Reviewer #3 (Public Review):

Summary:

The receptor binding domain of SARS-Cov-2 spike protein contains two N-glycans which have been conserved by the variants observed in these last 4 years. Through the use of extensive molecular dynamics, the authors demonstrate that even if glycosylation is conserved, the stabilization role of glycans at N343 differs among the strains. They also investigate the effect of this glycosylation on the binding of RBD towards sialylated gangliosides, as a function of evolution.

Strengths:

The molecular dynamics characterization is well performed and demonstrates differences in the effect of glycosylation as a factor of evolution. The binding of different strains to human gangliosides shows variations of strong interest. Analyzing the structure function of glycans on SARS-Cov-2 surface as a function of evolution is important for the surveillance of novel variants since it can influence their virulence.

Weaknesses:

The article is difficult to read, with no sufficient efforts of clarification for non-glycobiology audiences. The presentation of previous knowledge about RBD glycosylation and its effect on structure is very difficult to follow and should be reorganized. The choice of the nature of the biantennary glycan at N343 is not rationalized. A major weakness is the absence of data supporting the proposed binding site for ganglioside.

Reviewer #1 (Public Review):

Summary:

This is an interesting and potentially important paper, which however has some deficiencies.

Strengths:

A significant amount of potentially useful data.

Weaknesses:

One issue is a confusion of thermal stability with solubility. While thermal stability of a protein is a thermodynamic parameter that can be described by the Gibbs-Helmholtz equation, which relates the free energy difference between the folded and unfolded states as a function of temperature, as well as the entropy of unfolding. What is actually measured in PISA is a change in protein solubility, which is an empirical parameter affected by a great many variables, including the presence and concentration of other ambient proteins and other molecules. One might possibly argue that in TPP, where one measures the melting temperature change ∆Tm, thermal stability plays a decisive or at least an important role, but no such assertion can be made in PISA analysis that measures the solubility shift.

Another important issue is that the authors claim to have discovered for the first time a number of effects well described in prior literature, sometimes a decade ago. For instance, they marvel at the differences between the solubility changes observed in lysate versus intact cells, while this difference has been investigated in a number of prior studies. No reference to these studies is given during the relevant discussion.

The validity of statistical analysis raises concern. In fact, no calculation of statistical power is provided. As only two replicates were used in most cases, the statistical power must have been pretty limited. Also, there seems to be an absence of the multiple-hypothesis correction.

Also, the authors forgot that whatever results PISA produces, even at high statistical significance, represent just a prediction that needs to be validated by orthogonal means. In the absolute majority of cases such validation is missing.

Finally, to be a community-useful resource the paper needs to provide the dataset with a user interface so that the users can data-mine on their own.

Reviewer #2 (Public Review):

Summary:

Using K562 (Leukemia) cells as an experimental model, Van Vracken et. al. use Thermal Proteome Profiling (TPP) to investigate changes in protein stability after exposing either live cells or crude cell lysates to a library of anti-cancer drugs. This was a large-scale and highly ambitious study, involving thousands of hours of mass spectrometry instrument time. The authors used an innovative combination of TPP together with Proteome Integral Solubility Alternation (PISA) assays to reduce the amount of instrument time needed, without compromising on the amount of data obtained.

The paper is very well written, the relevance of this work is immediately apparent, and the results are well-explained and easy to follow even for a non-expert. The figures are well-presented. The methods appear to be explained in sufficient detail to allow others to reproduce the work.

Strengths:

Using CDK4/6 inhibitors, the authors observe strong changes in protein stability upon exposure to the drug. This is expected and shows their methodology is robust. Further, it adds confidence when the authors report changes in protein stability for drugs whose targets are not well-known. Many of the drugs used in this study - even those whose protein targets are already known - display numerous off-target effects. Although many of these are not rigorously followed up in this current study, the authors rightly highlight this point as a focus for future work.

Weaknesses:

While the off-target effects of several drugs could've been more rigorously investigated, it is clear the authors have already put a tremendous amount of time and effort into this study. The authors have made their entire dataset available to the scientific community - this will be a valuable resource to others working in the fields of cancer biology/drug discovery.

Reviewer #3 (Public Review):

Summary:

This work aims to demonstrate how recent advances in thermal stability assays can be utilised to screen chemical libraries and determine the compound mechanism of action. Focusing on 96 compounds with known mechanisms of action, they use the PISA assay to measure changes in protein stability upon treatment with a high dose (10uM) in live K562 cells and whole cell lysates from K562 or HCT116. They intend this work to showcase a robust workflow that can serve as a roadmap for future studies.

Strengths:

The major strength of this study is the combination of live and whole cell lysates experiments. This allows the authors to compare the results from these two approaches to identify novel ligand-induced changes in thermal stability with greater confidence. More usefully, this also enables the authors to separate the primary and secondary effects of the compounds within the live cell assay.

The study also benefits from the number of compounds tested within the same framework, which allows the authors to make direct comparisons between compounds.

These two strengths are combined when they compare CHEK1 inhibitors and suggest that AZD-7762 likely induces secondary destabilisation of CRKL through off-target engagement with tyrosine kinases.

Weaknesses:

One of the stated benefits of PISA compared to the TPP in the original publication (Gaetani et al 2019) was that the reduced number of samples required allows more replicate experiments to be performed. Despite this, the authors of this study performed only duplicate experiments. They acknowledge this precludes the use of frequentist statistical tests to identify significant changes in protein stability. Instead, they apply an 'empirically derived framework' in which they apply two thresholds to the fold change vs DMSO: absolute z-score (calculated from all compounds for a protein) > 3.5 and absolute log2 fold-change > 0.2. They state that the fold-change threshold was necessary to exclude non-specific interactors. While the thresholds appear relatively stringent, this approach will likely reduce the robustness of their findings in comparison to an experimental design incorporating more replicates. Firstly, the magnitude of the effect size should not be taken as a proxy for the importance of the effect. They acknowledge this and demonstrate it using their data for PIK3CB and p38α inhibitors (Figures 2B-C). They have thus likely missed many small, but biologically relevant changes in thermal stability due to the fold-change threshold. Secondly, this approach relies upon the fold-changes between DMSO and compound for each protein being comparable, despite them being drawn from samples spread across 16 TMT multiplexes. Each multiplex necessitates a separate MS run and the quantification of a distinct set of peptides, from which the protein-level abundances are estimated. Thus, it is unlikely the fold changes for unaffected proteins are drawn from the same distribution, which is an unstated assumption of their thresholding approach. The authors could alleviate the second concern by demonstrating that there is very little or no batch effect across the TMT multiplexes. However, the first concern would remain. The limitations of their approach could have been avoided with more replicates and the use of an appropriate statistical test. It would be helpful if the authors could clarify if any of the missed targets passed the z-score threshold but fell below the fold-change threshold.

The authors use a single, high, concentration of 10uM for all compounds. Given that many of the compounds likely have low nM IC50s, this concentration will often be multiple orders of magnitude above the one at which they inhibit their target. This makes it difficult to assess the relevance of the off-target effects identified to clinical applications of the compounds or biological experiments. The authors acknowledge this and use ranges of concentrations for follow-up studies (e.g. Figure 2E-F). Nonetheless, this weakness is present for the vast bulk of the data presented.

The authors claim that combining cell-based and lysate-based assays increases coverage (Figure 3F) is not supported by their data. The '% targets' presented in Figure 3F have a different denominator for each bar. As it stands, all 49 targets quantified in both assays which have a significant change in thermal stability may be significant in the cell-based assay. If so, the apparent increase in % targets when combining reflects only the subsetting of the data. To alleviate this lack of clarity, the authors could update Figure 3F so that all three bars present the % targets figure for just the 60 compounds present in both assays.

Aims achieved, impact and utility:

The authors have achieved their main aim of presenting a workflow that serves to demonstrate the potential value of this approach. However, by using a single high dose of each compound and failing to adequately replicate their experiments and instead applying heuristic thresholds, they have limited the impact of their findings. Their results will be a useful resource for researchers wishing to explore potential off-target interactions and/or mechanisms of action for these 96 compounds, but are expected to be superseded by more robust datasets in the near future. The most valuable aspect of the study is the demonstration that combining live cell and whole cell lysate PISA assays across multiple related compounds can help to elucidate the mechanisms of action.

Joint Public Review:

Summary:

Brauns et al. work to decipher the respective contribution of active versus passive contributions to cell shape changes during germ band elongation. Using a novel quantification tool of local tension, their results suggest that epithelial convergent extension results from internal forces.

Strengths:

The approach developed here, tension isogonal decomposition, is original and the authors made the demonstration that we can extract comprehensive data on tissue mechanics from this type of analysis.

They present an elegant diagram that quantifies how active and passive forces interact to drive cell intercalations.

The model qualitatively recapitulates the features of passive and active intercalation for a T1 event.

Regions of high isogonal strains are consistent with the proximity of known active regions.

They define a parameter (the LTC parameter) which encompasses the geometry of the tension triangles and allows the authors to define a criterium for T1s to occur.

The data are clearly presented, going from cellular scale to tissue scale, and integrating modeling approach to complement the thoughtful description of tension patterns.

Weaknesses:

The modeling is interesting, with the integration of tension through tension triangulation around vertices and thus integrating force inference directly in the vertex model. However, the authors are not using it to test their hypothesis and support their analysis at the tissue level. Thus, although interesting, the analysis at the tissue level stays mainly descriptive.

Major points:

(1) The authors mention that from their analysis, they can predict what is the tension threshold required for intercalations in different conditions and predict that in Snail and Twist mutants the T1 tension threshold would be around √2. Since movies of these mutants are most probably available, it would be nice to confirm these predictions.

(2) While the formalism is very elegant and convincing, and also convincingly allows making sense of the data presented in the paper, it is not all that clear whether the claims are compatible with previous experimental observations. In particular, it has been reported in different papers (including Collinet et al NCB 2015, Clement et al Curr Biol 2017) that affecting the initial Myosin polarity or the rate of T1s does not affect tissue-scale convergent extension. Analysis/discussion of the Tor phenotype (no extension with myosin anisotropy) and the Eve/Runt phenotype (extension without Myosin anisotropy), which seem in contradiction with an extension mostly driven by myosin anisotropy.

Reviewer #1 (Public Review):

The manuscript by Long et al. focused on SUL1, a gene encoding a sulfate transporter with signaling roles in yeast. The authors claim that the deletion of SUL1, rather than SUL2 (encoding a similar transporter), extended yeast replicative lifespan independent of sulfate transport. They also show that SUL1 loss-of-function mutants display decreased PKA activity, indicated by stress-protective carbohydrate accumulation, relevant transcription factor relocalization (measured during aging in single cells), and changes in gene expression. Finally, they show that loss of SUL1 increases autophagy, which is consistent with the longer lifespan of these cells. Overall, this is an interesting paper, but additional work should strengthen several conclusions, especially for the role of sulfate transport. Specific points include the following:

- What prompted the authors to measure the RLS of sul1 mutants? Prior systematic surveys of RLS in the same strain background (which included the same sul1 deletion strain they used) did not report lifespan extension in sul1 cells (PMID: 26456335).

- Cells carrying a mutant Sul1 (E427Q), which was reported to be disrupted in sulfate transport, did not have a longer lifespan (Figure 1), leading them to conclude that "lifespan extension by SUL1 deletion is not caused by decreased sulfate uptake". They would need to measure sulfate uptake in the mutants they test to draw that conclusion firmly.

- Related to my previous point, another simple experiment would be to repeat the assays in Figure 1 with exogenous sulfur added to see if the lifespan extension is suppressed.

- There needs to be more information in the text or the methods about how they did the enrichment analysis in Figure 2B. P-values are typically insufficient, and adjusted FDR values are reported from standard gene ontology platforms (e.g., PANTHER).

- It is somewhat puzzling that relocalization of Msn2 was not seen in very old cells (past the 17th generation), but it was evident in younger cells. The authors could consider another possibility, that it was early and midlife experiences that made those cells live longer. Past that window, loss of Sul1 may have no impact on longevity. A conditional shutoff system to regulate SUL1 expression would be needed to test the above, albeit this is probably beyond the scope of this report.

- The connections between glucose restriction, autophagy, and sul1 (Figure 4) could be further tested by measuring the RLS of sul1 cells in glucose-restricted cells. If RLS is further extended by glucose restriction, then whatever effects they see should be independent of glucose restriction.

- They made and tested the double (sul1, msn2) mutants, but they should also test the sul1, msn4 combination since Msn4 functions similarly to Msn2.

Reviewer #3 (Public Review):

Summary:

In this manuscript, Long et al. demonstrated that the deletion of SUL1, which encodes a sulfate transporter localized on the plasma membrane, extends the replicative lifespan in S. cerevisiae. The authors further investigated the mechanism underlying this lifespan extension. They found that, unlike sul1∆ mutants, other mutants that have been shown to have a deficiency in sulfate transport cannot extend lifespan, from which they concluded that it is unlikely that SUL1 deletion extends lifespan by impairing sulfate intake. The authors then performed a series of characterizations on sul1∆ mutants and found that consistent with previous studies, PKA activity is downregulated when SUL1 is deleted. The authors demonstrated that SUL1 deletion promotes the nuclear localization of Msn2, as well as autophagy, which are known downstream signals of the PKA pathway. In addition, the authors show that MSN2 and ATG8 are indispensable for the lifespan extension in sul1∆ cells. Altogether, this manuscript suggests that SUL1 deletion extends lifespan by affecting PKA activity.

Strengths:

This study reported an interesting phenotype that the deletion of SUL1, but not SUL2, promotes lifespan extension in budding yeast. The authors performed some characterizations on sul1∆ mutants and epistatic studies to demonstrate that this lifespan extension requires MSN2 and ATG8, which further support the importance of the PKA pathway in regulating lifespan.

Weaknesses:

However, one of the major findings in this paper that SUL1 deletion extends lifespan independently of its role in sulfate uptake was merely based on lifespan measurements on sul2∆, SUL1E427Q, and met3∆ mutants, which cannot exclude the possibility that yeast lifespan is affected by sulfate intake. In addition, the strength of evidence for whether SUL1 deletion extends lifespan through affecting PKA activity is incomplete. It has been shown that Sul1 and Sul2 have redundant functions in both sulfate transport and PKA activation (Kankipati et al. 2015). However, in this manuscript, as shown by the authors, the deletion of SUL2 does not extend the lifespan compared with sul1∆ mutants. Without a further characterization on why deletion of SUL1, but not SUL2, extends lifespan, it is likely that SUL1 deletion extends lifespan independently of either sulfate transport or PKA activation.

Reviewer #1 (Public Review):

This is an interesting study investigating the mechanisms underlying membrane targeting of the NLRP3 inflammasome and reporting a key role for the palmitoylation-depalmitoylation cycle of cys130 in NRLP3. The authors identify ZDHHC3 and APT2 as the specific ZDHHC and APT/ABHD enzymes that are responsible for the s-acylation and de-acylation of NLRP3, respectively. They show that the levels of ZDHHC3 and APT2, both localized at the Golgi, control the level of palmitoylation of NLRP3. The S-acylation-mediated membrane targeting of NLRP3 cooperates with polybasic domain (PBD)-mediated PI4P-binding to target NLRP3 to the TGN under steady-state conditions and to the disassembled TGN induced by the NLRP3 activator nigericin.

However, the study has several weaknesses in its current form as outlined below.

(1) The novelty of the findings concerning cys130 palmitoylation in NLRP3 is unfortunately compromised by recent reports on the acylation of different cysteines in NLRP3 (PMID: 38092000), including palmitoylation of the very same cys130 in NLRP3 (Yu et al https://doi.org/10.1101/2023.11.07.566005), which was shown to be relevant for NLRP3 activation in cell and animal models. What remains novel and intriguing is the finding that NLRP3 activators induce an imbalance in the acylation-deacylation cycle by segregating NLRP3 in late Golgi/endosomes from de-acylating enzymes confined in the Golgi. The interesting hypothesis put forward by the authors is that the increased palmitoylation of cys130 would finally contribute to the activation of NLRP3. However, the authors should clarify the trafficking pathway of acylated-NLRP3. This pathway should, in principle, coincide with that of TGN46 which constitutively recycles from the TGN to the plasma membrane and is trapped in endosomes upon treatment with nigericin.

(2) To affect the S-acylation, the authors used 16 hrs treatment with 2-bromopalmitate (2-BP). In Figure 1f, it is quite clear that NLRP3 in 2-BP treated cells completely redistributed in spots dispersed throughout the cells upon nigericin treatment. What is the Golgi like in those cells? In other words, does 2-BP alter/affect Golgi morphology? What about PI4P levels after 2-BP treatment? These are important missing pieces of data since both the localization of many proteins and the activity of one key PI4K in the Golgi (i.e. PI4KIIalpha) are regulated by palmitoylation.

(3) The authors argue that the spots observed with NLRP-GFP result from non-specific effects mediated by the addition of the GFP tag to the NLRP3 protein. However, puncta are visible upon nigericin treatment, as a hallmark of endosomal activation. How do the authors reconcile these data? Along the same lines, the NLRP3-C130S mutant behaves similarly to wt NLRP3 upon 2-BP treatment (Figure 1h). Are those NLRP3-C130S puncta positive for endosomal markers? Are they still positive for TGN46? Are they positive for PI4P?

(4) The authors expressed the minimal NLRP3 region to identify the domain required for NLRP3 Golgi localization. These experiments were performed in control cells. It might be informative to perform the same experiments upon nigericin treatment to investigate the ability of NLRP3 to recognize activating signals. It has been reported that PI4P increases on Golgi and endosomes upon NG treatment. Hence, all the differences between the domains may be lost or preserved. In parallel, also the timing of such recruitment upon nigericin treatment (early or late event) may be informative for the dynamics of the process and of the contribution of the single protein domains.

(5) As noted above for the chemical inhibitors (1) the authors should check the impact of altering the balance between acyl transferase and de-acylases on the Golgi organization and PI4P levels. What is the effect of overexpressing PATs on Golgi functions?

Reviewer #2 (Public Review):

Summary:

This paper examines the recruitment of the inflammasome seeding pattern recognition receptor NLRP3 to the Golgi. Previously, electrostatic interactions between the polybasic region of NLRP3 and negatively charged lipids were implicated in membrane association. The current study reports that reversible S-acylation of the conserved Cys-130 residue, in conjunction with upstream hydrophobic residues plus the polybasic region, act together to promote Golgi localization of NLRP3, although additional parts of the protein are needed for full Golgi localization. Treatment with the bacterial ionophore nigericin inhibits membrane traffic and prevents Golgi-associated thioesterases from removing the acyl chain, causing NLRP3 to become immobilized at the Golgi. This mechanism is put forth as an explanation for how NLRP3 is activated in response to nigericin.

Strengths:

The experiments are generally well presented. It seems likely that Cys-130 does indeed play a previously unappreciated role in the membrane association of NLRP3.

Weaknesses:

The interpretations about the effects of nigericin are less convincing. Specific comments follow.

(1) The experiments of Figure 4 bring into question whether Cys-130 is S-acylated. For Cys-130, S-acylation was seen only upon expression of a severely truncated piece of the protein in conjunction with overexpression of ZDHHC3. How do the authors reconcile this result with the rest of the story?

(2) Nigericin seems to cause fragmentation and vesiculation of the Golgi. That effect complicates the interpretations. For example, the FRAP experiment of Figure 5 is problematic because the authors neglected to show that the FRAP recovery kinetics of non-acylated resident Golgi proteins are unaffected by nigericin. Similarly, the colocalization analysis in Figure 6 is less than persuasive when considering that nigericin significantly alters Golgi structure and could indirectly affect colocalization.

Reviewer #1 (Public Review):

Summary<br /> In this work, Mouelhi et al investigated how the nucleus responds to long term confinement. They find that short-term confinement does not affect nuclear volume, whereas long-term confinement leads to a decrease in volume. The authors propose this decrease occurs after mitosis and relies on cPLA2 and myosin contractility.

Strengths

The ability to accurately control cell confinement allows authors to determine its effects on cellular function with high resolution. This provides a good addition to the existing collection of tools used for cellular micromanipulation. The results provided are relevant and timely and could help understand how cancer cells adapt to conditions of confinement.

Weaknesses

I have a few concerns which I believe should be addressed:

(1) It is unclear whether the authors took into consideration the contribution of nuclear blebs for nuclear volume measurements. This would be particularly relevant in situations of very strong confinement. Blebs were previously shown to affect volume (Mistriotis et al., JCB 2019). One could argue that the decreased nuclear volume was due to the increased blebbing observed in very strong confinements.

(2) From their experimental setup, it is unclear whether the reduced nuclear volume observed after confined cell division arises from a geometrical constraint or is due to an intrinsic nuclear feature. One could argue that cells exiting mitosis under confinement have clustered chromosomes and, therefore, will have decreased volume. This would imply that the nucleus is not "reset" but rather that a geometrical constraint is forcing nuclei to be smaller. One way to test this would be to follow individual cells under confinement, let them enter mitosis, and then release the confinement. If, under these conditions, the daughter nuclei are smaller, then it supports their model. If daughter nuclei recover to their initial value, then it´s simply due to a geometrical constraint that forces the clustering of chromosomes and the reassembly of the NE in a confined space.

(3) The authors claim that the nucleus adapts to confinement based on evidence that the nucleus no longer shrinks in the second division following the first division. I would argue no further decrease is possible because the DNA is already compacted in the smallest possible volume. If indeed nuclei are in a new homeostatic state as the authors claim, then one would expect nuclei to remain smaller even after confinement is removed. This analysis is missing.

(4) Also, if the authors want to claim that this is a mechanism used for cancer cells to adapt to confined situations as the title says, they need to show that normal, near-diploid cells do not behave in the same way. This analysis is missing.

(5) Authors state that "Loss of nuclear blebs is clearly linked to mitosis, suggesting that nuclear volume and nuclear envelope tension are tightly coupled, and supports the hypothesis that mitosis is a key regulator of nuclear envelope tension". I have a few issues with the way this sentence is written. Firstly, one could say that all nuclear structures (and not only blebs) are lost during mitosis because the nucleus disassembles. Hence, the new homeostatic state could be determined by envelope reassembly after mitosis and not mitosis itself. Secondly, I don´t understand why the loss of nuclear blebs suggests that volume and tension are tightly coupled. Thirdly, how can mitosis be a key regulator of nuclear envelope tension when the nucleus is disassembled during the process? These require clarification.

(6) The authors claim that, unlike previous studies (Lomakin et al), this work shows a "gradual nuclear adaptation". From their results, this is difficult to conclude simply because they do not analyse cPLA2 levels. This is solely based on indirect evidence obtained from cPLA2 inhibition. A gradual adaptation would mean that based on the level of confinement we would expect to have increasingly higher levels of cPLA2 (and therefore nuclear tension).

(7) The authors should refrain from saying that the mechanism behind DNA repair is coupled to the nuclear adaptation they show. There are several points regarding this statement. Firstly, increased DNA damage could be due to nuclear ruptures imposed by confinement at 2h. In fact, the authors show leakage of NLS from the nucleus after confinement (Figure S3A). Secondly, the decrease in DNA damage at 24h could be because these nuclei did not rupture. How can they ensure that cells with low DNA damage at 24h had increased DNA damage at 2h? Finally, one needs to confirm if the nuclei they are analysing at 24h did undergo a round of cell division previously. From the evidence provided, the authors cannot conclude that DNA damage regulation is occurring in confined cells. Moreover, cell cycle arrest is a known effect of DNA damage. Cells with high damage at 2h most likely are arrested or will present with increased mitotic errors (which the authors exclude from their analyses).

Reviewer #2 (Public Review):

Summary:

Extensive previous research has shown that cell confinement, e.g., vertical compression of cells to a height smaller than the height of the unconfined cells, results in the unfolding of nuclear membrane invaginations, calcium and membrane tension mediated recruitment of cPLA2 to the nuclear membrane (which triggers increased cortical myosin accumulation and activity, among other effects), nuclear blebbing, and DNA damage. However, the long-term effects of confinement, and how cells adapt to such confined conditions, have remained largely unexplored.

In this work, the authors use custom-built cell confinement devices that enable precise control of confinement for prolonged periods of time (up to several days), along with live cell and fixed cell imaging to compare short-term (2 hours) and long-term (24+ hours) effects of confinement on nuclear structure. The authors report that while vertical confinement results in a short-term increase in nuclear cross-sectional area, associated with an increase in nuclear surface area due to unfolding of nuclear envelope invaginations while maintaining nuclear volume, long-term confinement results in a decrease in nuclear volume, reduced cross-sectional area, and re-appearance of nuclear envelope invaginations. Using time-lapse imaging, the authors demonstrate that these effects are associated with a reduction in nuclear volume upon completion of the first mitosis under confinement. Pharmacological inhibition experiments indicate a requirement of cPLA2, calcium signaling, and actomyosin contractility in this process. Although it is not surprising that nuclear blebs disappear following mitosis, as the nuclear envelope breaks down at the onset of mitosis and subsequently reforms as the chromatin decondenses, the observed change in nuclear volume upon prolonged confinement is intriguing. Notably, the nuclear adaptation following prolonged confinement was also associated with a reduction in DNA damage when comparing cells at 2h and 24h of confinements, measured by the presence of gamma-H2AX foci in the nucleus. By fitting their experimental data of nuclear surface area measurements, the authors arrive at the conclusion that cells have an intrinsic nuclear envelope tension set-point and that completing mitosis enables cells to reset nuclear envelope tension to this set-point.

Strengths:

The use of an agarose confinement system with precise control over vertical confinement enables the authors to apply long-term confinement without depriving cells of nutrients while performing live cell imaging or immunofluorescence analysis following fixation. The live cell imaging is a powerful tool to assess the effect of confinement not only on nuclear morphology, but also on cell cycle progression (using the FUCCI fluorescent reporter) and to compare nuclear volume between mother and daughter cells. The data presented by the authors to demonstrate changes in nuclear volume and surface area are convincing and supported by several independent measurements. The model comparing total and apparent nuclear surface area nicely complements the experimental measurements and helps to make the point that cells have a nuclear envelope tension set-point, even though the authors were unable to directly measure nuclear envelope tension. The inhibitor experiments targeting cPLA2 (using AACOCF3), intracellular calcium (using BAPTA-Amand 2APB), and myosin contractility (using blebbistatin) identify key players in the underlying cellular mechanism.

Weaknesses:

Although the findings by the authors will be of interest to a broad community, several weaknesses limit the mechanistic insights gained from this study. One major limitation is that all experiments are performed in a single cell line, H-29 human colorectal cancer cells, which has an unusual nuclear envelope composition as it has no lamin B2, low lamin B1 levels, and contains a p53 mutation. Because lamins B1 and B2 play important functions in protecting the nuclear envelope from blebs and confinement-induced rupture, and p53 is crucial in the cellular DNA damage response, it remains unclear whether other cell lines exhibit similar adaptation behavior.

Furthermore, although the time-lapse experiments suggest that reduction in nuclear volume occurs primarily during mitosis, the authors do not address whether prolonged confinement, even in the absence of apoptosis, could also result in cells adjusting their nuclear volume, or alternatively normalizing nuclear envelope tension by recruiting additional membrane from the endoplasmic reticulum, which is continuous with the nuclear membranes.

Additionally, the molecular mechanisms underlying the observed loss in nuclear volume and the regulation of this process remain to be identified. The pharmacological studies implicate cPLA2, intracellular calcium, and actomyosin contractility in this process, but do not include validation to confirm the efficiency of the drug treatment or to rule out off-target effects. Regarding the proposed role of cPLA2, previous studies have shown that cPLA2 recruitment to the nuclear membrane, which is essential to mediate its nuclear mechanotransduction function, requires both an increase in nuclear membrane tension and intracellular calcium. However, the current study does not include any data showing the recruitment of cPLA2 to the nuclear membrane upon confinement, or the disappearance of nuclear membrane-associated cPLA2 during prolonged confinement, leaving unclear the precise function and dynamics of cPLA2 in the process.

Lastly, it remains unclear (1) whether the reduction in nuclear volume is caused by a reduction in nuclear water content, by chromatin compaction, e.g. associated with an increase in heterochromatin, or through other mechanisms, (2) whether the change in nuclear volume is reversible, and if so, how quickly, and (3) what functional consequences the substantial reduction in nuclear volume has on nuclear function, as one would expect that this reduction would be associated with a substantial increase in nuclear crowding, affecting numerous nuclear processes.

Reviewer #1 (Public Review):

Summary:

The authors aim to address a critical challenge in the field of bioinformatics: the accurate and efficient identification of protein binding sites from sequences. Their work seeks to overcome the limitations of current methods, which largely depend on multiple sequence alignments or experimental protein structures, by introducing GPSite, a multi-task network designed to predict binding residues of various molecules on proteins using ESMFold.

Strengths:

(1) Benchmarking. The authors provide a comprehensive benchmark against multiple methods, showcasing the performances of a large number of methods in various scenarios.

(2) Accessibility and Ease of Use. GPSite is highlighted as a freely accessible tool with user-friendly features on their website, enhancing its potential for widespread adoption in the research community.

Weaknesses:

(1) Lack of significant insights. The paper reproduces results and analyses already presented in previous literature, without providing significant novel analysis or interpretation. However, they show a novel method with an original approach.

The work is useful for the field, especially in disease mechanism elucidation and novel drug design. The availability of genome-scale binding residue annotations GPSite offers is a significant advancement.

Reviewer #2 (Public Review):

Summary:

This work provides a new framework, "GPsite" to predict DNA, RNA, peptide, protein, ATP, HEM, and metal ions binding sites on proteins. This framework comes with a webserver and a database of annotations. The core of the model is a Geometric featurizer neural network that predicts the binding sites of a protein. One major contribution of the authors is the fact that they feed this neural network with predicted structure from ESMFold for training and prediction (instead of native structure in similar works) and a high-quality protein Language Model representation. The other major contribution is that it provides the public with a new light framework to predict protein-ligand interactions for a broad range of ligands. It is a convincing outcome of previous efforts to Geometric Deep Learning approaches to model protein-ligand interactions. The authors have demonstrated the interest of their framework with comprehensive ablation studies and benchmarks.

Strengths:

- The performance of this framework as well as the provided dataset and web server make it useful to conduct studies.<br /> - The ablations of some core elements of the method, such as the protein Language Model part, the use of multiple ligands in the same model, the input structure, or the use of predicted structure to complement native structure are very insightful. They can help convince the reader that every part of the framework is necessary. This could also guide further developments in the field. As such, the presentation of this part of the work holds a critical place in this work.

Weaknesses:

- The authors made an important effort to compare their work to other similar frameworks. Yet, the lack of homogeneity of training methods and data from one work to the other makes the comparison slightly unconvincing, as the authors pointed out. Ablations performed by the authors were able to compensate for this general weakness, as well as the focus on several example structures.

Reviewer #3 (Public Review):

Summary

The authors of this work aim to address the challenge of accurately and efficiently identifying protein binding sites from sequences. They recognize that the limitations of current methods, including reliance on multiple sequence alignments or experimental protein structure, and the under-explored geometry of the structure, which limit the performance and genome-scale applications. The authors have developed a multi-task network, GPSite, that predicts binding residues for a range of biologically relevant molecules, including DNA, RNA, peptides, proteins, ATP, HEM, and metal ions, using sequence embeddings from protein language models and ESMFold-predicted structures. The reported results showed to be superior to current sequence-based and structure-based methods in terms of accuracy and efficiency.

Strengths<br /> (1) The GPSite model's ability to predict binding sites for a wide variety of molecules, including DNA, RNA, peptides, and various metal ions.<br /> (2) Based on the presented results, GPSite outperforms state-of-the-art methods in several benchmark datasets in terms of accuracy and efficiency.<br /> (3) GPSite adopts predicted structure instead of native structures as input, enabling the model to be applied to a wider range of scenarios where native structures are rare.<br /> (4) The low computational cost of GPSite is beneficial, which enables rapid genome-scale binding residue annotations, indicating the model's potential for large-scale downstream applications and discoveries.

Weaknesses

There are no major weaknesses after the revision.

Reviewer #2 (Public Review):

Summary:

The authors tried to understand the mechanism on how a drug candidate, VLZ, works on a receptor, 5-HTR1A, by activating the SRC/MAPK pathway to promote the formation of platelets.

Strengths:

The authors used both computational and experimental methods. This definitely saves time and funds to find a useful drug candidate and its therapeutic marker in the subfield of platelets reduction in cancer patients. The authors achieved the aim to explain the mechanism of VLZ on improving thrombocytopenia by using two cell lines and two animal models.

Weaknesses:

Only two cell lines, HEL and Meg-01 cells, were evaluated in this study. However, using more cell lines is really depending on the work flow and the grant situations of the current research team.

Reviewer #1 (Public Review):

Summary:

This manuscript examined the impact of prenatal alcohol exposure on genome-wide DNA methylation in the brain and liver, comparing ethanol-exposed mice to unexposed controls. They also investigated whether a high-methyl diet (HMD) could prevent the DNA methylation alterations caused by alcohol. Using bisulfite sequencing (n=4 per group), they identified 78 alcohol-associated differentially methylated regions (DMRs) in the brain and 759 DMRs in the liver, of which 85% and 84% were mitigated by the HMD group, respectively. The authors further validated 7 DMRs in humans using previously published data from a Canadian cohort of children with FASD.

Overall, the findings from this study provide new insight into the impact of prenatal alcohol exposure, while also showing evidence for methyl-rich diets as an intervention to prevent the effects of alcohol on the epigenome. Some methodological concerns and confounders limit the robustness of these results, and should be addressed in future studies to further strengthen the conclusions of this study and its applicability to broader settings.

Strengths:

- The use of whole genome bisulfite sequencing allowed for the interrogation of the entire DNA methylome and DMR analysis, rather than a subset of CpGs.<br /> - The combination of data from animal models and humans allowed the authors to make stronger inferences regarding their findings<br /> - The authors investigated a potential mechanism (high methyl diet) to buffer against the effects of prenatal alcohol exposure, which increases the relevance and applicability of this research.

Weaknesses:

- The sample size was small for the epigenetic analyses, which limits the robustness of the findings.<br /> - The authors could not account for potential confounders in their analyses, including birthweight, alcohol levels, and sex. This is a particular problem for the high-methyl diet analyses, in which the alcohol-exposed mice consumed less alcohol than their non-diet counterparts.

Joint Public Review:

In this manuscript, Xue and colleagues investigate the fundamental aspects of cellular fate decisions and differentiation, focusing on the dynamic behaviour of gene regulatory networks. It explores the debate between static (noise-driven) and dynamic (signal-driven) perspectives within Waddington's epigenetic landscape, highlighting the essential role of gene regulatory networks in this process. The authors propose an integrated analysis of fate-decision modes and gene regulatory networks, using the Cross-Inhibition with Self-activation (CIS) network as a model. Through mathematical modelling, they differentiate two logic modes and their effect on cell fate decisions: requires both the presence of an activator and absence of a repressor (AA configuration) with one where transcription occurs as long the repressor is not the only species on the promoter (OO configuration).

The authors establish a relationship between noise profiles, logic-motifs, and fate-decision modes, showing that defining any two of these properties allows the inference of the third. They also identify, under the signal-driven mode, two fundamental patterns of cell fate decisions: either prioritising progression or accuracy in the differentiation process. The authors apply this analysis to available high-throughput datasets of cell fate decisions in hematopoiesis and embryogenesis, proposing the underlying driving force in each case and utilising the observed noise patterns to nominate key regulators.

The paper significantly advances our understanding of gene regulatory networks through a well-described computational study, where the authors rigorously evaluate assumptions in modelling. Particularly commendable is their introduction of the concept of combinatorial logic, exemplified by the double 'and' and double 'or' (AA/OO) logic motifs, which they successfully map to previously described cell fate decision processes. This theoretical and computational exploration sheds light on the dynamic landscape of epigenetic cell fate decisions, emphasising the role of combinatorial logic in coordinating noise and signal-driven processes. The thorough comparison of two model configurations underscores the importance of integration logic, contributing to a clearer understanding of gene regulatory network dynamics. Importantly, the results of the simulations are presented clearly, enhancing accessibility and intuitive understanding. The paper's strength also lies in its predictive power, as the authors use simulations to make insightful predictions about the regulatory organisation of stem cell differentiation systems. While the exploration is restricted to specific scenarios, these limitations serve to highlight areas for future research rather than detract from the paper's strengths.

While the paper presents an intriguing framework for understanding gene regulatory networks and cell fate decisions, there are some weaknesses that warrant attention. Firstly, the framework would benefit from validation with more experimental data and application to diverse systems beyond those explored in the study, such as de-differentiation in adult tissues and regeneration processes. Additionally, while the authors successfully make predictions about the regulatory organisation of stem cell differentiation systems, there is a lack of discussion regarding how perturbations in the regulatory network could affect cell fate decisions. Furthermore, the paper could be strengthened by addressing the effects of mutations and other perturbations that may significantly influence cell fate decision-making processes, thus enhancing the robustness of the findings. Finally, there are instances where the clarity of the writing could be improved to enhance understanding and accessibility for readers.

Reviewer #1 (Public Review):

Induction of beta cell regeneration is a promising approach for the treatment of diabetes. In this study, Massoz et.al., identified calcineurin (CaN) as a new potential modulator of beta cell regeneration by using zebrafish as model. They also showed that calcineurin (CaN) works together with Notch signaling to promote the beta cell regeneration. Overall, the paper is well organized, and technically sound. However, some evidences seem weak to get the conclusion.

Reviewer #1 (Public Review):

Summary:

The research study under review investigated the relationship between the gut and identified potential biomarkers derived from the nasopharyngeal and gut microbiota-based that could aid in predicting COVID-19 severity. The study reported significant changes in the richness and Shannon diversity index in nasopharyngeal microbiome associated with severe symptoms. The study showed a high abundance of Bacillota and Pesudomonadota in patients exhibiting severe symptomatology. Positive correlations were also found between Corynebacterium, Acinetobacter, Staphylococcus, and Veillonella, with the severity of SARS-CoV-2 infection.

Strengths:

The study successfully identified differences in the microbiome diversity that could indicate or predict disease severity. Furthermore, the authors demonstrated a link between individual nasopharyngeal organisms and the severity of SARS-CoV-2 infection. The density of the nasopharyngeal organism was shown to be a potential predictor of the severity of COVID-19.

Weaknesses:

The authors claimed an association between nasopharyngeal organisms and severity of SARS-CoV-2 infection but omitted essential data on the statistical significance of these associations between groups. The authors frequently referred to a p-value < 0.05 without presenting the actual p-values and percentages to show the significance of their results. The discussion is hard to understand (lacked clarity), as it contained an extensive literature review without discussing the study findings. A more focused discussion and results section on the main findings could have improved the overall readability of the paper. The role of potential confounders, such as HIV infection, and ethnicity which impacts the nasopharyngeal microbiome composition, was not included in the paper. Addressing the potential confounders would contribute to a more comprehensive understanding of the study's implications, specifically the role of the nasopharyngeal microbiome as a predictor of COVID-19 severity.

Reviewer #2 (Public Review):

The study conducted by Benita et al studied the gut and nasopharyngeal microbiome in covid-19 severity. There are a lot of studies on this topic, and this study therefore cannot stand out from a pool of such similar studies. Beyond that, I have a number of major concerns:

(1) The sample size is limited. There were 3 cohorts, but only ~100 subjects in total. This indicates that there were only a small number of subjects in each cohort (the authors did not list this information), and beyond that, there was a lack of healthy individuals as controls. A cohort-specific effect should usually exist, I believe with such a small number of patients (they were further divided into 3 groups), the authors cannot find reproducible data between cohorts.

(2) The study did not meet the study goal. The authors say "Many factors have been described to be correlated with its severity but no specific determinants of infection outcome have been identified yet". However, numerous studies have shown the relationship between microbiome and covid. The present study only again showed a correlation between microbiome and covid severity and did not provide further insights, nor did they find specific determinants.

(3) This study only studied 16s-seq for microbiome profiling, which made this study lack depth and resolution. Many peer papers have used metagenomics sequencing for in-depth interrogation.

(4) Since there are fecal and nasopharyngeal microbiome data, the authors only listed their respective associations with covid severity yet did not provide further insights into whether and how these two microbiome types are linked to covid, or into whether there is a microbiome priority, resistance or transmission.

(5) The abstract is amiss where each sentence lacks a key message - I don't understand each of the sentences or the underlying meanings. One example of an unclear expression is "this ratio" - what ratio?

(6) The figures are all unclear and need significant improvement

Reviewer #3 (Public Review):

Summary:

How the microbial composition of the human body is influenced by and influences disease progression is an important topic. For people with COVID-19, symptomatic progression and deterioration can be difficult to predict. This manuscript attempts to associate the nasal and fecal microbiomes of COVID-19 patients with the severity of disease symptoms, with the goal of identifying microbial markers that can predict disease outcomes. However, the value of this work is held back by unclear methods and data presentation.

Strengths:

Analysis of microbiomes from two distinct anatomical locations and across three distinct patient groups is a substantial undertaking. How these microbiomes influence and are influenced by COVID-19 disease progression is an important question. In particular, the putative biomarker identified here could be of clinical value with additional research.

Weaknesses:

The methods and statistics used for several figures and comparisons are unclear or used in non-standard ways. For instance: the description of the Bray-Curtis test for Figure 1 is inaccurate and conflicts between the text and figure legend; the method used to compare the relative abundance of genera in Figure 2 is not clear; and it is not stated how the "total amount" of detected bacteria is inferred from the data presented in Figures 2C and 2D.

The description of results for Figure 1 is overstated or unclear for both the alpha diversity among disease groups and the overlap for nasal samples.

The most abundant phyla from nasal samples cumulatively account for less than 1% of abundance and it is unclear why this would be expected or how it compares to other work. Relatedly, the potential biological relevance of the very small proportional changes among phyla in the nasal samples is also not clear.

There is no real discussion of how the identified biomarkers might work in practice. While some microbes are detected in one condition but not others, it is unclear whether these organisms are expected to already exist below the detection threshold and then increase in abundance along with disease severity, or if they are picked up from the environment. For instance, would the presence of these 'severe' - associated microbes in patients with mild or moderate disease justify additional treatment to prevent disease progression?

The authors use the term "nasopharyngeal-faecal axis", but there is no substantial discussion of how these two microbiomes interact to influence disease progression, or how they are jointly affected to yield useful biomarkers. With one exception, correlation values between nasal and fecal microbes range from negligible to modest. It is unclear, then, how much parallel influence disease has on these microbiomes.

