This manuscript is in revision at eLife

The decision letter after peer review, sent to the authors on June 17, 2020, follows.

The reviewers feel that while many comments were adequately addressed, several essential points remain problematic and do not support the conclusions of the manuscript. These include experiments with technical difficulties or uninterpretable results. If you are willing and able to address the reviewers' concerns you may resubmit a revised manuscript with a detailed rebuttal letter.

It is required that you address the following to be reconsidered for publication:

1) Additional NSC markers must be optimized. Dpn staining in some figures is unconvincing and must be verified using additional markers.

2) Cell markers routinely used by many labs must work (Wor, Ase, Elav).

3) Dpn is a reagent that works well and should be clear.

Please note that this decision letter does not guarantee that this manuscript will be accepted. At least one reviewer feels that their concerns were not addressed in the revised manuscript and that it is in everyone's best interests that the authors can prove that the inability to provide the appropriate expression patterns is not indicative of a deeper problem with the underlying hypothesis.

1) Major comment. The main conclusion of the paper (glia transform into NSCs which produce neurons) but is not supported by data: only one NSC marker used out of many available. The authors tried two additional NSC markers but did not observe staining, despite these reagents working for many labs in many publications. "We did not consider these results satisfactory enough to present."

This is a major flaw, especially how unusual the Dpn staining looks like in the ectopic Dpn+ cells (very speckly). Failure to show additional NSC markers very concerning is areal issue; also no evidence for asymmetric cell division at mitosis (a hallmark of these NSCs).

2) There is no evidence for proliferation of the ectopic Dpn+ cells. The authors state that ectopic Dpn+ cells expressed the S phase marker PCNA:GFP and can be labeled with the mitotic marker pH3.

However, only panes 8A-C show PCNA+ Dpn+ cells, which are increased following dilp-6 overexpression. No data in the figure shows ectopic Dpn+ cells that are pH3. The rest of the figure shows glial markers and PCNA or pH3, which is irrelevant to the question of whether ectopic Dpn+ cells can divide.

3) To show evidence that ectopic Dpn+ cells produce neuronal progeny, the authors used the pros-Gal4 line to drive flybow expression, and observed a small cluster of cells that included one Dpn+ and one Elav+ cell. As the authors say "this does not prove these cells are related by lineage, but is consistent with it."

This does not show Dpn+ cells are producing neurons.

4) The authors also used "flip out" genetics to permanently mark glial cells.

The genetics shown in the figure, legend, and reviewer response will not specifically label glia. The genotype is: actGAL4>y+>UASGFP/UAS-FLP; repoGAL4/Dilp-6. This would induce Flp widely, in all cells due to ubiquitous expression of actin-gal4. Most likely, the authors wrote down the wrong genotype in the figure, legend, methods, and reviewer response - it is probably actin promotor-FRT-stop-FRT-GFP. They cite Table 1 for more information on genotypes but there is no Table 1 provided.

5) In order to call Kon and ia-2 partners, a direct physical interaction should be shown. The authors could not get the biochemical experiments to work for various reasons. Changed text from "partners" to "functional neuronal partner."

The continued use of 'partner' is inappropriate. The most accurate description of their relationship is that they show 'genetic interactions' - so the first results header should be changed from "Ia-2 is a functional partner of Kon" to "Ia-2 and Kon show genetic interactions."

6) Saying ectopic Pros+ cells are GMCs or neurons is premature and can be definitively resolved by staining for Wor or Dpn (neuroblast-specific), Ase (neuroblast and GMC), and Elav (neurons). All have been extensively used by many labs. The authors could not get the stains to work.

This is unsatisfactory.

7) Line 219 says loss of ia-2 "destabilizes cell fate" - which is a vague term that obscures the phenotype. The authors changed text to "... upregulated GMC and NSC markers."

They looked at Dpn but no other NSC marker, and Pros is not a specific GMC marker, also being expressed in neuropile glia near the midline (which is worrying).

8) Dpn staining in figure 3D is unconvincing; everything looks speckly. The authors state that Dpn staining is speckly in their hands.

Many labs have used Dpn to mark neuroblasts, it is a very reliable reagent. The authors have good Dpn staining in other figures; this suggest to me that the ectopic Dpn+ cells are different from the normal Dpn+ NPCs, leading to different protein localization/levels. This concern is reinforced by the failure of the authors to show the ectopic Dpn+ cells express any other NSC marker.

9) Ectopic Dpn+ cells were not quantified due to due to the disruption and variability of the abdominal crush procedure. The authors only counted the VNCs in which they could see ectopic Dpn+ (cells).

