins, the chr17 locus for mitochondrial ribonucleoprotein complex, and the chr7 locus for ubiquinone biosynthesis. They concluded that "common variations of certain mitochondrial proteins can act in trans to influence mitochondrial functions and contribute to heart hypertrophy, elucidating mechanisms that may underlie genetic susceptibility to heart failure in human populations."

Although these studies are interesting and provide novel findings in the genetics of cardiac hypertrophy, there are a number of technical and conceptual issues that need to be addressed.

Reviewer #2 (Public Review):

Krishnan, et al describe a unique and powerful approach to assessing the role of genetic variation on mitochondrial and cardiac function and health. Utilizing a panel of inbred mouse strains, on which they performed proteomics on heart samples, they measured 840 mitochondrial proteins and correlated these data to heart function using two heart stress models. This resulted in a number of correlative observations, three of which were explored in more detail to connect three specific genes to cardiac hypertrophy. This is an interesting dataset and there is clearly value in what is presented. The data were largely correlative, however, and there are only a couple of causation-oriented experiments. It's hard to adjudicate between these strengths and weaknesses in determining the overall impact of the manuscript.

Reviewer #3 (Public Review):

The goal of this study is to identify mitochondrial pathways that would have an impact on the process of pathological cardiac hypertrophy. The paper presents a state-of-the-art analysis of the SNP variant and regulatory hot spots associated with quantitative traits, here mitochondrial protein levels and cardiac hypertrophy, using the Hybrid Mouse Diversity Panel. They identify 3 hotspots of trans-acting genetic loci that correlate with the level of proteins involved in complex I assembly, mitochondrial mRNA stability, and CoQ synthesis.

The study is overall very interesting and brings valuable information to the field. However, the impact of each of these loci on cardiac hypertrophy level, even if statistically significant, seems to be rather limited raising questions on the clinical relevance of the findings. It is an interesting study anyway and points to pathways that will deserve to be further explored in the future in clinical studies on human patients.

Reviewer #1 (Public Review):

Mermithid nematodes are ecologically important parasitoids of arthropods, annelids and mollusks today. Their fossil record in amber reaches back into the Early Cretaceous, some 135 million years ago. Luo et al. more than triple this record by presenting, with ample illustrations, exceptionally well preserved new specimens from the beginning of the Late Cretaceous (99 Ma ago) of Myanmar. Their most important finding is that mermithids parasitized a number of insect clades in the Cretaceous that they are not known to infect today or in Cenozoic amber; further, the proportion of holometabolous insects among the hosts is found to be lower in the Cretaceous than in the Cenozoic. The strengths of the paper lie in the specimens, the illustrations of the specimens, and the documentation of when, where and how the specimens were acquired. Certain nomenclatural aspects of the paper require improvement. A potential weakness of the paper could be collection bias: it is not tested whether the collections used to show the shift toward holometabolous hosts from the mid-Cretaceous to the Cenozoic are representative of the fossil record as it is preserved and accessible today.

Reviewer #2 (Public Review):

This manuscript reports on mermithid nematode fossils from amber which dates from the Cretaceous period. The specimens described in the manuscript consist of insects and associated nematodes which have been trapped in amber and fossilised. The nematodes have been identified as belonging to the Mermithidae family, a family of nematode worm that infect insects.

The findings of this manuscript provide an insight into the evolution history of nematodes and parasitism. Despite the ubiquity of both nematodes and parasites in extant ecosystems, fossil records of both are very rare. This is because nematodes and many parasites are soft bodied, and many are located inside their hosts' bodies, thus they rarely become fossilised. Thus, most of what is known about the evolutionary history of nematodes, and evolution of parasitism are based on what could be inferred from extant examples.

The specimens described in this manuscript provides a valuable contribution to our understanding of parasitism in the geological past. These amber specimens are a snapshot of parasite-host interactions - interactions which are commonly found in nature but are rarely captured in fossils. The identification of the specimens as mermithid nematodes are based on sound scientific reasoning. The worms' morphology and position in relation to the insects are consistent with what have been observed with extant mermithid nematodes.