Joint Public Review:

This study investigates the role of Ikaros, a zinc finger family transcription factor related to Helios and Eos, in T-regulatory (Treg) cell functionality in mice. Through genome-wide association studies and chromatin accessibility studies, the authors find that Ikaros shares similar binding sites to Foxp3. Ikaros cooperates with Foxp3 to establish a major portion of the Treg epigenome and transcriptome. Ikaros-deficient Treg exhibits Th1-like gene expression with abnormal expression of IL-2, IFNg, TNFa, and factors involved in Wnt and Notch signalling. Further, two models of inflammatory/ autoimmune diseases - Inflammatory Bowel Disease (IBD) and organ transplantation - are employed to examine the functional role of Ikaros in Treg-mediated immune suppression. The authors provide a detailed analysis of the epigenome and transcriptome of Ikaros-deficient Treg cells.

These studies establish Ikaros as a factor required in Treg for tolerance and the control of inflammatory immune responses. The data are of high quality. Overall, the study is well organized, and reports new data consolidating mechanistic aspects of Foxp3 mediated gene expression program in Treg cells.

Strengths:

The authors have performed biochemical studies focusing on mechanistic aspects of molecular functions of the Foxp3-mediated gene expression program and complemented these with functional experiments using two models of autoimmune diseases, thereby strengthening the study. The studies are comprehensive at both the cellular and molecular levels. The manuscript is well organized and presents a plethora of data regarding the transcriptomic landscape of these cells.

Weakness:

The findings of markedly increased percentages of activated conventional T cells (CD44hi), major increases in TFH cells, and elevated serum Ig levels indicate disrupted immune homeostasis even in the absence of overt autoimmune manifestations seen in histopathology. Thus, some of the observed genetic changes observed by the authors are likely Treg cell extrinsic. Further, clear conclusions from the genome-wide studies are lacking.

Reviewer #1 (Public Review):

The manuscript describes the development of a mouse model that co-expresses a fluorescent protein ZsGreen) marker in gene fusion with the FSHR gene.

The authors are correct in that there is a lack of reliable antibodies against many of the GPCR family members. The approach is novel and interesting, with the potential to help understand the expression pattern of gonadotropin receptors. There has been a very long debate about the expression of gonadotropin receptors in other tissues other than gonads. While their expression of the FSHR in some of those tissues has been detected by a variety of methods, their physiological, or pathophysiological, function(s) remain elusive.

The authors in this manuscript assume that the expression of ZsGren and the FSHR are equal. While this is correct genetically (transcription->translation) it does not go hand in hand with other posttranslational processes.

(1) One of the shocking observations in this manuscript is the expression of FSHR in Leydig cells. Other observations are in the osteoblasts and endothelial cells as well as epithelial cells in different organs. The expression of ZsGreen in these tissues seems high and one shall start questioning if there are other mechanisms at play here.

First, the turnover of fluorescent proteins is long, longer than 48h, which means that they accumulate at a different speed than the endogenous FSHR This means that ZsGreen will accumulate in time while the FSHR receptor might be degraded almost immediately. This correlated with mRNA expression (by the authors) but does not with the results of other studies in single-cell sequencing (see below).

The expression of ZsGreen in Leydig cells seems much higher than in Sertoli cells, this is "disturbing" to put it mildly. This is visible in both the ZsGreen expression and the FISH assay (Figure 2 B-D).

(2) The expression in WAT and BAT is also questionable as the expression of ZsGreen is high everywhere. That makes it difficult to believe that the images are truly informative. For example, the stainings of aorta show the ZsGreen expression where elastin and collagen fibres are - these are not "cells" and therefore are not expressing ZsGreen.

(3) FISH expression (for FSHR) in WT mice is missing.

Also, the tissue sections were stained with the IgG only (neg control) but in practice both the KI and the WT tissues should be stained with the primary and secondary antibodies. The only control that I could think of to truly get a sense of this would be a tagged receptor (N-terminal) that could then be analysed by immunohistochemistry.

(4) The authors also claim:<br /> To functionally prove the presence of FSHR in osteoblasts/osteocytes, we also deleted FSHR in osteocytes using an inducible model. The conditional knockout of FSHR triggered a much more profound increase in bone mass and decrease in fat mass than blockade by FSHR antibodies (unpublished data).

This would be a good control for all their images. I think it is necessary to make the large claim of extragonadal expression, as well as intragonadal such as Leydig cells.

(5) Claiming that the under-developed Leydig cells in FSHR KO animals are due to a direct effect of the FSHR, and not via a cross-talk between Sertoli and Leydig cells, is too much of a claim. It might be speculated to some degree but as written at the moment it suggests this is "proven".

(6) We also do not know if this FSHR expressed is a spliced form that would also result in the expression of ZsGreen but in a non-functional FSHR, or whether the FSHR is immediately degraded after expression. The insertion of the ZsGreen might have disturbed the epigenetics, transcription, or biosynthesis of the mRNA regulation.

(7) The authors should go through single-cell data of WT mice to show the existence of the FSHR transcript(s).<br /> For example here:<br /> https://www.nature.com/articles/sdata2018192

Reviewer #2 (Public Review):

The authors developed an original knock-in reporter mice line expressing ZSGreen under the control of endogenous FSHR promoter. The existence of FSHR in various extra-gonadal tissues and the physio-pathological consequences indeed remains a debated question and could potentially have an important impact on many high-incidence diseases occurring in menopausal women. Unfortunately, the provided data set lacks crucial controls and therefore does not provide a robust/convincing answer to the above-mentioned question.

Summary:<br /> The authors investigated the expression pattern of the FSHR in the gonads, where its expression has been demonstrated for decades, but also in many extra-gonadal tissues. The question is important since the expression of FSHR outside of the gonads has been increasingly reported and associated with the dramatic increase of circulating FSH after menopause, and has been suggested to play an important role in the advent of multiple diseases occurring with high incidence in post-menopausal women. However, the reality of such extra-gonadal expression of FSHR remains debated, mainly because this receptor is expressed at a low level and because the specificity/affinity of the available anti-FSHR antibodies is questionable.

Strengths:<br /> The development of reporter mice expressing ZsGreen fluorescent protein under the control of endogenous FSHR promoter is an original and potentially powerful approach to tackle the problem.

Weaknesses:<br /> The data provided are provocative since the FSHR seems to be expressed in all tested tissues. In the testis, for instance, the authors report very high levels of FSHR in interstitial cells and germ cells. In the ovary, there seems to be no difference in FSHR expression between granulosa cells and the other cell types. These findings alone contradict all the knowledge on FSH expression patterns in the gonads that have been accumulated over decades by many independent labs. In view of such results, the validity of the reporter mice line should be questioned thoroughly:

(1) Is the FSHR expression pattern affected by the knockin mice (no side-by-side comparison between wt and GSGreen mice, using in situ hybridization and ddRTPCR, at least in the gonads, is provided)?

(2) Is the splicing pattern of the FSHR affected in the knockin compared to wt mice, at least in the gonads?

(3) Are there any additional off-target insertions of GSGreen in these mice?

(4) Are similar results observed in separate founder mice?

(5) How long is GSGreen half-life? Could a very long half-life be a major reason for the extremely large expression pattern observed?

In the absence of answers to these questions, the data produced in extra-gonadal tissues using the same reporter mice, are not convincing and do not support the authors' claims.

Reviewer #1 (Public Review):

As a pathogen, S. aureus has evolved strategies to evade the host's immune system. It effectively remains 'under the radar' in the host until it reaches high population densities, at which point it triggers virulence mechanisms, enabling it to spread within the host. The agr quorum sensing system is central to this process, as it coordinates the pathogen's virulence in response to its cell density.

In this study, Podkowik and colleagues suggest that cells activating agr signaling also benefit from protection against H2O2 stress, whereas inactivation of agr increases cell death. The underlying cause of this lack of protection is tied to an ATP deficit in the agr mutant, leading to increased glucose consumption and NADH production, ultimately resulting in a redox imbalance. In response to this imbalance, the agr mutant increases respiration, resulting in the endogenous production of ROS which synergizes with H2O2 to mediate killing of the agr mutant. Suppressing respiration in the agr mutant restored protection against H2O2 stress.

Additionally, the authors establish that agr-dependent protection against oxidative stress is also linked to RNAIII activation, and the subsequent block of Rot translation. However, the specific protective genes regulated by Rot remain unidentified. Thus, according to the evidence provided, agr triggers intrinsic mechanisms that not only decrease harmful ROS production within the cell but also alleviate its detrimental effects.

Interestingly, these protective mechanisms are long-lived, and guard the cells against external oxidative stressors such as H2O2, even after the agr system has been 'turned off' in the population.

Reviewer #2 (Public Review):

In their study, Podkowik et al. elucidate the protective role of the accessory gene regulator (agr) system in Staphylococcus aureus against hydrogen peroxide (H2O2) stress. Their findings demonstrate that agr safeguards the bacterium by controlling the accumulation of reactive oxygen species (ROS), independent of agr activation kinetics. This protection is facilitated through a regulatory interaction between RNAIII and Rot, impacting virulence factor production and metabolism, thereby influencing ROS levels. Notably, the study highlights the remarkable adaptive capabilities of S. aureus conferred by agr. The protective effects of agr extend beyond the peak of agr transcription at high cell density, persisting even during the early log-phase. This indicates the significance of agr-mediated protection throughout the infection process. The absence of agr has profound consequences, as observed by the upregulation of respiration and fermentation genes, leading to increased ROS generation and subsequent cellular demise. Interestingly, the study also reveals divergent effects of agr deficiency on susceptibility to hydrogen peroxide compared to ciprofloxacin. While agr deficiency heightens vulnerability to H2O2, it also upregulates the expression of bsaA, countering the endogenous ROS induced by ciprofloxacin. These findings underscore the complex and context-dependent nature of agr-mediated protection. Furthermore, in vivo investigations using murine models provide valuable insights into the importance of agr in promoting S. aureus fitness, particularly in the context of neutrophil-mediated clearance, with notable emphasis on the pulmonary milieu. Overall, this study significantly advances our understanding of agr-mediated protection in S. aureus and sheds light on the sophisticated adaptive mechanisms employed by the bacterium to fortify itself against oxidative stress encountered during infection.

The conclusions drawn in this paper are generally well-supported by the data.

Reviewer #1 (Public Review):

Summary:

Del Rosario et al characterized the extent and cell types of sibling chimerism in marmosets. To do so, they took advantage of the thousands of SNPs that are transcribed in single-nucleus RNA-seq (snRNA-seq) data to identify the sibling genotype of origin for all sequenced cells across 4 tissues (blood, liver, kidney, and brain) from many marmosets. They found that chimerism is prevalent and widespread across tissues in marmosets, which has previously been shown. However, their snRNA-seq approach allowed them to identify precisely which cells were of sibling origin, and which were not. In doing so they definitively show that sibling chimerism across tissues is limited to cells of myeloid and lymphoid lineages. The authors then focus on a large sample of microglia sequenced across many brain regions to quantify: (1) variation in chimerism across brain regions in the same individual, and (2) the relative importance of genetic vs. environmental context on microglia function/identity.

(1) Much like across different tissues in the same individual, they found that the proportion of chimeric microglia varies across brain regions collected from the same individuals (as well as differing from the proportion of sibling cells found in the blood of the same animals), suggesting that cells from different genetic backgrounds may differ in their recruitment and/or proliferation across regions and local tissue contexts, or that this may be linked to stochastic bottleneck effects during brain development.

(2) Their (admittedly smaller sample size) analyses of host-sibling gene expression showed that the local environment dominates genotype.

All told, this thoughtful and thorough manuscript accomplishes two important goals. First, it all but closes a previously open question on the extent and cell origins of sibling chimerism. Second, it sets the stage for using this unique model system to examine, in a natural context, how genetic variation in microglia may impact brain development, function, and disease.

The conclusions of this paper are well supported by the data, and the authors exert appropriate care when extrapolating their results that come from smaller samples. However, there are a few concerns that should be addressed.

The "modest correlation" mentioned in lines 170-172 does not take into account the uncertainty in estimates of each chimeric cell proportion (although the plot shows those estimates nicely). This is particularly important for the macrophages, which are far less abundant. Perhaps a more appropriate way to model this would be in a binomial framework (with a random effect for individuals of origin). Here, you could model the sibling identity of each macrophage as a function of the proportion of sibling-origin microglia and then directly estimate the percent variance explained.

A similar (albeit more complicated because of the number of regions being compared) approach could be applied to more rigorously quantify the variation in chimerism across brain regions (L198-215; Figure 4). This would also help to answer the question of whether specific brain regions are more "amenable" to microglia chimerism than others.

While the sample size is small, it would be exciting to see if any microglia eQTL are driven by sibling chimerism across the marmosets.

L290-292: The authors should propose ways in which they could test the two different explanations proposed in this paragraph. For instance, a simulation-based modeling approach could potentially differentiate more stochastic bottleneck effects from recruitment-like effects.

While intriguing, the gene expression comparison (Figure 5) is extremely underpowered. It would be helpful to clarify this and note the statistical thresholds used for identifying DEGs (the black points in the figure).

Reviewer #2 (Public Review):

Summary:

This manuscript reports a novel and quite important study of chimerism among common marmosets. As the authors discuss, it has been known for years that marmosets display chimerism across a number of tissues. However, as the authors also recognize, the scope and details of this chimerism have been controversial. Some prior publications have suggested that the chimerism only involves cells derived from hematopoietic stem cells, while other publications have suggested more cell types can also be chimeric, including a wide range of cell types present in multiple organs. The present authors address this question and several other important issues by using snRNA-seq to track the expression of host and sibling-derived mRNAs across multiple tissues and cell types. The results are clear and provide strong evidence that all chimeric cells are derived from hematopoietic cell lineages.

This work will have an impact on studies using marmosets to investigate various biological questions but will have the biggest impact on neuroscience and studies of cellular function within the brain. The demonstration that microglia and macrophages from different siblings from a single pregnancy, with different genomes expressing different transcriptomes, are commonly present within specific brain structures of a single individual opens a number of new opportunities to study microglia and macrophage function as well as interactions between microglia, macrophages, and other cell types.

Strengths:

The paper has a number of important strengths. This analysis employs the first unambiguous approach providing a clear answer to the question of whether sibling-derived chimeric cells arise only from hematopoietic lineages or from a wider array of embryonic sources. That is a long-standing open question and these snRNA-seq data seem to provide a clear answer, at least for the brain, liver, and kidney. In addition, the present authors investigate quantitative variation in chimeric cell proportions across several dimensions, comparing the proportion of chimeric cells across individual marmosets, across organs within an individual, and across brain regions within an individual. All these are significant questions, and the answers have important implications for multiple research areas. Marmosets are increasingly being used for a range of neuroscience studies, and a better understanding of the process that leads to the chimerism of microglia and macrophages in the marmoset brain is a valuable and timely contribution. But this work also has implications for other lines of study. Third, the snRNA-seq data will be made available through the Brain Initiative NeMO portal and the software used to quantify host vs. sibling cell proportions in different biosamples will be available through GitHub.

Weaknesses:

I find no major weaknesses, but several minor ones. First, the main text of the manuscript provides no information about the specific animals used in this study, other than sex. Some basic information about the sources of animals and their ages at the time of study would be useful within the main paper, even though more information will be available in the supplementary material. Second, it is not clear why only 14 pairs of animals were used for estimating the correlation of chimerism levels in microglia and macrophages. Is this lower than the total number of pairwise comparisons possible in order to avoid using non-independent samples? Some explanation would be helpful. Finally, I think more analysis of the consistency and variability of gene expression in microglia across different regions of the brain would be valuable. Are there genetic pathways expressed similarly in host and sibling microglia, regardless of region of the brain? Are there pathways that are consistently expressed differently in host vs sibling microglia regardless of brain region?

Reviewer #1 (Public Review):

Summary:<br /> The study presented by Atsumi et al. is about using smartphone-driven, community-sourced data to enhance biodiversity monitoring. The idea is to leverage the widespread use of smartphones to gather data from the community quickly, contributing to a more comprehensive understanding of biodiversity. The authors discuss the importance of ecosystem services linked to biodiversity and the threats posed by human activities. It emphasizes the need for comprehensive biodiversity data to implement the Kunming-Montreal Global Biodiversity Framework. The 'Biome' mobile app, launched in Japan, uses species identification algorithms and gamification to gather over 6 million observations since 2019. While community-sourced data may have biases, incorporating it into Species Distribution Models (SDMs) improves accuracy, especially for endangered species. The app covers urban-natural gradients uniformly, enhancing traditional survey data biased towards natural areas. Combining these sources provides valuable insights into species distributions for conservation, protected area designation, and ecosystem service assessment.

Strengths:

The use of a smartphone app ('Biome') for community-driven species occurrence data collection represents an innovative and inclusive approach to biodiversity monitoring, leveraging the widespread use of smartphones. The app has successfully accumulated a large volume of species occurrence data since its launch in 2019, showcasing its effectiveness in rapidly gathering information from diverse locations. Despite challenges with certain taxa, the study highlights high species identification accuracy, especially for birds, reptiles, mammals, and amphibians, making the 'Biome' app a reliable tool for species observation. The integration of community-sourced data into Species Distribution Models (SDMs) improves the accuracy of predicting species distributions. This has implications for conservation planning, including the designation of protected areas and assessment of ecosystem services. The rapid accumulation of data and advancements in machine learning methods open up opportunities for conducting time-series analyses, contributing to the understanding of ecosystem stability and interaction strength over time. The study emphasizes the collaborative nature of the platform, fostering collaboration among diverse stakeholders, including local communities, private companies, and government agencies. This inclusive approach is essential for effective biodiversity assessment and decision-making. The platform's engagement with various stakeholders, including local communities, supports biodiversity assessment, management planning, and informed decision-making. Additionally, the app's role in fostering nature-positive awareness in society is highlighted as a significant contribution to creating a sustainable society.

Weaknesses:

While the studies make significant contributions to biodiversity monitoring, they also have some weaknesses. Firstly, relying on smartphone-driven, community-sourced data may introduce spatial and taxonomic biases. The 'Biome' app, for example, showed lower accuracy for certain taxa like seed plants, molluscs, and fishes, potentially impacting the reliability of the gathered data. Furthermore, the effectiveness of Species Distribution Models (SDMs) relies on the assumption that biases in community-sourced data can be adequately accounted for. The unique distribution patterns of the 'Biome' data, covering urban-natural gradients uniformly, might not fully represent the diversity of certain ecosystems, potentially leading to inaccuracies in the models. Moreover, the divergence in data distribution patterns along environmental gradients between 'Biome' data and traditional survey data raises concerns. The app data shows a more uniform distribution across natural-urban gradients, while traditional data is biased towards natural areas. This discrepancy may impact the representation of certain ecosystems and influence the accuracy of Species Distribution Models (SDMs). While the integration of 'Biome' data into SDMs improves accuracy, the study notes that controlling the sampling efforts is crucial. Spatially-biased sampling efforts in community-sourced data need careful consideration, and efforts to control biases are essential for reliable predictions.

Reviewer #3 (Public Review):

This study explores sensory prediction errors in the sensory cortex. It focuses on the question of how these signals are shaped by non-hierarchical interactions, specifically multimodal signals arising from same-level cortical areas. The authors used 2-photon imaging of mouse auditory cortex in head-fixed mice that were presented with sounds and/or visual stimuli while moving on a ball. First, responses to pure tones, visual stimuli, and movement onset were characterized. Then, the authors made the running speed of the mouse predictive of sound intensity and/or visual flow. Mismatches were created through the interruption of sound and/or visual flow for 1 second while the animal moved, disrupting the expected sensory signal given the speed of movement. As a control, the same sensory stimuli triggered by the animal's movement were presented to the animal decoupled from its movement. The authors suggest that auditory responses to the unpredicted silence reflect mismatch responses. That these mismatch responses were enhanced when the visual flow was congruently interrupted, indicates the cross-modal influence of prediction error signals.

This study's strengths are the relevance of the question and the design of the experiment. The authors are experts in the techniques used. The analysis explores neither the full power of the experimental design nor the population activity recorded with 2-photon, leaving open the question of to what extent what the authors call mismatch responses are not sensory responses to sound interruption. The auditory system is sensitive to transitions and indeed responses to the interruption of the sound are similar in quality, if not quantity, in the predictive and the control situation.

Reviewer #2 (Public Review):

In this study, Solyga and Keller use multimodal closed-loop paradigms in conjunction with multiphoton imaging of cortical responses to assess whether and how sensorimotor prediction errors in one modality influence the computation of prediction errors in another modality. Their work addresses an important open question pertaining to the relevance of non-hierarchical (lateral cortico-cortical) interactions in predictive processing within the neocortex.

Specifically, they monitor GCaMP6f responses of layer 2/3 neurons in the auditory cortex of head-fixed mice engaged in VR paradigms where running is coupled to auditory, visual, or audio-visual sensory feedback. The authors find strong auditory and motor responses in the auditory cortex, as well as weak responses to visual stimuli. Further, in agreement with previous work, they find that the auditory cortex responds to audiomotor mismatches in a manner similar to that observed in visual cortex for visuomotor mismatches. Most importantly, while visuomotor mismatches by themselves do not trigger significant responses in the auditory cortex, simultaneous coupling of audio-visual inputs to movement non-linearly enhances mismatch responses in the auditory cortex.

Their results thus suggest that prediction errors within a given sensory modality are non-trivially influenced by prediction errors from another modality. These findings are novel, interesting, and important, especially in the context of understanding the role of lateral cortico-cortical interactions and in outlining predictive processing as a general theory of cortical function.

In its current form, the manuscript lacks sufficient description of methodological details pertaining to the closed-loop training and the overall experimental design. In several scenarios, while the results per se are convincing and interesting, their exact interpretation is challenging given the uncertainty about the actual experimental protocols (more on this below). Second, the authors are laser-focused on sensorimotor errors (mismatch responses) and focus almost exclusively on what happens when stimuli deviate from the animal's expectations.

While the authors consistently report strong running-onset responses (during open-loop) in the auditory cortex in both auditory and visual versions of the task, they do not discuss their interpretation in the different task settings (see below), nor do they analyze how these responses change during closed-loop i.e. when predictions align with sensory evidence.

However, I believe all my concerns can be easily addressed by additional analyses and incorporation of methodological details in the text.

Major concerns:

(1) Insufficient analysis of audiomotor mismatches in the auditory cortex:

Lack of analysis of the dependence of audiomotor mismatches on the running speed: it would be helpful if the authors could clarify whether the observed audiomotor mismatch responses are just binary or scale with the degree of mismatch (i.e. running speed). Along the same lines, how should one interpret the lack of dependence of the playback halt responses on the running speed? Shouldn't we expect that during playback, the responses of mismatch neurons scale with the running speed?

Slow temporal dynamics of audiomotor mismatches: despite the transient nature of the mismatches (1s), auditory mismatch responses last for several seconds. They appear significantly slower than previous reports for analogous visuomotor mismatches in V1 (by the same group, using the same methods) and even in comparison to the multimodal mismatches within this study (Figure 4C). What might explain this sustained activity? Is it due to a sustained change in the animal's running in response to the auditory mismatch?

(2) Insufficient analysis and discussion of running onset responses during audiomotor sessions: The authors report strong running-onset responses during open-loop in identified mismatch neurons. They also highlight that these responses are in agreement with their model of subtractive prediction error, which relies on subtracting the bottom-up sensory evidence from top-down motor-related predictions. I agree, and, thus, assume that running-onset responses during the open loop in identified 'mismatch' neurons reflect the motor-related predictions of sensory input that the animal has learned to expect. If this is true, one would expect that such running-onset responses should dampen during closed-loop, when sensory evidence matches expectations and therefore cancels out this prediction. It would be nice if the authors test this explicitly by analyzing the running-related activity of the same neurons during closed-loop sessions.

(3) Ambiguity in the interpretation of responses in visuomotor sessions.

Unlike for auditory stimuli, the authors show that there are no obvious responses to visuomotor mismatches or playback halts in the auditory cortex. However, the interpretation of these results is somewhat complicated by the uncertainty related to the training history of these mice. Were these mice exclusively trained on the visuomotor version of the task or also on the auditory version? I could not find this info in the Methods. From the legend for Figure 4D, it appears that the same mice were trained on all versions of the task. Is this the case? If yes, what was the training sequence? Were the mice first trained on the auditory and then the visual version?

The training history of the animals is important to outline the nature of the predictions and mismatch responses that one should expect to observe in the auditory cortex during visuomotor sessions. Depending on whether the mice in Figure 3 were trained on visual only or both visual and auditory tasks, the open-loop running onset responses may have different interpretations.

a) If the mice were trained only on the visual task, how should one interpret the strong running onset responses in the auditory cortex? Are these sensorimotor predictions (presumably of visual stimuli) that are conveyed to the auditory cortex? If so, what may be their role?

b) If the mice were also trained on the auditory version, then a potential explanation of the running-onset responses is that they are audiomotor predictions lingering from the previously learned sensorimotor coupling. In this case, one should expect that in the visual version of the task, these audiomotor predictions (within the auditory cortex) would not get canceled out even during the closed-loop periods. In other words, mismatch neurons should constantly be in an error state (more active) in the closed-loop visuomotor task. Is this the case?

If so, how should one then interpret the lack of a 'visuomotor mismatch' aligned to the visual halts, over and above this background of continuous errors?<br /> As such, the manuscript would benefit from clearly stating in the main text the experimental conditions such as training history, and from discussing the relevant possible interpretations of the responses.

(4) Ambiguity in the interpretation of responses in multimodal versus unimodal sessions.

The authors show that multimodal (auditory + visual) mismatches trigger stronger responses than unimodal mismatches presented in isolation (auditory only or visual only). Further, they find that even though visual mismatches by themselves do not evoke a significant response, co-presentation of visual and auditory stimuli non-linearly augments the mismatch responses suggesting the presence of non-hierarchical interactions between various predictive processing streams.

In my opinion, this is an important result, but its interpretation is nuanced given insufficient details about the experimental design. It appears that responses to unimodal mismatches are obtained from sessions in which only one stimulus is presented (unimodal closed-loop sessions). Is this actually the case? An alternative and perhaps cleaner experimental design would be to create unimodal mismatches within a multimodal closed-loop session while keeping the other stimulus still coupled to the movement.

Given the current experiment design (if my assumption is correct), it is unclear if the multimodal potentiation of mismatch responses is a consequence of nonlinear interactions between prediction/error signals exchanged across visual and auditory modalities. Alternatively, could this result from providing visual stimuli (coupled or uncoupled to movement) on top of the auditory stimuli? If it is the latter, would the observed results still be evidence of non-hierarchical interactions between various predictive processing streams?

Along the same lines, it would be interesting to analyze how the coupling of visual as well as auditory stimuli to movement influences responses in the auditory cortex in close-loop in comparison to auditory-only sessions. Also, do running onset responses change in open-loop in multimodal vs. unimodal playback sessions?

Minor concerns and comments:

(1) Rapid learning of audiomotor mismatches: It is interesting that auditory mismatches are present even on day 1 and do not appear to get stronger with learning (same on day 2). The authors comment that this could be because the coupling is learned rapidly (line 110). How does this compare to the rate at which visuomotor coupling is learned? Is this rapid learning also observable in the animal's behavior i.e. is there a change in running speed in response to the mismatch?

(2) The authors should clarify whether the sound and running onset responses of the auditory mismatch neurons in Figure 2E were acquired during open-loop. This is most likely the case, but explicitly stating it would be helpful.

(3) In lines 87-88, the authors state 'Visual responses also appeared overall similar but with a small increase in strength during running ...'. This statement would benefit from clarification. From Figure S1 it appears that when the animal is sitting there are no visual responses in the auditory cortex. But when the animal is moving, small positive responses are present. Are these actually 'visual' responses - perhaps a visual prediction sent from the visual cortex to the auditory cortex that is gated by movement? If so, are they modulated by features of visual stimuli eg. contrast, intensity? Or, do these responses simply reflect motor-related activity (running)? Would they be present to the same extent in the same neurons even in the dark?

(4) The authors comment in the text (lines 106-107) about cessation of sound amplitude during audiomotor mismatches as being analogous to halting of visual flow in visuomotor mismatches. However, sound amplitude versus visual flow are quite different in nature. In the visuomotor paradigm, the amount of visual stimulation (photons per unit time) does not necessarily change systematically with running speed. Whereas, in the audiomotor paradigm, the SNR of the stimulus itself changes with running speed which may impact the accuracy of predictions. On a broader note, under natural settings, while the visual flow is coupled to movement, sound amplitude may vary more idiosyncratically with movement.

Perhaps such differences might explain why unlike in the case of visual cortex experiments, running speed does not affect the strength of playback responses in the auditory cortex.

Reviewer #1 (Public Review):

Summary:

The manuscript presents a short report investigating mismatch responses in the auditory cortex, following previous studies focused on the visual cortex. By correlating the mouse locomotion speed with acoustic feedback levels, the authors demonstrate excitatory responses in a subset of neurons to halts in expected acoustic feedback. They show a lack of responses to mismatch in the visual modality. A subset of neurons show enhanced mismatch responses when both auditory and visual modalities are coupled to the animal's locomotion.

While the study is well-designed and addresses a timely question, several concerns exist regarding the quantification of animal behavior, potential alternative explanations for recorded signals, correlation between excitatory responses and animal velocity, discrepancies in reported values, and clarity regarding the identity of certain neurons.

Strengths:

(1) Well-designed study addressing a timely question in the field.

(2) Successful transition from previous work focused on the visual cortex to the auditory cortex, demonstrating generic principles in mismatch responses.

(3) The correlation between mouse locomotion speed and acoustic feedback levels provides evidence for a prediction signal in the auditory cortex.

(4) Coupling of visual and auditory feedback shows putative multimodal integration in the auditory cortex.

Weaknesses:

(1) Lack of quantification of animal behavior upon mismatches, potentially leading to alternative interpretations of recorded signals.

(2) Unclear correlation between excitatory responses and animal velocity during halts, particularly in closed-loop versus playback conditions.

(3) Discrepancies in reported values in a few figure panels raise questions about data consistency and interpretation.

(4) Ambiguity regarding the identity of the [AM+VM] MM neurons.

Reviewer #3 (Public Review):

Summary:

In this article, Hermannova et al catalog the changes in ribosome association with mRNAs when the eukaryotic translation initiation factor 3 is disrupted by knocking down subunits of the multisubunit protein. They find that RNAs relying on TOP motifs for translation, such as ribosomal protein RNAs, and RNAs encoding proteins that modify other proteins in the ER or components of the lysosome are upregulated. In contrast, proteins encoding components of MAP kinase cascades are downregulated when subunits of eIF3 are knocked down.

Strengths:

The authors use ribosome profiling of well-characterized mutants lacking subunits of eIF3 and assess the changes in translation that take place. They supplement the ribosome association studies with western blotting to determine protein level changes of affected transcripts. They analyze what is being encoded by the transcripts undergoing translation changes, which is important for understanding more broadly how translation initiation factor levels affect cancer cell translatomes.

Weaknesses:

(1) The data are presented as a catalog of effects, and the paper would be strengthened if there were a clear model tying the various effects together or linking individual subunit knockdown to cancerous phenotypes. It is unclear what the hypothesis is for cells having more MAPK activity with less of the MAPK proteins being translated, so the main findings of the paper become observational without context.

(2) The conclusions drawn are presented as very generalized other than in the last paragraph, but the experiments were only done in Hela cells. Since conclusions are being made about how translation changes affect MAP kinase signaling and there is mention in the abstract that dysregulation of these subunits is observed in cancer, at least one other cell line would need to be analyzed to provide evidence that the effects of subunit knockdown aren't cell-line specific.

(3) It is also unclear how replicates were performed and how many replicates were performed for several experiments. Biological replicates are mentioned, but what the authors did for biological replicates isn't defined and the description of the collection of cells for polysome/ribosome footprint/RNA seq samples makes it unclear whether the "biological replicates" are samples from separate transfections (true biological replicates) or different aliquots or wells from a single transfection (technical replicates) being run over a separate gradient. If using technical replicates, the data comparing the effects of knocking down D vs E vs H subunits are substantially weakened because subunit-specific differences could be the result of non-specific events that occurred in a transfection. It's also notable that while the pooled siRNAs will increase the potency of knockdown, it is possible that one or more of the siRNAs could have off-target effects, and analyzing individual siRNAs would be better for ensuring effects are specific.

(4) Many of the changes in protein levels reported by Western are subtle. Data from all western blots making claims of quantitative differences should really be quantified relative to nontreated over-loading control or total protein quantified from the gel, and presented with a degree of error from biological replicates to make conclusions about differences in protein levels between samples.

Reviewer #1 (Public Review):

Summary:

In this manuscript, Herrmannova et al explore changes in translation upon individual depletion of three subunits of the eIF3 complex (d, e, and f) in mammalian cells. The authors provide a detailed analysis of regulated transcripts, followed by validation by RT-qPCR and/or Western blot of targets of interest, as well as GO and KKEG pathway analysis. The authors confirm prior observations that eIF3, despite being a general translation initiation factor, functions in mRNA-specific regulation, and that eIF3 is important for translation re-initiation. They show that the global effects of eIF3e and eIF3d depletion on translation and cell growth are concordant. Their results support and extend previous reports suggesting that both factors control the translation of 5'TOP mRNAs. Interestingly, they identify MAPK pathway components as a group of targets coordinately regulated by eIF3 d/e. The authors also discuss discrepancies with other reports analyzing eIF3e function.

Strengths:

Altogether, a solid analysis of eIF3 d/e/h-mediated translation regulation of specific transcripts. The data will be useful for scientists working in the Translation field.

Weaknesses:

The authors could have explored in more detail some of their novel observations, as well as their impact on cell behavior.

Reviewer #2 (Public Review):

Summary:

mRNA translation regulation permits cells to rapidly adapt to diverse stimuli by fine-tuning gene expression. Specifically, the 13-subunit eukaryotic initiation factor 3 (eIF3) complex is critical for translation initiation as it aids in 48S PIC assembly to allow for ribosome scanning. In addition, eIF3 has been shown to drive transcript-specific translation by binding mRNA 5' cap structures through the eIF3d subunit. Dysregulation of eIF3 has been implicated in oncogenesis, however the precise eIF3 subunit contributions are unclear. Here, Herrmannová et al. aim to investigate how eIF3 subcomplexes, generated by knockdown (KD) of either eIF3e, eIF3d, or eIF3h, affect the global translatome. Using Ribo-seq and RNA-seq, the authors identified a large number of genes that exhibit altered translation efficiency upon eIF3d/e KD, while translation defects upon eIF3h KD were mild. eIF3d/e KD share multiple dysregulated transcripts, perhaps due to both subcomplexes lacking eIF3d. Both eIF3d/e KD increase the translation efficiency (TE) of transcripts encoding lysosomal, ER, and ribosomal proteins. This suggests a role of eIF3 in ribosome biogenesis and protein quality control. Many transcripts encoding ribosomal proteins harbor a TOP motif, and eIF3d KD and eIF3e KD cells exhibit a striking induction of these TOP-modified transcripts. On the other hand, eIF3d KD and eIF3e KD lead to a reduction of MAPK/ERK pathway proteins. Despite this downregulation, eIF3d KD and eIF3e KD activate MAPK/ERK signaling as ERK1/2 and c-Jun phosphorylation were induced. Finally, in all three knockdowns, MDM2 and ATF4 protein levels are reduced. This is notable because MDM2 and ATF4 both contain short uORFs upstream of the start codon, and further support a role of eIF3 in reinitiation. Altogether, Herrmannová et al. have gained key insights into precise eIF3-mediated translational control as it relates to key signaling pathways implicated in cancer.

Strengths:

The authors have provided a comprehensive set of data to analyze RNA and ribosome footprinting upon perturbation of eIF3d, eIF3e, and eIF3h. As described above in the summary, these data present many interesting starting points for understanding additional roles of the eIF3 complex and specific subunits in translational control.

Weaknesses:

- The differences between eIF3e and eIF3d knockdown are difficult to reconcile, especially since eIF3e knockdown leads to a reduction in eIF3d levels.

- The paper would be strengthened by experiments directly testing what RNA determinants allow for transcript-specific translation regulation by the eIF3 complex. This would allow the paper to be less descriptive.

- The paper would have more biological relevance if eIF3 subunits were perturbed to mimic naturally occurring situations where eIF3 is dysregulated. For example, eIF3e is aberrantly upregulated in certain cancers, and therefore an overexpression and profiling experiment would have been more relevant than a knockdown experiment.

Reviewer #3 (Public Review):

These studies reveal an S-phase requirement for the PARG dePARylation enzyme in removing ADP-ribosylation from PAR-modified proteins whose PARylation is promoted by the presence of unligated Okazaki fragments. The excessive protein ADP-ribosylation observed in S-phase of PARG-depleted human cells leads to trapping of the PARP1 ADP-ribosylation enzyme on chromatin. The findings would be strengthened by identification of the relevant ADP-ribosylation substrates of PARG whose dePARylation is needed for progression through S-phase.

Comments on revised version:

In the revised version the authors have addressed some of the reviewers' concerns, but, despite the new explanatory paragraph on page 16, the paper remains confusing because as shown in Figure 7 at the end of the Results the PARG KO 293A cells that were analyzed at the beginning of the Results are not true PARG knockouts. The authors stated that they did not rewrite the Results because they wanted to describe the experiments in the order in which they were carried out, but there is no imperative for the experiments to be described in the order in which they were done, and it would be much easier for the uninitiated reader to appreciate the significance of these studies if the true PARG KO cell data were presented at the beginning, as all three of the original reviewers proposed.

While the authors have to some extent clarified the nature of the PARG KO alleles, they have not been able to identify the source of the residual PARG activity in the PARG KO cells, in part because different commercial PARG antibodies give different and conflicting immunoblotting results. Additional sequence characterization of PARG mRNAs expressed in the PARG cKO cells, and also in-depth proteomic analysis of the different PARG bands could provide further insight into the origins and molecular identities of the various PARG proteins expressed from the different KO PARG alleles, and determine which of them might retain catalytic activity.

The authors have made no progress in identifying which are the key PARG substrates required for S phase progression, although they suggest that PARP1 itself may be an important target.

Reviewer #2 (Public Review):

Summary:

In this manuscript Nie et al investigate the effect of PARG KO and PARG inhibition (PARGi) on pADPR, DNA damage, cell viability and synthetic lethal interactions in HEK293A and Hela cells. Surprisingly, the authors report that PARG KO cells are sensitive to PARGi and show higher pADPR levels than PARG KO cells, which is abrogated upon deletion or inhibition of PARP1/PARP2. The authors explain the sensitivity of PARG KO to PARGi through incomplete PARG depletion and demonstrate complete loss of PARG activity when incomplete PARG KO cells are transfected with additional gRNAs in the presence of PARPi. Furthermore, the authors show that the sensitivity of PARG KO cells to PARGi is not caused by NAD depletion but by S-phase accumulation of pADPR on chromatin coming from unligated Okazaki fragments, which are recognized and bound by PARP1. Consistently, PARG KO or PARG inhibition show synthetic lethality with Pol beta, which is required for Okazaki fragment maturation. PARG expression levels in ovarian cancer cell lines correlate negatively with their sensitivity to PARGi.

Reviewer #2 (Public Review):

The authors aimed to understand how epistasis influences the genetic architecture of the DNA-binding domain (DBD) of steroid hormone receptor. An ordinal regression model was developed in this study to analyze a published deep mutational scanning dataset that consists of all combinatorial amino acid variants across four positions (i.e. 160,000 variants). This published dataset measured the binding of each variant to the estrogen receptor response element (ERE, sequence: AGGTCA) as well as the steroid receptor response element (SRE, sequence: AGAACA). This model has major strengths of being reference free and able to account for global nonlinearity in the genotype-phenotype relationship. Thorough analyses of the modelling results have performed, which provided convincing results to support the importance of epistasis in promoting evolution of protein functions. This conclusion is impactful because many previous studies have shown that epistasis constrains evolution. The novelty this study will likely stimulate new ideas in the field. The model will also likely be utilized by other groups in the community.

Reviewer #1 (Public Review):

Metzger et al develop a rigorous method filling an important unmet need in protein evolution - analysis of protein genetic architecture and evolution using data from combinatorially complete 20^N variant libraries. Addressing this need has become increasingly valuable, as experimental methods for generating these datasets expand in scope and scale. Their method integrates two key features - (1) it reports the effects of mutations relative to the average across all variants, rather than a particular genotype, making it useful for examining global genetic architecture, and (2) it does this for all possible 20 states at each site, in contrast to the binary analyses in prior work. These features are not individually novel but integrating them into a single analysis framework is novel and will be valuable to the protein evolution community. Using a previously published dataset generated by two of the authors, they conclude that (1) changes in function are largely attributable to pairwise but not higher-order interactions, and (2) epistasis potentiates, rather than constrains, evolutionary paths. These findings are well-supported by the data. Overall, this work has important implications for predicting the relationship between genotype and phenotype, which is of considerable interest to protein biochemistry, evolutionary biology, and numerous other fields.

Reviewer #1 (Public Review):

Summary:

The authors were trying to understand the relation between the development of large trunks and longirrostrine mandibles in bunodont proboscideans of Miocene, and how it reflects the variation in diet patterns.

Strengths:

The study is very well supported, written, and illustrated, with plenty Supplementary materials. The authors included all Asian bunodont proboscideans with long mandibles and I suggest that they should use the expression "bunodont proboscideans" instead of gomphotheres.

Weaknesses:

I believe that the only weakness is the lack of discussion comparing their results with the development of gigantism and long limbs in proboscideans from the same epoch.

The authors reviewed the manuscript according to my suggestions and responded well to all my comments.

Reviewer #3 (Public Review):

This study investigates subtelomeric repetitive sequences in the budding yeast Saccharomyces cerevisiae, known as Y' and X-elements. Taking advantage of yeast strain SY12 that contains only 3 chromosomes and six telomeres (normal yeast strains contain 32 telomeres) the authors are able to generate a strain completely devoid of Y'- and X-elements.

Strengths:

They demonstrate that the SY12 delta XY strain displays normal growth, with stable telomeres of normal length that were transcriptionally silenced, a key finding with wide implications for telomere biology. Inactivation of telomerase in the SY12 and SY12 delta XY strains frequently resulted in survivors that had circularized all three chromosomes, hence bypassing the need for telomeres altogether. They show that survivors with fused chromosomes and so-called atypical survivors arise independently of the central recombination protein Rad52. The SY12 and SY12 delta XY yeast strains can become a useful tool for future studies of telomere biology. The conclusions of this manuscript are well supported by the data and are valuable for researchers studying telomeres.