Picking only VNCs that show ectopic Dpn+ cells is inappropriate.

7) In response to InR-Gal4 expression concersn, the authors state "we do not know whether (InR-gal4) represents the endogenous expression pattern". It labels sparse patterns of neurons and sporadic glial cells.

The authors directly state in the revised manuscript "we visualized InR expression using available GAL4 lines to drive his-YFP" but in the reviewer response they acknowledge this is not accurate.

This manuscript is in revision at eLife

The decision letter after peer review, sent to the authors on May 19, 2020, follows.

This manuscript sets out to identify a role for ubiquitin phosphorylation and to identify the kinases necessary for it. The same group has previously shown that serine 57 phosphorylation can be detected in yeast cells. Here they generate strains expressing only phosphomimetic or phosphonull mutants and asses their phenotype in terms of Ubiquitin linkage alone and effect on cell physiology. Among other phenotypes, they find that a strain expressing a non phosphorylable ubiquitin likely fails to mount a response to low doses of H2O2, leading to a slightly increased sensitivity to this chemical. They also find that treatment with H2O2 slightly increases the amount of phosphorylated Ubiquitin. They then go on to identify the kinases responsible for this phosphorylation using a screen in E. coli, which homes in two kinases, Vhs1 and Sks1.

They delete both kinase and show that this, to a large extent phenocopies the expression of a non-phosphorylable Ubiquitin, and that expression of a phosphomimetic rescued some of the phenotypes of the kinase deleted strain. They also show that overexpressing one of the kinase increases the amount of phosphorylation on ubiquitin.

Finally, they perform a similar screen using human kinases and human ubiquitin and identify a family of kinases that have the ability to phosphorylate ubiquitin in E. coli.

All three reviewers found the work of interest. Yet, because pSer57-Ubiquitin is so rare, they expressed concerns that the observed phosphorylation of Ubiquitin could be an epiphenomenon of little incidence to cell function.

First, the phenotypes of the alanine and aspartate mutants may be due to general effects on Ubiquitin rather than true phospho-Null and -mimetics effects. This concern is minimized by showing that the deletion and overexpression of the kinases phenocopy the ubiquitin mutants. Indeed analysis of the ubiquitin mutant is only valid in the light of this phenocopy. Yet, because of its importance, this point can and should be pushed further. For instance, while the asp mutant is sensitive to hydroxyurea, the ala mutant behaves as a wildtype. This is at odds with the fact that the KO of each kinase individually increase HU resistance. In this case at least, the effect of deleting the kinase does not appear to involve a decrease in the level of ser57 phosphorylation. How can this be reconciled? Also, while you show that expressing the 57Asp bypasses the need for the kinase in the H2O2 sensitivity assay, is it also the case for the HU and tunicamicin resistance bestowed by the deletion of the kinases? Please find in the specific points a list of experiments required to better pinpoint the phenocopy that is so essential for the relevance of this study. Also, overexpression Vhs1 causes a slight canavanine resistance, reminiscent of canavanine resistance confered by s57d expression. Vhs1 overexpression should therefore not confer canavanine resistance if expressed in a s57a background. This is important to strengthen the phenocopy.

Second, while you show that both kinases can phosphorylate Ubiquitin in bacteria and in vitro, and that the overexpression of one of them increases the phosphorylation levels, you do not show how deletion of the kinase affect phosphorylation. This can and should be done, in particular to show if the observed increase in phosphorylation upon oxidative stress is mediated by these kinases.

Third, given the low abundance of pS57 ubiquitin, it is hard to conceive that this modification has an important effect on global chain linkage, unless this rare modification is applied to an equally rare set of substrates (like for instance PINK-1 mediated phosphorylation of ubiquitin is limited to the pool of ubiquitin that is on mitochondrial proteins). This should be better emphasized throughout the manuscript so as not to mislead readers into believing that a substantial fraction of ubiquitin is subjected to phosphorylation.

Fourth, in many cases, the experiments are not described in a sufficient amount of detail. For instance, vectors used herein are not described anywhere, nor is the way that all copies of ubiquitin have been replaced with mutant forms. The supplementary table 2 is absent, so is supplementary table 1. A much better methods section is required to ensure the reproducibility of the experiments. Better descriptions of numbers pertaining to quantitative analysis, statistical test employed an p-value threshold, description of error bars (Stdev, SEM...) are also needed in figures and legends.

Here are other major points.