Additionally, one of the values of such parasite fossils is that they provide us with insight into parasite-host combinations or interactions which may have existed throughout the geological past, but no longer exist today or cannot be inferred from extant taxa. It helps fill in major gaps in our understanding of parasitism. This was the case with the amber fossil that contained a bristletail with its nematode parasite.

Reviewer #3 (Public Review):

The authors provide a timely description of new mermithid nematodes from Cretaceous amber and use it to argue an important shift in insect host exploitation. The descriptions are state-of-the-art and will become valid once the appropriate zoobank numbers are used after publication. The authors also compiled crucial and detailed new information on the host exploitation in amber nematodes in the supplementary material. This data is also depicted in pie diagrams and seems at first glance to support their interpretations of a shifts in host exploitation in fossil amber deposits when analysed appropriately and statistically but such an true analysis and depiction should be part of the main manuscript to do the compilation and interpretation justice. For the sake of reproducibility and the field, such fundamental statistical analysis as well as a statistical comparison with modern hosts would make this broad-sweeping claim of a major host shift and importance of amber deposits containing such nematode-insect interactions since the Cretaceous (even) more robust and fundamental.

Reviewer #1 (Public Review):

This paper investigates the neural correlates of noise-induced hearing loss. The authors use an electrode array to capture neural responses across the inferior colliculus to speech and synthetic sounds in both normal-hearing gerbils, and gerbils with noise-induced hearing loss. They use dimensionality reduction to isolate a low-dimensional response subspace that captures most of the information about the speech signals, and find that this low-dimensional representation is altered considerably by hearing loss (evaluated with CCA). To probe the basis of these differences, the authors train an artificial neural network to predict the subspace responses to arbitrary stimuli, for instance to investigate the consequences of frequency-dependent amplification of sound with a hearing aid, or synthetic test stimuli. Using this approach, they find that the representation of sounds in quiet is largely restored by a hearing aid algorithm that amplifies high frequencies to render them audible. However, the representation of sounds in noise also differs between the IC of normal-hearing and hearing-impaired gerbils, and this difference is not eliminated by a hearing aid. Specifically, low-frequency maskers seem to distort the representation of high-frequency sounds (e.g. consonants in speech), even once the high-frequencies have been amplified to compensate for the hearing loss.

Overall, this is a strong paper. The topic is important, the methods are innovative, logical, and rigorous, and the whole thing is exceptionally clearly described. I greatly appreciate the care that clearly went into writing the paper. I have two major concerns. The first seems fairly critical to the paper's conclusions, but I hope can be addressed with some kind of control experiment. The second could potentially be thought of as more of a future direction, but it speaks to the specificity of the conclusions.

1. My main substantive concern is that the conclusions depend critically on believing the predictions of the DNN, and yet it is not clear we should expect it to generalize well to stimuli outside its training distribution. Current artificial neural networks typically work very well for stimuli like those they were trained on, but often do not generalize as well as one might like. The authors recorded responses to speech in quiet and in different noise levels, and show that the trained DNN (trained on these sounds and the associated responses) produces very accurate predictions on held-out sounds from this distribution. But the conclusions depend critically on the DNN predictions for sound processed by a hearing aid, and for synthetic sounds (pure tones, SAM noises) that are quite unlike the training data. The predictions look reasonable in places where we have some prior sense for what to expect (level-dependent frequency tuning to pure tones), which is reassuring, but I am not sure how to be confident that the predictions should be accurate for all of the conditions that are tested, in particular to the results with the simulated hearing aid. I am pretty sure that the predictions will be inaccurate for some types of stimuli (just based on the various pathologies that are known to occur with neural networks). I would hope that this would not be the case for the conditions tested by the authors, but it is hard to be sure, and this makes the conclusions seem a little more vulnerable than I would like.<br /> How do we know that the DNN generalizes beyond its training data well enough to render the conclusions airtight?

2. My second concern is the extent to which the results are specific to a) the IC, and b) noise. The authors assert that similar effects would not be present in the nerve, citing a Heinz paper, but I am not sure how clear this evidence is - it is not described in enough detail here to assess. It would be nice to show this, perhaps by repeating their analysis on a model of the nerve with and without simulated hearing loss. One can similarly wonder about the effects in the cortex, especially given the literature on noise invariance (Rabinowitz, Moore, Khalighinejad, Kell...), which would at least be worth discussing. It is similarly unclear whether the results are specific to additive noise. Would similar conclusions hold for any type of distortion? This could be easily addressed by an additional DNN analysis (e.g. with clipping, or segments of speech intermittently replaced by silence, or reverberation).