Weaknesses:

A weakness of the manuscript is the analysis of telomere transcriptional silencing. They state: "The results demonstrated a significant increase in the expression of the MPH3 and HSP32 upon Sir2 deletion, indicating that telomere silencing remains effective in the absence of X and Y'-elements". However, for the SY12 strain, their analyses indicate that the difference between the WT and sir2 strains is nonsignificant. In addition, a striking observation is that the SY12 strain (with only three chromosomes) express much less of both MPH3 and HSP32 than the parental strain BY4742 (16 chromosomes), both in the presence and absence of Sir2.

Reviewer #1 (Public Review):

The authors have generated a set of yeast S. cerevisiae strains containing different numbers of chromosomes.<br /> Elimination of telomerase activates homologous recombination (HR) to maintain telomeres in cells containing the original 16 chromosomes. However, elimination of telomerase leads to circularization of cells containing a single or two chromosomes. The authors examined whether the subtelomeric sequences X and Y' promote HR-mediated telomere maintenance using the strain SY12 carrying three chromosomes. They found that the subtelomeric sequences X and Y' are dispensable for cell proliferation and HR-mediated telomere maintenance in telomerase-minus SY12 cells. They conclude that subtelomeric X and Y' sequences do not play essential roles in both telomerase-proficient and telomerase-null cells and propose that these sequences represent remnants of genome evolution.

Interestingly, telomerase-minus SY12 generates survivors that are different from well-established Type I or Type II survivors. The authors uncover atypical telomere formation which does not depend on the Rad52 homologous recombination pathway.

Strengths:

The authors examined whether the subtelomeric sequences X and Y' promote HR-mediated telomere maintenance using the strain SY12 carrying three chromosomes. They show that subtelomeres do not have essential roles in telomere maintenance and cell proliferation.

Weaknesses:

It is not fully addressed how atypical survivors are generated independently of Rad52-mediated homologous recombination.<br /> It remains possible that X and Y elements influence homologous recombination, type 1 and type 2 (type X), at telomeres. In particular, the presence of X and Y elements appears to be important for promoting type 1 recombination, although the authors conclude "Elimination of subtelomeric repeat sequences exerts little effect on telomere functions".

Reviewer #2 (Public Review):

Summary:

In this work, Hu and colleagues investigate telomerase-independent survival in Saccharomyces cerevisiae strains engineered to have different chromosome numbers. The authors describe the molecular patterns of survival that change with fewer chromosomes and that differ from the well-described canonical Type I and Type II, including chromosome circularization and other atypical outcomes. They then take advantage of the strain with 3 chromosomes to examine the effect of deleting all the subtelomeric elements, called X and Y'. For most of the tested phenotypes, they find no significant effect of the absence of X- and Y'-element, and show that they are not essential for survivor formation. They speculate that X- and Y'-elements are remnants of ancient telomere maintenance mechanisms.

Strengths:

This work advances our understanding of the telomerase-independent strategies available to the cell by altering the structure of the genome and of the subtelomeres, a feat that was enabled by the set of strains they engineered previously. By using strains with non-standard genome structures, several alternative survival mechanisms are uncovered, revealing the diversity and plasticity of telomere maintenance mechanisms. Overall, the conclusions are well supported by the data, with adequate sample sizes for investigating survivors. The assessment of the genetic requirements for survivors in strains with different chromosome numbers greatly improved the quality of this work. The molecular analyses based on Southern blots are also very well-conducted.

Weaknesses:

The authors discovered alternative telomerase-independent survival strategies beyond the well-described type I and II (including circularization, type X and atypical, as they called them) at play in the context of reduced number of chromosomes. Their work provides a molecular and a partial genetic characterization of these survival pathways. A more thorough analysis of the frequency of each type of survivors and their genetic requirements would have advanced our understanding or the diversity of survival strategies in the absence of telomerase. However, as noted by the authors, the quantification of the rate of emergence of survivors (and their subtypes) is very difficult to achieve. This comment is therefore not meant as a criticism but rather as a perspective on exciting future research avenues.

Reviewer #2 (Public Review):

Summary:

In this manuscript, the authors revealed that genetic deficiencies of ACK1 and BRK are associated with human SLE. First, the authors found that compound heterozygous deleterious variants in the kinase domains of the non-receptor tyrosine kinases (NRTK) TNK2/ACK1 in one multiplex family and PTK6/BRK in another family. Then, by an experimental blockade of ACK1 or BRK in a mouse SLE model, they found an increase in glomerular IgG deposits and circulating autoantibodies. Furthermore, they reported that ACK and BRK variants from the SLE patients impaired the MERTK-mediated anti-inflammatory response to apoptotic cells in human induced pluripotent stem cells (hiPSC)-derived macrophages. This work identified new SLE-associated ACK and BRK variants and a role for the NRTK TNK2/ACK1 and PTK6/BRK in efferocytosis, providing a new molecular and cellular mechanism of SLE pathogenesis.

Strengths:

This work identified new SLE-associated ACK and BRK variants and a role for the NRTK TNK2/ACK1 and PTK6/BRK in efferocytosis, providing a new molecular and cellular mechanism of SLE pathogenesis.

Weaknesses:

Although the manuscript is well-organized and clearly stated, there are some points below that should be considered:

* In this study, the authors used forward genetic analyses to identify novel gene mutations that may cause SLE, combined with GWAS studies of SLE. To further explore the importance of these variants, haplotype analysis of two candidate genes could be performed, to observe the evolution and selection relationship of candidate genes in the population (UK 1000 biobank, for example).

* Although the authors focused on SLE and macrophage efferocytosis in their studies, direct evidence of how macrophage efferocytosis significantly affects SLE is lacking. This point should at least be explicitly introduced and discussed by citing appropriate literature.

* It is still not clear how the target molecules identified in this paper may influence macrophage efferocytosis. More direct evidence should be established.

* For some transcriptional repressors mentioned in their studies, the authors should check whether there is clear experimental evidence. If not, it is recommended to supplement the experimental verifications for clarity.

* In Figures 4C and 4D, it is seen that the usage of inhibitors causes cytoskeletal changes, however this reviewer would not have expected such large change. Did the authors check whether the cells die after heavy treatment by the inhibitors?

Reviewer #1 (Public Review):

Summary:

The authors report compound heterozygous deleterious variants in the kinase domains of the non-receptor tyrosine kinases (NRTK) TNK2/ACK1 in familial SLE. They suggest that ACK1 and BRK deficiencies are associated with human SLE and impair efferocytosis.

Strengths:

The identification of similar mutations in non-receptor tyrosine kinases (NRTKs) in two different families with familial SLE is a significant finding in human disease. Furthermore, the paper provides a detailed analysis of the molecular mechanisms behind the impairment of efferocytosis caused by mutations in ACK1 and BRK.

Weaknesses:

A critical point in this paper is whether the loss of function of ACK1 or BRK contributes to the onset of familial SLE. The authors emphasize that inhibitors of ACK1/BRK worsened IgG deposition in the kidneys in a pristane-induced SLE model, which contributes not to the onset but to the exacerbation of SLE, thus only partially supporting their claim.

Reviewer #1 (Public Review):

Summary:

This manuscript investigates the regulation of chlorophyll biosynthesis in rice embryos, focusing on the role of OsNF-YB7. The rigorous experimental approach, combining genetic, biochemical, and molecular analyses, provides a robust foundation for these findings. The research achieves its objectives, offering new insights into chlorophyll biosynthesis regulation, with the results convincingly supporting the authors' conclusions.

Strengths:

The major strengths include the detailed experimental design and the findings regarding OsNF-YB7's inhibitory role.

Weaknesses:

However, the manuscript's discussion on the practical implications for agriculture and the evolutionary analysis of regulatory mechanisms could be expanded.

Reviewer #2 (Public Review):

Summary:

The authors set out to establish the role of the rice LEC1 homolog OsNF-YB7 in embryo development, especially as it pertains to the development of photosynthetic capacity, with chlorophyll production as a primary focus.

Strengths:

The results are well-supported and each approach used complements each other. There are no major questions left unanswered and the central hypothesis is addressed in every figure.

Weaknesses:

There are a handful of sections that could use clarifying for readers, but overall this is a solidly composed manuscript.

The authors clearly achieved their aims; the results compellingly establish a disparity between how this system operates in rice and Arabidopsis. Conclusions are thoroughly supported by the provided data and interpretations. This work will force a reconsideration of the value of Arabidopsis as a model organism for embryo chlorophyll biosynthesis and possibly photosynthesis during embryo maturation more broadly, as rice is a major crop organism and it very clearly does not follow the Arabidopsis model. It will thus be useful to carry out similar tests in other organisms rather than relying on Arabidopsis and attempting to more fully establish the regulatory mechanism in rice.

Reviewer #3 (Public Review):

Summary:

In this study, the authors set out to understand the mechanisms behind chlorophyll biosynthesis in rice, focusing in particular on the role of OsNF-YB7, an ortholog of Arabidopsis LEC1, which is a positive regulator of chlorophyll (Chl) biosynthesis in Arabidopsis. They showed that OsNF-YB7 loss-of-function mutants in rice have chlorophyll-rich embryos, in contrast to Arabidopsis LEC1 loss-of-function mutants. This contrasting phenotype led the authors to carry out extensive molecular studies on OsNF-YB7, including in vitro and in vivo protein interaction studies, gene expression profiling, and protein-DNA interaction assays. The evidence provided well supported the core arguments of the authors, emphasising that OsNF-YB7 is a negative regulator of Chl biosynthesis in rice embryos by mediating the expression of OsGLK1, a transcription factor that regulates downstream Chl biosynthesis genes. In addition, they showed that OsNF-YB7 interacts with OsGLK1 to negatively regulate the expression of OsGLK1, demonstrating the broad involvement of OsNF-YB7 in rice Chl biosynthetic pathways.

Strengths:

This study clearly demonstrated how OsNF-YB7 regulates its downstream pathways using several in vitro and in vivo approaches. For example, gene expression analysis of OsNF-YB7 loss-of-function and gain-of-function mutants revealed the expression of selected downstream chl biosynthetic genes. This was further validated by EMSA on the gel. The authors also confirmed this using luciferase assays in rice protoplasts. These approaches were used again to show how the interaction of OsNF-YB7 and OsGLK1 regulates downstream genes. The main idea of this study is very well supported by the results and data.

Weaknesses:

From an evolutionary perspective, it is interesting to see how two similar genes have come to play opposite roles in Arabidopsis and rice. It would have been more interesting if the authors had carried out a cross-species analysis of AtLEC1 and OsNF-YB7. For example, overexpressing AtLEC1 in an osnf-yb7 mutant to see if the phenotype is restored or enhanced. Such an approach would help us understand how two similar proteins can play opposite roles in the same mechanism within their respective plant species.

Reviewer #1 (Public Review):

The authors observed a decline in autophagy and proteasome activity in the context of Milton knockdown. Through proteomic analysis, they identified an increase in the protein levels of eIF2β, subsequently pinpointing a novel interaction within eIF subunits where eIF2β contributes to the reduction of eIF2α phosphorylation levels. Furthermore, they demonstrated that overexpression of eIF2β suppresses autophagy and leads to diminished motor function. It was also shown that in a heterozygous mutant background of eIF2β, Milton knockdown could be rescued. This work represents a novel and significant contribution to the field, revealing for the first time that the loss of mitochondria from axons can lead to impaired autophagy function via eIF2β, potentially influencing the acceleration of aging. To further support the authors' claims, several improvements are necessary, particularly in the methods of quantification and the points that should be demonstrated quantitatively. It is crucial to investigate the correlation between aging and the proteins eIF2β and eIF2α.

Reviewer #2 (Public Review):

In the manuscript, the authors aimed to elucidate the molecular mechanism that explains neurodegeneration caused by the depletion of axonal mitochondria. In Drosophila, starting with siRNA depletion of Milton and Miro, the authors attempted to demonstrate that the depletion of axonal mitochondria induces the defect in autophagy. From proteome analyses, the authors hypothesized that autophagy is impacted by the abundance of eIF2β and the phosphorylation of eIF2α. The authors followed up the proteome analyses by testing the effects of eIF2β overexpression and depletion on autophagy. With the results from those experiments, the authors proposed a novel role of eIF2β in proteostasis that underlies neurodegeneration derived from the depletion of axonal mitochondria.

The manuscript has several weaknesses. The reader should take extra care while reading this manuscript and when acknowledging the findings and the model in this manuscript.

The defect in autophagy by the depletion of axonal mitochondria is one of the main claims in the paper. The authors should work more on describing their results of LC3-II/LC3-I ratio, as there are multiple ways to interpret the LC3 blotting for the autophagy assessment. Lysosomal defects result in the accumulation of LC3-II thus the LC3-II/LC3-I ratio gets higher. On the other hand, the defect in the early steps of autophagosome formation could result in a lower LC3-II/LC3-I ratio. From the results of the actual blotting, the LC3-I abundance is the source of the major difference for all conditions (Milton RNAi and eIF2β overexpression and depletion). In the text, the authors simply state the observation of their LC3 blotting. The manuscript lacks an explanation of how to evaluate the LC3-II/LC3-I ratio. Also, the manuscript lacks an elaboration on what the results of the LC3 blotting indicate about the state of autophagy by the depletion of axonal mitochondria.

Another main point of the paper is the up-regulation of eIF2β by depleting the axonal mitochondria leads to the proteostasis crisis. This claim is formed by the findings from the proteome analyses. The authors should have presented their proteomic data with much thorough presentation and explanation. As in the experiment scheme shown in Figure 4A, the author did two proteome analyses: one from the 7-day-old sample and the other from the 21-day-old sample. The manuscript only shows a plot of the result from the 7-day-old sample, but that of the result from the 21-day-old sample. For the 21-day-old sample, the authors only provided data in the supplemental table, in which the abundance ratio of eIF2β from the 21-day-old sample is 0.753, meaning eIF2β is depleted in the 21-day-old sample. The authors should have explained the impact of the eIF2β depletion in the 21-day-old sample, so the reader could fully understand the authors' interpretation of the role of eIF2β on proteostasis.

The manuscript consists of several weaknesses in its data and explanation regarding translation.

(1) The authors are likely misunderstanding the effect of phosphorylation of eIF2α on translation. The P-eIF2α is inhibitory for translation initiation. However, the authors seem to be mistaken that the down-regulation of P-eIF2α inhibits translation.

(2) The result of polysome profiling in Figure 4H is implausible. By 10%-25% sucrose density gradient, polysomes are not expected to be observed. The authors should have used a gradient with much denser sucrose, such as 10-50%.

(3) Also on the polysome profiling, as in the method section, the authors seemed to fractionate ultra-centrifuged samples from top to bottom and then measured A260 by a plate reader. In that case, the authors should have provided a line plot with individual data points, not the smoothly connected ones in the manuscript.

(4) For both the results from polysome profiling and puromycin incorporation (Figure 4H and I), the difference between control siRNA and Milton siRNA are subtle, if not nonexistent. This might arise from the lack of spatial resolution in their experiment as the authors used head lysate for these data but the ratio of Phospho-eIF2α/eIF2α only changes in the axons, based on their results in Figure 4E-G. The authors could have attempted to capture the spatial resolution for the axonal translation to see the difference between control siRNA and Milton siRNA.

Reviewer #1 (Public Review):

Here the authors discuss mechanisms of ligand binding and conformational changes in GlnBP (a small E Coli periplasmic binding protein, which binds and carries L-glutamine to the inner membrane ATP-binding cassette (ABC) transporter). The authors have distinguished records in this area and have published seminal works. They include experimentalists and computational scientists. Accordingly, they provide comprehensive, high-quality, experimental and computational work.

They observe that apo- and holo- GlnBP does not generate detectable exchange between open and (semi-) closed conformations on timescales between 100 ns and 10 ms. Especially, the ligand binding and conformational changes in GlnBP that they observe are highly correlated. Their analysis of the results indicates a dominant induced-fit mechanism, where the ligand binds GlnBP prior to conformational rearrangements. They then suggest that an approach resembling the one they undertook can be applied to other protein systems where the coupling mechanism of conformational changes and ligand binding.

They argue that the intuitive model where ligand binding triggers a functionally relevant conformational change was challenged by structural experiments and MD simulations revealing the existence of unliganded closed or semi-closed states and their dynamic exchange with open unbound conformations, discuss alternative mechanisms that were proposed, their merits and difficulties, concluding that the findings were controversial, which, they suggest is due to insufficient availability of experimental evidence to distinguish them. As to further specific conclusions they draw from their results, they determine that a conformational selection mechanism is incompatible with their results, but induced fit is. They thus propose induced fit as the dominant pathway for GlnBP, further supported by the notion that the open conformation is much more likely to bind substrate than the closed one based on steric arguments.

Considering the landscape of substrate-free states, in my view, the closed state is likely to be the most stable and, thus most highly populated. As the authors note and I agree that state can be sterically infeasible for a deep-pocketed substrate. As indeed they also underscore, there is likely to be a range of open states. If the populations of certain states are extremely low, they may not be detected by the experimental (or computational) methods. The free energy landscape of the protein can populate all possible states, with the populations determined by their relative energies. In principle, the protein can visit all states. Whether a particular state is observed depends on the time the protein spends in that state. The frequencies, or propensities, of the visits can determine the protein function. As to a specific order of events, in my view, there isn't any. It is a matter of probabilities which depend on the populations (energies) of the states. The open conformation that is likely to bind is the most favorable, permitting substrate access, followed by minor, induced fit conformational changes. However, a key factor is the ligand concentration. Ligand binding requires overcoming barriers to sustain the equilibrium of the unliganded ensemble, thus time. If the population of the state is low, and ligand concentration is high (often the case in in vitro experiments, and high drug dosage scenarios) binding is likely to take place across a range of available states.

This is however a personal interpretation of the data. The paper here, which clearly embodies massive careful, and high-quality work, is extensive, making use of a range of experimental approaches, including isothermal titration calorimetry, single-molecule Förster resonance energy transfer, and surface-plasmon resonance spectroscopy. The problem the authors undertake is of fundamental importance.

Reviewer #2 (Public Review):

Summary:

The manuscript by Han et al and Cordes is a tour-de-force effort to distinguish between induced fit and conformational selection in glutamine binding protein (GlnBP). It is important to say that I don't agree that a decision needs to be made between these two limiting possibilities in the sense that whether a minor population can be observed depends on the experiment and the energy difference between the states. That said, the authors make an important distinction which is that it is not sufficient to observe both states in the ligand-free solution because it is likely that the ligand will not bind to the already closed state. The ligand binds to the open state and the question then is whether the ligand sufficiently changes the energy of the open state to effectively cause it to close. The authors point out that this question requires both a kinetic and a thermodynamic answer. Their "method" combines isothermal titration calorimetry, single-molecule FRET including key results from multi-parameter photon-by-photon hidden Markov modelling (mpH2MM), and SPR. The authors present this "method" of combination of experiments as an approach to definitively differentiate between induced fit and conformational selection. I applaud the rigor with which they perform all of the experiments and agree that others who want to understand the exact mechanism of protein conformational changes connected to ligand binding need to do such a multitude of different experiments to fully characterize the process. However, the situation of GlnBP is somewhat unique in the high affinity of the Gln (slow off-rate) as compared to many small molecule binding situations such as enzyme-substrate complexes. It is therefore not surprising that the kinetics result in an induced fit situation. In the case of the E-S complexes I am familiar with, the dissociation is much more rapid because the substrate binding affinity is in the micromolar range and therefore the re-equilibration of the apo state is much faster. In this case, the rate of closing and opening doesn't change much whether ligand is present or not. Here, of course, once the ligand is bound the re-equilibration is slow. Therefore, I am not sure if the conclusions based on this single protein are transferrable to most other protein-small molecule systems. I am also not sure if they are transferrable to protein-protein systems where both molecules the ligand and the receptor are expected to have multiscale dynamics that change upon binding.

Strengths:

The authors provide beautiful ITC data and smFRET data to explore the conformational changes that occur upon Gln binding. Figure 3D and Figure 4 (mpH2MM data) provide the really critical data. The multi-parameter photon-by-photon hidden Markov modelling (mpH2MM) data. In the presence of glutamine concentrations near the Kd, two FRET-active sub-populations are identified that appear to interconvert on timescales slower than 10 ms. They then do a whole bunch of control experiments to look for faster dynamics (Figure 5). They also do TIRF smFRET to try to compare their results to those of previous publications. Here, they find several artifacts are occurring including inactivation of ~50% of the proteins. They also perform SPR experiments to measure the association rate of Gln and obtain expectedly rapid association rates on the order of 10^8 M-1s-1.

Weaknesses:

Looking at the traces presented in the supplementary figures, one can see that several of the traces have more than one molecule present. The authors should make sure that they use only traces with a single photobleaching event for each fluorophore. One can see steps in some of the green traces that indicate two green fluorophors (likely from 2 different molecules) in the traces. This is one of the frequent problems with TIRF smFRET with proteins, that only some of the spots represent single molecules and the rest need to be filtered out of the analysis.

The NMR experiments that the authors cite are not in disagreement with the work presented here. NMR is capable of detecting "invisible states" that occur in 1-5% of the population. SmFRET is not capable of detecting these very minor states. I am quite sure that if NMR spectroscopists could add very high concentrations of Gln they would also see a conversion to the closed population.

Reviewer #1 (Public Review):

Summary:

The paper measures the prevalence and mortality of stroke and its comorbidities across geographic regions in order to find differences in risks that may lead to more effective guidance for these subpopulations. It also does a genetic analysis to look for variants that may drive these phenotypic variations.

Strengths:

The data provided here will provide a foundation for a lot of future research into the causes of the observed correlations as well as whether the observed differences in comorbidities across regions have clinically relevant effects on risk management.

Weaknesses:

As with any cross-national analysis of rates, the data is vulnerable to differences in classification and reporting across jurisdictions. Furthermore, given the increased death rate from COVID-19 associated with many of these comorbid conditions and the long-term effects of COVID-19 infection on vascular health, it is expected that many of the correlations observed in this dataset will shift along with the shifting health of the underlying populations.

Reviewer #2 (Public Review):

Summary:

The authors have analyzed ethnogeographic differences in the comorbidity factors, such as diabetes and heart disease, for the incidences of stroke and whether it leads to mortality.

Strengths:<br /> The idea is interesting and the data are compelling. The results are technically solid.

The authors identify specific genetic loci that increase the risk of a stroke and how they differ by region.

Weaknesses:

The presentation is not focused. It would be better to include p-values and focus presentation on the main effects of the dataset analysis.

Reviewer #1 (Public Review):

Summary:

The manuscript by Duilio M. Potenza et al. explores the role of Arginase II in cardiac aging, majorly using whole-body arg-ii knock-out mice. In this work, the authors have found that Arg-II exerts non-cell-autonomous effects on aging cardiomyocytes, fibroblasts, and endothelial cells mediated by IL-1b from aging macrophages. The authors have used arg II KO mice and an in vitro culture system to study the role of Arg II. The authors have also reported the cell-autonomous effect of Arg-II through mitochondrial ROS in fibroblasts that contribute to cardiac aging. These findings are sufficiently novel in cardiac aging and provide interesting insights. While the phenotypic data seems strong, the mechanistic details are unclear. How Arg II regulates the IL-1b and modulates cardiac aging is still being determined. The authors still need to determine whether Arg II in fibroblasts and endothelial contributes to cardiac fibrosis and cell death. This study also lacks a comprehensive understanding of the pathways modulated by Arg II to regulate cardiac aging.

Strengths:

This study provides interesting information on the role of Arg II in cardiac aging.

The phenotypic data in the arg II KO mice is convincing, and the authors have assessed most of the aging-related changes.

The data is supported by an in vitro cell culture system.

Weaknesses:

The manuscript needs more mechanistic details on how Arg II regulates IL-1b and modulates cardiac aging.

The authors used whole-body KO mice, and the role of macrophages in cardiac aging is not studied in this model. A macrophage-specific arg II Ko would be a better model.

Experiments need to validate the deficiency of Arg II in cardiomyocytes.

The authors have never investigated the possibility of NO involvement in this mice model.

A co-culture system would be appropriate to understand the non-cell-autonomous functions of macrophages.

The Myocardial infarction data shown in the mice model may not be directly linked to cardiac aging.

Reviewer #2 (Public Review):

Summary:

The results from this study demonstrated a cell-specific role of mitochondrial enzyme arginase-II (Arg-II) in heart aging and revealed a non-cell-autonomous effect of Arg-II on cardiomyocytes, fibroblasts, and endothelial cells through the crosstalk with macrophages via inflammatory factors, such as by IL-1, as well as a cell-autonomous effect of Arg-II through mtROS in fibroblasts contributing to cardiac aging phenotype. These findings highlight the significance of non-cardiomyocytes in the heart and bring new insights into the understanding of pathologies of cardiac aging. It also provides new evidence for the development of therapeutic strategies, such as targeting the ArgII activation in macrophages.

Strengths:

This study targets an important clinical challenge, and the results are interesting and innovative. The experimental design is rigorous, the results are solid, and the representation is clear. The conclusion is logical and justified.

Weaknesses:

The discussion could be extended a little bit to improve the realm of the knowledge related to this study.

Reviewer #1 (Public Review):

Summary:

Semenova et al. have studied a large cross-sectional cohort of people living with HIV on suppressive ART, N=115, and performed high dimensional flow cytometry to then search for associations between immunological and clinical parameters and intact/total HIV DNA levels.

A number of interesting data science/ML approaches were explored on the data and the project seems a serious undertaking. However, like many other studies that have looked for these kinds of associations, there was not a very strong signal. Of course, the goal of unsupervised learning is to find new hypotheses that aren't obvious to human eyes, but I felt in that context, there were (1) results slightly oversold, (2) some questions about methodology in terms mostly of reservoir levels, and (3) results were not sufficiently translated back into meaning in terms of clinical outcomes.

Strengths:

The study is evidently a large and impressive undertaking and combines many cutting-edge statistical techniques with a comprehensive experimental cohort of people living with HIV, notably inclusive of populations underrepresented in HIV science. A number of intriguing hypotheses are put forward that could be explored further. Sharing the data could create a useful repository for more specific analyses.

Weaknesses:

Despite the detailed experiments and methods, there was not a very strong signal for the variable(s) predicting HIV reservoir size. The Spearman coefficients are ~0.3, (somewhat weak, and acknowledged as such) and predictive models reach 70-80% prediction levels, though sometimes categorical variables are challenging to interpret.

There are some questions about methodology, as well as some conclusions that are not completely supported by results, or at minimum not sufficiently contextualized in terms of clinical significance.

On associations: the false discovery rate correction was set at 5%, but data appear underdetermined with fewer observations than variables (144vars > 115ppts), and it isn't always clear if/when variables are related (e.g inverses of one another, for instance, %CD4 and %CD8).

The modeling of reservoir size was unusual, typically intact and defective HIV DNA are analyzed on a log10 scale (both for decays and predicting rebound). Also sometimes in this analysis levels are normalized (presumably to max/min?, e.g. S5), and given the large within-host variation of level we see in other works, it is not trivial to predict any downstream impact of normalization across population vs within-person.

Also, the qualitative characterization of low/high reservoir is not standard and naturally will split by early/later ART if done as above/below median. Given the continuous nature of these data, it seems throughout that predicting above/below median is a little hard to translate into clinical meaning.

Lastly, the work is comprehensive and appears solid, but the code was not shared to see how calculations were performed.

Reviewer #2 (Public Review):

Summary:

Semenova et. al., performed a cross-sectional analysis of host immunophenotypes (using flow cytometry) and the peripheral CD4+ T cell HIV reservoir size (using the Intact Proviral DNA Assay, IPDA) from 115 people with HIV (PWH) on ART. The study mostly highlights the machine learning methods applied to these host and viral reservoir datasets but fails to interpret these complex analyses into (clinically, biologically) interpretable findings. For these reasons, the direct translational take-home message from this work is lost amidst a large list of findings (shown as clusters of associated markers) and sentences such as "this study highlights the utility of machine learning approaches to identify otherwise imperceptible global patterns" - lead to overinterpretation of their data.

Strengths:

Measurement of host immunophenotyping measures (multiparameter flow cytometry) and peripheral HIV reservoir size (IPDA) from 115 PWH on ART.

Major Weaknesses:

(1) Overall, there is little to no interpretability of their machine learning analyses; findings appear as a "laundry list" of parameters with no interpretation of the estimated effect size and directionality of the observed associations. For example, Figure 2 might actually give an interpretation of each X increase in immunophenotyping parameter, we saw a Y increase/decrease in HIV reservoir measure.

(2) The correlations all appear to be relatively weak, with most Spearman R in the 0.30 range or so.

(3) The Discussion needs further work to help guide the reader. The sentence: "The correlative results from this present study corroborate many of these studies, and provide additional insights" is broad. The authors should spend some time here to clearly describe the prior literature (e.g., describe the strength and direction of the association observed in prior work linking PD-1 and HIV reservoir size, as well as specify which type of HIV reservoir measures were analyzed in these earlier studies, etc.) and how the current findings add to or are in contrast to those prior findings.

(4) The most interesting finding is buried on page 12 in the Discussion: "Uniquely, however, CD127 expression on CD4 T cells was significantly inversely associated with intact reservoir frequency." The authors should highlight this in the abstract, and title, and move this up in the Discussion. The paper describes a very high dimensional analysis and the key takeaways are not clear; the more the author can point the reader to the take-home points, the better their findings can have translatability to future follow-up mechanistic and/or validation studies.

(5) The authors should avoid overinterpretation of these results. For example in the Discussion on page 13 "The existence of two distinct clusters of PWH with different immune features and reservoir characteristics could have important implications for HIV cure strategies - these two groups may respond differently to a given approach, and cluster membership may need to be considered to optimize a given strategy." It is highly unlikely that future studies will be performing the breadth of parameters resulting here and then use these directly for optimizing therapy.

(6) There are only TWO limitations listed here: cross-sectional study design and the use of peripheral blood samples. (The subsequent paragraph notes an additional weakness which is misclassification of intact sequences by IPDA). This is a very limited discussion and highlights the need to more critically evaluate their study for potential weaknesses.

(7) A major clinical predictor of HIV reservoir size and decay is the timing of ART initiation. The authors should include these (as well as other clinical covariate data - see #12 below) in their analyses and/or describe as limitations of their study.

Reviewer #3 (Public Review):

Summary:

This valuable study by Semenova and colleagues describes a large cross-sectional cohort of 115 individuals on ART. Participants contributed a single blood sample which underwent IPDA, and 25-color flow with various markers (pre and post-stimulation). The authors then used clustering, decision tree analyses, and machine learning to look for correlations between these immunophenotypic markers and several measures of HIV reservoir volume. They identified two distinct clusters that can be somewhat differentiated based on total HIV DNA level, intact HIV DNA level, and multiple T cell cellular markers of activation and exhaustion.

The conclusions of the paper are supported by the data but the relationships between independent and dependent variables in the models are correlative with no mechanistic work to determine causality. It is unclear in most cases whether confounding variables could explain these correlations. If there is causality, then the data is not sufficient to infer directionality (ie does the immune environment impact the HIV reservoir or vice versa or both?). In addition, even with sophisticated and appropriate machine learning approaches, the models are not terribly predictive or highly correlated. For these reasons, the study is very much hypothesis-generating and will not impact cure strategies or HIV reservoir measurement strategies in the short term.

Strengths:

The study cohort is large and diverse in terms of key input variables such as age, gender, and duration of ART. Selection of immune assays is appropriate. The authors used a wide array of bioinformatic approaches to examine correlations in the data. The paper was generally well-written and appropriately referenced.

Weaknesses:

(1) The major limitation of this work is that it is highly exploratory and not hypothesis-driven. While some interesting correlations are identified, these are clearly hypothesis-generating based on the observational study design.

(2) The study's cross-sectional nature limits the ability to make mechanistic inferences about reservoir persistence. For instance, it would be very interesting to know whether the reservoir cluster is a feature of an individual throughout ART, or whether this outcome is dynamic over time.

(3) A fundamental issue is that I am concerned that binarizing the 3 reservoir metrics in a 50/50 fashion is for statistical convenience. First, by converting a continuous outcome into a simple binary outcome, the authors lose significant amounts of quantitative information. Second, the low and high reservoir outcomes are not actually demonstrated to be clinically meaningful: I presume that both contain many (?all) data points above levels where rebound would be expected soon after interruption of ART. Reservoir levels would also have no apparent outcome on the selection of cure approaches. Overall, dividing at the median seems biologically arbitrary to me.

(4) The two reservoir clusters are of potential interest as high total and intact with low % intact are discriminated somewhat by immune activation and exhaustion. This was the most interesting finding to me, but it is difficult to know whether this clustering is due to age, time on ART, other co-morbidity, ART adherence, or other possible unmeasured confounding variables.

(5) At the individual level, there is substantial overlap between clusters according to total, intact, and % intact between the clusters. Therefore, the claim in the discussion that these 2 cluster phenotypes may require different therapeutic approaches seems rather speculative. That said, the discussion is very thoughtful about how these 2 clusters may develop with consideration of the initial insult of untreated infection and / or differences in immune recovery.

(6) The authors state that the machine learning algorithms allow for reasonable prediction of reservoir volume. It is subjective, but to me, 70% accuracy is very low. This is not a disappointing finding per se. The authors did their best with the available data. It is informative that the machine learning algorithms cannot reliably discriminate reservoir volume despite substantial amounts of input data. This implies that either key explanatory variables were not included in the models (such as viral genotype, host immune phenotype, and comorbidities) or that the outcome for testing the models is not meaningful (which may be possible with an arbitrary 50/50 split in the data relative to median HIV DNA volumes: see above).

(7) The decision tree is innovative and a useful addition, but does not provide enough discriminatory information to imply causality, mechanism, or directionality in terms of whether the immune phenotype is impacting the reservoir or vice versa or both. Tree accuracy of 80% is marginal for a decision tool.

(8) Figure 2: this is not a weakness of the analysis but I have a question about interpretation. If total HIV DNA is more predictive of immune phenotype than intact HIV DNA, does this potentially implicate a prior high burden of viral replication (high viral load &/or more prolonged time off ART) rather than ongoing reservoir stimulation as a contributor to immune phenotype? A similar thought could be applied to the fact that clustering could only be detected when applied to total HIV DNA-associated features. Many investigators do not consider defective HIV DNA to be "part of the reservoir" so it is interesting to speculate why these defective viruses appear to have more correlation with immunophenotype than intact viruses.

(9) Overall, the authors need to do an even more careful job of emphasizing that these are all just correlations. For instance, HIV DNA cannot be proven to have a causal effect on the immunophenotype of the host with this study design. Similarly, immunophenotype may be affecting HIV DNA or the correlations between the two variables could be entirely due to a separate confounding variable.

(10) In general, in the intro, when the authors refer to the immune system, they do not consistently differentiate whether they are referring to the anti-HIV immune response, the reservoir itself, or both. More specifically, the sentence in the introduction listing various causes of immune activation should have citations. (To my knowledge, there is no study to date that definitively links proviral expression from reservoir cells in vivo to immune activation as it is next to impossible to remove the confounding possible imprint of previous HIV replication.) Similarly, it is worth mentioning that the depletion of intact proviruses is quite slow such that provial expression can only be stimulating the immune system at a low level. Similarly, the statement "Viral protein expression during therapy likely maintains antigen-specific cells of the adaptive immune system" seems hard to dissociate from the persistence of immune cells that were reactive to viremia.

(11) Given the many limitations of the study design and the inability of the models to discriminate reservoir volume and phenotype, the limitations section of the discussion seems rather brief.

Reviewer #1 (Public Review):

Summary:

The current study aims to quantify associations between the regular use of proton-pump inhibitors (PPI) - defined as using PPI most days of the week during the last 4 weeks at one cross-section in time - with several respiratory outcomes up to several years later in time. There are 6 respiratory outcomes included: risk of influenza, pneumonia, COVID-19, other respiratory tract infections, as well as COVID-19 severity and mortality).

Strengths:

Several sensitivity analyses were performed, including i) estimation of the e-value to assess how strong unmeasured confounders should be to explain observed effects, ii) comparison with another drug with a similar indication to potentially reduce (but not eliminate) confounding by indication.

Weaknesses:

(1) The main exposure of interest seems to be only measured at one time-point in time (at study enrollment) while patients are considered many years at risk afterwards without knowing their exposure status at the time of experiencing the outcome. As indicated by the authors, PPI are sometimes used for only short amounts of time. It seems biologically implausible that an infection was caused by using PPI for a few weeks many years ago.

(2) Previous studies have shown that by focusing on prevalent users of drugs, one often induces several biases such as collider stratification bias, selection bias through depletion of susceptible, etc.

(3) It seems Kaplan Meier curves are not adjusted for confounding through e.g. inverse probability weighting. As such the KM curves are currently not informative (or the authors need to make clearer that curves are actually adjusted for measured confounding).

(4) Throughout the manuscript the authors seem to misuse the term multivariate (using one model with e.g. correlated error terms to assess multiple outcomes at once) when they seem to mean multivariable.

(5) Given multiple outcomes are assessed there is a clear argument for accounting for multiple testing, which following the logic of the authors used in terms of claiming there is no association when results are not significant may change their conclusions. More high-level, the authors should avoid the pitfall of stating there is evidence of absence if there is only an absence of evidence in a better way (no statistically significant association doesn't mean no relationship exists).

(6) While the authors claim that the quantitative bias analysis does show results are robust to unmeasured confounding, I would disagree with this. The e-values are around 2 and it is clearly not implausible that there are one or more unmeasured risk factors that together or alone would have such an effect size. Furthermore, if one would use the same (significance) criteria as used by the authors for determining whether an association exists, the required effect size for an unmeasured confounder to render effects 'statistically non-significant' would be even smaller.

(7) Some patients are excluded due to the absence of follow-up, but it is unclear how that is determined. Is there potentially some selection bias underlying this where those who are less healthy stop participating in the UK biobank?

(8) Given that the exposure is based on self-report how certain can we be that patients e.g. do know that their branded over-the-counter drugs are PPI (e.g. guardium tablets)? Some discussion around this potential issue is lacking.

(9) Details about the deprivation index are needed in the main text as this is a UK-specific variable that will be unfamiliar to most readers.

(10) It is unclear how variables were coded/incorporated from the main text. More details are required, e.g. was age included as a continuous variable and if so was non-linearity considered and how?

(11) The authors state that Schoenfeld residuals were tested, but don't report the test statistics. Could they please provide these, e.g. it would already be informative if they report that all p-values are above a certain value.

(12) The authors would ideally extend their discussion around unmeasured confounding, e.g. using the DAGs provided in https://www.ncbi.nlm.nih.gov/pmc/articles/PMC7832226/, in particular (but not limited to) around severity and not just presence/absence of comorbidities.

(13) The UK biobank is known to be highly selected for a range of genetic, behavioural, cardiovascular, demographic, and anthropometric traits. The potential problems this might create in terms of collider stratification bias - as highlighted here for example: https://www.nature.com/articles/s41467-020-19478-2 - should be discussed in greater detail and also appreciated more when providing conclusions.

Reviewer #2 (Public Review):

Summary:

Zeng et al investigate in an observational population-based cohort study whether the use of proton pump inhibitors (PPIs) is associated with an increased risk of several respiratory infections among which are influenza, pneumonia, and COVID-19. They conclude that compared to non-users, people regularly taking PPIs have increased susceptibility to influenza, pneumonia, as well as COVID-19 severity and mortality. By performing several different statistical analyses, they try to reduce bias as much as possible, to end up with robust estimates of the association.

Strengths:

The study comprehensively adjusts for a variety of critical covariates and by using different statistical analyses, including propensity-score-matched analyses and quantitative bias analysis, the estimates of the associations can be considered robust.

Weaknesses:

As it is an observational cohort study there still might be bias. Information on the dose or duration of acid suppressant use was not available, but might be of influence on the results. The outcome of interest was obtained from primary care data, suggesting that only infections as diagnosed by a physician are taken into account. Due to the self-limiting nature of the outcome, differences in health-seeking behavior might affect the results.

Reviewer #1 (Public Review):

The manuscript, "A versatile high-throughput assay based on 3D ring-shaped cardiac tissues generated from human induced pluripotent stem cell-derived cardiomyocytes," developed a unique culture platform with PEG hydrogel that facilitates the in-situ measurement of contractile dynamics of the engineered cardiac rings. The authors optimized the tissue seeding conditions, demonstrated tissue morphology with expressions of cardiac and fibroblast markers, mathematically modeled the equation to derive contractile forces and other parameters based on imaging analysis, and concluded by testing several compounds with known cardiac responses.

The authors answered my questions with appropriate experiments and explanation.

(1) This paper presents an intriguing platform that creates miniature cardiac rings with merely thousands of cardiomyocytes per tissue in a 96-well plate format. The shape of the ring and the squeezing motion can recapitulate the contraction of the cardiac chamber to a certain degree. However, Thavandiran et al. (PNAS 2013) created a larger version of the cardiac ring and found that electrical propagation revealed spontaneous infinite loop-like cycles of activation propagation traversing the ring. This model was used to mimic a reentrant wave during arrhythmia. Therefore, there are concerns about whether a large number of cardiac tissues experience arrhythmia due to geometry-induced re-entry current and cannot be used as a healthy tissue model.

In the new experiment, the authors demonstrated with voltage-sensitive dye that these miniaturized tissues do not experience any arrhythmia, potentially due to their small size.

(2) The platform can produce 21 cardiac rings per well in 96-well plates, with the throughput being the highest among competing platforms. The resulting tissues exhibit good sarcomere striation due to the strain from the pillars. However, emerging questions pertain to culture longevity and reproducibility among tissues. According to Figure 1E, uneven ring formation around the pillar leads to tissue thinning and breakage. Only 50% survival is observed after 20 days of culture in the optimized seeding group. Are there any strategies to improve this survival rate? Additionally, do the cardiac rings detach from the glass slides and roll up, given the two compartments with cardiac and fibroblast-rich regions where fibroblasts maintain attachment to the glass slides? Moreover, the standard deviation of force measurement is a quarter of the value, which is suboptimal given the high replicate number. As the platform utilizes imaging analysis to derive contractile dynamics, calibration based on the angle and distance of the camera lens to individual tissues should be conducted to reduce error. On the other hand, how reproducible are the pillars? It is highly recommended to mechanically evaluate the consistency of the hydrogel-based pillars across different wells and within wells to understand the variance.

The authors stated that the platform has been tested and improved with multiple cell lines to enhance tissue survival rates. The methodology of image capture and calculation of contractile dynamics were explained in detail to address concerns. Moreover, the reproducibility of the pillars was demonstrated by consistent results of Young's Modulus (AFM) from each pillar, showing low standard deviations.