1) In Figure 1A and Figure 3 supplement 1, the authors test the effect of ubiquitin phospho-mutants and absence of kinases, respectively, on the ability of yeast cells to recover from acute heat stress. Firstly, it is puzzling though the experimental conditions are the same (39ᵒC for 18 hours and shifted back to 26ᵒC for recovery) in both cases, the wild-type strain is as good as dead in Figure 1A while it grows fine in Figure 3 supplement 1. Importantly, to validate the resistance phenotype of the S57D mutant, the authors should rather over-express the kinases and see that cells grow better in this condition compared to the wild-type and much better compared to the S57A mutant.

2) In Figure 1F, the authors employ anti-K48 ubiquitin and anti-K63 ubiquitin antibodies to show the specificity varies between S57A and the S57D mutant. The concern here is whether the serine mutants affect the binding of the antibodies. For instance, the epitope recognized by the anti-K63 ubiquitin antibody could involve the serine 57, however, when mutated to aspartate, the antibody can lose its ability to bind K63-linked ubiquitin. Is there a way to rule this out?

3) The authors show that S57D increase K48 but decrease K63-linkages whereas S57A decrease K48 but increase K63-linkages upon H2O2 treatment (Figure 1F). What about overexpression or deletion of Vhs1 and Sks1? Does absence of the kinases impact the mutual abundance of ubiquitin K48 and K63 linkages in vivo? Gly-Gly peptides analysis of the data in the experiment from Figure 2G might answer this.

4) Deletion of the kinases increase resistance to tunicamycin. However expression of S57A does not. To strengthen the case of the phenocopy, it is important to check if kinases have ubiquitin-independet effects and how much of the phenocopy is actually wrought by independent mechanisms.

5) In general, the growth assays on tunicamycin, hydroxyurea or canavanin in F1S1, F3S2, F3S3 and F3S4 should rather be moved to the main figures.

6) In Figure 4, human MARK kinases are found to trigger phosphorylation on UbS57 in vitro. It would be insightful to validate this finding in vivo and check whether phosphorylation of UbS57 also regulate the oxidative stress response in mammalian cells. I understand however that this might be take much longer to do than the timeframe which is allocated for revision. In this context, the authors may consider avoiding finishing the paper with these preliminary mammalian data and move them elsewhere in the manuscript. For instance, splitting data from Figure 2 in Figures 2 and 3 and moving figure 4C in the new Figure 2 (and figures 4A and B in supplement) would save some space to end the paper with the current Figure 3 and its supplements.

This manuscript is in revision at eLife

The decision letter after peer review, sent to the authors on June 15, 2020, follows.

Summary

In the manuscript by Yang et al. the authors investigate in zebrafish the effect of leakage of pro-inflammatory LPS form the brain in peripheral tissues. Using beautiful live imaging and genetic manipulations, they find that macrophages infiltrate the liver and their recruitment depends on myd88 and il34, thus underscoring the existence of rapid communication between the brain and the liver that may play a role in immune surveillance.

Two new reviewers and one reviewer that evaluated the previous version of this work agreed in that the manuscript has been greatly improved with substantial new data and an in-depth revision. Two key experimental manipulations, the knock down of myd88 and il34, are now backed by stable loss of function mutations and several experiments have been strengthen with new or improved analyses. However, there are still two important experimental manipulations using morpholinos that have not been properly controlled. In addition, editorial changes are needed to better explain the use of LPS injections as an experimental tool.

Essential Revisions

1) The authors use morpholinos targeting csf3r and pu.1 expression and draw important conclusions based on those experiments. Given the inherent problems of morpholinos, particularly for inflammation studies, it is necessary to support the use of those reagents with stable mutants and/or additional controls. If mutants are not available or cannot be generated, the knockdown experiments may be further supported with rescue experiments and or F0 Criprs, in which case the significance of any findings related to those experiments should be tempered with an appropriate discussion of the caveats.

2) While brain injections of LPS can be a useful tool as used in this work, it is hardly a physiological condition. An editorial revision should address caveats and limitations, perhaps highlighting the use of this experimental approach as a tool.

Reviewer #2

This is an interesting study demonstrating the use of CRISPR/Cas9 to prevent development of Fuchs' corneal dystrophy in a mouse model in which the human mutation (Q455K / Q455K) was knocked into the Col8a2 gene. This gene mutation has been previously shown to induce early-onset Fuchs' dystrophy in patients. This is an important observation with translational potential to treat a subpopulation of patients with Fuchs' dystrophy.

In general, the data support the author's conclusion that Adenovirus-Cas9-gRNA restores the phenotype in adult post-mitotic cells.