Reviewer #2 (Public Review):

This very interesting study uses a combination of high channel count neural recordings and machine learning to characterize neural representations of complex natural and synthetic sounds in the inferior colliculus. The authors use deep neural networks to model sound evoked activity in a large number of IC multiunits with high accuracy in gerbils with normal hearing and hearing loss. They then use the DNNs to simulate activity evoked by a wide range of stimuli and demonstrate systematic differences in latent population representations between normal hearing and hearing-impaired animals. Models for hearing impaired animals show activity consistent with impaired representations of speech in noise. These results lay the groundwork for a potentially valuable approach to improving signal processing in hearing aids and prosthetics.

The large speech dataset and clean hearing loss effects are particularly impressive. While the approach and associated data are novel and likely to be of broad interest, there are some substantial concerns about the study. First, the authors fail to acknowledge substantial previous work on super-threshold activity in cortex of animals with hearing loss, making it appear that they overstate the novelty of the current results. There are also many cases where they fail to clearly report the details of statistics used to support their claims. Finally, while the accuracy of the DNN models is compelling for the speech stimuli in the data set, it is not clear that the comparisons of simulated activity reflect actual neural activity in the stimulus conditions tested.

Reviewer #1 (Public Review):

In this manuscript, Li et al characterize sex differences in the impact of macrophage RELMa in protection against diet-induced obesity [DIO]. This is a key area of interest as obesity studies in mice have generally focused exclusively on male animals, as they tend to gain more weight, faster than female mice. The authors use a combination of flow cytometry, adoptive transfer, and single-cell transcriptomics to characterize the mechanism of action for female-specific DIO protection. They identify a potential role for eosinophils in mediating female DIO protection downstream of RELMa production by macrophage. They also use the transcriptomic characterization of the stromal vascular fraction of the adipose tissue to evaluate molecular and cellular drivers of this sex-specific DIO protection.<br /> Although the authors provide solid evidence for many claims in the manuscript, there is generally not enough information about the studies' methods (especially on the computational/data analysis aspects) for a careful evaluation of the result's robustness at this stage.

Reviewer #2 (Public Review):

In the study by Li et al., the authors hypothesize that RELMa, a macrophage-derived protein, plays a sex-dimorphic role as a protective factor in obesity in females vs males. The authors perform largely in vivo studies utilizing male and female WT and RELMa KO mice on a high-fat diet and perform an in-depth analysis of immune cell composition, gene expression, and single-cell RNA Sequencing. The authors find that WT females are protected from obesity and inflammation vs males, and this protection is lost in female RELMa KO mice. Further analysis by the authors including flow cytometry of the visceral fat SVF in female WT mice showed reduced macrophage infiltration, higher levels of eosinophils, and Th2 cytokine expression compared to WT male mice and female KO mice. The authors show that protection from obesity and inflammation in female RELMa KO mice can be rescued with an injection of eosinophils and recombinant RELMa. Lastly, the authors use single-cell RNA-Sequencing to further analyze SVF cells in WT and KO male and female mice on a high-fat diet.

Overall, we find that the study represents an important finding in the immunometabolism field showing that RELMa is a key myeloid-derived factor that helps influence the macrophage-eosinophil function in female mice and protects from diet-induced obesity and inflammation in a sexually dimorphic manner. Overall, the study provides strong and convincing data supporting the authors' hypothesis and conclusion.

Reviewer #3 (Public Review):

Li, Ruggiero-Ruff et al. examine the role of RELMα, an anti-inflammatory macrophage signature gene, in mediating sex differences in high-fat diet (HFD)-induced obesity in young mice. Specifically, the authors hypothesize that RELMα protects females against HFD-induced obesity. Comparisons between RELMα-knockout (KO) and wildtype (WT) mice of both sexes revealed sex- and RELMα-specific differences in weight gain, immune cell populations, and inflammatory signaling in response to HFD. RELMα-deficiency in females led to increased weight gain, expansion of pro-inflammatory macrophage populations, and eosinophil loss in response to HFD. Female RELMα-deficiency could be rescued by RELMα treatment or eosinophil transfer. Single-cell RNA-sequencing (scRNA-seq) of adipose stromal vascular fraction (SVF) revealed sex- and RELMα-dependent differences under HFD conditions and identified potential "pro-obesity" and "anti-obesity" genes in a cell-type-specific manner. Using trajectory analysis, the authors suggest dysregulation of macrophage-to-monocyte transition in RELMα-deficient mice.