(3) Does the platform allow the observation of non-synchronized beating when testing with compounds? This can be extremely important as the intended applications of this platform are drug testing and cardiac disease modeling. The author should elaborate on the method in the manuscript and explain the obtained results in detail.

Referring to Question #1, the platform does not present arrythmia potentially due to the small size of the tissue.

(4) The results of drug testing are interesting. Isoperenoral is typically causing positive chronotropic and positive inotropic responses, where inotropic responses are difficult to obtain due to low tissue maturity. It is inconsistent with other reported results that cardiac rings do not exhibit increased beating frequency, but slightly increased forces only.

The authors repeated the experiment with the same results and hypothesized that the results would be line-dependent, since the maturation of iPSC-CM is not consistent. The additional dose curves provided more information on the tissue behaviors against well-known compounds.

Overall, the manuscript is well-written, and the designed platform presents unique advantages for high-throughput cardiac tissue culture. The paper has adequate data to demonstrate the proof-of-concept study of the platform. The throughput, consistency of the tissue, and the potential integration of high-throughput automation would be the highlights of this platform.

Reviewer #1 (Public Review):

Thermogenic adipocyte activity associate with cardiometabolic health in humans, but decline with age. Identifying the underlying mechanisms of this decline is therefore highly important.

To address this task, Holman and co-authors present compelling data from their investigations of the effects of two major determinants of thermogenic activity: cold, which induce thermogenic de novo differentiation as well as conversion of dormant thermogenic inguinal adipocytes: and aging, which strongly reduce thermogenic activity. The authors study young and middle-aged mice at thermoneutrality and following cold exposure.

Using linage tracing, the authors conclude that the older group produce less thermogenic adipocytes from progenitor differentiation. However, they found no differences between thermogenic differentiation capacity between the age groups when progenitors are isolated and differentiated in vitro. This finding is consistent with previous findings in humans, demonstrating that progenitor cells derived from dormant perirenal brown fat of humans differentiate into thermogenic adipocytes in vitro. Taken together, this underscores that age-related changes in the microenvironment rather than autonomous alterations in the ASPCs explain the age related decline in thermogenic capacity, This is an important finding in terms of identifying new approaches to switch dormant adipocytes into an active thermogenic phenotype.

To gain insight into the age-related changes, the authors use single cell and single nuclei RNA sequencing mapping of their two age groups, comparing thermoneutral and cold conditions between the two groups. Interestingly, where the literature previously demonstrated that de novo lipogenesis (DNL) occurs in relation to thermogenic activation, the authors show that DNL in fact is activated in a white adipocyte cell type, whereas the beige thermogenic adipocytes form a separate cluster.

Considering recent findings, that adipose tissue contains several subtypes of ASPCs and adipocytes, mapping the changes at single cell resolution following cold intervention provides an important contribution to the field, in particular as an older group with limited thermogenic adaptation is analyzed in parallel with a younger, more responsive group. This model also allowed for detection of microenvironment as a determining factor of thermogenic response.

The use of only two time points (young and middle-aged) along the aging continuum limits the conclusions that can be made on aging as the only driver of the observed differences between the groups. Furthermore, as the authors also discuss, aging is a complex phenotype, and in this case the older mice were heavier and had larger fat depots, which should be taken into consideration when interpreting the data.

In conclusion, this study provides an important resource for further studies, which should investigate how the findings can be translated into humans for reactivation of dormant thermogenic fat and a potential improvement of metabolic health.

Reviewer #2 (Public Review):

This manuscript focused on why aging leads to decreased beiging of white adipose tissue. The authors used an inducible lineage tracing system and provided in vivo evidence that de novo beige adipogenesis from Pdgfra+ adipocyte progenitor cells is blocked during early aging in subcutaneous fat. Single-cell RNA sequencing of adipocyte progenitor cells and in vitro assays showed that these cells have similar beige adipogenic capacities in vitro. Single-cell nucleus RNA sequencing of mature adipocytes indicated that aged mice have more Npr3 high-expressing adipocytes in the subcutaneous fat from aged mice. Meanwhile, adipocytes from aged mice have significantly lower expression of genes involved in de novo lipogenesis, which may contribute to the declined beige adipogenesis.

The mechanism that leads to age-related impairment of white adipose tissue beiging is not very clear. The finding that Pdgfra+ adipocyte progenitor cells contribute to beige adipogenesis is novel and interesting. It is more intriguing that the aging process represses Pdgfra+ adipocyte progenitor cells from differentiating into beige adipocytes during cold stimulation. Mature adipocytes that have high de novo lipogenesis activity may support beige adipogenesis is also novel and worth further pursuing. The study was carried out with a nice experimental design, and the authors provided sufficient data to support the major conclusions. I only have a few comments that could potentially improve the manuscript.

(1) It is interesting that after three days of cold exposure, aged mice also have much fewer beige adipocytes. Is de novo adipogenesis involved at this early stage? Or does the previous beige adipocyte that acquired white morphology have a better "reactivation" in young mice? It would be nice if the author could discuss the possibilities.

(2) Is the absolute number of Pdgfra+ cells decreased in aged mice? It would be nice to include quantifications of the percentage of tomato+ beige adipocytes in total tomato+ cells to reflect the adipogenic rate.

Reviewer #1 (Public Review):

Summary: In this article, Mirza et al developed a continuum active gel model of actomyosin cytoskeleton that account for nematic order and density variations in actomyosin. Using this model, they identify the requirements for the formation of dense nematic structures. In particular, they show that self-organization into nematic bundles requires both flow-induced alignment and active tension anisotropy in the system. By varying model parameters that control active tension and nematic alignment, the authors show that their model reproduces a rich variety of actomyosin structures, including tactoids, fibres, asters as well as crystalline networks. Additionally, discrete simulations are employed to calculate the activity parameters in the continuum model, providing a microscopic perspective on the conditions driving the formation of fibrillar patterns.

Strengths: The strength of the work lies in its delineation of the parameter ranges that generate distinct types of nematic organization within actomyosin networks. The authors pinpoint the physical mechanisms behind the formation of fibrillar patterns, which may offer valuable insights into stress fiber assembly. Another strength of the work is connecting activity parameters in the continuum theory with microscopic simulations.

Weaknesses: This paper is a very difficult read for nonspecialists, especially if you are not well-versed in continuum hydrodynamic theories. Efforts should be made to connect various elements of theory with biological mechanisms, which is mostly lacking in this paper. The comparison with experiments is predominantly qualitative. It is unclear if the theory is suited for in vitro or in vivo actomyosin systems. The justification for various model assumptions, especially concerning their applicability to actomyosin networks, requires a more thorough examination. The classification of different structures demands further justification. For example, the rationale behind categorizing structures as sarcomeric remains unclear when nematic order is perpendicular to the axis of the bands. Sarcomeres traditionally exhibit a specific ordering of actin filaments with alternating polarity patterns. Similarly, the criteria for distinguishing between contractile and extensile structures need clarification, as one would expect extensile structures to be under tension contrary to the authors' claim. Additionally, its unclear if the model's predictions for fiber dynamics align with observations in cells, as stress fibers exhibit a high degree of dynamism and tend to coalesce with neighboring fibers during their assembly phase. Finally, it seems that the microscopic model is unable to recapitulate the density patterns predicted by the continuum theory, raising questions about the suitability of the simulation model.

Reviewer #2 (Public Review):

Summary:

The article by Waleed et al discusses the self organization of actin cytoskeleton using the theory of active nematics. Linear stability analysis of the governing equations and computer simulations show that the system is unstable to density fluctuations and self organized structures can emerge. While the context is interesting, I am not sure whether the physics is new. Hence I have reservations about recommending this article.

Strengths:

(i) Analytical calculations complemented with simulations (ii) Theory for cytoskeletal network

Weaknesses:

Not placed in the context or literature on active nematics.

Reviewer #3 (Public Review):

The manuscript "Theory of active self-organization of dense nematic structures in the actin cytoskeleton" analysis self-organized pattern formation within a two-dimensional nematic liquid crystal theory and uses microscopic simulations to test the plausibility of some of the conclusions drawn from that analysis. After performing an analytic linear stability analysis that indicates the possibility of patterning instabilities, the authors perform fully non-linear numerical simulations and identify the emergence of stripe-like patterning when anisotropic active stresses are present. Following a range of qualitative numerical observations on how parameter changes affect these patterns, the authors identify, besides isotropic and nematic stress, also active self-alignment as an important ingredient to form the observed patterns. Finally, microscopic simulations are used to test the plausibility of some of the conclusions drawn from continuum simulations.

The paper is well written, figures are mostly clear and the theoretical analysis presented in both, main text and supplement, is rigorous. Mechano-chemical coupling has emerged in recent years as a crucial element of cell cortex and tissue organization and it is plausible to think that both, isotropic and anisotropic active stresses, are present within such effectively compressible structures. Even though not yet stated this way by the authors, I would argue that combining these two is of the key ingredients that distinguishes this theoretical paper from similar ones. The diversity of patterning processes experimentally observed is nicely elaborated on in the introduction of the paper, though other closely related previous work could also have been included in these references (see below for examples).

To introduce the continuum model, the authors exclusively cite their own, unpublished pre-print, even though the final equations take the same form as previously derived and used by other groups working in the field of active hydrodynamics (a certainly incomplete list: Marenduzzo et al (PRL, 2007), Salbreux et al (PRL, 2009, cited elsewhere in the paper), Jülicher et al (Rep Prog Phys, 2018), Giomi (PRX, 2015),...). To make better contact with the broad active liquid crystal community and to delineate the present work more compellingly from existing results, it would be helpful to include a more comprehensive discussion of the background of the existing theoretical understanding on active nematics. In fact, I found it often agrees nicely with the observations made in the present work, an opportunity to consolidate the results that is sometimes currently missed out on. For example, it is known that self-organised active isotropic fluids form in 2D hexagonal and pulsatory patterns (Kumar et al, PRL, 2014), as well as contractile patches (Mietke et al, PRL 2019), just as shown and discussed in Fig. 2. It is also known that extensile nematics, \kappa<0 here, draw in material laterally of the nematic axis and expel it along the nematic axis (the other way around for \kappa>0, see e.g. Doostmohammadi et al, Nat Comm, 2018 "Active Nematics" for a review that makes this point), consistent with all relative nematic director/flow orientations shown in Figs. 2 and 3 of the present work.

The results of numerical simulations are well-presented. Large parts of the discussion of numerical observations - specifically around Fig. 3 - are qualitative and it is not clear why the analysis is restricted to \kappa<0. Some of the observations resonate with recent discussions in the field, for example the observation of effectively extensile dynamics in a contractile system is interesting and reminiscent of ambiguities about extensile/contractile properties discussed in recent preprints (https://arxiv.org/abs/2309.04224). It is convincingly concluded that, besides nematic stress on top of isotropic one, active self-alignment is a key ingredient to produce the observed patterns.

I compliment the authors for trying to gain further mechanistic insights into this conclusion with microscopic filament simulations that are diligently performed. It is rightfully stated that these simulations only provide plausibility tests and, within this scope, I would say the authors are successful. At the same time, it leaves open questions that could have been discussed more carefully. For example, I wonder what can be said about the regime \kappa>0 (which is dropped ad-hoc from Fig. 3 onward) microscopically, in which the continuum theory does also predict the formation of stripe patterns - besides the short comment at the very end? How does the spatial inhomogeneous organization the continuum theory predicts fit in the presented, microscopic picture and vice versa?

Overall, the paper represents a valuable contribution to the field of active matter and, if strengthened further, might provide a fruitful basis to develop new hypothesis about the dynamic self-organisation of dense filamentous bundles in biological systems.

Reviewer #1 (Public Review):

Summary:

In this manuscript, Liu et al. used scRNA-seq to characterize cell type-specific responses during allergic contact dermatitis (ACD) in a mouse model, specifically the hapten-induced DNFB model. Using the scRNA-seq data, they deconvolved the cell types responsible for the expression of major inflammatory cytokines such as IFNG (from CD4 and CD8 T cells), IL4/13 (from basophils), IL17A (from gd T cells), and IL1B from neutrophils and macrophages. They found the highest upregulation of a type 1 inflammatory response, centering around IFNG produced by CD4 and CD8 T cells. They further identified a subpopulation of dermal fibroblasts that upregulate CXCL9/10 during ACD and provided functional genetic evidence in their mouse model that disrupting IFNG signaling to fibroblasts decreases CD8 T cell infiltration and overall inflammation. They identify an increase in IFNG-expressing CD8 T cells in human patient samples of ACD vs. healthy control skin and co-localization of CD8 T cells with PDGFRA+ fibroblasts, which suggests this mechanism is relevant to human ACD. This mechanism is reminiscent of recent work (Xu et al., Nature 2022) showing that IFNG signaling in dermal fibroblasts upregulates CXCL9/10 to recruit CD8 T cells in a mouse model of vitiligo. Overall, this is a very well-presented, clear, and comprehensive manuscript. The conclusions of the study are mostly well supported by data, but some aspects of the work could be improved by additional clarification of the identity of the cell types shown to be involved, including the exact subpopulation discovered by scRNA-seq and the subtype of CD8 T cell involved. The study was limited by its use of one ACD model (DNFB), which prevents an assessment of how broadly relevant this axis is. The human sample validation is slightly circumstantial and limited by the multiplexing capacity of immunofluorescence markers.

Strengths:

Through deep characterization of the in vivo ACD model, the authors were able to determine which cell types were expressing the major cytokines involved in ACD inflammation, such as IFNG, IL4/13, IL17A, and IL1B. These analyses are well-presented and thoughtful, showing first that the response is IFNG-dominant, then focusing on deeper characterization of lymphocytes, myeloid cells, and fibroblasts, which are also validated and complemented by FACS experiments using canonical markers of these cell types as well as IF staining. Crosstalk analyses from the scRNA-seq data led the authors to focus on IFNG signaling fibroblasts, and in vitro experiments demonstrate that CXCL9 and CXCL10 are expressed by fibroblasts stimulated by IFNG. In vivo functional genetic evidence demonstrates an important role for IFNG signaling in fibroblasts, as KO of Ifngr1 using Pdgfra-Cre Ifngr1 fl/fl mice, showed a reduction in inflammation and CD8 T cell recruitment.

Weaknesses:

The use of one model limits an understanding of how broad this fibroblast-T cell axis is during ACD. However, the authors chose the most commonly employed model and cited additional work in a vitiligo model (another type 1 immune response). The identity of the involved fibroblasts and T cells in the mouse model is difficult to assess as scRNA-seq identified subpopulations of these cell types, but most work in the Pdgfra-Cre Ifngr1 fl/fl mice used broad markers for these cell types as opposed to matched subpopulation markers from their scRNA-seq data. Human patient samples of ACD were co-stained with two markers at a time, demonstrating the presence of CD8+IFNG+ T cells, PDGFRA+CXCL10+ fibroblasts, and co-localization of PDGFRA+ fibroblasts and CD8+ T cells. However, no IF staining demonstrates co-expression of all 4 markers at once; thus, the human validation of co-localization of CD8+IFNG+ T cells and PDGFRA+CXCL10+ fibroblasts is ultimately indirect, although not a huge leap of faith. Although n=3 samples of healthy control and ACD samples are used, there is no quantification of any results to demonstrate the robustness of differences.

Reviewer #2 (Public Review):

Summary:

The investigators apply scRNA seq and bioinformatics to identify biomarkers associated with DNFB-induced contact dermatitis in mice. The bioinformatics component of the study appears reasonable and may provide new insights regarding TH1-driven immune reactions in ACD in mice. However, the IF data and images of tissue sections are not clear and should be improved to validate the model.

Strengths:

The bioinformatics analysis.

Weaknesses:

The IF data presented in 4H, 6H, 7E and 7F are not convincing and need to be correlated with routine staining on histology and different IF markers for PDGFR. Some of the IF staining data demonstrates a pattern inconsistent with its target.

Reviewer #1 (Public Review):

Summary:

In this manuscript, the authors employed direct RNA sequencing with nanopores, enhanced by 5' end adaptor ligation, to comprehensively interrogate the human transcriptome at single-molecule and nucleotide resolution. They conclude that cellular stress induces prevalent 5' end RNA decay that is coupled to translation and ribosome occupancy. Contrary to the literature, they found that, unlike typical RNA decay models in normal conditions, stress-induced RNA decay is dependent on XRN1 but does not depend on the removal of the poly(A) tail. The findings presented are interesting but a substantial amount of work is needed to fully establish these paradigm-shifting findings.

Strengths:

These are paradigm-shifting observations using cutting-edge technologies.

Weaknesses:

The conclusions do not appear to be fully supported by the data presented.

Reviewer #2 (Public Review):

In the manuscript "Full-length direct RNA sequencing uncovers stress-granule dependent RNA decay upon cellular stress", Dar, Malla, and colleagues use direct RNA sequencing on nanopores to characterize the transcriptome after arsenite and oxidative stress. They observe a population of transcripts that are shortened during stress. The authors hypothesize that this shortening is mediated by the 5'-3' exonuclease XRN1, as XRN1 knockdown results in longer transcripts. Interestingly, the authors do not observe a polyA-tail shortening, which is typically thought to precede decapping and XRN1-mediated transcript decay. Finally, the authors use G3BP1 knockout cells to demonstrate that stress granule formation is required for the observed transcript shortening.

The manuscript contains intriguing findings of interest to the mRNA decay community. That said, it appears that the authors at times overinterpret the data they get from a handful of direct RNA sequencing experiments. To bolster some of the statements additional experiments might be desirable.

A selection of comments:

(1) Considering that the authors compare the effects of stress, stress granule formation, and XRN1 loss on transcriptome profiles, it would be desirable to use a single-cell system (and validated in a few more). Most of the direct RNAseq is performed in HeLa cells, but the experiments showing that stress granule formation is required come from U2OS cells, while short RNAseq data showing loss of coverage on mRNA 5'ends is reanalyzed from HEK293 cells. It may be plausible that the same pathways operate in all those cells, but it is not rigorously demonstrated.

(2) An interesting finding of the manuscript is that polyA tail shortening is not observed prior to transcript shortening. The authors would need to demonstrate that their approach is capable of detecting shortened polyA tails. Using polyA purified RNA to look at the status of polyA tail length may not be ideal (as avidity to oligodT beads may increase with polyA tail length and therefore the authors bias themselves to longer tails anyway). At the very least, the use of positive controls would be desirable; e.g. knockdown of CCR4/NOT.

(3) The authors use a strategy of ligating an adapter to 5' phosphorylated RNA (presumably the breakdown fragments) to be able to distinguish true mRNA fragments from artifacts of abortive nanopore sequencing. This is a fantastic approach to curating a clean dataset. Unfortunately, the authors don't appear to go through with discarding fragments that are not adapter-ligated (presumably to increase the depth of analysis; they do offer Figure 1e that shows similar changes in transcript length for fragments with adapter, compared to Figure 1d). It would be good to know how many reads in total had the adapter. Furthermore, it would be good to know what percentage of reads without adapters are products of abortive sequencing. What percentage of reads had 5'OH ends (could be answered by ligating a different adapter to kinase-treated transcripts). More read curation would also be desirable when building the metagene analysis - why do the authors include every 3'end of sequenced reads (their RNA purification scheme requires a polyA tail, so non-polyadenylated fragments are recovered in a non-quantitative manner and should be discarded).

(4) The authors should come to a clear conclusion about what "transcript shortening" means. Is it exonucleolytic shortening from the 5'end? They cannot say much about the 3'ends anyway (see above). Or are we talking about endonucleolytic cuts leaving 5'P that then can be attached by XRN1 (again, what is the ratio of 5'P and 5'OH fragments; also, what is the ratio of shortened to full-length RNA)?

(5) The authors should clearly explain how they think the transcript shortening comes about. They claim it does not need polyA shortening, but then do not explain where the XRN1 substrate comes from. Does their effect require decapping? Or endonucleolytic attacks?

(6) XRN1 KD results in lengthened transcripts. That is not surprising as XRN1 is an exonuclease - and XRN1 does not merely rescue arsenite stress-mediated transcript shortening, but results in a dramatic transcript lengthening.

Reviewer #3 (Public Review):

The work by Dar et al. examines RNA metabolism under cellular stress, focusing on stress-granule-dependent RNA decay. It employs direct RNA sequencing with a Nanopore-based method, revealing that cellular stress induces prevalent 5' end RNA decay that is coupled to translation and ribosome occupancy but is independent of the shortening of the poly(A) tail. This decay, however, is dependent on XRN1 and enriched in the stress granule transcriptome. Notably, inhibiting stress granule formation in G3BP1/2-null cells restores the RNA length to the same level as wild-type. It suppresses stress-induced decay, identifying RNA decay as a critical determinant of RNA metabolism during cellular stress and highlighting its dependence on stress-granule formation.

This is an exciting and novel discovery. I am not an expert in sequencing technologies or sequencing data analysis, so I will limit my comments purely to biology and not technical points. The PI is a leader in applying innovative sequencing methods to studying mRNA decay.

One aspect that appeared overlooked is that poly(A) tail shortening per se does lead to decapping. It is shortening below a certain threshold of 8-10 As that triggers decapping. Therefore, I found the conclusion that poly(A) tail shortening is not required for stress-induced decay to be somewhat premature. For a robust test of this hypothesis, the authors should consider performing their analysis in conditions where CNOT7/8 is knocked down with siRNA.

Similarly, as XRN1 requires decapping to take place, it necessitates the experiment where a dominant-negative DCP2 mutant is over-expressed.

Are G3BP1/2 stress granules required for stress-induced decay or simply sites for storage? This part seems unclear. A very worthwhile test here would be to assess in XRN1-null background.

Finally, the authors speculate that the mechanism of stress-induced decay may have evolved to relieve translational load during stress. But why degrade the 5' end when removing the cap may be sufficient? This returns to the question of assessing the role of decapping in this mechanism.

Reviewer #1 (Public Review):

In this study Cacho-Navas et al. describes the role of ICAM-1 expressed on the apical membrane of bile canaliculi and its function to control the homeostasis of the bile canaliculi (BCs). This is a previously unrecognized function of this protein in hepatocytes. The same authors have previously shown that basolateral ICAM-1 plays a role in controlling lymphocyte adhesion to hepatocytes during inflammation and that this interaction is responsible on the loss of polarity of hepatocytes during the disease.<br /> In this new study they show that ICAM-1, is mainly localized in the apical domain of the BC and in association with EBP-50, comunicates with the subapical acto-myosin ring to regulate the size and morphology of the BC.<br /> In this study they used the well-known immortal cell line of liver cells (HepG2) in which they knocked-out ICAM-1 using CRISPR-Cas9 editing and hepatic organoid derived from WT and ICAM-1-KO mice. alternating knocking-out as well as rescue experiments they show that in the absence of apical ICAM-1, the BC dimension and shape are altered.<br /> The conclusions of the study are sufficiently supported by the data.

Comments on revision:

The authors have addressed most of the reviewer's comments in the re-submission, however the use of the organoids as a model to study bile canaliculi is still not convincing.<br /> The HA-4 staining and the space wehere CFDA is secreted does not overlap considering the nuclei position in the middle z-stack section. Also, the interdigitations between cells identified by EM do not form an enclosed space as we should expect for a bile canaliculi.<br /> I understand that other studies have used these organoids to show some hepatocytic functions but at the same time none has characterized before the formation of bile canaliculi as suggested in this study. Therefore a characterization showing the expression of specific markers (i.e mrp2, bsep) should be provided to support this claim.<br /> I would suggest the authors to carefully read the helpful review by Marsee et al., Cell Stem Cell 2021 that clearly and carefully address the classification and validation of liver organoids from experts in the field.

Reviewer #3 (Public Review):

This study from the Flores group aims at understanding neuronal circuit changes during adolescence which is an ill-defined, transitional period involving dramatic changes in behavior and anatomy. They focus on DA innervation of the prefrontal cortex, and their interaction with the guidance cue Netrin-1. They propose DA axons in the PFC increase in the postnatal period, and their density is reduced in a Netrin 1 knockdown, suggesting that Netrin abets the development of this mesocortical pathway. In such mice impulsivity gauged by a go-no go task is reduced. They then provide some evidence that Unc5c is developmentally regulated in DA axons. Finally they use an interesting hamster model, to study the effect of light hours on mesocortical innervation, and make some interesting observations about the timing of innervation and Unc5c expression, and the fact that females housed in winter day length conditions display an accelerated innervation of the prefrontal cortex.

Comments on the revision. Several points were addressed; some remain to be addressed.

4. It's not clear to me that TH doesnt stain noradrenergic axons in the PFC. See Islam and Blaess, 2021, and references therein.

6. The Netrin knockdown data provided is from a previous study/samples.

8. While the authors make the argument that the behavior is linked to DA, they still haven't formally tested it, in my opinion.

13. Fig 3, UNc 5c levels are not yet quantified. Furthermore, I agree with the previous reviewer that Unc5C knockdown would corroborate key aspects of the model.

New - Developmental trajectory of prefrontal TH-positive axons from early adolescence to adulthood is similar in male and female rats, (Willing Juraska et al., 2017). This needs discussion.

Reviewer #1 (Public Review):

In this study, Hoops et al. showed that Netrin-1 and UNC5c can guide dopaminergic innervation from nucleus accumbens to cortex during adolescence in rodent models. They found that these dopamine axons project to the prefrontal cortex in a Netrin-1 dependent manner and knocking down Netrin-1 disrupted motor and learning behaviors in mice. Furthermore, the authors used hamsters, a seasonal model that is affected by the length of daylight, to demonstrate that the guidance of dopamine axons is mediated by the environmental factor such as daytime length and in sex dependent manner.

Regarding the cell type specificity of Netrin-1 expression, the authors began by stating "this question is not the focus of the study and we consider it irrelevant to the main issue we are addressing, which is where in the forebrain regions we examined Netrin-1+ cells are present." This statement contradicts the exact issue regarding the specificity issue I raised. They then went on to show the RNAscope data for Netriin-1 in Figure 2, which showed Netrin-1 mRNA was actually expressed quite ubiquitously in anterior cingulate cortex, dorsopeduncular cortex, infralimbic cortex, prelimbic cortex, etc. In addition, contrary to the authors' statement that Netrin-1 is a "secreted protein", the confocal images in Figure 1 in the rebuttal letter actually show Netrin-1 present in "granule-like" organelles inside the cytoplasm of neurons. Finally, the authors presented Figure 7 to indicate the location where virus expressing Netrin-1 shRNA might be located. Again, the brain region targeted was quite focal and most likely did not cover all the Netrin-1+ brain regions in Figure 2. Collectively, these results raised more questions regarding the specificity of Netrin-1 expression in brain regions that are behaviorally relevant to this study.

With respect to the effectiveness of Netrin-1 knockdown in the animals in this study, the authors cited data in HEK293 cells (Figure 5), which did not include any statistics, and previously published in vivo data in a separate, independent study (Figure 6). They do not provide any data regarding the effectiveness of Netrin-1 knockdown in THIS study.

Similar concerns regarding UNC5C knockdown (points #6, #7, and #8) were not adequately addressed.

In brief, while this study provides a potential role of Netrin-1-UNC5C in target innervation of dopaminergic neurons and its behavioral output in risk-taking, the data lack sufficient evidence to firmly establish the cause-effect relationship.

Reviewer #2 (Public Review):

In this manuscript, Hoops et al., using two different model systems, identified key developmental changes in Netrin-1 and UNC5C signaling that correspond to behavioral changes and are sensitive to environmental factors that affect the timing of development. They found that Netrin-1 expression is highest in regions of the striatum and cortex where TH+ axons are travelling, and that knocking down Netrin-1 reduces TH+ varicosities in mPFC and reduces impulsive behaviors in a Go-No-Go test. Further, they show that the onset of Unc5 expression is sexually dimorphic in mice, and that in Siberian hamsters, environmental effects on development are also sexually dimorophic. This study addresses an important question using approaches that link molecular, circuit and behavioral changes. Understanding developmental trajectories of adolescence, and how they can be impacted by environmental factors, is an understudied area of neuroscience that is highly relevant to understanding the onset of mental health disorders. I appreciated the inclusion of replication cohorts within the study.

Reviewer #2 (Public Review):

Summary:

In this work, Song et al. propose a locus-based framework for performing GWAS and related downstream analyses including finemapping and polygenic risk score (PRS) estimation. GWAS are not sufficiently powered to detect phenotype associations with low-frequency variants. To overcome this limitation, the manuscript proposes a method to aggregate variant impacts on chromatin and transcription across a 4096 base pair (bp) loci in the form of a haplotype function score (HFS). At each locus, an association is computed between the HFS and trait. Computing associations at the level of imputed functional genomic scores enables integration of information across variants spanning the allele frequency spectrum and bolster the power of GWAS.

The HFS for each locus is derived from a sequence-based predictive model - Sei. Sei predicts 21,907 chromatin and TF binding tracks, which can be projected onto 40 pre-defined sequence classes ( representing promoters, enhancers etc.). For each 4096 bp haplotype in their UKB cohort, the proposed method uses the Sei sequence class scores to derive the haplotype function score (HFS). The authors apply their method to 14 polygenic traits, identifying ~16,500 HFS-trait associations. They finemap these trait-associated loci with SuSie, as well perform target gene/pathway discovery and PRS estimation.

Strengths:

Sequence-based deep learning predictors of chromatin status and TF binding have become increasingly accurate over the past few years. Imputing aggregated variant impact using Sei, and then performing an HFS-trait association is therefore an interesting approach to bolster power in GWAS discovery. The manuscript demonstrates that region-level associations can be identified at the level of an aggregated functional score using sequence-based deep learning models. The finemapping and pathway identification analyses suggest that HFS-based associations identify relevant causal pathways and genes from an association study. Identifying associations at the level of functional genomics increases portability of PRSs across populations. Imputing functional genomic predictions using a sequence-based deep learning model does not suffer from the limitation of TWAS where gene expression is imputed from a limited size reference panel such as GTEx and is an interesting direction to bolster discovery power.

However, a few limitations to this method in its current form are:

(1) HFS-based association is going to miss coding variation as well as noncoding regulatory variants such as splicing variants/polyadenylation variants which are not modeled by Sei. This will lead to false negatives in the HFS-based association and additionally false negatives + associated false positives in the finemapping. Going forward, it'll therefore be important to characterize how this influences the genome-wide finemapping.

(2) Sei predicts chromatin status / ChIP-seq peaks in the center of a 4kb region. It is thus not clear therefore whether the functional effects of variants not in the center of the 4kb region would be captured in a single Sei score. It also remains unclear how much the choice of window affects the association tests / finemapping.

(3) There are going to be cases where there's an association driven by a variant that is correlated with a Sei prediction in a neighboring window. These would represent false positives for the method, it would be useful to identify or characterize these cases.

Minor Concerns:<br /> (1) Sequence based deep learning model predictions can be miscalibrated for insertions and deletions (INDELs) as compared to SNPs. It'll be important to note that model INDEL scores may not be calibrated, which might also lead to false positives / false negatives in the finemapping.

Reviewer #1 (Public Review):

Summary:

In this paper, Song, Shi, and Lin use an existing deep learning-based sequence model to derive a score for each haplotype within a genomic region, and then perform association tests between these scores and phenotypes of interest. The authors then perform some downstream analyses (fine-mapping, various enrichment analyses, building polygenic scores) to ensure that these associations are meaningful. The authors find that their approach allows them to find additional associations, the associations have biologically interpretable enrichments in terms of tissues and pathways, and can slightly improve polygenic scores when combined with standard SNP-based PRS.

Strengths:

- I found the central idea of the paper to be conceptually straightforward and an appealing way to use the power of sequence models in an association testing framework.

- The findings are largely biologically interpretable, and it seems like this could be a promising approach to boost power for some downstream applications.

Weaknesses:

- While not a weakness of the manuscript, the proposed method is computationally intensive.

Reviewer #2 (Public Review):

In this manuscript, Yao et al. present a series of experiments aiming at generating a cellular atlas of the human hippocampus across aging, and how it may be affected by injury, in particular, stroke. Although the aim of the study is interesting and relevant for a larger audience, due to the ongoing controversy around the existence of adult hippocampal neurogenesis in humans, a number or technical weaknesses result in a poor support for many of the conclusions made from the results of these experiments.<br /> In particular, a recent meta analysis of five previous studies applying similar techniques to human samples has identified different aspects of sample size as main determinants of the statistical power needed to make significant conclusions. Some of this aspects are the number of nuclei sequenced and subject stratification. These two aspects are of concern in Yao's study. First, the number of sequenced nuclei is lower than the calculated numbers of nuclei required for detecting rare cell types. However, Yao et al. report succeeding in detecting rare populations, including several types of neural stem cells in different proliferation states, which have been demonstrated to be extremely scarce by previous studies. It would be very interesting to read how the authors interpret these differences. Secondly, the number of donors included in some of the groups is extremely low (n=1) and the miscellaneous information provided about the donors is practically inexistent. As individual factors such as chronic conditions, medication, lifestyle parameters, etc... are considered determinant for the variability of adult hippocampal neurogenesis levels across individuals, this represents a series limitation of the current study. Overall, several technical weaknesses severely limit the relevance of this study and the ability of the authors to achieve their experimental aims.

After a first review round, the manuscript is still lacking a clear discussion of its several technical limitations, which will help the audience to grasp the relevance of the findings. In particular, detailed information about individual patients health status and relevant lifestyle parameters that may have affected it is lacking. The authors make the point themselves that the discrepancies among studies might be caused by health state differences across hippocampi, which subsequently lead to different degrees of hippocampal neurogenesis." So, even in the authors own interpretation this is a serious limitation to the manuscript, that however out of the authors control, impacts on the quality of their findings.

Reviewer #1 (Public Review):

In this manuscript, Yao et al. explored the transcriptomic characteristics of neural stem cells (NSCs) in the human hippocampus and their changes under different conditions using single-nucleus RNA sequencing (snRNA-seq). They generated single-nucleus transcriptomic profiles of human hippocampal cells from neonatal, adult, and aging individuals, as well as from stroke patients. They focused on the cell groups related to neurogenesis, such as neural stem cells and their progeny. They revealed genes enriched in different NSC states and performed trajectory analysis to trace the transitions among NSC states and towards astroglial and neuronal lineages in silico. They also examined how NSCs are affected by aging and injury using their datasets and found differences in NSC numbers and gene expression patterns across age groups and injury conditions. One major issue of the manuscript is questionable cell type identification. For example, more than 50% of the cells in the astroglial lineage clusters are NSCs, which is extremely high and inconsistent with classic histology studies.

While the authors have made efforts to address previous critics, major concerns have not been adequately addressed, including a very limited sample size and patient information. In addition, some analytical approaches are still questionable and the authors acknowledge some issues they cannot address. Therefore, while the topic is interesting, some results are preliminary and some conclusions are not fully supported by the data presented.

Reviewer #2 (Public Review):

Summary:

In this study, Ghafari et al. explored the correlation between hemispheric asymmetry in the volume of various subcortical regions and lateralization of posterior alpha band oscillations in a spatial attention task with varying cognitive demands. To this end, they combined structural MRI and task MEG to investigate the relationship between hemispheric differences in volume of basal ganglia, thalamus, hippocampus and amygdala and hemisphere-specific modulation of alpha-band power. The authors report that differences in the thalamus, caudate nucleus and globus pallidus volume are linked to the attention-related changes in alpha band oscillations with differential correlations for different regions in different conditions of the design (depending on the salience of the distractor and/or the target).

The manuscript contributes to filling an important gap in current research on attention allocation which commonly focuses exclusively on cortical structures. Because it is not possible to reliably measure subcortical activity with non-invasive electrophysiological methods, they correlate volumetric measurements of the relevant subcortical regions with cortical measurements of alpha band power. Specifically, they build on their own previous finding showing a correlation between hemispheric asymmetry of basal ganglia volumes and alpha lateralization by assessing a task without an explicit reward component. Furthermore, the authors use differences in saliency and perceptual load to disentangle the individual contributions of the subcortical regions. These remain somewhat hard to interpret, given their post hoc nature, and the lack of statistical power to compare task demand effects directly, but the results raise interesting new hypotheses for future work.

Reviewer #1 (Public Review):

Summary:

The authors re-analysed the data of a previous study in order to investigate the relation between asymmetries of subcortical brain structures and the hemispheric lateralization of alpha oscillations during visual spatial attention. The visual spatial attention task crossed the factors of target load and distractor salience, which made it possible to also test the specificity of the relation of subcortical asymmetries to lateralized alpha oscillations for specific attentional load conditions. Asymmetry of globus pallidus, caudate nucleus, and thalamus explained inter-individual differences in attentional alpha modulation in the left versus right hemisphere. Multivariate regression analysis revealed that the explanatory potential of these regions' asymmetries varies as a function of target load and distractor salience.

In the revision of the article, the authors addressed my concerns.

However, my concern with regard to the statistical analysis of the specificity of certain subcortical regions predicting HLM seems to be not fully addressed. The authors added an additional statistical analysis for "testing the null hypothesis that a given regressor does not impact all dependent variables". To my understanding, this is a somewhat unusual definition of a null hypothesis. Typically, the null hypothesis is the hypothesis of no effect, meaning here it should state that the effect is the same across predictors.

In the new statistical analysis, the authors seem to take non-significant results (p>.05) as evidence for the specificity of subcortical regions in predicting HLM. The rationale of this statistical approach is difficult to follow and was somewhat unclear to me.

A much simpler and more straight-forward approach would be to contrast beta-estimates per subcortical region between experimental conditions. For instance, if the beta estimates in the thalamus for the "low-load target, non-salient distractor" condition would be significantly larger than the beta estimates for the other conditions, this would speak to specificity.

Reviewer #2 (Public Review):

Summary:

This study investigates the neural substrates of syntax variation in Bengalese finch song. Here, the authors tested the effects of bilateral lesions of mMAN, a brain area with inputs to HVC, a premotor area required for song production. Lesions in mMAN induce variability in syntactic elements of song specifically through increased transition entropy, variability within stereotyped song elements known as chunks and increases in the repeat number of individual syllables. These results suggest that mMAN projections to HVC contribute to multiple aspects of song syntax in the Bengalese finch. Overall the experiments are well-designed, the analysis excellent, and the results are of high interest.

Strengths:

The study identifies a novel role for mMAN, medial magnocellular nucleus of the anterior nidopallium, in the control of syntactic variation within adult Bengalese finch song. This is of particular interest as multiple studies previously demonstrated that mMAN lesions to do not effect song structure in zebra finches. The study undertakes a thorough analysis to characterise specific aspects of variability within the song of lesioned animals. The conclusions are well supported by the data.

Reviewer #1 (Public Review):

Summary:

Songbirds provide a tractable system to examine neural mechanisms of sequence generation and variability. In past work, the projection from LMAN to RA (output of the anterior forebrain pathway) was shown to be critical for driving vocal variability during babbling, learning, and adulthood. LMAN is immediately adjacent to MMAN, which projects to HVC. MMAN is less well understood but, anatomically, appears to resemble LMAN in that it is the cortical output of a BG-thalamocortical loop. Because it projects to HVC, a major sequence generator for both syllable phonology and sequence, a strong prediction would be that MMAN drives sequence variability in the same way that LMAN drives phonological variability. This hypothesis predicts that MMAN lesions in a Bengalese finch would reduce sequence variability. Here, the authors test this hypothesis. They provide a surprising and important result that is well motivated and well analyzed: MMAN lesions increase sequence variability - this is exactly the opposite result from what would be predicted based on the functions of LMAN.

Strengths:

(1) A very important and surprising result shows that lesions of a frontal projection from MMAN to HVC, a sequence generator for birdsong, increase syntactical variability.

(2) The choice of Bengalese finches, which have complex transition structures, to examine the mechanisms of sequence generation, enabled this important discovery.

(3) The idea that frontal outputs of BG-cortical loops can generate vocal variability comes from lesions/inactivations of a parallel pathway from LMAN to RA. The difference between MMAN and LMAN functions is striking and important.

Reviewer #2 (Public Review):

Summary:

In this manuscript, L&S investigates the important general question of how humans achieve invariant behavior over stimuli belonging to one category given the widely varying input representation of those stimuli and more specifically, how they do that in arbitrary abstract domains. The authors start with the hypothesis that this is achieved by invariance transformations that observers use for interpreting different entries and furthermore, that these transformations in an arbitrary domain emerge with the help of the transformations (e. g. translation, rotation) within the spatial domain by using those as "scaffolding" during transformation learning. To provide the missing evidence for this hypothesis, L&S used behavioral category learning studies within and across the spatial, auditory and visual domains, where rotated and translated 4-element token sequences had to be learned to categorize and then the learned transformation had to applied in new feature dimensions within the given domain. Through single- and multiple-day supervised training and unsupervised tests, L&S demonstrated by standard computational analyses that in such setups, space and spatial transformations can, indeed, help with developing and using appropriate rotational mapping whereas the visual domain cannot fulfill such a scaffolding role.

Strengths:

The overall problem definition and the context of spatial mapping-driven solution to the problem is timely. The general design of testing the scaffolding effect across different domains is more advanced than any previous attempts clarifying the relevance of spatial coding to any other type of representational codes. Once the formulation of the general problem in a specific scientific framework is done, the following steps are clearly and logically defined and executed. The obtained results are well interpretable, and they could serve as a good steppingstone for deeper investigations. The analytical tools used for the interpretations are adequate. The paper is relatively clearly written.

Weaknesses:

Some additional effort to clarify the exact contribution of the paper, the link between analyses and the claims of the paper and its link to previous proposals would be necessary to better assess the significance of the results and the true nature of the proposed mechanism of abstract generalization.

(1) Insufficient conceptual setup: The original theoretical proposal (the Tolman-Eichenbaum-Machine, Whittington et al., Cell 2020) that L&S relate their work proposes that just as in the case of memory for spatial navigation, humans and animal create their flexible relational memory system of any abstract representation by a conjunction code that combines on the one hand, sensory representation and on the other hand, a general structural representation or relational transformation. The TEM also suggest that the structural representation could contain any graph-interpretable spatial relations, albeit in their demonstration 2D neighbor relations were used. The goal of L&S's paper is to provide behavioral evidence for this suggestion by showing that humans use representational codes that are invariant to relational transformations of non-spatial abstract stimuli and moreover, that humans obtain these invariances by developing invariance transformers with the help of available spatial transformers. To obtain such evidence, L&S use the rotational transformation. However, the actual procedure they used actually solved an alternative task: instead of interrogating how humans develop generalizations in abstract spaces, they demonstrated that if one defines rotation in an abstract feature space embedded in visual or auditory modality that is similar to the 2D space (i.e. has two independent dimensions that are clearly segregable and continuous), humans cannot learn to apply rotation of 4-piece temporal sequences in those spaces while they can do it in 2D space, and with co-associating a one-to-one mapping between locations in those feature spaces with locations in the 2D space an appropriate shaping mapping training will lead to successful application of rotation in the given task (and in some other feature spaces in the given domain). While this is an interesting and challenging demonstration, it does not shed light on how humans learn and generalize only that humans CAN do learning and generalization in this, highly constrained scenario. This result is a demonstration of how a stepwise learning regiment can make use of one structure for mapping a complex input into a desired output. The results neither clarify how generalizations would develop in abstract spaces nor the question if this generalization uses transformations developed in the abstract space. The specific training procedure ensures success in the presented experiments but the availability and feasibility of an equivalent procedure in natural setting is a crucial part of validating the original claim and that has not been done in the paper.

(2) Missing controls: The asymptotic performance in Exp 1 after training in the three tasks was quite different in the three tasks (intercepts 2.9, 1.9, 1.6 for spatial, visual and auditory, respectively; p. 5. para. 1, Fig 2BFJ). It seems that the statement "However, or main question was how participants would generalise learning to novel, rotated exemplars of the same concept." assumes that learning and generalization are independent. Wouldn't it be possible, though, that the level of generalization depends on the level of acquiring a good representation of the "concept" and after obtaining an adequate level of this knowledge, generalization would kick in without scaffolding? If so, a missing control is to equate the levels of asymptotic learning and see whether there is a significant difference in generalization. A related issue is that we have no information what kind of learning in the three different domains were performed, albeit we probably suspect that in space the 2D representation was dominant while in the auditory and visual domains not so much. Thus, a second missing piece of evidence is the model fitting results of the ⦰ condition that would show which way the original sequences were encoded (similar to Fig 2 CGK and DHL). If the reason for lower performance is not individual stimulus difficulty but the natural tendency to encode the given stimulus type by a combo of random + 1D strategy that would clarify that the result of the cross-training is, indeed, transferring the 2D-mapping strategy.

Reviewer #1 (Public Review):

Summary:

This manuscript reports a series of experiments examining category learning and subsequent generalization of stimulus representations across spatial and nonspatial domains. In Experiment 1, participants were first trained to make category judgments about sequences of stimuli presented either in nonspatial auditory or visual modalities (with feature values drawn from a two-dimensional feature manifold, e.g., pitch vs timbre), or in a spatial modality (with feature values defined by positions in physical space, e.g., Cartesian x and y coordinates). A subsequent test phase assessed category judgments for 'rotated' exemplars of these stimuli: i.e., versions in which the transition vectors are rotated in the same feature space used during training (near transfer) or in a different feature space belonging to the same domain (far transfer). Findings demonstrate clearly that representations developed for the spatial domain allow for representational generalization, whereas this pattern is not observed for the nonspatial domains that are tested. Subsequent experiments demonstrate that if participants are first pre-trained to map nonspatial auditory/visual features to spatial locations, then rotational generalization is facilitated even for these nonspatial domains. It is argued that these findings are consistent with the idea that spatial representations form a generalized substrate for cognition: that space can act as a scaffold for learning abstract nonspatial concepts.

Strengths:

I enjoyed reading this manuscript, which is extremely well written and well presented. The writing is clear and concise throughout, and the figures do a great job of highlighting the key concepts. The issue of generalization is a core topic in neuroscience and psychology, relevant across a wide range of areas, and the findings will be of interest to researchers across areas in perception and cognitive science. It's also excellent to see that the hypotheses, methods and analyses were pre-registered.

The experiments that have been run are ingenious and thoughtful; I particularly liked the use of stimulus structures that allow for disentangling of one-dimensional and two-dimensional response patterns. The studies are also well powered for detecting effects of interest. The model-based statistical analyses are thorough and appropriate throughout (and it's good to see model recovery analysis too). The findings themselves are clear-cut: I have little doubt about the robustness and replicability of these data.

Weaknesses:

In my original review I raised a concern related to a potential alternative interpretation of the findings: the idea that participants have substantial experience of representing space in terms of multiple, independent, and separable dimensions, whereas this may not be the case for the visual and auditory stimuli used here. As I noted in that prior review, on this view "the impact of spatial pre-training and (particularly) mapping is simply to highlight to participants that the auditory / visual stimuli comprise two separable (and independent) dimensions."

In addressing this point, the authors note that performance in the visual/auditory "mapping" task in Experiments 2c and 3c suggests that most participants were paying attention to both dimensions of auditory and visual stimuli. I agree that seems to have been the case. But there is a difference between making use of information from both dimensions, and realizing that ***the two dimensions are separable and independent*** (which is what is required for rotational generalization in this task).

As an analogy, suppose I have a task where participants have to map a pillow and a shuttlecock to category A, and a surfboard and a bicycle to category B. A participant could learn to do this just by memorizing the correct response for each item considered as a "whole thing". Or they could realize that the items contain component information, learning that "things with feathers" belong in category A, and "things that can carry people" go in category B. Performance may be the same in both cases, but the underlying process is quite different.

The "attention to dimensions" account that I advanced in my previous review was referring to something more like the latter (feathers/vehicle) case: that spatial pre-training helps people to understand that items can be decomposed into separable pieces of information. Above-chance performance in the visual-auditory mapping task does not (necessarily) demonstrate this ability because it could reflect memorization of "whole" stimuli rather than reflecting decomposition into separable component parts. I agree that it does at least show that participants were paying attention to and making use of information from both dimensions when making their mapping decisions; it's just that they may not have *realized* that they were using information from two separable dimensions.

Reviewer #1 (Public Review):

Tu et al investigated how LFPs recorded simultaneously with rsfMRI explain the spatiotemporal patterns of functional connectivity in sedated and awake rats. They find that connectivity maps generated from gamma band LFPs (from either area) explain very well the spatial correlations observed in rsfMRI signals, but that the temporal variance in rsfMRI data is more poorly explained by the same LFP signals. The authors excluded the effects of sedation in this effect by investigating rats in the awake state (a remarkable feat in the MRI scanner), where the findings generally replicate. The authors also performed a series of tests to assess multiple factors (including noise, outliers, and nonlinearity of the data) in their analysis.

This apparent paradox is then explained by a hypothetical model in which LFPs and neurovascular coupling are generated in some sense "in parallel" by different neuron types, some of which drive LFPs and are measured by ePhys, while others (nNOS, etc.) have an important role in neurovascular coupling but are less visible in Ephys data. Hence the discrepancy is explained by the spatial similarity of neural activity but the more "selective" LFPs picked up by Ephys account for the different temporal aspects observed.

This is a deep, outstanding study that harnesses multidisciplinary approaches (fMRI and ephys) for observing brain activity. The results are strongly supported by the comprehensive analyses done by the authors, which ruled out many potential sources for the observed findings. The study's impact is expected to be very large.

There are very few weaknesses in the work, but I'd point out that the 1-second temporal resolution may have masked significant temporal correlations between LFPs and spontaneous activity, for instance, as shown by Cabral et al Nature Communications 2023, and even in earlier QPP work from the Keilholz Lab. The synchronization of the LFPs may correlate more with one of these modes than the total signal. Perhaps a kind of "dynamic connectivity" analysis on the authors' data could test whether LFPs correlate better with the activity at specific intervals. However, this could purely be discussed and left for future work, in my opinion.

Reviewer #2 (Public Review):

The authors address a question that is interesting and important to the sub-field of rsfMRI that examines electrophysiological correlates of rsfMRI. That is, while electrophysiology-produced correlation maps often appear similar to correlation maps produced from BOLD alone (as has been shown in many papers) is this actually coming from the same source of variance, or independent but spatially-correlated sources of variance? To address this, the authors recorded LFP signals in 2 areas (M1 and ACC) and compared the maps produced by correlating BOLD with them to maps produced by BOLD-BOLD correlations. They then attempt to remove various sources of variance and see the results.

The basic concept of the research is sound, though primarily of interest to the subset of rsfMRI researchers who use simultaneous electrophysiology. However, there are major problems in the writing, and also a major methodological problem.

Major problems with writing:

(1) There is substantial literature on rats on site-specific LFP recording compared to rsfMRI, and much of it already examined removing part of the LFP and examining rsfMRI, or vice versa. The authors do not cover it and consider their work on signal removal more novel than it is.

(2) The conclusion of the existence of an "electrophysiology-invisible signal" is far too broad considering the limited scope of this study. There are many factors that can be extracted from LFP that are not used in this study (envelope, phase, infraslow frequencies under 0.1Hz, estimated MUA, etc.) and there are many ways of comparing it to the rsfMRI data that are not done in this study (rank correlation, transformation prior to comparison, clustering prior to comparison, etc.). The one non-linear method used, mutual information, is low sensitivity and does not cover every possible nonlinear interaction. Mutual information is also dependent upon the number of bins selected in the data. Previous studies (see 1) have seen similar results where fMRI and LFP were not fully commensurate but did not need to draw such broad conclusions.

(3) The writing refers to the spatial extent of correlation with the LFP signal as "spatial variance." However, LFP was recorded from a very limited point and the variance in the correlation map does not necessarily reflect underlying electrophysiological spatial distributions (e.g. Yu et al. Nat Commun. 2023 Mar 24;14(1):1651.)

Major method problem:

(4) Correlating LFP to fMRI is correlating two biological signals, with unknown but presumably not uniform distributions. However, correlating CC results from correlation maps is comparing uniform distributions. This is not a fair comparison, especially considering that the noise added is also uniform as it was created with the rand() function in MATLAB.

Reviewer #1 (Public Review):

In this paper, the authors developed an image analysis pipeline to automatically identify individual ‎‎neurons within a population of fluorescently tagged neurons. This application is optimized to deal with ‎‎multi-cell analysis and builds on a previous software version, developed by the same team, to resolve ‎‎individual neurons from whole-brain imaging stacks. Using advanced statistical approaches and ‎‎several heuristics tailored for C. elegans anatomy, the method successfully identifies individual ‎‎neurons with a fairly high accuracy. Thus, while specific to C. elegans, this method can ‎become ‎instrumental for a variety of research directions such as in-vivo single-cell gene expression ‎analysis ‎and calcium-based neural activity studies.‎

Reviewer #2 (Public Review):

The authors succeed in generalizing the pre-alignment procedure for their cell identification method to allow it to work effectively on data with only small subsets of cells labeled. They convincingly show that their extension accurately identifies head angle, based on finding auto florescent tissue and looking for a symmetric l/r axis. Their demonstrated method works to allow the identification of a particular subset of neurons. Their approach should be a useful one for researchers wishing to identify subsets of head neurons in C. elegans, and the ideas might be useful elsewhere.

The authors also assess the relative usefulness of several atlases for making identity predictions. They attempt to give some additional general insights on what makes a good atlas, and clearly demonstrate the value of more data. Some insights seem less clear as available data do not allow for experiments that cleanly decouple: 1) the number of examples in the atlas; 2) the completeness of the atlas; and 3) the match in strain and imaging modality discussed. In the presented experiments the custom atlas, besides the strain and imaging modality congruence discussed is also the only complete atlas with more than one example. The main neuroPAL atlas is an imperfect stand-in since a significant fraction of cells could not be identified in these data sets, making it a 60/40 mix of Openworm and a hypothetical perfect neuroPAL comparison. The alternate neuroPal atlases shown in supplemental figure 4 are complete but provide only one point cloud.

It is striking that in the best available apples to apples match the single data set glr-1 atlas produces qualitatively better results than the single (complete) neuroPAL atlas. This is a clear performance advantage given the ground truth. This is as good an evaluation as is possible given current data however given the inexact nature of assigning ground truth identities I think it is difficult from results to tease out if this is due to strain, imaging conditions or systematically different identifications of cells from different sources.

The experiments do usefully explore the volume of data needed. Though generalization to other arbitrary cell subsets remains to be shown the insight is useful for future atlas building that for the specific (small) set of cells labeled in the experiments 5-10 examples is sufficient to build an accurate atlas.

Reviewer #1 (Public Review):

The authors show that concurrently presenting foreign words and their translations during sleep leads to the ability to semantically categorize the foreign words above chance. Specifically, this procedure was successful when stimuli were delivered during slow oscillation troughs as opposed to peaks, which has been the focus of many recent investigations into the learning & memory functions of sleep. Finally, further analyses showed that larger and more prototypical slow oscillation troughs led to better categorization performance, which offers hints to others on how to improve or predict the efficacy of this intervention.

Comments on the revised version:

I applaud the authors on a nice rebuttal. Many responses use solid arguments based on the existing literature, such as their response regarding the possibility that low-level acoustic characteristics explaining EEG differences between conditions. Their new analyses also clarify the paper. Additionally, I appreciate their labeling their more speculative claims as such. Below are my remaining thoughts:

Major point:

The largest remaining issue for me regards the term 'episodic'. Before I begin, I should say that I imagine the authors have thought considerably about this definition and may disagree with what I will say. That would be fine - it's their choice at this journal. My main point in writing this is to help them clarify their case further. R3 had a similar concern on the first round of review, and I imagine others holding the "traditional" view of episodic memory would be similarly skeptical. If the authors have a great rebuttal to these points, I imagine it will address others' concerns too.<br /> I believe I understand the authors' argument: I read the Henke (2010, Nature Reviews Neuroscience) piece years back with great interest and again now, and I've gone back to read their other papers cited in this manuscript. Again, I applaud the authors on producing a large collection of fascinating findings expanding knowledge of what can be accomplished via unconscious learning. That includes this paper! But I still disagree with the term 'episodic' for what is measured here. The authors state in the Methods section that they prompted participants to 'guess whether the presented pseudoword designates an animal, a tool, or a place'. IMHO, the main issue of using 'episodic' is the nature of the memory representation - 'guessing' does not ask participants anything about the source (the who-what-when-why-where) of the information (anything about an episode).<br /> Notably, it does seem to fit their own definition from Henke (2010). Rapid? I believe so - 4 trial-learning is fairly quick. Certainly, there are studies of supposed episodic memory that use a few rounds of learning the same stimuli (rather than single trial learning) and one can still get away with calling the nature of the memories 'episodic'. Flexible? I believe the authors mean that their task is flexible because participants learn a category exemplar during sleep (e.g., 'aryl'-'bird') but then only respond based on its category membership ('animal'?). If this is the case, I agree that the representations are flexible. Reliant on the 'episodic memory system' (lines 495-9)? Reasonably likely, given their prior findings (e.g., Züst et al., 2019). However, there is considerable data suggesting the hippocampus contributes to functions beyond episodic memory, including statistical learning (e.g., Schapiro et al., 2013, Current Biology), motor learning (e.g., Schendan et al., 2003, Neuron; Dohring et al., 2017, Cortex; Jacobacci et al., 2020, PNAS), attention (e.g., Aly & Turk-Browne, 2016, Cerebral Cortex), perception (e.g., Lee et al., 2012), and semantic memory (e.g., Cutler et al., 2019, Frontiers in Human Neuroscience). Therefore, given that the hippocampus contributes to other tasks too, saying the task is episodic in part because it likely relies on the hippocampus (the 'episodic memory system') is an incorrect reverse inference. But regardless of this concern, it seems true to me that the term fits 'episodic' according to Henke (2010).<br /> So, it seems I'm raising an issue with this entire way of defining memory. IMHO, the biggest issue is that there is no reason to assume the participant relies upon any source-related information in making their guess. There is room in the field for a new type of rapid, unconscious, flexible, hippocampal-dependent learning that does not need to align with the term, 'episodic', for it to be important and fascinating! The term, 'episodic', is convenient for a reason - namely, for labeling the behavioral output of what it measures, not the process that underlies it. The authors have continually made an excellent case for rapid, unconscious, flexible, hippocampal-dependent learning, and it would seem even more beneficial for the field for the authors to just call this its own thing.

A related point:<br /> - I see that the authors do not use 'episodic' in prior papers with similar tasks (e.g., Züst et al., 2019), and I am curious if anything changed in their thinking or why they use the term now. They can ignore this if they'd like, but it would perhaps give useful context.

Other points:<br /> IMHO, the issue of repeated tests is more legitimate than the authors suggest. They state in their response letter, "However, recent literature suggests that retrieval practice is only beneficial when corrective feedback is provided (Belardi et al., 2021; Metcalfe, 2017)." This is incorrect. While retrieval practice is often less effective without feedback, it can be effective without feedback if retrieval accuracy is high and if the experimenters later employ a long enough retention interval to witness long-term effects. This is clear in various papers (e.g., Roediger & Karpicke, 2006, Psychological Science; Karpicke & Roediger, 2008, Science) and there is a nice theoretical model explaining how these complex effects could arise (Halamish & Bjork, 2011, JEP:LMC; Kornell et al., 2011, JML). The authors do not heavily rely on this in their paper, but they could consider tempering their claims that it is 'unlikely' (line 509) that delayed retrieval was affected by the first retrieval.<br /> The authors claim that fast spindles are part of a speculative model underlying their learning effects (lines 605-6). However, they did not find any differential spindle effects in determining later performance, so they could consider keeping just points #1&2 or mentioning that spindles differ by condition but may not directly influence the learning effects here.

Reviewer #3 (Public Review):

This is a revision in response to the reviewer's comments. The authors provided new analyses and try to acknowledge limitations, overall doing a good job, but the interpretation still seems to me going above the available evidence, especially for the claim that it is episodic memory formation during sleep. I still believe the paper will be fairer in dropping this speculative part and omitting the word "episodic" from the title (like actually they did in the abstract). The argument of the authors is that they refer to a computational definition of episodic memory, which is to some extent valid, but I am afraid it is not the way it will be understood by most readers, and it will thus indirectly contribute to an erroneous (or at least, not substantiated) interpretation of the brain's sleeping capabilities.

My main concern is that I have not seen any proposal for a control condition allowing to exclude the alternative, simpler hypothesis that mere perceptual associations between two elements (foreign word and translation) have been created and stored during sleep (which, I repeat, is already in itself an interesting finding). The authors argue that it seems to them not an efficient processing, but this an opinion, not a demonstration.

Reviewer #1 (Public Review):

This manuscript from Clayton and co-authors, entitled "Mechanism of dimer selectivity and binding cooperativity of BRAF inhibitors", aims to clarify the molecular mechanism of BRAF dimer selectivity. Indeed, first-generation BRAF inhibitors, targeting monomeric BRAFV600E, are ineffective in treating resistant dimeric BRAF isoforms. Here, the authors employed molecular dynamics simulations to study the conformational dynamics of monomeric and dimeric BRAF, in the presence and absence of inhibitors. Multi-microsecond MD simulations showed an inward shift of the αC helix in the BRAFV600E mutant dimer. This helped in identifying a hydrogen bond between the inhibitors and the BRAF residue Glu501 as critical for dimer compatibility. The stability of the aforementioned interaction seems to be important to distinguish between dimer-selective and equipotent inhibitors.

The study is overall valuable and robust. The authors used the recently developed particle mesh Ewald constant pH molecular dynamics, a state-of-the-art method, to investigate the correct histidine protonation considering the dynamics of the protein. Then, multi-microsecond simulations showed differences in the flexibility of the αC helix and DFG motif. The dimerization restricts the αC position in the inward conformation, in agreement with the result that dimer-compatible inhibitors can stabilize the αC-in state. Noteworthy, the MD simulations were used to study the interactions between the inhibitors and the protein, suggesting a critical role for a hydrogen bond with Glu501. Finally, simulations of a mixed state of BRAF (one protomer bound to the inhibitor and the other apo) indicate that the ability to stabilize the inward αC state of the apo protomer could be at the basis of the positive cooperativity of PHI1.

One potential weakness in the manuscript is the lack of reported uncertainties related to the analyzed quantities. Providing this information would significantly enhance the clarity regarding the reliability of the analyses and the confidence in the claims presented.

Reviewer #2 (Public Review):

The authors employ molecular dynamics simulations to understand the selectivity of FDA-approved inhibitors within dimeric and monomeric BRAF species. Through these comprehensive simulations, they shed light on the selectivity of BRAF inhibitors by delineating the main structural changes occurring during dimerization and inhibitor action. Notably, they identify the two pivotal elements in this process: the movement and conformational changes involving the alpha-C helix and the formation of a hydrogen bond involving the Glu-501 residue. These findings find support in the analyses of various structures crystallized from dimers and co-crystallized monomers in the presence of inhibitors. The elucidation of this mechanism holds significant potential for advancing our understanding of kinase signaling and the development of future BRAF inhibitor drugs.

The authors employ a diverse array of computational techniques to characterize the binding sites and interactions between inhibitors and the active site of BRAF in both dimeric and monomeric forms. They combine traditional and advanced molecular dynamics simulation techniques such as CpHMD (all-atom continuous constant pH molecular dynamics) to provide mechanistic explanations. Additionally, the paper introduces methods for identifying and characterizing the formation of the hydrogen bond involving the Glu501 residue without the need for extensive molecular dynamics simulations. This approach facilitates the rapid identification of future BRAF inhibitor candidates.

The use of molecular dynamics yields crucial structural insights and outlines a mechanism to elucidate dimer selectivity and cooperativity in these systems. However, the authors could consider the adoption of free energy methods to estimate the values of hydrogen bond energies and hydrophobic interactions, thereby enhancing the depth of their analysis.

Reviewer #1 (Public Review):

Zhang et al. tackle the important topic of primate-specific structural features of the brain and the link with functional specialization. The authors explore and compare gyral peaks of the human and macaque cortex through non-invasive neuroimagery, using convincing techniques that have been previously validated elsewhere. They show that nearly 60% of the macaque peaks are shared with humans, and use a multi-modal parcellation scheme to describe the spatial distribution of shared and unique gyral peaks in both species.

The claim is made that shared peaks are mainly located in lower-order cortical areas whereas unique peaks are located in higher-order regions, however, no systematic comparison is made. The authors then show that shared peaks are more consistently found across individuals than unique peaks, and show a positive but small and non-significant correlation between cross-individual counts of the shared peaks of the human and the macaque i.e. the authors show a non-significant trend for shared peaks that are more consistently found across humans to be those that are also more found across macaques.

In order to identify if unique and shared peaks could be identified based on the structural features of the cortical regions containing them, the authors compared them with t-tests. A correction for multiple comparisons should be applied and t-values reported. Graph-theoretical measures were applied to functional connectivity datasets (resting-state fMRI) and compared between unique and shared peak regions for each species separately. Again the absence of multiple comparison correction and t-values make the results hard to interpret. The same comment applies to the analysis reporting that shared peaks are surrounded by a larger number of brain regions than unique peaks. Finally, the potentially extremely interesting results about differential human gene expression of shared and unique peaks regions are not systematically reported e.g. the 28 genes identified are not listed and the selection procedure of 7 genes is not fully reported.

The paper is well written and the methods used for data processing are very compelling i.e. the peak cluster extraction pipeline and cross-species registration.

Comments on revision:

The authors have convincingly addressed all my previous concerns such that, as the revised paper stands now, the presented results provide solid support for the conclusions of the authors. The revised paper is now of interest for a large part of the neuroscience community and specifically for those interested in primate-specific structural features of the brain and the link with functional specialization.

Reviewer #1 (Public Review):

SUMMARY:

Parkinson's disease (PD) and other synucleinopathies, including Parkinson's Disease Dementia (PDD), Dementia with Lewy Bodies (DLB), and Multiple System Atrophy (MSA), pose significant challenges for early diagnosis, as their clinical manifestations often emerge after substantial neurodegeneration has occurred. In this context, the Alpha-Synuclein Seeding Amplification Assay (SAA) has garnered considerable attention for its potential as a diagnostic tool, capable of detecting pathological forms of alpha-synuclein (αSyn) even before the onset of classical clinical symptoms and signs. The assay exploits αSyn's intrinsic property to convert healthy forms into pathological ones, subsequently amplifying these pathological forms for visualization. This study aims to investigate the efficacy of SAA in accurately identifying subtypes of synucleinopathies, including PD, PDD, DLB, and MSA. To achieve this, the results from the patient brain-derived αSyn SAA are compared with those obtained through conformational stability assays, immunolabeling, and electron microscopy. Study shows that brain-derived αSyn fibrils exhibit significant differences across various synucleinopathies in their conformation, biochemical profile and phosphorylation patterns. Importantly, the SAA method appears to fall short in capturing these distinctions.

The study's findings are highly relevant given the rapidly advancing landscape of utilizing the SAA for the diagnosis and differentiation of various forms of PD and synucleinopathies using patient biofluids. It is somewhat surprising that the authors primarily characterize SAA as a research tool without delving into its potential as a biomarker detection assay, especially in the context of the field's excitement about its diagnostic applications. Additionally, a missed opportunity lies in not referencing a recent study that employed SAA successfully to diagnose PD and subtype the condition using a vast sample size. To further strengthen the results, the inclusion of healthy control brains in the biochemical and immunostaining/immunoblot experiments would provide more robust comparisons. Overall, the authors have conducted their experiments diligently, and their study offers valuable insights that align with the ongoing efforts to enhance early diagnosis and subtype differentiation in the domain of synucleinopathies.

STRENGTH:

The strengths of this research article are indeed notable and contribute to the credibility and significance of the study:

Important Research Question: The study addresses a crucial question in the field of neurodegenerative diseases by evaluating the effectiveness of the αSyn SAA in diagnosing and differentiating synucleinopathies. This question is of significant clinical and scientific interest.<br /> Comprehensive Introduction: The article provides a thorough and well-structured introduction to the topic with an illustration, setting the stage for the research. It ensures that readers, including those unfamiliar with the subject matter, can grasp the context and significance of the study.<br /> Use of Patient Brain Tissue: The use of patient-derived brain tissue samples from various synucleinopathies, including PD, PDD, DLB, and MSA, enhances the clinical relevance and applicability of the findings.<br /> Replication and Statistical Significance: Conducting the experiments six times for each sample demonstrates the rigor of the study and the robustness of the results, and increases the confidence in the conclusions drawn.<br /> Clarity in Experimental Results and Discussion: The authors have presented the experimental results in a clear and understandable manner. I was personally impressed by images showing twisted and straight conformations of αSyn, as well as immunogold labeling for phosphorylation of αSyn, which aids in conveying the findings effectively to the readers. The results clearly show distinct differences in the characteristics of αSyn fibrils across different synucleinopathies. It also highlights the more aggressive seeding capacities and higher biochemical stability of αSyn in PDD and DLB patients, offering valuable insights into the pathophysiology of these conditions. The authors also clearly show that SAA fails in differentiating the disease types within the synucleinopathies.<br /> Clinical relevance: The study underscores the importance of considering complementary diagnostic methods alongside SAA for a more comprehensive understanding of synucleinopathy subtypes. The study might also play an important role in potential FDA approval of SAA as a diagnostic tool for synucleinopathies, especially for PD.<br /> These strengths collectively make the study a valuable contribution to the field of neurodegenerative diseases, shedding light on the limitations and potential applications of SAA in the diagnosis and differentiation of various synucleinopathies.

WEAKNESS:

While this study is overall robust, there are several aspects that could further enhance the quality and interpretation of the findings.

Clinical Data on Patient Brain Samples: The inclusion of specific details such as post-mortem intervals and the age at disease onset for patient brain samples would be valuable. These factors could significantly affect the quality of the tissues and their relevance to the study. Moreover, given the large variation in disease duration between PD and PDD, it's important to consider disease duration as a potential confounding factor, especially when concluding that PDD patients have a more severe form of synucleinopathy compared to PD.<br /> Inclusion of Healthy Controls in Multiple Tests: Given the importance of healthy controls in scientific studies, especially those involving human brain samples, the authors could consider using healthy controls in more tests to strengthen the robustness of the findings. Expanding the use of healthy controls in biochemical profiling and phosphorylation profiles would provide a better basis for comparison and clarify the significance of results in a disease context.<br /> This will help the authors to elaborate on the interpretation of results, for example, in Figure 3, where the authors claim that PD brains show mostly monomeric αSyn forms (line 119 and 120, and also in 222 and 223). Whether it implies the absence of alpha-syn pathology in PD brains? If there are differences from healthy controls? What are these low molecular weight bands (<15kD) (line 125-126) and whether they are also present in healthy controls? Also, we do not have a perfect pS129-specific (anti-p𝛼Syn) antibody. They are known for non-specific labeling. Investigating the phosphorylation levels in healthy controls and comparing them to PD brains, especially considering the predominance of monomeric (healthy αSyn?) in PD brains, would help clarify the observed changes.<br /> Age of Healthy Controls: Providing information about the age at death for healthy controls is crucial, as age can impact the accumulation of αSyn. Also include if the brain samples were age-matched, or analyses were age-adjusted.<br /> Braak Staging Discrepancy: The study reports the same Braak staging for both PD and PDD, despite the significant difference in disease duration. Maybe other reviewers with clinical experience might have a better take on this. This observation merits discussion in the paper, allowing readers to better understand the implications of this finding.<br /> Citation of Relevant Studies: The paper should consider citing and discussing a recent celebrated study on PD biomarkers that used thousands of cerebrospinal fluid (CSF) samples from different PD patient cohorts to demonstrate the effectiveness of SAA as a biochemical assay for diagnosing PD and its subtypes (https://doi.org/10.1016/S1474-4422(23)00109-6).<br /> In summary, these suggestions aim to enhance the study's quality and the clarity of its findings, ultimately contributing to a more comprehensive understanding of synucleinopathies and the diagnostic potential of SAA.

Reviewer #2 (Public Review):

Most neurodegenerative diseases are characterized by the self-templated misfolding of a particular protein in a manner that enables progressive spread throughout the central nervous system. In diseases including Parkinson's disease (PD) and multiple system atrophy (MSA), the protein alpha-synuclein misfolds into unique shapes, or strains, which use this self-replicating mechanism to encode disease-specific information. Previous research suggests that a major contributor to the lack of successful clinical trials across neurodegenerative diseases is the lack of disease-relevant strains used in preclinical testing. While MSA patient samples are known to replicate efficiently in cell and mouse models of disease, Lewy body disease (LBD) patient samples do not. To overcome this obstacle, the seeding amplification assay (SAA) uses recombinant alpha-synuclein to amplify the misfolded protein structure present in a human patient sample. The resulting fibrils are then widely used by many laboratories as a model of PD. In this manuscript, Lee et al., set out to compare the strain properties of alpha-synuclein fibrils isolated from LBD and MSA patient samples with the resulting amplified fibrils following SAA. Using orthogonal biochemical and structural approaches to strengthen their analyses, the authors report that the SAA-amplified fibrils do not recapitulate the disease-relevant strains present in the patient samples. Moreover, their data suggest that regardless of which strain is used to seed the SAA reaction, the same strain is generated. These results clearly demonstrate that the SAA-amplified material is not disease-relevant. SAA fibrils are broadly used in academic and pharmaceutical laboratories. They are used in ongoing drug discovery efforts and recombinant fibrils broadly inform much of what is known about alpha-synuclein strain biology in LBD patients. The implications of the reported work are, therefore, expansive. These findings add to the growing ledger of reasons that the use of SAA fibrils in research should be halted until improved methods for amplification with high fidelity are developed.

Reviewer #3 (Public Review):

Summary:

This interesting manuscript presents a comparison of biophysical properties, TEM appearances, and phosphorylation patterns of brain-derived synuclein fibrils from 3 subjects each with Parkinson Disease (PD), Parkinson Disease with Dementia (PDD), Dementia with Lewy bodies (DLB) and Multiple System Atrophy (MSA), the effects of studying these brain-derived fibrils in a Seeding Aggregation Assay (SAA), and a comparison of the seeded and resultant fibers. The results are not unexpected.

Strengths:

The work explores an important question. Namely, what is the fidelity of synuclein fibrils produced during an SAA reaction to the starting material if that material has been extracted from the brains of deceased patients with synucleinopathies.

Weaknesses:

The work suffers from several methodological flaws

The experiments are missing two important controls. 1) what to fibrils generated by different in vitro fibril preparations made from recombinant synclein protein look like; and 2) the use of CSF from the same patients whose brain tissue was used to assess whether CSF and brain seeds look and behave identically. The latter is perhaps the most important question of all - namely how representative are CSF seeds of what is going on in patients' brains?

In their discussion the authors do not comment on the obvious differences in the conditions leading to the formation of seeds in the brain and in the artificial conditions of the seeding assay. Why should the two sets of conditions be expected to yield similar morphologies, especially since the extracted fibrils are subjected to harsh conditions for solubilization and re-suspension.

Finally, the key experiment was not performed - would the resultant seeds from SAA preparations from the different nosological entities produce different pathologies when injected into animal brains? But perhaps this is the subject of a future manuscript.

Furthermore, the authors comment on phosphorylation patterns, stating that the resultant seeds are less heavy phosphorylated than the original material. Again, this should not be surprising, since the SAA assay conditions are not known to contain the enzymes necessary to phosphorylate synuclein. The discussion of PTMs is limited to pS-129 phosphorylation. What about other PTMs? How does the pattern of PTMs affect the seeding pattern.

Lastly, the manuscript contains no data on how the diagnostic categories were assigned at autopsy. This information should be included in the supplementary material.

Reviewer #1 (Public Review):

Summary:

This is an interesting report examining activity patterns in mouse ACC and in the OFC neurons projecting to ACC. In addition, the effects of inactivation are examined. In aggregate, the results provide new and interesting information about these two brain areas and they translate motivation into action - a function that it seems intuitively plausible that ACC might perform but, despite this intuition, there have been comparatively few direct tests of the idea and little is known of the specific mechanisms. The study is performed carefully and is written up clearly. There were just a few points where I wondered if a little more clarification might be helpful.

Strengths:

The combination of recording and inactivation/inhibition experiments and the combination of investigation of ACC neurons and of OFC regions projecting to ACC are very impressive.

Weaknesses:

These are all minor points of clarification.

(1) An important conclusion (Figure 4) is that when mice are trained to run through no reward (N) cues in order to reach reward (R) cues, the OFC neurons projecting to ACC each respond to different specific events in a manner that ensures that collectively they tile the extended behavioural sequence. What I was less sure of was whether the ACC neurons do the same or not. Figure 3 suggests that on average ACC neurons maintain activity across N cues in order to get to R cues but I was not sure whether this was because all individual neurons did this or whether some had activity patterns like the OFC neurons projecting to ACC.

(2) Figure 1 versus Figure 2: There does not seem to be a particular motivation for whether chemogenetic inactivation or optogenetic inhibition were used in different experiments. I think that this is not problematic but, if I am wrong and there were specific reasons for performing each experiment in a certain way, then further clarification as to why these decisions were made would be useful. If there is no particular reason, then simply explaining that this is the case might stop readers from seeking explanations.

(3) P5, paragraph 2. The authors argue that OFC and anteriomedial (AM) thalamic inputs into ACC are especially important for mediating motivation through N cues in order to reach R cues. Is this based on a statistical comparison between the activity in OFC or AM inputs as opposed to the other inputs?

(4) P3, paragraph 2. Some papers by Khalighinejad and colleagues (eg Neuron 2020, Current Biology, 2022) might be helpful here in as much as they assess ACC roles in determining action frequency, initiation, and speed and mediating the relationship between reward availability and action frequency and speed.

(5) Paragraph 1 "This learning is of a more deliberate, informed nature than habitual learning, as they are sensitive to the current value of outcomes and can lead to a novel sequence of actions for a desired outcome1-3." Should "they" be "it"?

Reviewer #2 (Public Review):

Summary:

Regalado et al. studied how an extended motivational state, necessary for maintaining behavioural drive despite unrewarding experiences, could be encoded in the ACC and its potential causal implications for learning discriminatory behaviour and avoiding unrewarding stimuli. They designed a self-initiated learning task and identified bulk neural responses tuned specifically to reward delivery as well as trial initiation. Interestingly, in both cases, neural activity precedes behavioural onset, indicating the encoding of a motivational signal. To investigate the neural encoding of motivational signals during unrewarded, distracting stimuli presentation, they created a discrimination task by introducing 'no reward' cues, during which animals need to learn not to reduce running speed and not engage in licking. Interestingly, with mice learning to increase running speed and reduce licking rates after 'no reward' cues, the preceding ACC activity also gradually increased. Importantly, only the increase in running speed after 'no reward' cues was impaired upon optogenetic inhibition of ACC activity during early training, linking the extended motivational signal in ACC and learning to maximise rewards by actively avoiding distracting and unrewarded stimuli. Such motivational signals could also be observed in OFC-ACC projecting neurons. Especially the continuous ramping of activity upon repeated 'non-reward' cues, which could be exclusively observed in the 'fast learner' subgroup, provides an interesting concept of how an extended motivational signal necessary for learning avoidance of unrewarded stimuli could be implemented in ACC. The shift in the temporal activity of initially reward-responsive neurons towards the preceding 'no reward' cue, provides a potential mechanism linking extended motivation to reward maximisation. This mechanism seems to be particularly important in periods of persistent 'non-reward' cues, as demonstrated in the impairment of running speed increase after two consecutive 'non-reward' cues.

Appraisal:

The authors provide convincing experimental evidence to support their claims of an extended motivational signal encoded in the ACC that is implemented by OFC-ACC signalling and critically involved in learning avoidance of unrewarded stimuli. The newly designed task seems appropriate to identify correlates of relevant cognitive and behavioural variables (e.g. sustained motivation). The combination of recording Ca2+ transients (bulk as well as longitudinal single neuron recordings) to identify potential neural responses and subsequent evaluation of their causal role in establishing and maintaining this persistent motivational state using opto- and pharmacogenetic manipulations is generally accepted.

Impact:

The findings will be valuable for further research on the impact of motivational states on behaviour and cognition. The authors provided a promising concept of how persistent motivational states could be maintained, as well as established a novel, reproducible task assay. While experimental methods used are currently state-of-the-art, theoretical analysis seems to be incomplete/not extensive.

Reviewer #1 (Public Review):

Summary:

Wang and colleagues present a study aimed at demonstrating the feasibility of repeated ultrasound localization microscopy (ULM) recording sessions on mice chronically implanted with a cranial window transparent to ultrasound. They provided quantitative information on their protocol, such as the required number of contrast-enhancing microbubbles (MBs) to get a clear image of the vasculature of a brain coronal section. Also, they quantified the co-registration quality over time-distant sessions and the vasodilator effect of isoflurane.

Strengths:

The study showed a remarkable performance in recording precisely the same brain coronal section over repeated imaging sessions. In addition, it sheds light on the vasodilator effect of isoflurane (an anesthetic whose effects are not fully understood) on the different brain vasculature compartments, although, as the authors stated, some insights in this aspect have already been published with other imaging techniques. The experimental setting and protocol are very well described.

Weaknesses:

While the title is fair with respect to the data shown, in the summary and the rest of the paper, the comparison between anesthetized and awake conditions is systematically stated, while more caution should be used.

First, isoflurane is one of the (many) anesthetics commonly used in pre-clinical research, and its effect on the brain vasculature cannot be generalized to all the anesthetics. Indeed, other anesthesia approaches do not produce evident vasodilation; see ketamine + medetomidine mixtures. Second, the imaged awake state is head-fixed and body-constrained in mice. A condition that can generate substantial stress in the animals. In this study, there is no evaluation of the stress level of the mice. In addition, the awake imaging sessions were performed a few minutes after the mouse woke up from isoflurane induction, which is necessary to inject the MB bolus. It is known that the vasodilator effects of isoflurane last a long time after its withdrawal. This aspect would have influenced the results, eventually underestimating the difference with respect to the awake state.

These limitations should be clearly described in the Discussion.

Looking at Figure 2e, it takes more than 5' to reach the 5 Millions MB count useful for good imaging. However, the MB count per pixel drops to a few % at that time. This information tells me that (i) repeated measurements are feasible but with limited brain coverage since a single 'wake up' is needed to acquire a single brain section and (ii) this approach cannot fit the requirements of functional ULM that requires to merge the responses to multiple stimuli to get a complete functional image. Of course, a chronic i.v. catheter would fix the issue, but this configuration is not trivial to test in the experimental setup proposed by the authors, hindering the extension of the approach to fULM.

Statistics are often poor or not properly described. The legend and the text referring to Figure 2 do not report any indication of the number of animals analyzed. I assume it is only one, which makes the findings strongly dependent on the imaging quality of THAT mouse in THAT experiment. Three mice have been displayed in Figure 3, as reported in the text, but it is not clear whether it is a mouse for each shown brain section. Figure 5 reports quantitative data on blood vessels in awake VS isoflurane states but: no indication about the number of tested mice is provided, nor the number of measured blood vessels per type and if statistics have been done on mice or with a multivariate method. Also, a T-test is inappropriate when the goal is to compare different brain regions and blood vessel types. Similar issues partially apply to Figure 6, too.

Reviewer #2 (Public Review):

Summary:

The authors present a very interesting collection of methods and results using brain ultrasound localization microscopy (ULM) in awake mice. They emphasize the effect of the level of anesthesia on the quantifiable elements assessable with this technique (i.e. vessel diameter, flow speed, in veins and arteries, area perfused, in capillaries) and demonstrate the possibility of achieving longitudinal cerebrovascular assessment in one animal during several weeks with their protocol.

Strengths:

Even if the methods elements considered separately are not new (brain ULM in rodents, setup for longitudinal awake imaging similar to those used in fUS imaging, quantification of vessel diameters/bubble flow/vessel area), when masterfully combined as it is done in this paper, they answer two questions that have been long-running in the community: what is the impact of anesthesia on the parameters measured by ULM (and indirectly in fUS and other techniques)? Is it possible to achieve ULM in awake rodents for longitudinal imaging? The authors answer quite exhaustively the first question. The manuscript is well-constructed and well-written, and the graphics are appealing.

Weaknesses:

The only major comment (calling for further work) I would like to make is the relative weakness of the manuscript regarding longitudinal imaging (mostly Figure 6), compared to the exhaustive review of the effect of isoflurane on the vasculature (3 rats, 3 imaging planes, quantification on a large number of vessels, in 9 different brain regions). The 6 cortical vessels evaluated in Figure 6 feel really disappointing. As longitudinal imaging is supposed to be the salient element of this manuscript (first word appearing in the title), it should be as good and trustworthy as the first part of the paper. Figure 6c. is of major importance, and should be supported by a more extensive vessel analysis, including various brain areas, and validated on several animals to validate the robustness of longitudinal positioning with several instances of the surgical procedure. Figure 6d estimates the reliability of flow measurements on 3 vessels only. Therefore I recommend showing something similar to what is done in Figures 4 and 5: 3 animals, and more extensive quantification in different brain regions.