The conclusions of this paper are mostly well supported by the data, but some aspects of the statistical and single-cell analyses will need to be corrected, clarified, and extended to enhance the report.

Strengths:<br /> The authors use several orthogonal approaches (i.e., flow cytometry, immunohistochemistry, scRNA-Seq) and models to support their hypotheses.

The authors demonstrate that phenotypes observed in HFD-fed females with RELMα-deficiency (i.e., weight gain, loss of eosinophils, a gain of M1 macrophages) can be rescued by RELMα treatment or eosinophil transfer.

The authors recognized the complexity of macrophage activation that is beyond the 'M1/M2' paradigm and informed readers in the introduction as to why this paradigm was used in this study. During the scRNA-seq analyses, the authors further sub-cluster macrophages to include more granularity.

Weaknesses:<br /> There are several instances in the text where the authors claim that there is a significant difference between the two groups, but the statistics for these comparisons are not shown in the figure.

It is unfortunate that eosinophils could not be identified in the single-cell analysis since this population of cells was shown to be important in rescuing the RELMα-deficiency in HFD-fed females. The authors should note in the discussion how future scRNA-Seq experiments could overcome this limitation (i.e., enriching immune cells prior to scRNA-Seq).

There are several issues with the scRNA-Seq analysis and interpretation. More details on the steps taken in the single-cell analyses should be included in the methods section. With regards to the 'pseudobulk' analyses presented in Figs. 5-6, several of the differentially expressed genes identified in Fig. 6 are hemoglobin genes (i.e., Hba, Hbb genes). It is not uncommon to filter these genes out of single-cell analysis since their presence usually indicates red blood cell (RBC) contamination (PMID: 31942070, PMID: 35672358). We would recommend assessing RBC contamination as well as removing Fig. 6 from the manuscript and focusing on cell-type-specific analyses. Re-analysis will likely have an impact on the overall conclusions of the study.

Within the text, there are several instances where the authors claim that a pathway is upregulated based on their Gene Ontology (GO) over-representation analysis (ORA). To come to this conclusion, the authors identify genes that are upregulated in one condition and then perform GO-ORA on these genes. However, the authors do not consider negative regulators, whose upregulation would actually decrease the pathway. Authors should either replace their GO-ORA analysis with one that considers the magnitude and direction of differentially expressed genes and provides an activation z-score (i.e., Ingenuity Pathway Analysis) or replace instances of 'upregulated' or 'downregulated' pathways with 'over-represented' pathways.

For Fig.7A, a representative tSNE plot for each group (WT Female, KO Female, WT Male, KO Male) should be shown to ensure there is proper integration of the clusters across groups. There are some instances where the scRNA-Seq data do not appear to be integrated properly (i.e., Supplemental Figure 2C). The authors should explore integration techniques (i.e., Seurat; PMID: 29608179) to correct for potential batch effects within the analysis.

LncRNA Gm47283 is identified as a gene that is differentially expressed by genotype in HFD females (Fig. 7G); however, according to Ensembl this gene is encoded on the Y-chromosome (https://uswest.ensembl.org/Mus_musculus/Gene/Summary?g=ENSMUSG00000096768;r=Y:90796007-90827734). The authors should use the RELMα genotype and sex chromosomally-encoded genes to confirm that their multiplexing was appropriate.

For Fig. 8, samples should be co-clustered and integrated across groups before performing trajectory analysis to allow for direct comparisons between groups.

Since the experiments presented in this report were from young mice using a single diet intervention, the authors should comment on how age and other obesogenic diets may impact the results found here. Also, the authors should expand their discussion as to what upstream regulators (i.e., hormones or genetics) may be driving the sex differences in RELMα expression in response to HFD.