Reviewer #3 (Public Review):

Summary:

In this manuscript, Wang et al. performed a study looking at vascular changes in response to anesthesia in awake mice using ultrasound localization microscopy (ULM). The authors report a reduction of vascularity and blood flow velocity in the awake state. In addition, they demonstrate the reproducibility of ULM measurements in time.

Strengths:

Demonstration that high-quality, state-of-the-art ULM images can be performed using cranial windows in awake animals.<br /> Demonstration that repeated imaging in time produces comparable images.

Weaknesses:

It is unclear whether multiple animals were used in the statistical analysis.<br /> Generalizations are sometimes drawn from what seems to be the analysis of a single vessel.<br /> The description of the statistical analysis is mostly qualitative.<br /> Some terms used are insufficiently defined.<br /> Additional limitations should be included in the discussion.<br /> Some technical details are lacking.

Without information about whether the results obtained come from multiple animals, it is difficult to conclude that the authors generally achieved their aim. They do achieve it in a single animal.

The results that are shown are interesting and could have an impact on the ULM community and beyond. In particular, the experimental setup they used along with the high reproducibility they report could become very important for the use of ULM in larger animal cohorts.

Reviewer #2 (Public Review):

The authors combine genetic tools, dye fills and connectome analysis techniques to generate a "first-of-its-kind", near complete, synaptic resolution map of the head bristle neurons of Drosophila. While some of the BMN anatomy was already known based on previous work by the authors and other researchers, this is the first time a near complete map has been created for the head BMNs at electron microscopy resolution.

Strengths:

(1) The authors cleverly use techniques that allow moving back and forth between periphery (head bristle location) and brain, as well as moving between light microscopy and electron microscopy data. This allows them to first characterize the pathways taken by different head BMNs to project to the brain and also characterize anatomical differences among individual neurons at the level of morphology and connectivity.<br /> (2) The work is very comprehensive and results in a near complete map of all head BMNs.<br /> (3) Authors also complement this anatomical characterization with a first-level functional analysis using optogenetic activation of BMNs that results in expected directed grooming behavior.

Weaknesses:<br /> (1) While not strictly needed here, it could help provide context if authors revealed some of the important downstream pathways that could explain optogenetics behavioral phenotypes: This point was addressed by authors in the revisions and I agree a detailed description of downstream circuits is not needed at this point.<br /> (2) In contrast to the rigorous quantitative analysis of the anatomical data, the behavioral data is analyzed using much more subjective methods. While I do not think it is necessary to perform a rigorous analysis of behaviors in this anatomy focused manuscript, the conclusions based on behavioral analysis should be treated as speculative in the current form e.g. calling "nodding + backward motions" as an avoidance response is not justified as it currently stands. Strong optogenetic activation could lead to sudden postural changes that due to purely biomechanical constraints could lead to a couple of backward steps as seen in the example videos. Moreover since the quantification is manual, it is not clear what the analyst interprets as backward walking or nodding. Interpretation is also concerning because controls show backward walking (although in fewer instances based on subjective quantification): This point was addressed by the authors during revisions and I'm mostly satisfied with their response, where authors agree that the behavioral results are currently used to speculate about the role of BMNs in aversive behaviors. Still, the fact that controls show some "backward motions" is a bit concerning when talking about "significant differences" between control and test groups based on manual annotations and I would recommend future studies focusing on these behaviors to use more unbiased quantitative analysis wherever possible.

Summary:

The authors end up generating a near-complete map of head BMNs that will serve as a long-standing resource to the Drosophila research community. This will directly shape future experiments aimed at modeling or functionally analyzing the head grooming circuit to understand how somatotopy guides behaviors. I appreciate the authors taking the time to revise the manuscript and address reviewer concerns.

Reviewer #3 (Public Review):

Eichler et al. set out to catalog the mechanosensory bristles of the fly head in an effort to understand the extent to which their organization is consistent with the parallel model of hierarchical suppression in the context of grooming behavior. They map the locations of the mechanosensory bristles on the fly head, examine the axonal morphology of the bristle mechanosensory neurons (BMNs) that innervate them, and match these to electron microscopy reconstructions of the same BMNs in a previously published EM volume of the female adult fly brain. They use BMN synaptic connectivity information to create clusters of BMNs that they show occupy different regions of the subesophageal zone brain region and use optogenetic activation of subsets of BMNs to evaluate the behaviors evoked by specific activation of BMN subpopulations innervating the head.

The authors have beautifully cataloged the mechanosensory bristles and the projection paths and patterns of the corresponding BMN axons in the brain using detailed and painstaking methods. The result is a neuroanatomy resource that will be an important community resource. To match BMNs reconstructed in an electron microscopy volume of the adult fly brain, the authors matched clustered reconstructed BMNs with light-level BMN classes observed using precise dye-fills and stochastic labeling techniques. The authors then employ a variety of clustering methods to demonstrate that BMN populations that innervate different regions of the head project into the subesophageal zone and terminate in distinctive yet, in some cases, partially overlapping zones. By clustering BMNs on the basis of their synaptic partners, the authors find that BMNs from distant areas of the head have non-overlapping synaptic partners while those from neighbor areas have overlapping synaptic partners. This result calls into question the scale at which the parallel model of hierarchical suppression may be operating. Finally, the authors use tools that were generated during the light-level characterization of BMN projections to show that activating BMNs that innervate specific areas of the head leads to grooming of the innervated regions and neighboring regions, consistent with the observed overlap in downstream circuits between BMNs innervating neighboring regions of the head. This result suggests that while the parallel model could be operating on a broad scale, additional circuit mechanisms may be operating on a finer scale to produce grooming of the area surrounding the source of mechanosensory input.

This work will have a positive impact on the field by contributing a complete accounting of the mechanosensory bristles of the fruit fly head, describing the brain projection patterns of the BMNs that innervate them, and linking them to BMN sensory projections in an electron microscopy volume of the adult fly brain. It will also have a positive impact on the field by providing genetic tools to help functionally subdivide the contributions of different BMN populations to circuit computations and behavior. This contribution will pave the way for further mechanistic study of central circuits that subserve grooming circuits.

Reviewer #1 (Public Review):

Summary:

The motivating questions are an accurate reflection of the current state of knowledge surrounding striatal pathway function. The comparisons of pathway function across striatal subregion, activation & inhibition, and task context are laudable and extremely important for advancing the subfield. Had these manipulations, to the largest extent possible been performed in single animals (e.g. activate dSPNs of DMS or DLS in the same mouse across the 3 tasks), this would have significantly strengthened the impact and conclusions that could be drawn by making this set of studies even more so internally consistent and directly comparable. While this is no longer possible, a conceptually related and fantastic contribution to the subfield (and likely beyond in terms of Opto manipulations of brain areas) would be to directly demonstrate that within their studies their DMS pathway manipulations do not impact nearby DLS activity (and vice versa). This is a significant and non-essential request. More feasibly and reasonably, it would be fantastic and strengthen the conclusions here to more fully detail their opsin expression patterns in DMS vs DLS groups and perhaps attempt to relate individual opsin profiles and fiberoptic targeting with behavioral outcomes across tests.

Strengths:

A comprehensive and paired comparison of inhibition and activation of striatal pathways across subregions and tasks is a very important and meaningful step towards reconciling contradictory results on striatal pathway function that are observed across labs (who typically focus on one subregion, one task setting, and often do not directly report comparisons of activation and inhibition).

Weaknesses:

Figure 1A - the example DMS vs DLS opsin expression and fiber targeting are not terribly convincing that the manipulations will be specific to each subregion (the example in Figure 2A is a little better but I have a similar concern still). The specificity of these manipulations is key to interpretation and conclusions and I strongly feel they should be strengthened here. The best evidence would be direct neural recordings (light in DMS, no effect in DLS, and vice versa), but this is a tall ask and not expected. The next best option, which is readily feasible, is to show not only fiberoptic targeting summaries (as in Figure 1A, Figure 2A) but also a summary of opsin spread for all animals (especially given the two examples appear to have significant spread across DMS and DLS). It would be of great benefit to the field to have these in the Allen Common Coordinate Framework. It would also be fine and useful to utilize the authors' current classical histological atlas alignment methods (e.g. Paxinos pdf). These histological summary figures would also benefit from being larger and more visible (perhaps as separate supplemental figures associated with the main figures).

Related to the above, it is a concern that the classic view is supported or not because of individual variations in virus/fiber targeting to striatal subregions which likely have greater granularity than the traditional dorsal medial vs lateral (e.g. Hunnicutt et al 2016, Foster et al 2021, Hintiryan et al 2016). Although there may not be enough animals or variation in targeting in the present study to find meaningful relationships, it would strengthen the paper and be a great benefit to the field to know whether for key findings if the strength of behavioral effects correlated with anterior/posterior or medial/lateral or dorsal/ventral fiberoptic coordinates (or the volume of opsin expression profiles).

Conceptually, a clear new idea or integrative interpretation of prior work (nor even the large body of results within this work) comes to the fore, save for the already appreciated fact that the classic view of opposing pathways is sometimes supported and sometimes not. Two tangible suggestions that I believe would facilitate the influence of this study - (1) can the authors more thoughtfully bridge the logical steps in their results sections and the prior context around them (some topic sentences jump right into results, e.g. line 195: "The inhibition experiment showed), and (2) in discussion, rather than emphasizing when/where the classic view is supported and not, more content on precisely why would be helpful. Some questions more specifically, if DMS/DLS pathway activation/inhibition is *mostly* oppositely appetitive/aversive, what does that mean in the context of spontaneous or reward-guided locomotion? Self-initiated pathway activation/inhibition is in part learned (with very intriguing differences across pathways in the expression across learning) - how should we think about striatal pathway function with regards to learning, spontaneous/innate behaviors, vs over-trained behaviors? When the classic view fails in the dorsal striatum - why? And is a complimentary "model" an actual alternative concept, a distinct mode of circuit function, or just a negative result on the classic view?

Reviewer #2 (Public Review):

Summary:

Cuevas et al. investigate the involvement of DMS and DLS direct and indirect pathways in locomotion and action selection using optogenetic manipulation techniques. They show that optical excitation of dSPNs in both DMS and DLS induces place preference, with optical inhibition resulting in the opposite effect. Interestingly, and somewhat not coming as a surprise given many previous data on this, optical excitation of iSPNs in both regions resulted in place aversion - in line with the classical view of functional opposition.

Then, the authors performed a two-choice task in which animals would have to choose between pressing in a lever alone or in a lever+stim to obtain a food reward. Again, and not surprisingly, they show that optical activation of dSPNs results in selection from pressing in the lever+stim with the opposite being observed for iSPN, in both DMS and DLS. What was concerting was the increase in lever pressing when inhibiting dSPNs in the DMS, since before authors show that it should cause aversion. When looking at locomotor effects, the authors report an increase in spontaneous displacement when exciting dSPNs in DMS, and the opposite in DLS. Contrary, the excitation of iSPNs either in DMS or DLS increased spontaneous displacement. In reward-seeking, displacement excitation of either dSPNs or iSPNs in both regions resulted in decreased locomotion.

Strengths:

Overall this manuscript brings a new light to the involvement of DLS SPNs in both locomotion and behavioral preference.

Weaknesses:

Some of the main claims would benefit from further discussion or new data on the effect of optogenetic manipulation on the activity of SPNs. This could allow for the creation of a clearer picture of the involvement of iSPNs and dSPNs of DMS and DLS for behavior.

Reviewer #1 (Public Review):

Gazula and co-workers presented in this paper a software tool for 3D structural analysis of human brains, using slabs of fixed or fresh brains. This tool will be included in Freesurfer, a well-known neuroimaging processing software. It is possible to reconstruct a 3D surface from photographs of coronal sliced brains, optionally using a surface scan as model. A high-resolution segmentation of 11 brain regions is produced, independent of the thickness of the slices, interpolating information when needed. Using this method, the researcher can use the sliced brain to segment all regions, without the need of ex vivo MRI scanning.

The software suite is freely available and includes 3 modules. The first accomplishes preprocessing steps, for correction of pixel sizes and perspective. The second module is a registration algorithm that registers a 3D surface scan obtained prior to sectioning (reference) to the multiple 2D slices. It is not mandatory to scan the surface, -a probabilistic atlas can also be used as reference- however the accuracy is lower. The third module uses machine learning to perform the segmentation of 11 brain structures in the 3D reconstructed volume. This module is robust, dealing with different illumination conditions, cameras, lens and camera settings. This algorithm ("Photo-SynthSeg") produces isotropic smooth reconstructions, even in high anisotropic datasets (when the in-plane resolution of the photograph is much higher than the thickness), interpolating the information between slices.

To verify the accuracy and reliability of the toolbox, the authors reconstructed 3 datasets, using real and synthetic data. Real data of 21 postmortem confirmed Alzheimer's disease cases from the Massachusetts Alzheimer's Disease Research Center (MADRC)and 24 cases from the AD Research at the University of Washington(who were MRI scanned prior to processing)were employed for testing. These cases represent a challenging real-world scenario. Additionally, 500 subjects of the Human Connectome project were used for testing error as a continuous function of slice thickness. The segmentations were performed with the proposed deep-learning new algorithm ("Photo-SynthSeg") and compared against MRI segmentations performed to "SAMSEG" (an MRI segmentation algorithm, computing Dice scores for the segmentations. The methods are sound and statistically showed correlations above 0.8, which is good enough to allow volumetric analysis. The main strengths of the methods are the datasets used (real-world challenging and synthetic) and the statistical treatment, which showed that the pipeline is robust and can facilitate volumetric analysis derived from brain sections and conclude which factors can influence in the accuracy of the method (such as using or not 3D scan and using constant thickness).

Although very robust and capable of handling several situations, the researcher has to keep in mind that processing has to follow some basic rules in order for this pipeline to work properly. For instance, fiducials and scales need to be included in the photograph, and the slabs should be photographed against a contrasting background. Also, only coronal slices can be used, which can be limiting for certain situations.

The authors achieved their aims, and the statistical analysis confirms that the machine learning algorithm performs segmentations comparable to the state-of-the-art of automated MRI segmentations.<br /> Those methods will be particularly interesting to researchers who deal with post-mortem tissue analysis and do not have access to ex vivo MRI. Quantitative measurements of specific brain areas can be performed in different pathologies and even in the normal aging process. The method is highly reproducible, and cost-effective since allows the pipeline to be applied by any researcher with small pre-processing steps.

Reviewer #2 (Public Review):

Summary

The authors proposed a toolset Photo-SynthSeg to the software FreeSurfer which performs 3D reconstruction and high-resolution 3D segmentation on a stack of coronal dissection photographs of brain tissues. To prove the performance of the toolset, three experiments were conducted, including volumetric comparison of brain tissues on AD and HC groups from MADRC, quantitative evaluation of segmentation on UW-ADRC and quantitative evaluation of 3D reconstruction on HCP digitally sliced MRI data.

Strengths

To guarantee the successful workflow of the toolset, the authors clearly mentioned the prerequisites of dissection photograph acquisition, such as fiducials or rulers in the photos and tissue placement of brain slices with more than one connected component. The quantitative evaluation of segmentation and reconstruction on synthetic and real data demonstrates the accuracy of the methodology. Also, the successful application of this toolset on two brain banks with different slice thicknesses, tissue processing and photograph settings demonstrates its robustness. By working with tools of the SynthSeg pipeline, Photo-SynthSeg could further support volumetric cortex parcellation. The toolset also benefits from its adaptability of different 3D references, such as surface scan, ex vivo MRI and even probabilistic atlas, suiting the needs for different brain banks.

Weaknesses

Certain weaknesses are already covered in the manuscript. Cortical tissue segmentation could be further improved. The quantitative evaluation of 3D reconstruction is quite optimistic due to random affine transformations. Manual edits of slice segmentation task are still required and take a couple of minutes per photograph. Finally, the current toolset only accepts coronal brain slices and should adapt to axial or sagittal slices in future work.

Reviewer #1 (Public Review):

The authors have developed and optimized a footprinting assay to monitor the recruitment of mRNAs to a reconstituted translation initiation system. This assay is named Recruitment-Sequencing (Rec-Seq) and enables the analysis of many purified mRNAs in the reconstituted system.

This system possesses the ability to determine how competition occurs between mRNAs for the initiation machinery. This is the first approach using a reconstituted system that enables this important feature, and this is an important advance for the field.

Using purified mRNAs in a fully reconstituted system together with the ability to monitor start site selection is an important advance. The method enables one to observe for the first time how competition between mRNAs is altered in response to the absence or presence of different initiation components or accessory proteins.

Start site fidelity in purified reconstituted systems can be altered in different buffer conditions and by the concentration of various initiation factors involved in start site fidelity. Future experiments will reveal how these variables can regulate start site selection in this powerful system.

Comments on revised version:

The authors have addressed all of my original comments. This is an impressive manuscript.

Reviewer #2 (Public Review):

Summary:

Zhou et al report development of a new method, Rec-Seq, that allows rigorous quantitation of the efficiency of 48S ribosomal pre-initiation complex (PIC) formation on messenger RNAs at transcriptome scale in vitro. With a next-generation deep-sequencing approach, Rec-Seq allows precisely targeted dissection of the roles of translation initiation factors in PIC assembly. This level of molecular precision is important to understanding mechanisms of translational control, making Rec-Seq a significant methodological advance. The authors leverage Rec-Seq to investigate the relative roles of two key helicase enzymes, Ded1p and eIF4A. While past work has pointed to differing roles for Ded1p and eIF4A helicase activity in PIC assembly, unambiguous interpretation of prior in-vivo data has been hindered by technical requirements for performing the experiments in cells. Rec-Seq circumvents these challenges, providing robust mechanistic insights. The authors find that Ded1p stimulates PIC formation selectively on mRNAs with long, structured leaders in the Rec-Seq system, while eIF4A provides much more general stimulation across mRNAs. The findings substantiate the past in-vivo results, along with adding new insights. They contrast with evidence that Ded1p promotes translation by suppressing inhibitory upstream initiation through structural remodeling, or through formation of intracellular, phase-separated granules. The conclusions of the study are well-supported by the data, and are likely to be of broad interest.

Strengths:

The quantitative nature of Rec-Seq, which uses an internal standard to measure absolute recruitment efficiencies, is an important strength.

The methodology decisively overcomes past experimental limitations, allowing the authors to make clear conclusions with regard to the relative roles of Ded1p and eIF4A in PIC formation. An important and useful addition to the toolbox for studying translation and translational control mechanisms, Rec-Seq substantially expands the throughput and scope of mechanistic analyses for translation initiation.

One significant finding to emerge is that the in-vitro reconstituted system used here recapitulates effects of in-vivo perturbations of translation initiation. Despite the lack of a cellular environment and its components, PIC formation appears to operate much as it does in the cell. Importantly, this highlights an inherent "modularity" to the system that is especially of interest in the context of how regulatory machinery beyond the PIC may control translation.

Weaknesses:

The study finds that Ded1p stimulates accumulation of PICs at internal AUG codons, i.e., within mRNA coding sequences, at an incidence of up to ~50% - thus, bypassing "canonical" translation start sites. Understanding the physiological significance of this activity will require further study. The authors address this in the text.

A limitation of the methodology is that, as an endpoint assay, Rec-Seq does not readily decouple effects of Ded1p on PIC-mRNA loading from those on the subsequent scanning step where the PIC locates the start codon. Considering that Ded1p activity may influence each of these initiation steps through distinct mechanisms - i.e., binding to the mRNA cap-recognition factor eIF4F, or direct mRNA interaction outside eIF4F - additional studies will be needed to gain deeper mechanistic insights. The authors discuss this in the text.

Comments on revised version:

In revising their manuscript, the authors have responded very thoughtfully and insightfully to the initial review. The final manuscript is an important contribution to the field, and I am sure it will be of broad interest.

Reviewer #1 (Public Review):

Summary:

The CPC plays multiple essential roles in mitosis such as kinetochore-microtubule attachment regulation, kinetochore assembly, spindle assembly checkpoint activation, anaphase spindle stabilization, cytokinesis, and nuclear envelope formation, as it dynamically changes its mitotic localization: it is enriched at inner centromeres from prophase to metaphase but it is relocalized at the spindle midzone in anaphase. The business end of the CPC is Aurora B and its allosteric activation module IN-box, which is located at the C-terminus of INCENP. In most well-studied eukaryotic species, Aurora B activity is locally controlled by the localization module of the CPC, Survivin, Borealin and the N-terminal portion of INCENP. Survivin and Borealin, which bind the N-terminus of INCENP, recognize histone residues that are specifically phosphorylated in mitosis, while anaphase spindle midzone localization is supported by the direct microtubule-binding capacity of the SAH (single alpha helix) domain of INCENP and other microtubule-binding proteins that specifically interact with INCENP during anaphase, which are under the regulation of CDK activity. One of these examples includes the kinesin-like protein MKLP2 in vertebrates. Trypanosoma is an evolutionarily interesting species to study mitosis since its kinetochore and centromere proteins do not show any similarity to other major branches of eukaryotes, while orthologs of Aurora B and INCENP have been identified. Combining molecular genetics, imaging, biochemistry, cross-linking IP-MS (IP-CLMS), and structural modeling, this manuscript reveals that two orphan kinesin-like proteins KIN-A and KIN-B act as localization modules of the CPC in Trypanosoma brucei. The IP-CLMS, AlphaFold2 structural predictions, and domain deletion analysis support the idea that (1) KIN-A and KIN-B form a heterodimer via their coiled-coil domains, (2) Two alpha helices of INCENP interact with the coiled-coil of the KIN-A-KIN-B heterodimer, (3) conserved KIN-A C-terminal CD1 and CD2 interact with the heterodimeric KKT9-KKT11 complex, which is a submodule of the KKT7-KKT8 kinetochore complex composed of KKT7, KKT8, KKT9, KKT11, and KKT12 unique to Trypanosoma, (4) KIN-A and KIN-B coiled-coil domains and the KKT7-KKT8 complex are required for CPC localization at the centromere, (5) CD1 and CD2 domains of KIN-A support its centromere localization. The authors further introduced a KIN-A rigor mutant and knocked-down wild-type KIN-A to show that the ATPase activity of KIN-A seems dispensable for centromere targeting but critical for spindle midzone enrichment of the CPC. The imaging data of the KIN-A rigor mutant suggest that dynamic KIN-A-microtubule interaction is required for metaphase alignment of the kinetochores and proliferation. Overall, the study reveals novel pathways of CPC localization regulation via KIN-A and KIN-B by multiple complementary approaches.

Strengths:

The major conclusion is collectively supported by multiple approaches, combining CRISPR-mediated gene deletion and complementation/site specific genome engineering, epistasis analysis of cellular localization, AlphaFold2 structure prediction of protein complexes, IP-CLMS and biochemical reconstitution (the complex of KKT8, KKT9, KKT11 and KKT12)

Weaknesses:

Minor weakness. The authors imply that KIN-A, but not KIN-B, interacts with microtubules based on microtubule pelleting assay (Fig. S6), but the substantial insoluble fractions of 6HIS-KINA and 6HIS-KIN-B make it difficult to conclusively interpret the data. It is possible that these two proteins are not stable unless they form a heterodimer.

Reviewer #2 (Public Review):

How the chromosomal passenger complex (CPC) and its subunit Aurora B kinase regulate kinetochore-microtubule attachment, and how the CPC relocates from kinetochores to the spindle midzone as a cell transitions from metaphase to anaphase are questions of great interest. In this study, Ballmer and Akiyoshi take a deep dive into the CPC in T. brucei, a kinetoplastid parasite with a kinetochore composition that varies greatly from other organisms.

Using a combination of approaches, most importantly in silico protein predictions using alphafold multimer and light microscopy in dividing T. brucei, the authors convincingly present and analyse the composition of the T. brucei CPC. This includes the identification of KIN-A and KIN-B, proteins of the kinesin family. This is a clear advancement over earlier work, for example by Li and colleagues in 2008. The involvement of KIN-A and KIN-B is of particular interest, as it provides a clue for the (re)localization of the CPC during the cell cycle. The evolutionary perspective makes the paper potentially interesting for a wide audience of cell biologists, a point that the authors bring across properly in the title, the abstract, and their discussion.

The evolutionary twist of the paper would be strengthened 'experimentally' by predictions of the structure of the CPC beyond T. brucei. Depending on how far the authors can extend their in-silico analysis, it would be of interest to discuss a) available/predicted CPC structures in well-studied organisms and b) structural predictions in other euglenozoa. What are the general structural properties of the CPC (e.g. flexible linkers, overall dimensions, structural differences when subunits are missing etc.)? How common is the involvement of kinesin-like proteins?

Reviewer #3 (Public Review):

Summary:

The protein kinase, Aurora B, is a critical regulator of mitosis and cytokinesis in eukaryotes, exhibiting a dynamic localisation. As part of the Chromosomal Passenger Complex (CPC), along with the Aurora B activator, INCENP, and the CPC localisation module comprised of Borealin and Survivin, Aurora B travels from the kinetochores at metaphase to the spindle midzone at anaphase, which ensures its substrates are phosphorylated in a time- and space-dependent manner. In the kinetoplastid parasite, T. brucei, the Aurora B orthologue (AUK1), along with an INCENP orthologue known as CPC1, and a kinetoplastid-specific protein CPC2, also displays a dynamic localisation, moving from the kinetochores at metaphase, to the spindle midzone at anaphase, to the anterior end of the newly synthesised flagellum attachment zone (FAZ) at cytokinesis. However, the trypanosome CPC lacks orthologues of Borealin and Survivin, and T. brucei kinetochores also have a unique composition, being comprised of dozens of kinetoplastid-specific proteins (KKTs). Of particular importance for this study are KKT7 and the KKT8 complex (comprising KKT8, KKT9, KKT11, and KKT12). Here, Ballmer and Akiyoshi seek to understand how the CPC assembles and is targeted to its different locations during the cell cycle in T. brucei.

Strengths & Weaknesses:

Using immunoprecipitation and mass-spectrometry approaches, Ballmer and Akiyoshi show that AUK1, CPC1, and CPC2 associate with two orphan kinesins, KIN-A and KIN-B, and with the use of endogenously expressed fluorescent fusion proteins, demonstrate for the first time that KIN-A and KIN-B display a dynamic localisation pattern similar to other components of the CPC, providing compelling evidence for KIN-A and KIN-B being bona fide CPC proteins.

They then demonstrate, by using RNAi to deplete individual components, that the CPC proteins have hierarchical interdependencies for their localisation to the kinetochores at metaphase. These experiments appear to have been well performed.

Ballmer and Akiyoshi then go on to determine the kinetochore localisation domains of KIN-A and KIN-B. Using ectopically expressed GFP-tagged truncations, they show that coiled coil domains within KIN-A and KIN-B, as well as a disordered C-terminal tail present only in KIN-A, but not the N-terminal motor domains of KIN-A or KIN-B, are required for kinetochore localisation. These data are strengthened by immunoprecipitating CPC complexes and crosslinking them prior to mass spectrometry analysis (IP-CLMS), a state-of-the-art approach, to determine the contacts between the CPC components. Structural predictions of the CPC structure are also made using AlphaFold2, suggesting that coiled coils form between KIN-A and KIN-B, and that KIN-A/B interact with the N termini of CPC1 and CPC2. Experimental results showing that CPC1 and CPC2 are unable to localise to kinetochores if they lack their N-terminal domains are consistent with these predictions. Altogether these data provide compelling evidence of the protein domains required for CPC kinetochore localisation and CPC protein interactions and indicate that both KIN-A and KIN-B have a role to play.

Next, using a mixture of RNAi depletion and LacI-LacO recruitment experiments, the authors show that kinetochore proteins KKT7 and KKT9 are required for AUK1 to localise to kinetochores (other KKT8 complex components were not tested here) and that all components of the KKT8 complex are required for KIN-A kinetochore localisation. Further, both KKT7 and KKT8 were able to recruit AUK1 to an ectopic locus in S phase, and KKT7 recruited KKT8 complex proteins, indicating it is upstream of KKT8, in line with previous work showing kinetochore localization of KKT7 is unaffected by disruption of the KKT8 complex. This leads to the conclusion that the KKT8 complex is likely the main kinetochore receptor of the CPC.

Further IP-CLMS experiments, in combination with recombinant protein pull down assays and structural predictions, suggested that within the KKT8 complex, there are two subcomplexes of KKT8:KKT12 and KKT9:KKT11, and that KKT7 interacts with KKT9:KKT11 to recruit the remainder of the KKT8 complex. The authors also assess the interdependencies between KKT8 complex components for localisation and expression, showing that all four subunits are required for the assembly of a stable KKT8 complex and present AlphaFold2 structural modelling data to support the two subcomplex model. In general, these data are of high quality and convincing, although it is a shame that data showing the effects of KKT8, KKT9 and KKT12 depletion on KKT11 localisation and abundance could not be presented alongside the reciprocal experiments in Fig S4I-L.

The authors also convincingly show that AlphaFold2 predictions of interactions between KKT9:KKT11 and a conserved domain (CD1) in the C-terminal tail of KIN-A are correct, with CD1 and a second conserved domain, CD2, identified through sequence analysis, acting synergistically to promote KIN-A kinetochore localisation at metaphase, but not being required for KIN-A to move to the central spindle at anaphase. They then hypothesise that the kinesin motor domain of KIN-A (but not KIN-B which is predicted to be inactive based on non-conservation of residues key for activity) determines its central spindle localisation at anaphase through binding to microtubules. In support of this hypothesis, the authors show that KIN-A, but not KIN-B can bind microtubules in vitro and in vivo. However, ectopically expressed GFP-NLS fusions of full length KIN-A or KIN-A motor domain did not localise to the central spindle at anaphase. The authors suggest this is due to the GFP fusion disrupting the ATPase activity of the motor domain, although they provide no evidence that this is the case. Instead, they replace endogenous KIN-A with a predicted ATPase-defective mutant (G210A), showing that while this still localises to kinetochores, the kinetochores were frequently misaligned at metaphase, and that it no longer concentrates at the central spindle (with concomitant mis-localisation of AUK1), causing cells to accumulate at anaphase. From these data, the authors conclude that KIN-A ATPase activity is required for chromosome congression to the metaphase plate and its central spindle localisation at anaphase. While these data are highly suggestive that KIN-A possesses ATPase activity, and that this activity is essential for its function, definitive biochemical evidence of KIN-A's ATPase activity is still lacking.

Impact:

Overall, this work uses a wide range of cutting edge molecular and structural predictive tools to provide a significant amount of new and detailed molecular data that shed light on the composition of the unusual trypanosome CPC and how it is assembled and targeted to different cellular locations during cell division. Given the fundamental nature of this research, it will be of interest to many parasitology researchers as well as cell biologists more generally, especially those working on aspects of mitosis and cell division, and those interested in the evolution of the CPC.

Reviewer #1 (Public Review):

Summary:

This is a follow-up study to the authors' previous eLife report about the roles of an alpha-arrestin called protein thioredoxin interacting protein (Txnip) in cone photoreceptors and in the retinal pigment epithelium. The findings are important because they provide new information about the mechanism of glucose and lactate transport to cone photoreceptors and because they may become the basis for therapies for retinal degenerative diseases.

Strengths:

Overall, the study is carefully done and, although the analysis is fairly comprehensive with many different versions of the protein analyzed, it is clearly enough described to follow. Figure 4 greatly facilitated my ability to follow, understand and interpret the study. The authors have appropriately addressed a few concerns about statistical significance and the relationship between their findings and previous studies of the possible roles of Txnip on GLUT1 expression and localization on the surfaces of RPE cells.

Reviewer #2 (Public Review):

The hard work of the authors is much appreciated. With overexpression of a-arrestin Txnip in RPE, cones and the combined respectively, the authors show a potential gene agnostic treatment that can be applied to retinitis pigmentosa. Furthermore, since Txnip is related to multiple intracellular signaling pathway, this study is of value for research in the mechanism of secondary cone dystrophy as well.

There are a few areas in which the article may be improved through further analysis and application of the data, as well as some adjustments that should be made in to clarify specific points in the article.

Strengths

- The follow-up study builds on innovative ground by exploring the impact of TxnipC247S and its combination with HSP90AB1 knockdown on cone survival, offering novel therapeutic pathways.<br /> - Testing of different Txnip deletion mutants provides a nuanced understanding of its functional domains, contributing valuable insights into the mechanism of action in RP treatment.<br /> - The findings regarding GLUT1 clearance and the differential effects of Txnip mutants on cone and RPE cells lay the groundwork for targeted gene therapy in RP.

Weaknesses

- The focus on specific mutants and overexpression systems might overlook broader implications of Txnip interactions and its variants in the wider context of retinal degeneration.<br /> - The study's reliance on cell count and GLUT1 expression as primary outcomes misses an opportunity to include functional assessments of vision or retinal health, which would strengthen the clinical relevance.<br /> - The paper could benefit from a deeper exploration of why certain treatments (like Best1-146 Txnip.C247S) do not lead to cone rescue and the potential for these approaches to exacerbate disease phenotypes through glucose shortages.<br /> - Minor inconsistencies, such as the missing space in text references and the need for clarification on data representation (retinas vs. mice), should be addressed for clarity and accuracy.<br /> - The observation of promoter leakage and potential vector tropism issues raise questions about the specificity and efficiency of the gene delivery system, necessitating further discussion and validation.

Reviewer #1 (Public Review):

Summary:

In this manuscript, Sang et al. proposed a pair of IR60b-expressing pharyngeal neurons in Drosophila use IR25a, IR76b, and IR60b channels to detect high Na+ and limit its consumption. Some of the key findings that support this thesis are: 1) animals that lacked any one of these channels - or with their IR60b-expressing neurons selectively silenced - showed much reduced rejection of high Na+, but restored rejection when these channels were reintroduced back in the IR60b neurons; 2) animals with TRPV artificially expressed in their IR60b neurons rejected capsaicin-laced food whereas WT did not; 3) IR60b-expressing neurons exhibited increased Ca2+ influx in response to high Na+ and such response went away when animals lacked any of the three channels.

The experiments were thorough and well designed and further improved after revision. The results are compelling and support the main claim. The development and the use of the DrosoX two-choice assay put forward for a more quantitative and automatic/unbiased assessment for ingestion volume and preference.

Reviewer #2 (Public Review):

Summary:

In this paper, Sang et al. set out to identify gustatory receptors involved in salt taste sensation in Drosophila melanogaster. In a two-choice assay screen of 30 Ir mutants, they identify that Ir60b is required for avoidance of high salt. In addition, they demonstrate that activation of Ir60b neurons is sufficient for gustatory avoidance using either optogenetics or TRPV1 to specifically activate Ir60b neurons. Then, using tip recordings of labellar gustatory sensory neurons and proboscis extension response behavioral assays in Ir60b mutants, the authors demonstrate that Ir60b is dispensable for labellar taste neuron responses to high salt and the suppression of proboscis extension by high salt. Since external gustatory receptor neurons (GRNs) are not implicated, they look at Poxn mutants, which lack external chemosensory sensilla but have intact pharyngeal GRNs. High salt avoidance was reduced in Poxn mutants but was still greater than Ir60b mutants, suggesting that pharyngeal gustatory sensory neurons alone are sufficient for high salt avoidance. The authors use a new behavioral assay to demonstrate that Ir60b mutants ingest a higher volume of sucrose mixed with high salt than control flies do, suggesting that the action of Ir60b is to limit high salt ingestion. Finally, they identify that Ir60b functions within a single pair of gustatory sensory neurons in the pharynx, and that these neurons respond to high salt but not bitter tastants.

Strengths:

A great strength of this paper is that it rigorously corroborates previously published studies that have implicated specific Irs in salt taste sensation. It further introduces a new role for Ir60b in limiting high salt ingestion, demonstrating that Ir60b is necessary and sufficient for high salt avoidance and convincingly tracing the action of Ir60b to a particular subset of gustatory receptor neurons. Overall the authors have achieved their aim by identifying a new gustatory receptor involved in limiting high salt ingestion. They use rigorous genetic, imaging, and behavioral studies to achieve this aim, often confirming a given conclusion with multiple experimental approaches. They have further done a great service to the field by replicating published studies and corroborating the roles of a number of other Irs in salt taste sensation.

Reviewer #3 (Public Review):

Sang et al. successfully demonstrate that a set of single sensory neurons in the pharynx of Drosophila promotes avoidance of food with high salt concentrations, complementing previous findings on Ir7c neurons with an additional internal sensing mechanism. The experiments are well-conducted and presented, convincingly supporting their important findings and extending the understanding of internal sensing mechanisms.

The authors convincingly demonstrate the avoidance phenotype using different behavioral assays, thus comprehensively analyzing different aspects of the behavior. The experiments are straightforward and well-contextualized within existing literature.

Reviewer #3 (Public Review):

Summary:

The authors found two endosomal fusion modes by live cell imaging of endosomes in yolk sac lateral endoderm cells of 8.5-day-old embryonic mice and described the fusion modes by mathematical models and simulations. They also showed that actin polymerization is involved in the regulation of one of the fusion modes.

Strengths:

The strength of this study is that the authors' claims are well supported by beautiful live cell images and theoretical models. By using specialized cells, yolk sac visceral endoderm cells, the live images of endosomal fusion, localization of actin-related molecules, and validation data from multiple inhibitor experiments are clear.

Weaknesses:

This study does not include any assessment of whether the two types of endosome fusions claimed by the authors occur in general cells, so the article is limited to showing a phenomenon specific to yolk sac lateral endoderm cells. Also, the study does not show the physiological importance of the two types of fusion. There are some unclear points in the method of image analysis and some of the descriptions in the text are not logical.

Reviewer #1 (Public Review):

Summary:

This manuscript employs yolk sac visceral endoderm cells as a novel model for studying endosomal fusion, observing two distinct fusion behaviors: quick homotypic fusion between late endosomes, and slower heterotypic fusion between late endosomes and lysosomes. The mathematical modeling suggests that vesicle size critically influences the mode of fusion. Further investigations reveal that actin filaments are dynamically associated with late endosomal membranes, and are oriented in the x-y plane and along the apical-basal axis. Actin and Arf2/3 were shown to appear at the rear end of the endosomes along the moving direction suggesting polymerization of actin may provide force for the movement of endosomes. Additionally, the authors found that actin dynamics regulate homotypic and heterotypic fusion events in a different manner. The authors also provide evidence to suggest that Cofilin-dependent actin dynamics are involved in late endosome fusion.

Strengths:

The unique feature of this study is that the authors use yolk sac visceral endoderm cells to study endosomal fusion. Yolk sac visceral endoderm cells have huge endocytic vesicles, endosomes, and lysosomes, offering an excellent system to explore endosomal fusion dynamics and the assembly of cellular factors on membranes. The manuscript provides a valuable and convincing observation of the modes of endosomal fusion and the roles of actin dynamics in this process, and the conclusions of the study are justified by the data.

Weaknesses:

While the study offers compelling observations, it falls short of delivering clear mechanistic insights. Key questions remain unaddressed, such as the functional significance of actin filaments that extend apically in positioning late endosomes, the ways in which actin dynamics influence fusion events, and the functional implications of the slower bridge fusion process.

Reviewer #2 (Public Review):

Summary:

Seiichi Koike et al. studied two fusion models, explosive fusion, and bridge fusion, utilizing yolk sac visceral endoderm cells. They elucidated these two fusion models in vivo by employing mathematical modeling and incorporating fluctuations derived from actin dynamics as a key regulator for rapid homotypic fusion between late endosomes.

Strengths:

This study uncovered the role of actin dynamics in regulating the transition of fusion models in homotypic fusion between late endosomes and introduced a method for observing the fusion of single vesicles with two different targets. The role of actin dynamics in vesicle fusion in other systems has been extensively studied. This study could offer useful insights for research on vesicle fusion.

Weaknesses:<br /> The physiological significance of different fusion models is lacking.

Joint Public Review:

The present study focuses on the structure and function of human PURA, a regulator of gene transcription and mRNA transport and translation whose mutation causes the neurodevelopmental PURA syndrome, characterized by developmental delay, intellectual disability, hypotonia, epileptic seizures, a.o. deficits. The authors combined structural biology, molecular dynamics simulation, and various cell biological assays to study the effects of disease-causing PURA mutations on protein structure and function. The corresponding data reveal a highly dynamic PURA structure and show that disease-related mutations in PURA cause complex defects in folding, DNA-unwinding activity, RNA binding, dimerization, and partitioning into processing bodies. These findings provide first insights into how very diverse PURA mutations can cause penetrant molecular, cellular, and clinical defects. This will be of substantial interest to cell biologists, neurogeneticists, and neurologists alike.

A particular strength of the present study is the structural characterization of human PURA, which is a challenging target for structural biology approaches. The molecular dynamics simulations are state-of-the-art, allowing a statistically meaningful assessment of the differences between wild-type and mutant proteins. The functional consequences of PURA mutations at the cellular level are fascinating, particularly the differential compartmentalization of wild-type and mutant PURA variants into certain subcellular condensates.

Reviewer #4 (Public Review):

Summary:

Walker et al. investigated the function of TMEM127 on RET regulation and function that could contribute to the development of pheochromocytoma (PCC). The authors showed that deletion of TMEM127 causes RET protein accumulation on the cell surface and, thereby, increased its constitutive ligand-independent activity and downstream signaling. They also unveiled the mechanism of how TMEM127 regulates cell membrane dynamics, particularly focusing on clathrin distribution and its effects on cargo internalization.

Strengths:

They showed that the deletion of TMEM127 affected multiple classes of transmembrane proteins, including RTKs (RET, EGFR), cell adhesion molecules (N-Cadherin, Integrin Beta-3), and carrier proteins (Transferrin Receptor-1), suggesting a global effect on cell surface proteins. This, at least in part, may explain how TMEM127 mutations act as drivers in PCC as well as in other cancers, such as renal cell carcinoma, where RET is not highly expressed. Overall, these findings provide new insights into the understanding of pheochromocytoma pathogenesis and potentially other cancers.

Weaknesses:

The major weakness of this study is the lack of human PCC cell lines for evaluating the function of TMEM127. Currently, the cell line models for pheochromocytoma are unavailable, and manipulation of patient-derived organoids is challenging. To complement this weakness, they provided immunohistochemical data showing that RET protein is highly expressed in TMEM127-mutant PCC.

Furthermore, some of the authors in this manuscript recently published a paper titled 'TMEM127 suppresses tumor development by promoting RET ubiquitination, positioning, and degradation' (Guo et al. Cell Reports 42, 113070, 2023, which is also cited in the current manuscript). In this manuscript, they showed that TMEM127 binds to RET and recruits the NEDD4 E3 ubiquitin ligase for RET ubiquitination and degradation via TMEM127. In general, the ubiquitination of proteins is highly specific to each molecule. In the current version of the manuscript, there is no description of the relevance between these two potentially different mechanisms (clathrin-mediated or ubiquitin-mediated) of accumulating RET and/or other proteins mentioned in two separate papers. I believe the authors should at least discuss this.

Reviewer #5 (Public Review):

Summary:

The manuscript by Walker et al., nicely demonstrated a role of TMEM127 in regulating membrane dynamics of RET, a receptor tyrosine kinase and oncogene for multiple cancers, particularly in pheochromocytoma (PCC). They provided compelling cellular and biochemical evidence on how TMEM127 deficiency reduces RET internalization and degradation in specific cancer cell lines, thus stabilizing cell surface RET and promoting its signaling related to cell proliferation. Moreover, TMEM127 may have a broad function beyond RET, and may affect other surface protein activity such as EGFR etc. These findings provided novel mechanisms and key insights to the field of cancer biology.

Strengths:

Very interesting findings that nicely explained the mechanistic link between TMEM127 and tumorigenesis by RET regulation...the biochemical analysis was quite thorough and impressive.... the general messages delivered by this study are considered as important to the field of TMEM127 biology and tumorigenesis.

Weaknesses:

As acknowledged by the authors, the role of TMEM127 can be conditional and beyond RET modulation, the authors may need to include more discussion that why the loss of TMEM127 is more linked to the development of PCC compared to other cancer types, and why TMEM127 can have such a broad effects in those membrane molecules...in addition, TMEM127 deficiency has been recently linked to enhanced MHC-I-mediated tumor immunity and tumor eradication, in some cancer types...it is then worthwhile to discuss the dual effects of TMEM127 in tumor control in the context of immunity...<br /> Moreover, the authors may need to tune down their "ligand independent" claim on the loss of TMEM127 in driving RET signaling, which should be more related to the level of RET expression/strength of clustering...

Reviewer #2 (Public Review):

The manuscript from deHaro-Arbona et al, entitled "Dynamic modes of Notch transcription hubs conferring memory and stochastic activation revealed by live imaging the co-activator Mastermind", uses single molecule microscopy imaging in live tissues to understand the dynamics and molecular determinants of transcription factor recruitment to the E(spl)-C locus in Drosophila salivary gland cells under Notch-ON and -OFF conditions. Previous studies have identified the major players that are involved in transcription regulation in the Notch pathway, as well as the importance of general transcriptional coregulators, such as CBP/P300 and the Mediator CDK module, but the detailed steps and dynamics involved in these processes are poorly defined. The authors present a wealth of single molecule data that provides significant insights into Notch pathway activation, including:

(1) Activation complexes, containing CSL and Mam, have slower dynamics than the repressor complexes, containing CSL and Hairless.<br /> (2) Contribution of CSL, NICD, and Mam IDRs to recruitment.<br /> (3) CSL-Mam slow-diffusing complexes are recruited and form a hub of high protein concentrations around the target locus in Notch-ON conditions.<br /> (4) Mam recruitment is not dependent on transcription initiation or RNA production.<br /> (5) CBP/P300 or its associated HAT activity is not required for Mam recruitment<br /> (6) Mediator CDK module and CDK8 activity is required for Mam recruitment, and vice-versa, but not CSL recruitment.<br /> (7) Mam is not required for chromatin accessibility but is dependent on CSL and NICD.<br /> (8) CSL recruitment and increased chromatin accessibility persist after NICD removal and loss of Mam, which confers a memory state that enables rapid re-activation in response to subsequent Notch activation<br /> (9) Differences in the proportions of nuclei with both Pol II and with Mam enrichment, which results in transcription being probabilistic/stochastic. These data demonstrate that presence of Mam-complexes is not sufficient to drive all the steps required for transcription in every Notch-ON nucleus.<br /> (10) The switch from more stochastic to robust transcription initiation was elicited when ecdysone was added.

Overall, the manuscript is well written, concise, and clear, and makes significant contributions to the Notch field, which are also important for a general understanding of transcription factor regulation and behavior in the nucleus. The authors have satisfactorily addressed all my criticisms of their initial submission and therefore congratulate the authors on an excellent paper.

Reviewer #3 (Public Review):

Summary:

DeHaro-Arbona and colleagues investigate the in vivo dynamics of Notch-dependent transcriptional activation with a focus on the role of the Mastermind (MAM) transcriptional co-activator. They use GFP and HALO-tagged versions of the CSL DNA-binding protein and MAM to visualize the complex, and Int/ParB to visualize the site of Notch-dependent E(Spl)-C transcription. They make several conclusions. First, MAM accumulates at E(Spl)-C when Notch signaling is active, just like CSL. Second, MAM recruits the CDK module of Mediator but does not initiate chromatin accessibility. Third, after signaling is turned off, MAM leaves the site quickly but CSL and chromatin accessibility are retained. Fourth, RNA pol II recruitment, Mediator recruitment and active transcription were similar and stochastic. Fifth, ecdysone enhance the probability of transcriptional initiation.

Strengths:

The conclusions are well supported by multiple lines of extensive data that is carefully executed and controlled. A major strength is the strategic combination of Drosophila genetics, imaging and quantitative analyses to conduct compelling and easily interpretable experiments. A second major strength is the focus on MAM to gain insights into dynamics of transcriptional activation specifically.

Weaknesses:

Weaknesses were minor. and have been addressed in the revised manuscript.

Reviewer #1 (Public Review):

In this paper, N'Guessan et al report a study of expression QTL (eQTL) mapping in yeast using single cells. The authors make use of advances in single-cell RNAseq (scRNAseq) in yeast to increase the efficiency with which this type of analysis can be undertaken. Building on prior research led by the senior author that entailed genotyping and fitness profiling of almost 100,000 cells derived from a cross between two yeast strains (BY and RM) they performed scRNAseq on a subset of 4,489 individual cells. To address the sparsity of genotype data in the expression profiling they used a Hidden Markov Model (HMM) to infer genotypes and then identify the most likely known lineage genotype from the original dataset. To address the relationship between variance in fitness and gene expression the authors partition the variance to investigate the sources of variation. They then perform eQTL mapping and study the relationship between eQTL and fitness QTL identified in the earlier study.

This paper seeks to address the challenging question of how quantitative trait variation and expression variation are related. scRNAseq represents an appealing approach to eQTL mapping as it is possible to simultaneously genotype individual cells and measure expression in the same cell. As eQTL mapping requires large sample sizes to identify statistical relationships, this approach is likely to dramatically increase the statistical power of such studies. However, there are several technical challenges associated with scRNAseq and the authors' study is focused on addressing those challenges. Although the authors present results suggesting the feasibility of the approach there are limitations in the conclusions that can be drawn in the current study owing to the lack of clarity in the presentation of the results. Ultimately, this study presents a proof of concept with limited novel biological insights that would nonetheless make a useful contribution to the literature if the following major points were addressed:

(1) There is insufficient information provided about the nature of data. At a minimum, the following information should be provided to enable assessment of the study: What is the total library size, how many genes are identified per cell, how many UMIs are found per cell, what is the doublet rate, and how are doublets identified (e.g. on the basis of heterozygous calls at polymorphic loci?), how many times is each genotype observed, and how many polymorphic sites are identified per cell that are the basis of genotype inferences?

(2) The prior study analyzed 18 different conditions, whereas this study only assays expression in a single condition. However, the power of the authors' approach is that its efficiency enables testing eQTLs in multiple conditions. The study would be greatly strengthened through analysis of at least one more condition, and ideally several more conditions. The previous fitness study would be a useful guide for choosing additional conditions as identifying those conditions that result in the greatest contrasts in fitness QTL would be best suited to testing the generalizations that can be drawn from the study.

(3) Alternatively, the authors could demonstrate the power of their approach by applying it to a cross between two other yeast strains. As the cross between BY and RM has been exhaustively studied, applying this approach to a different cross would increase the likelihood of making novel biological discoveries.

(4) Figure 1 is misleading as A presents the original study from 2022 without important details such as how genotypes were identified. It is unclear what the barcode is in this study and how it is used in the analysis. Is the barcode for each lineage transcribed so that it is identified in the scRNAseq data? Or, does the barcode in B refer to the cell index barcode? A clearer presentation and explanation of terms are needed to understand the method.

(5) The rationale for the analysis reported in Figure 2B is unclear. The fitness data are from the previous study and the goal is to estimate the heritability using the genotyping data from the scRNAseq data. What is the explanation for why the data don't agree for only one condition, i.e. 37C? And, what are we to understand from the overall result?

(6) Figure 3 presents an analysis of variance partitioning as a Venn diagram. This summarized result is very hard to understand in the absence of any examples of what the underlying raw data look like. For example, what does trait variation look like if only genotype explains the variance or if only gene expression explains the variance? The presented highly summarized data is not intuitive and its presentation is poor - the result that is currently provided would be easier to read in a table format, but the reader needs more information to be able to interpret and understand the result.

(7) I am concerned about the conclusions that can be drawn about expression heritability. The authors claim that expression heritability is correlated with expression levels. It seems likely that this reflects differing statistical power. How can this possibility be excluded?

(8) Conversely, the authors claim that the genes with the lowest heritability are genes involved in the cell cycle. However, uniquely in scRNAseq, cell cycle regulated genes appear to have the highest variance in the data as they are only expressed in a subset of cells. Without incorporating this fact one would erroneously conclude that the variation is not heritable. To test the heritability of cell cycle regulation genes the authors should partition the cells into each cell cycle stage based on expression.

(9) I do not understand Figure S5 and how eQTL sites are assigned to these specific classes given that the authors say that causative variation cannot be resolved because of linkage disequilibrium.

(10) The paragraph starting at line 305 is very confusing. In particular, the authors state that they identify a hotspot of regulation at the mating type locus. It is not obvious why this would be the case. Moreover, they claim that they find evidence for both MATa and MATalpha gene expression. Information is not provided about how segregants were isolated, but assuming that the authors did not dissect 25,000 tetrads to obtain 100,000 segregants I would infer that random spore using SGA was used. In that case, all cells should be MATa. The authors should clarify and explain this observation.

(11) Ultimately, it is not clear what new biological findings the authors have made. There are no novel findings with respect to causative variation underlying eQTLs and I would encourage the authors to make clearer statements in their abstract, introduction, and conclusion about the key discoveries. E.g. What are the "new associations between phenotypic and transcriptomic variations" mentioned in the abstract?

The following minor points should be addressed:

(1) The segregants should be referred to as F2 segregants as they are derived from an F1 cross.

(2) The connections to eQTLs in other organisms should be addressed in the introduction and conclusion. For example, in humans, there has been little evidence for trans eQTLs in contrast to what has been found in yeast.

(3) The authors state that an advantage of scRNAseq over bulk is that it captures rare cell populations (line 79), but this advantage is not exploited in this study.

(4) The authors use ~5% of the lineages from the original study. There is no rationale for why this is an appropriate sample size. Is there an argument for using more cells in eQTL mapping or conversely could the authors ask if fewer cells would provide similar conclusions by downsampling?

(5) I do not agree that the use of UMIs overcomes the challenges of low sequencing depth. UMIs mitigate the possible technical artifacts due to massive PCR amplification.

(6) There is an inadequate reference to prior work on scRNAseq in yeast that established the methods used by the authors and eQTL mapping in human cells using scRNAseq.

(7) The use of empty quotes in Figure 4A is confusing and an alternative presentation method should be used.

(8) The authors speculate about the use of predicted fitness instead of observed fitness, but this is something they could explicitly address in their current study.

Reviewer #2 (Public Review):

Summary:

The experiments and analysis appear to be carefully done. My concerns center on the impact of the work in its current form on the research community.

The focal yeast cross here has been the subject of many previous publications (for smaller sets of recombinant progeny), by the last author and others, including phenotyping, genotyping, transcriptomics, and proteomics. This mini-literature has proven relevant to the community because it has empirically pinpointed exactly how many variants underlie a given trait, both molecular and cellular. That is, whereas in more complex organisms we try our best to estimate/infer the full genetic architecture of varying traits from the results of mapping of necessarily weaker power, the highly-powered yeast system can access a more comprehensive mapping of the dozens of loci impinging on a given trait and learn from it. The question is what exactly we learn from the current study?

Strengths and weaknesses:

Most of the figures center on methods development and validation for the authors' single-cell RNA-seq in the yeast cross, including generating the large raw data set; analysis pipelines for mapping and genotyping (Figure 1); and higher-level analyses that recapitulate previously reported trends in heritability (Figure 2) and eQTL mapping (Figure 3 and Figure 4B-C). One potential novelty of the study is the methods per se: that is, showing that scRNA-seq works for concomitant genotyping and gene expression profiling in the natural variation context. The authors' rigor and effort notwithstanding: in my view, this can be described as modest in terms of principles. That is, the authors did a good job putting the scRNA-seq idea into practice, but their success is perhaps not surprising or highly relevant for work outside of yeast (as the discussion says). The more substantive claim by the authors for the impact of the study is that they make new observations about the role of expression in phenotype (lines 333-335). The major display item of the manuscript on this theme is Figure 4A, reporting which loci that control growth phenotype (from an earlier paper) also control expression. This is solid but I regret to say that the results strike me as modest. The discussion makes some perhaps fairly big claims that the work has helped "bridge understanding of how genetic variation influences transcriptomic variation" and ultimately cellular phenotype. But with the data as they stand, the authors have missed an opportunity to crystallize exactly how a given variant affects expression (perhaps in waves of regulators affecting targets that affect more regulators) and then phenotype, except for the speculations in the text on lines 305-319. The field started down this road years ago with Bayesian causality inference methods applied to eQTL and phenotype mapping (via e.g. the work of Eric Schadt). The authors could now try Mendelian randomization-type fine-grained detailed models for more firepower toward the same end, and/or experimental tests of the genotype-to-expression-to-phenotype relationship. I would see these directions, motivated by fundamental questions that are relevant to the field at large, as leading to a major advance for this very crowded field. As it stands, I felt their absence in this manuscript especially if the authors are selling principles about linking expression and phenotype as their take-home. I also wonder whether the co-mapping of expression and growth traits in Figure 4A would have been possible with e.g. the bulk RNA-seq from Albert et al., 2018, and I recommend that the authors repeat the Figure 4A-type analyses with the latter to justify their statement that their massive scRNA data set would actually be necessary for them to bear fruit (lines 386-388).

I also read the discussion of the manuscript as bringing to the fore some of the challenges a reader has in judging the current state of the results to be of actionable impact. The discussion, and the manuscript, will be improved if the authors can put the work in context, posing concrete questions from the field and stating how they are addressed here and what's left to do.

Reviewer #1 (Public Review):

Summary:

This is an experimentally soundly designed work and a very well-written manuscript. There is a very clear logic that drives the reader from one experiment to the next, the experimental design is clearly explained throughout and the relevance of the acquired data is well analyzed and supports the claims made by the authors. The authors made an evident effort to combine imaging, genetic, and molecular data to describe previously unknown early embryonic movement patterns and to identify regulatory mechanisms that control several aspects of it.

Strengths:

The authors develop a new method to analyze, quantitatively, the onset of movement during the latter embryonic stages of Drosophila development. This setup allows for a high throughput analysis of general movement dynamics based on the capture of variations of light intensity reflected by the embryo. This setup is capable of imaging several embryos simultaneously and provides a detailed measure of movement over time, which proves to be very useful for further discoveries in the manuscript. This setup already provides a thorough and quantifiable description of a process that is little known and identifies two different phases during late embryonic movements: a myogenic phase and a neurogenic phase, which they elegantly prove is dependent on neuronal activity by knocking down action potentials across the nervous system.

However, in this system, movement is detected as a whole, and no further description of the type of movement is provided beyond frequency and amplitude; it would be interesting to know from the authors if a more precise description of the movements that take place at this stage can be achieved with this method (e.g. motion patterns across the A-P body axis).

Importantly, this highly quantitative experimental setup is an excellent system for performing screenings of motion regulators during late embryonic development, and its use could be extended to search for different modulators of the process, beyond miRNAs (genetic mutants, drugs, etc.).

Using their newly established motion detection pipeline, the authors identify miR-2b-1 as required for proper larval and embryonic motion, and identify an overall reduction in the quantity of both myogenic and neurogenic movements, as well as an increased frequency in neurogenic movement "pulses".

Focusing on the neurogenic movement phenotype the authors use in situ probes and perform RT-PCR on FACS-sorted CNS cells to unambiguously detect miR-2b-1 expression in the embryonic nervous system. The neurogenic motion defects observed in miR-2b-1 mutant embryos and early larvae can be completely rescued by the expression of ectopic miR-2b-1 specifically in the nervous system, providing solid evidence of the requirement and sufficiency of miR-2b-1 expressed in the nervous system to regulate these phases of movement.

To explore the mechanism through which miR-2b-1 impacts embryonic movement, the authors use a state-of-the-art bioinformatic approach to identify potential targets of miR-2b-1, and find that the expression levels of an uncharacterized gene, CG3638, are indeed regulated by miR-2b-1. Furthermore, they prove that by knocking down the expression of CG3638 in a miR-2b-1 mutant background, the neurogenic embryonic movement defects are rescued, pointing that the repression of CG3638 by miR-2b-1 is necessary for correct motion patterns in wild-type embryos. Therefore, this paper provides the first functional characterization of CG3638, and names this gene Janus.

Finally, the authors aim to discriminate which elements of the embryonic motor system miR-2b-1/Janus are required. Using directed overexpression of miR-2b-1 and Janus knockdown in the motor neurons and the chordotonal (sensory) organs, they prove that the miR-2b-1/Janus regulatory axis is specifically required in the sensory organs to promote normal embryonic and larval movement.

Weaknesses:

The authors do not describe properly how the miRNA screening was performed and just claim that only miR-2b-1 mutants presented a defective motion phenotype in early L1. How many miRNAs were tested, and how candidates were selected is never explicitly mentioned in the text or the Methods section.

The initial screening to identify miRNAs involved in motion behaviors is performed in early larval movement. The logic presented by the authors is clear - it is assumed that early larval movement cannot proceed normally in the absence of previous embryonic motion - and ultimately helped them identify a miRNA required for modulation of embryonic movement. However, it is possible that certain miRNAs play a role in the modulation of embryonic movement while being dispensable for early L1 behaviors. Such regulators might have been missed with the current screening setup.

Although similar changes to those described for the neurogenic phase of embryonic movement are described for the myogenic phase in miR-2b-1 mutants (reduction in motion amplitude), this phenotype goes unexplored. This is not a big issue, as the authors convincingly demonstrate later that miR-2b-1 is specifically required in the nervous system for proper embryonic and larval movement, and the effects of miR-2b-1 on myogenic movement might as well be the focus of future work. However, it will be interesting to discuss here the implications of a reduced myogenic movement phase, especially as miR-2b-1 is specifically involved in regulating the activity of the chordotonal system - which precisely detects early myogenic movements.

FACS-sorting of neuronal cells followed by RT-PCR convincingly detects the presence of miR-2b-1 in the embryonic CNS. However, control of non-neuronal cells would be required to explore whether miR-2b-1 is not only present but enriched in the nervous system compared to other tissues. This is also the case in the miR-2b-1 and Janus expression analysis in the chordotonal organs: a control sample from the motor neurons would help discriminate whether miR-2b-1/Janus regulatory axis is specifically enriched in chordotonal organs or whether both genes are expressed throughout the CNS but operate under a different regulation or requirements for the movement phenotypes.

Reviewer #2 (Public Review):

Summary:<br /> The manuscript, "A microRNA that controls the emergence of embryonic movement" by Menzies, Chagas, and Alonso provides evidence that Drosophila miR-2b-1 is expressed in neurons and controls the expression of the predicted chloride channel CG3638, here named "Janus". Loss of the miRNA leads to movement phenotypes that can be rescued by downregulation of Janus; using specific drivers, the authors show that a larval movement phenotype (slower movement) can be rescued by knockdown of Janus in the chordotonal organs, suggesting that the increase in Janus found in the chordotonal organs is likely the root of the movement defects. Overall, I found the data presented in the manuscript of reasonable quality and are well enough supported by the presented data. That being said, I do have a few problems with the manuscript, mostly stemming from what I feel is an inflated presentation of the importance of the findings.

Strengths:<br /> The genetic and phenotypic analysis seems to be correct. The nicest part of the manuscript is the connection between the loss of a miRNA and finding its likely target in generating a phenotype. The authors also develop some protocols for the analysis of the movement phenotypes which may be useful for others.

Weaknesses:<br /> As I mentioned above, I felt the presentation was a bit overstated. The authors present their data in a way that focuses on movement, the emergence of movement, and how their miRNA of interest is at the center of this topic. I only point to the title and name that they wish to give the target of their miRNA to emphasize this point. "Janus" the god of movement and change. The results and discussion section starts with a paragraph saying, "Movement is the main output of the nervous system... how developing embryos manage to organise the necessary molecular, cellular, and physiological processes to initiate patterned movement is still unknown. Although it is clear that the genetic system plays a role, how genes control the formation, maturation and function of the cellular networks underlying the emergence of motor control remains poorly understood." While there is nothing inherently untrue about these statements, it is a question of levels of understanding. One can always argue that something in biology is still unknown at a certain level. However, one could also argue that much is known about the molecular nature of movement. Next, I am not sure how much this work impacts the area of study regarding the emergence of movement. The authors show that a reduction of a miRNA can affect something about certain neurons, that affects movement. The early movements, although slightly diminished, still emerge. Thus, their work only suggests that the function of some neurons, or perhaps the development of these neurons may impact the early movements. This is not new as it was known already from early work from the Bate lab.

Later larval movements were also shown to be modified in the miRNA mutants and were traced to "janus" overexpression in the chordotonal organs. As neurons are quite sensitive to the levels of Cl- and Janus is thought to be a Cl- channel, this could lead to a slight dysfunction of the chordotonal neurons. So, based on this, the work suggests that dysfunction of the chordotonal organs could impact larval movement. This was, of course, already known. The novelty of this work is in the genes being studied (important or not). We now know that miR 2b-1 and Janus are expressed in the early neurons and larval chordotonal neurons and their removal is consistent with a role for these genes in the functioning of these neurons. This is not to trivialize these findings, simply to state that these results are not significantly changing our overall understanding of movement and the emergence of movement. I would call it a stretch to say that this miRNA 'controls' the emergence of movement, as in the title.

Finally, the name Janus should be changed as it is already being used. A quick scan of flybase shows that there is a Janus A and B in flies (phosphatases) and I am surprised the authors did not check this. I was initially worried about the Janus kinase (JAK) when I performed the search. While I understand that none are only called Janus, studies of the jan A and B genes refer to the locus as the janus region, which could lead to confusion. The completely different molecular functions of the genes relative to CG3638 add to the confusion. Thus, I ask that the authors change the name of CG3638 to something else.

Reviewer #1 (Public Review):

This work provides new mechanistic insights into the competitive inhibition in the mammalian P2X7 receptors using structural and functional approaches. The authors solved the structure of panda (pd) P2X7 in the presence of the classical competitive antagonists PPNDS and PPADS. They find that both the drugs bind to the orthosteric site employed by the physiological agonist ATP. However, owing to the presence of a single phosphate group, they prevent movements in the flipper domain required for channel opening. The authors performed structure based mutational analysis together with electrophysiological characterization to understand the subtype specific binding of these drugs. It is known from previous studies that P2X1 and P2X3 are more sensitive to these drugs as compared to P2X7, hence, the residues adjacent to the ATP binding site in pdP2X7 were mutated to those present in P2X1. They observed that mutations of Q143, I214 and Q248 into lysine (hP2X1) increased the P2X7 sensitivity to PPNDS, whereas in P2X1, mutations of these lysines to alanine reduced sensitivity to PPNDS, suggesting that these key residues contribute to the subunit specific sensitivity to these drugs. Similar experiments were done in hP2X3 to demonstrate its higher sensitivity to PPNDS. This preprint provides a useful framework for developing subtype specific drugs for the family of P2X receptor channels, an area that is currently relatively unexplored.<br /> The conclusions of the paper are well supported.

The revised manuscript is well written and presents its data with more clarity.

Reviewer #2 (Public Review):

Summary:

P2X receptors play pivotal roles in physiological processes such as neurotransmission and inflammation, making them promising drug targets. This study, through cryo-EM and functional experiments, reveals the structural basis of the competitive inhibition of the PPNDS and PPADS on mammalian P2X7 receptors. Key findings include the identification of the orthosteric site for these antagonists, the revelation of how PPADS/PPNDS binding impedes channel-activating conformational changes, and the pinpointing of specific residues in P2X1 and P2X3 subtypes that determine their heightened sensitivity to these antagonists. These insights present a comprehensive understanding that could guide the development of improved drugs targeting P2X receptors. This work will be a valuable addition to the field.

Strengths:

The combination of structural experiments and mutagenesis analyses offers a deeper understanding of the mechanism. While the inclusion of MD simulation is appreciated, providing more insights from the simulation might further strengthen this already compelling story.

Reviewer #1 (Public Review):

Summary:

The manuscript describes the crystal structures of Streptococcus pneumoniae NOXs. Crystals were obtained for the wild-type and mutant dehydrogenase domain, as well as for the full-length protein comprising the membrane domain. The manuscript further carefully studies the enzyme's kinetics and substrate-specificity properties. Streptococcus pneumoniae NOX is a non-regulated enzyme, and therefore, its structure should provide a view of the NOX active conformation. The structural and biochemical data are discussed on this ground.

Strengths:

This is very solid work. The protein chemistry and biochemical analysis are well executed and carefully described. Similarly, the crystallography must be appreciated given the difficulty of obtaining good enzyme preparations and the flexibility of the protein. Even if solved at medium resolution, the crystal structure of the full-length protein conveys relevant information. The manuscript nicely shows that the domain rotations are unlikely to be the main mechanistic element of NOX regulation. It rather appears that the NADPH-binding conformation is pivotal to enzyme activation. The paper extensively refers to the previous literature and analyses the structures comprehensively with a comparison to previously reported structures of eukaryotic and prokaryotic NOXs.

Reviewer #2 (Public Review):

The authors describe the structure of the S. pneumoniae Nox protein (SpNOX). This is a first. The relevance of it to the structure and function of eukaryotic Noxes is discussed in depth.

One of the strengths of this work is the effort put into preparing a pure and functionally active SpNOX preparation. The protein was expressed in E. coli and the purification and optimization of its thermostability and activity are described in detail, involving salt concentration, glycerol concentration, and pH.

Comments on revised version:

This reviewer would like to compliment the authors for the conscientious revision of the manuscript. Their response to the comments and the detailed explanations of the issues that did not appear clear enough to the reviewer are much appreciated. Their reaction to the review was not only superbly competent but also prominently good natured.

The revised version is perfect and represents a major contribution to our understanding of the molecular details of Nox function. As for the questions not yet answered, I shall quote the authors: "Time will tell".

Reviewer #2 (Public Review):

Summary:

In this paper, the authors set out to better understand the mechanism by which the FtsZ-associated protein ZapD crosslinks FtsZ filaments to assemble a large scale cytoskeletal assembly. For this aim, they use purified proteins in solution and a combination of biochemical, biophysical experiments and cryo-EM. The most significant finding of this study is the observation of FtsZ toroids that form at equimolar concentrations of the two proteins.

Strengths:

Many experiments in this paper confirm previous knowledge about ZapD. For example, it shows that ZapD promotes the assembly of FtsZ polymers, that ZapD bundles FtsZ filaments, that ZapD forms dimers and that it reduces FtsZ's GTPase activity.

The most novel discovery is the observation of different assemblies as a function of ZapD:FtsZ ratio. In addition, using CryoEM to describe the structure of toroids and bundles, the papers provides some information about the orientation of ZapD in relation to FtsZ filaments. For example, they found that the organization of ZapD in relation to FtsZ filaments is "intrinsic heterogeneous" and that FtsZ filaments were crosslinked by ZapD dimers pointing in all directions. The authors conclude that it is this plasticity that allows for the formation of toroids and its stabilization. Unfortunately, a high-resolution structure of the protein organization was not possible.

Weaknesses:

While the data is convincing, their interpretation has some substantial weaknesses that the authors should address for the final version of this paper.

For example, as the authors are the first to describe FtsZ-ZapD toroids, a discussion why this has not been observed in previous studies would be very interesting, i.e. is it due to buffer conditions, sample preparation?

At parts of the manuscript, the authors try a bit too hard to argue for the physiological significance of these toroids. This, however, is at least very questionable, because:<br /> The typical diameter is in the range of 0.25-1.0 μm, which requires some flexibility of the filaments to be able to accommodate this. It's difficult to see how a FtsZ-ZapD toroid, which appears to be quite rigid with a narrow size distribution of 502 nm {plus minus} 55 nm could support cell division rather than stalling it at that cell diameter. which the authors say is similar to the E. coli cell.

For cell division, FtsZ filaments are recruited to the membrane surface via an interaction of FtsA or ZipA the C-terminal peptide of FtsZ. As ZapD also binds to this peptide, the question arises who wins this competition or where is ZapD when FtsZ is recruited to the membrane surface? Can such a toroidal structure of FtsZ filaments form on the membrane surface? Additional experiments would be helpful, but a more detailed discussion on how the authors think ZapD could act on membrane-bound filaments would be essential.

The authors conclude that the FtsZ filaments are dynamic, which is essential for cell division. But the evidence for dynamic FtsZ filaments within these toroids seems rather weak, as it is solely the partial reassembly after addition of GTP. As ZapD significantly slows down GTP hydrolysis, I am not sure it's obvious to make this conclusion.

On a similar note, on page 5 the authors claim that ZapD would transiently interact with FtsZ filaments. What is the evidence for this? They also say that this transient interaction could have a "mechanistic role in the functionality of FtsZ macrostructures." Could they elaborate?

The author should also improve in putting their findings into the context of existing knowledge. For example:

The authors observe a straightening of filament bundles with increasing ZapD concentration. This seems consistent with what was found for ZapA, but this is not explicitly discussed (Caldas et al 2019)

A paragraph summarizing what is known about the properties of ZapD in vivo would be essential: i.e. what has been found regarding its intracellular copy number, location and dynamics?

In the introduction, the authors write that "GTP binding and hydrolysis induce a conformational change in each monomer that modifies its binding potential, enabling them to follow a treadmilling behavior". This seems inaccurate, as shown by Wagstaff et al. 2022, the conformational change of FtsZ is not associated with the nucleotide state. In addition, they write that FtsZ polymerization depends on the GTPase activity. It would be more accurate to write that polymerization depends on GTP, and disassembly on GTPase activity.

On page 2 they also write that "the mechanism underlying bundling of FtsZ filaments is unknown". I would disagree, the underlying mechanism is very well known (see for example Schumacher, MA JBC 2017), but how this relates to the large-scale organization of FtsZ filaments was not clear.

The authors describe the toroid as a dense 3D mesh, how would this be compatible with the Z-ring and its role for cell division? I don't think this corresponds to the current model of the Z-ring (McQuillen & Xiao, 2020). Apart from the fact it's a ring, I don't think the organization of FtsZ obviously similar to the current of the Z-ring in the bacterial cell, in particular because it's not obvious how FtsZ filaments can bind ZapD and membrane anchors simultaneously.

The authors write that "most of these modulators" interact with FtsZ's CTP, but then later that ZapD is the only Zap protein that binds CTP. This seems to be inconsistent. Why not write that membrane anchors usually bind the CTP, most Zaps do not, but ZapD is the exception?

I also have some comments regarding the experiments and their analysis:

Regarding cryoET: the filaments appear like flat bands, even in the absence of ZapD, which further elongates these bands. Is this due to an anisotropic resolution? This distortion makes the conclusion that ZapD forms bi-spherical dimers unconvincing.

The authors say that the cryoET visualization provides crucial information on the length of the filaments within this toroid. How long are they? Could the authors measure it?

Regarding the dimerization mutant of ZapD: there is actually no direct confirmation that mZapD is monomeric. Did the authors try SEC MALS or AUC? Accordingly, the statement that dimerization is "essential" seems exaggerated (although likely true).

What do the authors mean that toroid formation is compatible with robust persistence length? I.e. What does robust mean? It was recently shown that FtsZ filaments are actually surprisingly flexible, which matches well the fact that the diameter of the Z-ring must continuously decrease during cell division (Dunajova et al Nature Physics 2023).

the authors claim that their observations suggest „that crosslinkers ... allows filament sliding in an organized fashion". As far as I know there is no evidence of filament sliding, as FtsZ monomers in living cells and in vitro are static.

What is the „proto-ring FtsA protein"?

The authors refer to „increasing evidence" for „alternative network remodling mechanisms that do not rely on chemical energy consumption as those in which entropic forces act through diffusible crosslinkers, similar to ZapD and FtsZ polymers." A reference should be given, I assume the authors refer to the study by Lansky et al 2015 of PRC on microtubules. However, I am not sure how the authors made the conclusion that this applies to FtsZ and ZapD, on which evidence is this assumption based?

Some inconsistencies in supplementary figure 3: The normalized absorbances in panel a do not seem to agree with the absolute absorbance shown in panel e, i.e. compare maximum intensity for ZapD = 20 µM and 5 µM in both panels.

It's not obvious to me why the structure formed by ZapD and FtsZ disassembles after some time even before GTP is exhausted, can the authors explain? As the structures disassemble, how is the "steady-state turbidity" defined? Do the structures also disassemble when they use a non-hydrolyzable analog of GTP?

Conclusion:

Despite some weaknesses in the interpretation of their findings, I think this paper will likely motivate other structural studies on large scale assemblies of FtsZ filaments and its associated proteins. A systematic comparison of the effects of ZapA, ZapC and ZapD and how their different modes of filament crosslinking can result in different filament networks will be very useful to understand their individual roles and possible synergistic behavior.

Reviewer #1 (Public Review):

Summary:

The major result in the manuscript is the observation of the higher order structures in a cryoET reconstruction that could be used for understanding the assembly of toroid structures. The cross-linking ability of ZapD dimers result in bending of FtsZ filaments to a constant curvature. Many such short filaments are stitched together to form a toroid like structure. The geometry of assembly of filaments - whether they form straight bundles or toroid like structures - depends on the relative concentrations of FtsZ and ZapD.

Strengths:

In addition to a clear picture of the FtsZ assembly into ring-like structures, the authors have carried out basic biochemistry and biophysical techniques to assay the GTPase activity, the kinetics of assembly, and the ZapD to FtsZ ratio.

Weaknesses:

The discussion does not provide an overall perspective that correlates the cryoET structural organisation of filaments with the biophysical data.

The crosslinking nature of ZapD is already established in the field. The work carried out is important to understand the ring assembly of FtsZ. However, the availability of the cryoET observations can be further analysed in detail to derive many measurements that will help validate the model, and obtain new insights.

Reviewer #3 (Public Review):

Summary:

The authors provide the first image analysis by cryoET of toroids assembled by FtsZ crosslinked by ZapD. Previously toroids of FtsZ alone have been imaged only in projection by negative stain EM. The authors attempt to distinguish ZapD crosslinks from the underlying FtsZ filaments. I did not find this distinction convincing, especially because it seems inconsistent with the 1:1 stoichiometry demonstrated by pelleting. I was intrigued by one image showing straight filament pairs, which may suggest a new model for how ZapD crosslinks FtsZ filaments.

Strengths:

(1) The first image analysis of FtsZ toroids by cryoET.<br /> (2) The images are accompanied by pelleting assays that convincingly establish a 1:1 stoichiometry of FtsZ:ZapD subunits.<br /> (3) Fig. 5 shows an image of a pair of FtsZ filaments crosslinked by ZapD. This seems to have higher resolution than the toroids. Importantly, it suggests a new model for the structure of FtsZ-ZapD that resolves previously unrecognized conflicts. (This is discussed below under weaknesses, because it is so far only supported by a single image.)

Weaknesses:

This paper reports a study by cryoEM of polymers and bundles assembled from FtsZ plus ZapD. Although previous studies by other labs have focused on straight bundles of filaments, the present study found toroids mixed with these straight bundles, and they focused most of their study on the toroids. In the toroids they attempt to delineate FtsZ filaments and ZapD crosslinks. A major problem here is with the stoichiometry. Their pelleting assays convincingly established a stoichiometry of 1:1, while the mass densities identified as ZapD are sparse and apparently well below the number of FtsZ (FtsZ subunits are not resolved in the reconstructions, but the continuous sheets or belts seem to have a lot more mass than the identified crosslinks.) Apart from the stoichiometry I don't find the identification of crosslinks to be convincing. It is missing an important control - cryoET of toroids assembled from pure FtsZ, without ZapD.

However, if I ignore these and jump to Fig. 5, I think there is an important discovery that resolves controversies in the present study as well as previous ones, controversies that were not even recognized. The controversy is illustrated by the Schumacher 2017 model (their Fig. 7), which is repeated in a simplified version in Fig. 1a of the present mss. That model has a two FtsZ filaments in a plane facing ZapD dimers which bridge them. In this planar model the C-terminal linker, and the ctd of FtsZ that binds ZapD facing each other and the ZapD in the middle, with. The contradiction arises because the C-terminus needs to face the membrane in order to attach and generate a bending force. The two FtsZ filaments in the planar model are facing 90{degree sign} away from the membrane. A related contradiction is that Houseman et al 2016 showed that curved FtsZ filaments have the C terminus on the outside of the curve. In a toroid the C termini should all be facing the outside. If the paired filaments had the C termini facing each other, they could not form a toroid because the two FtsZ filaments would be bending in opposite directions.

Fig. 5 of the present mss seems to resolve this by showing that the two FtsZ filaments and ZapD are not planar, but stacked. The two FtsZ filaments have their C termini facing the same direction, let's say up, toward the membrane, and ZapD binds on top, bridging the two. The spacing of the ctd binding sites on the Zap D dimer is 6.5 nm, which would fit the ~8 nm width of the paired filament complex observed in the present cryoEM (Fig S13). In the Schumacher model the width would be about 20 nm. Importantly, the stack model has the ctd of each filament facing the same direction, so the paired filaments could attach to the membrane and bend together (using ctd's not bound by ZapD). Finally, the new arrangement would also provide an easy way for the complex to extend from a pair of filaments to a sheet of three or four or more.

A problem with this new model from Fig. 5 is that it is supported by only a single example of the paired FtsZ-ZapD complex. If this is to be the basis of the interpretation, more examples should be shown. Maybe examples could be found with three or four FtsZ filaments in a sheet.

What then should be done with the toroids? I am not convinced by the identification of ZapD as "connectors." I think it is likely that the ZapD is part of the belts that I discuss below, although the relative location of ZapD in the belts is not resolved. It is likely that the resolution in the toroid reconstructions of Fig. 4, S8,9 is less than that of the isolated pf pair in Fig. 5c.

Importantly, If the authors want to pursue the location of ZapD in toroids, I suggest they need to compare their ZapD-containing toroids with toroids lacking ZapD. Popp et al 2009 have determined a variety of solution conditions that favor the assembly of toroids by FtsZ with no added protein crosslinker. It would be very interesting to investigate the structure of these toroids by the present cryoEM methods, and compare them to the FtsZ-ZapD toroids. I suspect that the belts seen in the ZapD toroids will not be found in the pure FtsZ toroids, confirming that their structure is generated by ZapD.

Reviewer #1 (Public Review):

Using a pharmacological and knock-down approach, the authors could demonstrate that ROCK activity is required for the normal development of the larval skeleton. The presence of ROCK in the pluteus stage depends on the activity of VEGF that is responsible for the formation of the tubular syncytial sheath of the calcifying primary mesenchyme cells in which the skeleton forms. The importance of ROCK in skeleton formation was confirmed in cell culture experiments, demonstrating that ROCK inhibition leads to decreased elongation and abnormal branching of spicules. µCT analyses underline this finding demonstrating that the inhibition of ROCK mainly affects elongation of spicules while growth in girth is little affected. F-actin labeling experiments could demonstrate that ROCK inhibition interferes with the organization of the actomyosin network in the early phase of skeleton formation, while f-actin organization in the tips of the elongating spicule is unaffected by the pharmacological inhibition of ROCK. Finally, ROCK inhibition strongly affects the expression of major regulatory and calcification-related genes in the calcifying cells. Based on these findings the authors propose a model for the regulatory interaction between the skeletogenic GRN, ROCK and the f-actin system relevant for skeletogenesis.

Comments on revised version:

In their manuscript Hijaze et al. adequately addressed the majority of my previous concerns in a satisfactory manner. In particular, they validated their morpholino knock-down experiments by explaining how they determined the optimal concentrations and provided an immunohistological evidence for the reduction in ROCK protein abundance. The authors also added new antibody stainings providing evidence that ROCK and F-actin do not interact directly but likely through other kinases that modulate f-actin, and that the localization of f-actin at the spicule tips remains unaffected by the knock-down. In addition, the authors revised their discussion to not overstate their observations, and by focusing on the potential mechanisms by which ROCK may affect biomineralization (i.e. mechano sensing and exocytosis of vesicles). Here I would like to add, that f-actin mediated exocytosis does not necessarily target mineral baring vesicles but may also promote the exocytosis of matrix proteins that are essential for the normal formation of the spicules and that are an integral component of other biominerals, as well. I strongly encourage the authors to continue on this exciting research, including the development of methods to analyze the molecular mechanisms that control vesicular trafficking in mineralizing systems.

Reviewer #2 (Public Review):

This project is on the role of ROCK in skeletogenesis during sea urchin development. That skeleton is produced by a small number of cells in the embryo with signaling inputs from the ectoderm providing patterning cues. The skeleton is built from secretion of CaCO3 by the skeletogenic cells. The authors conclude that ROCK is involved in the regulation of skeletogenesis with a role both in regulating actomyosin in the process, and in the gene regulatory network (GRN) underlying the entire sequence of events.

The strength of the paper is that they show in detail how perturbations of ROCK results in abnormal actomyosin activity in the skeletogenic cells, and they show alterations both in expression of transcription factors of the GRN, and expression of genes involved in assembly of the skeletal matrix. Two different approaches lead to this conclusion: morpholino perturbations and the actions of a selective inhibitor of the kinase activity. Thus, they achieved their goal which was to test the hypothesis that ROCK is involved in the process of skeletogenesis. Those tests support the hypothesis with data that was quantitatively significant.

The discussion was transparent regarding where the analysis ended and where the next phase of work should begin. While actomyosin involvement was altered when ROCK was perturbed, it isn't known how direct or indirect the role of ROCK might be. Also, while the regulatory input to spicule initiation and growth is affected when ROCK is inhibited, it isn't clear exactly where ROCK is involved.

Reviewer #1 (Public Review):

Summary:

The authors want to understand fundamental steps in ligand binding to muscle nicotinic receptors using computational methods. Overall, although the work provides new information and support for existing models of ligand activation of this receptor type, some limitations in the methods and approach mean that the findings are not as conclusive as hoped.

Strengths:

The strengths include the number of ligands tried, and the comparison to the existing mature analysis of receptor function from the senior author's lab.

Weaknesses:

The weakness are the brevity of the simulations, the concomitant lack of scope of the simulations, the lack of depth in the analysis and the incomplete relation to other relevant work. The free energy methods use seem to lack accuracy - they are only correct for 2 out of 4 ligands.

Reviewer #2 (Public Review):

Summary:

The aim of this manuscript is to use molecular dynamics (MD) simulations to describe the conformational changes of the neurotransmitter binding site of a nicotinic receptor. The study uses a simplified model including the alpha-delta subunit interface of the extracellular domain of the channel and describes the binding of four agonists to observe conformational changes during the weak to strong affinity transition.

Strength:

The 200 ns-long simulations of this model suggest that the agonist rotates about its centre in a 'flip' motion, while loop C 'flops' to restructure the site. The changes appear to reproduced across simulations and different ligands and are thus a strong point of the study.

Weaknesses:

After carrying out all-atom molecular dynamics, the authors revert to a model of binding using continuum Poisson-Boltzmann, surface area and vibrational entropy. The motivations for and limitations associated with this approximate model for the thermodynamics of binding, rather than using modern atomistic MD free energy methods (that would fully incorporate configurational sampling of the protein, ligand and solvent) could be provided. Despite this, the authors report correlation between their free energy estimates and those inferred from experiment. This did, however, reveal shortcomings for two of the agonists. The authors mention their trouble getting correlation to experiment for Ebt and Ebx and refer to up to 130% errors in free energy. But this is far worse than a simple proportional error, because -24 Vs -10 kcal/mol is a massive overestimation of free energy, as would be evident if it the authors were to instead to express results in terms of KD values (which would have error exceeding a billion fold). The MD analysis could be improved with better measures of convergence, as well as more careful discussion of free energy maps as function of identified principal components, as described below. Overall, however, the study has provided useful observations and interpretations of agonist binding that will help understand pentameric ligand-gated ion channel activation.

Main points:

Regarding the choice of model, some further justification of the reduced 2 subunit ECD-only model could be given. On page 5 the authors argue that, because binding free energies are independent of energy changes outside the binding pocket, they could remove the TMD and study only an ECD subunit dimer. While the assumption of distant interactions being small seems somewhat reasonable, provided conformational changes are limited and localised, how do we know the packing of TMD onto the ECD does not alter the ability of the alpha-delta interface to rearrange during weak or strong binding? They further write that "fluctuations observed at the base of the ECD were anticipated because the TMD that offers stability here was absent.". As the TMD-ECD interface is the "gating interface" that is reshaped by agonist binding, surely the TMD-ECD interface structure must affect binding. It seems a little dangerous to completely separate the agonist binding and gating infrastructure, based on some assumption of independence. Given the model was only the alpha and delta subunits and not the pentamer with TMD, I am surprised such a model was stable without some heavy restraints. The authors state that "as a further control we carried out MD simulation of a pentamer docked with ACh and found similar structural changes at the binding pocket compared to the dimer." Is this sufficient proof of the accuracy of the simplified model? How similar was the model itself with and without agonist in terms of overall RMSD and RMSD for the subunit interface and the agonist binding site, as well as the free energy of binding to each model to compare?

Although the authors repeatedly state that they have good convergence with their MD, I believe the analysis could be improved to convince us. On page 8 the authors write that the RMSD of the system converged in under 200 ns of MD. However, I note that the graph is of the entire ECD dimer, not a measure for the local binding site region. An additional RMSD of local binding site would be much more telling. You could have a structural isomerisation in the site and not even notice it in the existing graph. On page 9 the authors write that the RMSF in Fig.S2 showed instability mainly in loops C and F around the pocket. Given this flexibility at the alpha-delta interface, this is why collecting those regions into one group for the calculation of RMSD convergence analysis would have been useful. They then state "the final MD configuration (with CCh) was well-aligned with the CCh-bound cryo-EM desensitized structure (7QL6)... further demonstrating that the simulation had converged." That may suggest a change occurred that is in common with the global minimum seen in cryo EM, which is good, but does not prove the MD has "converged". I would also rename Fig.S3 accordingly.

The authors draw conclusions about the dominant states and pathways from their PCA component free energy projections that need clarification. It is important first to show data to demonstrate that the two PCA components chosen were dominant and accounted for most of the variance. Then when mapping free energy as a function of those two PCA components, to prove that those maps have sufficient convergence to be able to interpret them. Moreover, that if the free energies themselves cannot be used to measure state stability (as seems to be the case), that the limitations are carefully explained. First, was PCA done on all MD trajectories combined to find a common PC1 & PC2, or were they done separately on each simulation? If so, how similar are they? The authors write "the first two principal components (PC-1 and PC-2) that capture the most pronounced C. displacements". How much of the total variance did these two components capture? The authors write the changes mostly concern loop C and loop F, but which data proves this? e.g. A plot of PC1 and PC2 over residue number might help?

The authors map the -kTln rho as a free energy for each simulation as function of PC1 & PC2. It is important to reveal how well that PC1-2 space was sampled, and how those maps converged over time. The shapes of the maps and the relative depths of the wells look very different for each agonist. If the maps were sampled well and converged, the free energies themselves would tell us the stabilities of each state. Instead, the authors do not even mention this and instead talk about "variance" being the indicator of stability, stating that m3 is most stable in all cases. While I can believe 200ns could not converge a PC1-2 map and that meaningful delta G values might not be obtained from them, the issue of lack of sampling must be dealt with. On page 12 they write "Although the bottom of the well for 3 energy minima from PCA represent the most stable overall conformation of the protein, they do not convey direct information regarding agonist stability or orientation". The reasons why not must be explained; as they should do just that if the two order parameters PC1 and PC2 captured the slowest degrees of freedom for binding and sampling was sufficient. The authors write that "For all agonists and trajectories, m3 had the least variance (was most stable), again supporting convergence by 200 ns." Again the issue of actual free energy values in the maps needs to be dealt with. The probabilities expressed as -kTln rho in kcal/mol might suggest that m2 is the most stable. Instead, the authors base stability only on variance (I guess breadth of the well?), where m3 may be more localised in the chosen PC space, despite apparently having less preference during the MD (not the lowest free energy in the maps).

The motivations and justifications for use of approximate PBSA energetics instead of atomistic MD free energies should be dealt with in the manuscript, with limitations more clearly discussed. Rather than using modern all-atom MD free energy methods for relative or absolute binding free energies, the author select clusters from their identified states and do Poisson-Boltzmann estimates (electrostatic, vdW, surface area, vibrational entropy). I do believe the following sentence does not begin to deal with the limitations in that method: "there are limitations with regard to MM-PBSA accurately predicting absolute binding free energies (Genheden & Ryde, 2015; Hou et al., 2011) that depends on parameterization of the ligand (Oostenbrink et al., 2004)." What are the assumptions and limitations in taking a continuum electrostatics (presumably with parameters for dielectric constants and their assignments to regions after discarding solvent), surface area (with its assumptions and limitations) and of course assuming vibration of a normal mode can capture entropy. On page 30, regarding their vibrational entropy estimate, they write that the "entropy term provides insights into the disorder within the system, as well as how this disorder changes during the binding process". It is important that the extent of disorder captured by the vibrational estimate be discussed, as it is not obvious that it has captured entropy involving multiple minima on the system's true 3N-dimensional energy surface, and especially the contribution from solvent disorder in bound Vs dissociated states.

As discussed above, errors in the free energy estimates need to be more faithfully represented, as fractional errors are not meaningful. On page 21 the authors write "The match improved when free energy ratios rather than absolute values were compared." But a ratio of free energies is not a typical or expected measure of error in delta G. They also write "For ACh and CCh, there is good agreement between.Gm1 and GLA and between.Gm3 and GHA. For these agonists, in silico values overestimated experimental ones only by ~8% and ~25%. The agreement was not as good for the other 2 agonists, as calculated values overestimated experimental ones by ~45%(Ebt) and ~130% (Ebt). However, the fractional overestimation was approximately the same for GLA and GHA." See above comment on how this may misrepresent the error. On page 21 they write, in relation to their large fractional errors, that they "do not know the origin of this factor but speculate that it could be caused by errors in ligand parameterization". But the estimates from the PBSA approach are, by design, only approximate. Both errors in parameterisation (and their likely origin) and the approximate model used, need discussion.

Reviewer #3 (Public Review):

Summary:

The authors use docking and molecular dynamics (MD) simulations to investigate transient conformations that are otherwise difficult to resolve experimentally. The docking and simulations suggest an interesting series of events whereby agonists initially bind to the low affinity site and then flip 180 degrees as the site contracts to its high affinity conformation. This work will be of interest to the ion channel community and to biophysical studies of pentameric ligand-gated channels.

Strengths:

I find the premise for the simulations to be good, starting with an antagonist bound structure as an estimate of the low affinity binding site conformation, then docking agonists into the site and using MD to allow the site to relax to a higher affinity conformation that is similar to structures in complex with agonists. The predictions are interesting and provide a view into what a transient conformation that is difficult to observe experimentally might be like.

Weaknesses:

A weakness is that the relevance of the initial docked low affinity orientations depend solely on in silco results, for which simulated vs experimental binding energies deviate substantially for two of the four ligands tested. This raises some doubt as to the validity of the simulations. I acknowledge that the calculated binding energies for two of the ligands were closer to experiment, and simulated efficiencies were a good representation of experimental measures, which gives some support to the relevance of the in silico observations. Regardless, some of the reviewers comments regarding the simulation methodology were not seriously addressed.

Reviewer #4 (Public Review):

Summary:

In their revised manuscript "Conformational dynamics of a nicotinic receptor neurotransmitter binding site," Singh and colleagues present molecular docking and dynamics simulations to explore the initial conformational changes associated with agonist binding in the muscle nicotinic acetylcholine receptor, in context with the extensive experimental literature on this system. Their central findings are of a consistently preferred pose for agonists upon initial association with a resting channel, followed by a dramatic rotation of the ligand and contraction of a critical loop over the binding site. Principal component analysis also suggests the formation of an intermediate complex, not yet captured in structural studies. Binding free energy estimates are consistent with the evolution of a higher-affinity complex following agonist binding, with a ligand efficiency notably similar to experimental values. Snapshot comparisons provide a structural rationale for these changes on the basis of pocket volume, hydration, and rearrangement of key residues at the subunit interface.

Strengths:

Docking results are clearly presented and remarkably consistent. Simulations are produced in triplicate with each of four different agonists, providing an informative basis for internal validation. They identify an intriguing transition in ligand pose, not well documented in experimental structures, and potentially applicable to mechanistic or even pharmacological modeling of this and related receptor systems. The paper seems a notable example of integrating quantitative structure-function analysis with systematic computational modeling and simulations, likely applicable to the wider journal audience.

Weaknesses:

The response to initial review is somewhat disappointing, declining in some places to implement suggested clarifications, and propagating apparent errors in at least one table (Fig 2-source data 1). Some legends (e.g. Fig 2-supplement 4, Fig 3, Fig 4) and figure shadings (e.g. Fig 2-supplement 2, Fig 6-supplement 2) remain unclear. Apparent convergence of agonist-docked simulations towards a desensitized state (l 184) is difficult to interpret in absence of comparative values with other states, systems, etc. In more general concerns, aside from the limited timescales (200 ns) that do not capture global rearrangements, it is not obvious that landscapes constructed on two principal components to identify endpoint and intermediate states (Fig 3) are highly robust or reproducible, nor whether they relate consistently to experimental structures.

Reviewer #1 (Public Review):

Summary:

The work by Joseph et al "Impact of the clinically approved BTK inhibitors on the conformation of full-length BTK and analysis of the development of BTK resistance mutations in chronic lymphocytic leukemia" seeks to comparatively analyze the effect of a range of covalent and noncovalent clinical BTK inhibitors upon BTK conformation. The novel aspect of this manuscript is that it seeks to evaluate the differential resistance mutations that arise distinctly from each of the inhibitors.

Strengths:

This is an exciting study that builds upon the fundamental notion of ensemble behavior in solutions for enzymes such as BTK. The HDX-MS and NMR experiments are adequately and comprehensively presented.

Weaknesses:

While I commend the novelty of the study, the absence of important controls greatly tempers my enthusiasm for this work. As stated in the abstract, there are no broad takeaways for how resistance mutation bias operated from this study, although the mechanism of action of 2 common resistance mutations is useful. How these 2 resistance mutations connect to ensemble behavior, is not obvious. This is partly because BTK does not populate just binary "open"/"closed" conformations, but there are likely multiple intermediate conformations. Each inhibitor appears to preferentially "select" conformations by the authors' own assessment (line 236) and this carries implications for the emergence of resistance mutations. The most important control that would help is to use ADP or nonhydrolyzable and ATP as a baseline to establish the "inactive" and "active" conformations. All of the HDX-MS and NMR studies use protein that has no nucleotide present. A major question that remains is whether each of the inhibitors preferentially favors/blocks ADP or ATP binding. This then means it is not equivalent to correlate functional kinase assay conditions with either HDX-MS or NMR experiments.

Reviewer #2 (Public Review):

Summary:

Previous NMR and HDX-MS studies on full-length (FL) BTK showed that the covalent BTKi, ibrutinib, causes long-range effects on the conformation of BTK consistent with disruption of the autoinhibited conformation, based on HDX deuterium uptake patterns and NMR chemical shift perturbations. This study extends the analyses to four new covalent BTKi, acalabrutinib, zanubrutinib, tirabrutinib/ONO4059, and a noncovalent ATP competitive BTKi, pirtobrutinib/LOXO405.

The results show distinct conformational changes that occur upon binding each BTKi. The findings show consistent NMR and HDX changes with covalent inhibitors, which move helix aC to an 'out' position and disrupt SH3-kinase interactions, in agreement with X-ray structures of the BTKi complexed with the BTK kinase domain. In contrast, the solution measurements show that pirtobrutinib maintains and even stabilizes the helix aC-in and autoinhibited conformation, even though the BTK:pritobrutinib crystallizes with helix aC-out. This and unexpected variations in NMR and HDX behavior between inhibitors highlight the need for solution measurements to understand drug interactions with the full-length BTK. Overall the findings present good evidence for allosteric effects by each BTKi that induce distal conformational changes which are sensitive to differences in inhibitor structure.

The study goes on to examine BTK mutants T474I and L528W, which are known to confer resistance to pirtobrutinib, zanubritinib, and tirabrutinib. T474I reduces and L528W eliminates BTK autophosphorylation at pY551, while both FL-BTK-WT and FL-BTK-L528W increase HCK autophosphorylation and PLCg phosphorylation. These show that mutants partially or completely inactivate BTK and that inactive FL-BTK can activate HCK, potentially by direct BTK-HCK interactions. But they do not explain drug resistance. However, HDX and NMR show that each mutant alters the effects of BTKi binding compared to WT. In particular, T474I alters the effects of all three inhibitors around W395 and the activation loop, while L528W alters interactions around W395 with tirabrutinib and pirtobrutinib, and does not appear to bind zanubrutinib at all. The study concludes that the mutations might block drug efficacy by reducing affinity or altering binding mode.

Strengths:

The work presents convincing evidence that BTK inhibitors alter the conformation of regions distal to their binding sites, including those involved in the SH3-kinase interface, the activation loop, and a substrate binding surface between helix aF and helix aG. The findings add to the growing understanding of allosteric effects of kinase inhibitors, and their potential regulation of interactions between kinase and binding proteins.

Weaknesses:

The interpretation of HDX, NMR, and kinase assays is confusing in some places, due to ambiguity in quantifying how much kinase is bound to the inhibitor. It would be helpful to confirm binding occupancy, in order to clarify if mutants lower the amount of BTK complexed with BTKi as implied in certain places, or if they instead alter the binding mode. In addition, the interpretation of the mutant effects might benefit from a more detailed examination of how each inhibitor occupies the ATP pocket and how substitutions of T474 and L528 with Ile and Trp respectively might change the contacts with each inhibitor.

Reviewer #1 (Public Review):

The Calcium Homeostasis Modulators (CALHM) are a family of large pore channels, of which the physiological role of CALHM1 and 3 is well understood, in particular their key role in taste sensation via the release of the neurotransmitter ATP. The activation mechanism of CALHM1 involves membrane depolarization and a decrease in extracellular Ca concentration, allowing the passage of large cellular metabolites. However, the activation mechanism and physiological roles of other family members are much less well understood. Many structures of homomeric CALHM proteins have been determined, revealing distinct oligomeric assemblies despite a common transmembrane domain topology. CALHM1 and 3 have been shown functionally to form heteromeric assemblies with properties distinct from those of homomeric CALHM1. However, the structural basis of heteromeric CALHM1 and 3 remains unexplored.

In this paper, Drozdzyk et al. present an important study on the structures of heteromeric channels composed of CALHM2 and CALHM4, extending the structural understanding of the CALHM family beyond homomeric channels. The study relies primarily on cryo-EM. Despite the inherent challenges of structural determination due to the similar structural features of CALHM2 and CALHM4, the authors innovatively use synthetic nanobodies to distinguish between the subunits. Their results show a broad distribution of different heteromeric assemblies, with CALHM4 conformation similar to its homomeric form and CALHM2 conformation influenced by its proximity to CALHM4, and provide detailed insights into the interaction between CALHM2 and CALHM4.

The manuscript is well-structured and presents clear results that support the conclusions drawn. The discovery of heteromeric CALHM channels, although currently limited to an overexpressed system, represents a significant advance in the field of large-pore channels and will certainly encourage further investigation into the physiological relevance and roles of heteromeric CALHM channels. The manuscript would benefit from further insight into the functional properties of these heteromeric channels. However, this is not a weakness as the identification of precise activation stimuli for CALHM2 and 4 is beyond the scope of this work.

A challenge noted is the wide distribution of heteromeric assemblies in the 3D classification, resulting in insufficient particles for high-resolution structure determination of each assembly. The authors choose to combine particles from assemblies with 2-4 copies of CALHM4, which reveals the interface between CALHM2 and 4 but may compromise the quality of structural details. I recommend an alternative data processing strategy. First, refine particles with 2-4 CALHM4 subunits with symmetry imposed. This is followed by symmetry expansion, signal subtraction of two adjacent subunits, and subsequent classification and refinement of the subtracted particles. This approach, while not guaranteed, can potentially provide a clearer definition of CALHM2 and CALHM4 interfaces and show whether CALHM2 subunits adopt different conformations based on their proximity to CALHM4 subunits.

Reviewer #2 (Public Review):

Summary:

The authors identified that two of the placental CALHM orthologs, CALHM2 and CALHM4 can form heterooligomeric channels that are stable following detergent solubilization. By adding fiducial markers that specifically recognize either CALHM2 or CALHM4, the authors determine a cryo-EM density map of heterooligomeric CALHM2/CALHM4 from which they can determine how the channel is assembled. Surprisingly, the two orthologs segregate into two distinct segments of the channel. This segregation enables the interfacial subunits to ease the transition between the preferred conformations of each ortholog, which are similar to the confirmation that each ortholog adopts in homooligomeric channels.

Strengths:

Through the use of fiducial markers, the authors can clearly distinguish between the CALHM2 and CALHM4 promoters in the heterooligomeric channels, strengthening their assignment of most of the promoters. The authors take appropriate caution in identifying two subunits that are likely a mix of the two orthologs in the channel.

Weaknesses:

Despite the authors' efforts, no currents could be observed that corresponded to CALHM2/CALHM4 channels and thus the functional effect of their interaction is not known.

Reviewer #1 (Public Review):

Summary:

This paper shows that E. coli exhibits a chemotactic response to potassium by measuring both the motor response (using a bead assay) and the intracellular signaling response (CheY phosporylation level via FRET) to step changes in potassium concentration. They find increase in potassium concentration induces a considerable attractant response, with amplitude comparable to aspartate, and cells can quickly adapt (and generally over-adapt). The authors propose that the mechanism for potassium response is through modifying intracellular pH; they find both that potassium modifies pH and other pH modifiers induce similar attractant responses. It is also shown, using Tar- and Tsr-only mutants, that these two chemoreceptors respond to potassium differently. Tsr has a standard attractant response, while Tar has a biphasic response (repellent-like then attractant-like). Finally, the authors use computer simulations to study the swimming response of cells to a periodic potassium signal secreted from a biofilm and find a phase delay that depends on the period of oscillation.

Strengths:

The finding that E. coli can sense and adapt to potassium signals and the connection to intracellular pH is quite interesting and this work should stimulate future experimental and theoretical studies regarding the microscopic mechanisms governing this response. The evidence (from both the bead assay and FRET) that potassium induces an attractant response is convincing, as is the proposed mechanism involving modification of intracellular pH. The updated manuscript controls for the impact of pH on the fluorescent protein brightness that can bias the measured FRET signal. After correction the response amplitude and sharpness (hill coefficient) are comparable to conventional chemoattractants (e.g. aspartate), indicating the general mechanisms underlying the response may be similar. The authors suggest that the biphasic response of Tar mutants may be due to pH influencing the activity of other enzymes (CheA, CheR or CheB), which will be an interesting direction for future study.

Weaknesses:

The measured response may be biased by adaptation, especially for weak potassium signals. For other attractant stimuli, the response typically shows a low plateau before it recovers (adapts). In the case of potassium, the FRET signal does not have an obvious plateau following the stimuli of small potassium concentrations, perhaps due to the faster adaptation compared to other chemoattractants. It is possible cells have already partially adapted when the response reaches its minimum, so the measured response may be a slight underestimate of the true response. Mutants without adaptation enzymes appear to be sensitive to potassium only at much larger concentrations, where the pH significantly disrupts the FRET signal; more accurate measurements would require development of new mutants and/or measurement techniques.

Reviewer #2 (Public Review):

Zhang et al investigated the biophysical mechanism of potassium-mediated chemotactic behavior in E coli. Previously, it was reported by Humphries et al that the potassium waves from oscillating B subtilis biofilm attract P aeruginosa through chemotactic behavior of motile P aeruginosa cells. It was proposed that K+ waves alter PMF of P aeruginosa. However, the mechanism was this behaviour was not elusive. In this study, Zhang et al demonstrated that motile E coli cells accumulate in regions of high potassium levels. They found that this behavior is likely resulting from the chemotaxis signalling pathway, mediated by an elevation of intracellular pH. Overall, a solid body of evidence is provided to support the claims. However, the impacts of pH on the fluorescence proteins need to be better evaluated. In its current form, the evidence is insufficient to say that the fluoresce intensity ratio results from FRET. It may well be an artefact of pH change.

The authors now carefully evaluated the impact of pH on their FRET sensor by examining the YFP and CFP fluorescence with no-receptor mutant. The authors used this data to correct the impact of pH on their FRET sensor. This is an improvement, but the mathematical operation of this correction needs clarification. This is particularly important because, looking at the data, it is not fully convincing if the correction was done properly. For instance, 3mM KCl gives 0.98 FRET signal both in Fig3 and FigS4, but there is almost no difference between blue and red lines in Fig 3. FigS4 is very informative, but it does not address the concern raised by both reviewers that FRET reporter may not be a reliable tool here due to pH change.

The authors show the FRET data with both KCl and K2SO4, concluding that the chemotactic response mainly resulted from potassium ions. However, this was only measured by FRET. It would be more convincing if the motility assay in Fig1 is also performed with K2SO4. The authors did not address this point. In light of complications associated with the use of the FRET sensor, this experiment is more important.

Reviewer #1 (Public Review):

Summary:

This paper provides a straightforward mechanism of how mycobacterial cAMP level is increased under stressful conditions and shows that the increase is important for the survival of the bacterium in animal hosts. The cAMP level is increased by decreasing the expression of an enzyme that degrades cAMP.

Strengths:

The paper shows that under different stresses the response regulator PhoP represses a phosphodiesterase (PDE) that degrades cAMP specifically. Identification of<br /> PhoP as a regulator of cAMP is significant progress in understanding Mtb pathogenesis, as increase in cAMP apparently increases bacterial survival upon infection. On the practical side, reduction of cAMP by increasing PDE can be a means to attenuate the growth of the bacilli. The results have wider implications since PhoP is implicated in controlling diverse mycobacterial stress responses and many bacterial pathogens modulate host cell cAMP level. The results here are straightforward, internally consistent, and of both theoretical and applied interests. The results also open considerable future work, especially how increases in cAMP level help to increase survival of the pathogen.

Weaknesses:

It is not clear whether PhoP-PDE Rv0805 is the only pathway to regulate cAMP level under stress.

Reviewer #2 (Public Review):

Summary: In the manuscript, the authors have presented new mechanistic details to show how intracellular cAMP levels are maintained linked to the phosphodiesterase enzyme which in turn is controlled by PhoP. Later, they showed the physiological relevance linked to altered cAMP concentrations.

Strengths: Well thought out experiments. The authors carefully planned the experiments well to uncover the molecular aspects of it diligently.

Weaknesses: Some fresh queries were made based on the author's previous responses and hope to get satisfactory answers this time.

Reviewer #1 (Public Review):

Summary:

This work describes the mechanism of protein disaggregation by the ClpL AAA+ protein of Listeria monocytogenes. Using several model subtrate proteins the authors first show that ClpL possesses a robust disaggregase activity that does not further require the endogenous DnaK chaperone in vitro. In addition, they found that ClpL is more thermostable than the endogenous L. monocytogenes DnaK and has the capacity to unfold tightly folded protein domains. The mechanistic basis for the robust disaggregase activity of ClpL was also dissected in vitro and in some cases, supported by in vivo data performed in chaperone-deficient E. coli strains. The data presented show that the two AAA domains, the pore-2 site and the N-terminal domain (NTD) of ClpL are critical for its disaggregase activity. Remarkably, grafting the NTD of ClpL to ClpB converted ClpB into an autonomous disaggregase, highlighting the importance of such a domain in the DnaK-independent disaggregation of proteins. The role of the ClpL NTD domain was further dissected, identifying key residues and positions necessary for aggregates recognition and disaggregation. Finally, using sets of SEC and negative staining EM experiments combined with conditional covalent linkages and disaggregation assays the authors found that ClpL shows significant structural plasticity, forming dynamic hexameric and heptameric active single rings that can further form higher assembly states via their middle domains.

Strengths:

The manuscript is well written and the experimental work well executed. It contains a robust and complete set of in vitro data that push further our knowledge of such important disaggregases. It shows the importance of the atypical ClpL N-terminal domain in the disaggregation process as well as the structural malleability of such AAA+ proteins. More generally, this work expands our knowledge of heat resistance in bacterial pathogens.

Weaknesses:

There is no specific weakness in this work, although it would have helped to have a drawing model showing how ClpL performs protein disaggregation based on their new findings. The function of the higher assembly states of ClpL remains unresolved and will need further extensive research. Similarly, it will be interesting in the future to see whether the sole function of the plasmid encoded ClpL is to cope with general protein aggregates under heat stress.

Reviewer #2 (Public Review):

The manuscript by Bohl et al. is an interesting and carefully done study on the biochemical properties and mode of action of potent autonomous AAA+ disaggregase ClpL from Listeria monocytogenes. ClpL is encoded on plasmids. It shows high thermal stability and provides Listeria monocytogenes food-pathogen substantial increase in resistance to heat. The authors show that ClpL interacts with aggregated proteins through the aromatic residues present in its N-terminal domain and subsequently unfolds proteins from aggregates translocating polypeptide chains through the central pore in its oligomeric ring structure. The structure of ClpL oligomers was also investigated in the manuscript. The results suggest that mono-ring structure and not dimer or tetramer of rings, observed in addition to mono-ring structures under EM, is an active specie of disaggregase. In the revised version additional data is presented suggesting that dimer or tetramer of ClpL rings play a protective role in cell by restricting ClpL activity.

Presented experiments are conclusive and well controlled. I think the presentation and discussion of results are better in revised version.<br /> The study's strength lies in the direct comparison of ClpL biochemical properties with autonomous ClpG disaggregase present in selected Gram-negative bacteria and well-studied E. coli system consisting of ClpB disaggregase and DnaK and its cochaperones. This puts the results in a broader context.

Reviewer #3 (Public Review):

Summary:

This manuscript details the characterization of ClpL from L. monocytogenes as a potent and autonomous AAA+ disaggregase. The authors demonstrate that ClpL has potent and DnaK-independent disaggregase activity towards a variety of aggregated model substrates, and that this disaggregase activity appears to be greater than that observed with the canonical DnaK/ClpB co-chaperone. Furthermore, LmClpL appears to have greater thermostability as compared to LmDnaK, suggesting that ClpL-expressing cells may be able to withstand more severe heat stress conditions. Interestingly, LmClpL can provide thermotolerance to E. coli that have been genetically depleted of either ClpB or in cells expressing a mutant DnaK103. The authors further characterized the mechanisms by which ClpL interacts with protein aggregates, identifying that the N-terminal domain of ClpL is essential for disaggregase function. Lastly, by EM and mutagenesis analysis the authors report that ClpL can exist in a variety of larger macromolecular complexes, including dimer or trimers of hexamers/heptamers, and they provide evidence that the N-terminal domains of ClpL prevent dimer ring formation, thus promoting an active and substrate-binding ClpL complex. Throughout this manuscript the authors compare LmClpL to ClpG, another potent and autonomous disaggregase found in gram-negative bacteria that has been reported on previously, demonstrating that these two enzymes share homologous activity and qualities. Taken together this report clearly establishes ClpL as a novel and autonomous disaggregase.

Analysis:

The work presented in this report amounts to a significant body of novel and significant work that will be of interest to protein chaperone community. Furthermore, by providing examples of how ClpL can provide in vivo thermotolerance to both E. coli and L. gasseri the authors have expanded the significance of this work and provides novel insight into potential mechanisms responsible for thermotolerance in food-borne pathogens. The figures are clearly depicted, well-labeled, and easy to understand, and the manuscript is well-written. Experimentally the work was performed to a high standard with excellent controls, aiding in the ability for the audience to understand the major findings and conclusions. Additionally, the authors have effectively and efficiently expanded on their work through the peer review process, further increasing the understandability and significance of their work. Overall, the data presented, and analysis thereof, support the authors' conclusions, and thus this study represents an important addition to our understanding of molecular chaperone biochemistry. Lastly, this study establishes new avenues for research into autonomous disaggregates, their role in in vivo thermotolerance, and the mechanisms by which AAA+ chaperones recognize and interact with substrate proteins.

Joint Public Review:

Summary:

Previously, this group showed that Tgfbr1 regulates the reorganization of the epiblast and primitive streak into the chordo-neural hinge and tailbud during the trunk-to-tail transition. Gdf11 signaling plays a crucial role in orchestrating the transition from trunk to tail tissues in vertebrate embryos, including the reallocation of axial progenitors into the tailbud and Tgfbr1 plays a key role in mediating its signaling activity. Progenitors that contribute to the extension of the neural tube and paraxial mesoderm into the tail are located in this region. In this work, the authors show that Tgfbr1 also regulates the reorganization of the posterior primitive streak/base of allantois and the endoderm as well.

By analyzing the morphological phenotypes and marker gene expression in Tgfbr1 mutant mouse embryos, they show that it regulates the merger of somatic and splanchnic layers of the lateral plate mesoderm, the posterior streak derivative. They also present evidence suggesting that Tgfbr1 acts upstream of Isl1 (key effector of Gdf11 signaling for controlling differentiation of lateral mesoderm progenitors) and regulates the remodelling of the major blood vessels, the lateral plate mesoderm and endoderm associated with the trunk-to-tail transition. Through a detailed phenotypic analysis, the authors observed that, similarly to Isl1 mutants, the lack of Tgfbr1 in mouse embryos hinders the activation of hindlimb and external genitalia maker genes and results in a failure of lateral plate mesoderm layers to converge during tail development. As a result, they interpret that ventral lateral mesoderm, which generates the peri cloacal mesenchyme and genital tuberculum, fails to specify.

They also show defects in the morphogenesis of the dorsal aorta at the trunk/tail juncture, resulting in an aberrant embryonic/extraembryonic vascular connection. Endoderm reorganization defects following abnormal morphogenesis of the gut tube in the Tgfbr1 mutants cause failure of tailgut formation and cloacal enlargement. Thus, Tgfbr1 activity regulates the morphogenesis of the trunk/tail junction and the morphogenetic switch in all germ layers required for continuing post-anal tail development. Taken together with the previous studies, this work places Gdf11/8 - Tgfbr1 signaling at the pivot of trunk-to-tail transition and the authors speculate that critical signaling through Tgfbr1 occurs in the posterior-most part of the caudal epiblast, close to the allantois.

Strengths:

The data shown is solid with excellent embryology/developmental biology. This work demonstrates meticulous execution and is presented in a comprehensive and coherent manner. Although not completely novel, the results/conclusions add to the known function of Gdf11 signaling during the trunk-to-tail transition.

Weaknesses:

The authors rely on the expression of a small number of key regulatory genes to interpret the developmental defects. The alternative possibilities remain to be ruled out thoroughly. The manuscript is also quite descriptive and would benefit from more focused highlighting of the novelty regarding the absence of Tgfbr1 in the mouse embryo. They should also strengthen some of their conclusions with more details in the results.

Reviewer #1 (Public Review):

Summary:<br /> In the present study, Rincon-Torroella et al. developed ME3BP-7, a microencapsulated formulation of 3BP, as an agent to target MCT1 overexpressing PDACs. They provided evidence showing the specific killing of PDAC cells with MCT1 overexpressing in vitro, along with demonstrating the safety and anti-tumor efficacy of ME3BP-7 in PDAC orthotopic mouse models.

Strengths:<br /> * Developed a novel agent.<br /> * Well-designed experiments and an organized presentation of data that support the conclusions drawn.

Weaknesses:<br /> There are some minor issues that could enhance the clarity and completeness of the study:

(1) Statistical results should be visually presented in Figure 4 and Figure S1.

(2) Given the tumor heterogeneity and the identification of focal high expression of MCT1 in Figure 7 and Figure S5B, it is suggested that the authors include the results of immunohistochemical (IHC) analysis of MCT1 expression in both control and ME3BP-7 treated tumor tissues. This addition may offer insight into whether the remaining tumors are composed of PDAC cells with negative MCT1 expression, while the cells with relatively high levels of MCT1 expression were eliminated by ME3BP-7 treatment.

(3.)The authors are encouraged to discuss the future directions for improving the efficacy of this study. For example, exploring the combination of ME3BP-7 with a glutaminase-1 inhibitor (PMID 37891897) could be a valuable avenue for further research.

Reviewer #2 (Public Review):

Summary:<br /> In the manuscript by Rincon-Torroella et al, the authors evaluated the therapeutic potential of ME3BP-7, a microencapsulated formulation of 3BP which specifically targets MCT-1 high tumor cells, in pancreatic cancer models. The authors showed that, compared to 3BP, ME3BP-7 exhibited much-enhanced stability in serum. In addition, the authors confirmed the specificity of ME3BP-7 toward MCT-1 high tumor cells and demonstrated the in vivo anti-tumor effect of ME3BP-7 in orthotopic xenograft of human PDAC cell line and PDAC PDX model.

Strengths:<br /> (1) The study convincingly demonstrated the superior stability of ME3BP-7 in serum.<br /> (2) The specificity of ME3BP-7 and 3BP toward MCT-1 high PDAC cells was clearly demonstrated with CRISPR-mediated knockout experiments.

Weaknesses:<br /> The advantage of ME3BP-7 over 3BP under an in vivo situation was not fully established.

Reviewer #1 (Public Review):

Summary:

This work presents an in-depth characterization of the factors that influence the structural dynamics of the Clostridium botulinum guanidine-IV riboswitch (riboG). Using a single-molecule FRET, the authors demonstrate that riboG undergoes ligand and Mg2+ dependent conformational changes consistent with the dynamic formation of a kissing loop (KL) in the aptamer domain. Formation of the KL is attenuated by Mg2+ and Gua+ ligand at physiological concentrations as well as the length of the RNA. Interestingly, the KL is most stable in the context of just the aptamer domain compared to longer RNAs capable of forming the terminator stem. To attenuate transcription, binding of Gua+ and formation of the KL must occur rapidly after transcription of the aptamer domain but before transcription of the rest of the terminator stem.

Strengths:

(1) Single-molecule FRET microscopy is well suited to unveil the conformational dynamics of KL formation and the authors provide a wealth of data to examine the effect of the ligand and ions on riboswitch dynamics. The addition of complementary transcriptional readthrough assays provides further support for the author's proposed model of how the riboswitch dynamics contribute to function.

(2) The single-molecule data strongly support that the effect of Gua+ ligand and Mg2+ influence the RNA structure differently for varying lengths of the RNA. The authors also demonstrate that this is specific for Mg2+ as Na+ and K+ ions have little effect.

(3) The PLOR method utilized is clever and well adapted for both dual labeling of RNAs and examining RNA at various lengths to mimic co-transcriptional folding. Using PLOR, they demonstrate that a change in the structural dynamics and ligand binding can occur after the extension of the RNA transcript by a single nucleotide. Such a tight window of regulation has intriguing implications for kinetically controlled riboswitches.

Weaknesses:

(1) The authors use only one mutant to confirm that their FRET signal indicates the formation of the KL. Importantly, this mutation does not involve the nucleotides that are part of the KL interaction. It would be more convincing if the authors used mutations in both strands of the KL and performed compensatory mutations that restore base pairing. Experiments like this would solidify the structural interpretation of the work, particularly in the context of the full-length riboG RNA or in the co-transcriptional mimic experiments, which appear to have more conformational heterogeneity.

(2) The existence of the pre-folded state (intermediate FRET ~0.5) is not well supported in their data and could be explained by an acquisition artifact. The dwell times are very short often only a single frame indicating that there could be a very fast transition (< 0.1s) from low to high FRET that averages to a FRET efficiency of 0.5. To firmly demonstrate that this intermediate FRET state is metastable and not an artifact, the authors need to perform measurements with a faster frame rate and demonstrate that the state is still present.

(3) The PLOR method employs a non-biologically relevant polymerase (T7 RNAP) to mimic transcription elongation and folding near the elongation complex. T7 RNAP has a shorter exit channel than bacterial RNAPs and therefore, folding in the exit channel may be different between different RNAPs. Additionally, the nascent RNA may interact with bacterial RNAP differently. For these reasons, it is not clear how well the dynamics observed in the T7 ECs recapitulate riboswitch folding dynamics in bacterial ECs where they would occur in nature.

Reviewer #2 (Public Review):

Summary:

Gao et al. used single-molecule FRET and step-wise transcription methods to study the conformations of the recently reported guanidine-IV class of bacterial riboswitches that upregulate transcription in the presence of elevated guanidine. Using three riboswitch lengths, the authors analyzed the distributions and transitions between different conformers in response to different Mg2+ and guanidine concentrations. These data led to a three-state kinetic model for the structural switching of this novel class of riboswitches whose structures remain unavailable. Using the PLOR method that the authors previously invented, they further examined the conformations, ligand responses, and gene-regulatory outcomes at discrete transcript lengths along the path of vectorial transcription. These analyses uncover that the riboswitch exhibits differential sensitivity to ligand-induced conformational switching at different steps of transcription, and identify a short window where the regulatory outcome is most sensitive to ligand binding.

Strengths:

Dual internal labeling of long RNA transcripts remains technically very challenging but essential for smFRET analyses of RNA conformations. The authors should be commended for achieving very high quality and purity in their labelled RNA samples. The data are extensive, robust, thorough, and meticulously controlled. The interpretations are logical and conservative. The writing is reasonably clear and the illustrations are of high quality. The findings are significant because the paradigm uncovered here for this relatively simple riboswitch class is likely also employed in numerous other kinetically regulated riboswitches. The ability to quantitatively assess RNA conformations and ligand responses at multiple discrete points along the path towards the full transcript provides a rare and powerful glimpse into co-transcriptional RNA folding, ligand-binding, and conformational switching.

Weaknesses:

The use of T7 RNA polymerase instead of a near-cognate bacterial RNA polymerase in the termination/antitermination assays is a significant caveat. It is understandable as T7 RNA polymerase is much more robust than its bacterial counterparts, which probably will not survive the extensive washes required by the PLOR method. The major conclusions should still hold, as the RNA conformations are probed by smFRET at static, halted complexes instead of on the fly. However, potential effects of the cognate RNA polymerase cannot be discerned here, including transcriptional rates, pausing, and interactions between the nascent transcript and the RNA exit channel, if any. The authors should refrain from discussing potential effects from the DNA template or the T7 RNA polymerase, as these elements are not cognate with the riboswitch under study.

Reviewer #3 (Public Review):

Summary:

In this article, Gao et. al. uses single-molecule FRET (smFRET) and position-specific labelling of RNA (PLOR) to dissect the folding and behavioral ligand sensing of the Guanidine-IV riboswitch in the presence and absence of the ligand guanidine and the cation Mg2+. The results provided valuable information on the mechanistic aspects of the riboswitch, including the confirmation of the kissing loop present in the structure as essential for folding and riboswitch activity. Co-transcriptional investigations of the system provided key information on the ligand-sensing behavior and ligand-binding window of the riboswitch. A plausible folding model of the Guanidine-IV riboswitch was proposed as a final result. The evidence presented here sheds additional light on the mode of action of transcriptional riboswitches.

Strengths:

The investigations were very thorough, providing data that supports the conclusions. The use of smFRET and PLOR to investigate RNA folding has been shown to be a valuable tool for the understanding of folding and behavior properties of these structured RNA molecules. The co-transcriptional analysis brought important information on how the riboswitch works, including the ligand-sensing and the binding window that promotes the structural switch. The fact that investigations were done with the aptamer domain, aptamer domain + terminator/anti-terminator region, and the full-length riboswitch were essential to inform how each domain contributes to the final structural state if in the presence of the ligand and Mg2+.

Weaknesses:

The system has its own flaws when compared to physiological conditions. The RNA polymerase used (the study uses T7 RNA polymerase) is different from the bacterial RNA polymerase, not only in complexity, but also in transcriptional speed, which can directly interfere with folding and ligand-sensing. Additionally, rNTPs concentrations were much lower than physiological concentrations during transcription, likely causing a change in the polymerase transcriptional speed. These important aspects and how they could interfere with results are important to be addressed to the broad audience. Another point of consideration to be aware of is that the bulky fluorophores attached to the nucleotides can interfere with folding to some extent.