I have a two major questions/issues:

1) The data presented in Fig. 3 are critical to the paper and show that Ad-Cas9-Col8a2gRNA treatment reduces expression of the Col8A2 protein in corneal endothelial cells. However, there is no quantitative assessment of the protein reduction other than the images presented from three cross sections. Since Fig 2a indicates the transduction of the corneal endothelial cells is not evenly distributed, some type of quantitative assessment is needed for Fig. 3, either measuring the antibody staining in numerous sections from several different corneas, or by western blot. This is necessary, even though there is quantitative assessment of the change in phenotype of the treated corneas (corneal endothelial cell density, morphology, and guttae-like lesion expression).

2) To demonstrate that Ad-Cas9-Col8a2gRNA treatment rescued corneal endothelial cell function in the mutant mice, the authors developed an assay that measured the ability of endothelial cell pump function to reduce swelling of the stroma after the corneas were induced to swell by adding hypertonic solutions. While this assay does measure pump function, there is a more direct measure of mutant corneal endothelial cells. The investigators that created the Col8A2 (Q455K / Q455K) mutant mice demonstrated the mutation caused an activation of UPR (unfolded protein response) as shown by an increase in Grp78 and Grp153 in corneal endothelial cells. In my opinion, demonstrating rescue of this function in the mutant mice would have been significantly more impressive.

Reviewer #1

The study by Uehara et al titled "Start codon disruption with CRISPR/Cas9 prevents murine Fuchs' endothelial corneal dystrophy" describes a strategy for resolving a dominant negative disease phenotype by CRISPR/Cas9 targeting of the start codon of the causative gene, Col8a2. The authors employ recombinant adenovirus packaging SpCas9 and a single gRNA targeting the start codon of the Col8a2 ORF. In vivo efficacy in wild type mice correlates with a qualitative reduction in COL8A2 expression in these mice by immunostaining. Using a mouse model homozygous for a causative mutation, Col8a2Q455K/Q455K, the authors show a significant reduction in disease pathology, qualitatively via tissue architecture and quantitatively by assaying corneal endothelial pump function. Off-target effects are modeled in vitro and identify several sites, but no significant concerns noted. Overall, the study provides proof-of-concept and feasibility of utilizing this approach, with significant possible outcomes for FECD. Significant concerns pertaining to cassette design, data analysis and additional experiments are highlighted below.

1) The vector construct utilizes a ubiquitous promoter, Chicken beta actin (truncated) to drive Cas9 expression and a U6 promoter to drive guide RNA. It is unclear why the authors only see a qualitative effect on protein knockdown by immunostaining in the endothelium. Does Adenovirus not infect underlying stromal or epithelial cells? The presence/absence of Ad DNA in these other cells has not been evaluated.

2) A correlation between expression of Cas9, gRNA and COL8A2 (protein and mRNA) would be important to establish in mice. This is especially critical to demonstrate in the disease model not only to correlate protein knockdown with restored function, but because the efficiency of Ad infection or gene editing could vary in diseased cells.

3) The authors note that the indel frequency, determined by deep sequencing, appears inconsistent with the observed protein knockdown as determined by immunostaining of tissue sections. However, while the indel frequency is determined quantitatively (~20-25%), but the protein and mRNA levels are not quantified. Is the half-life of wt and mutant COL8A2 known? The authors also report an editing normalized indel rate of 102% in endothelial cells. While the hypothesis of gDNA contamination from non-targeted tissue is likely true (supported by experimental evidence from Supplemental Figure 2), the method used for correction is insufficient to be used to report a true, corrected indel frequency.

4) Overall what is the minimum/threshold % of endothelial cells that need to be edited to restore function? This information will be critical in designing vector dose and altering promoter strength/specificity to reduce off-target effects. While the impact of vector dose on COL8A2 expression knockdown is assessed, data pertaining to off-target effects at different doses are not presented.

5) Does overexpression of spCas9, gRNA and knockdown of COL8A2 affect the expression of other genes in the endothelium? The authors analyze the impact of Ad dosing at the inflammatory level, but consequences of control vs treatment vector on endothelial cell gene expression have not been evaluated (e.g., Yu et al., Nat Commun, 2017).

This manuscript is in revision at eLife

The decision letter after peer review, sent to the authors on June 12, 2020, follows.

Summary

Repair of any genetic disease is of interest, and Uehara and colleagues have shown an improvement in corneal tissue architecture and function in a mouse model of Fuchs' Dystrophy using gene editing delivered by adenovirus. The current review raises a number of important points. A quantitative assessment of Col protein level relative to the expression of Cas9 and gRNA (Reviewer 1, point 2) would strengthen the data shown in Figure 3, as was also suggested by Reviewer 2 (point 1), and must be carried out. This would also help the argument presented by authors regarding genomic DNA contamination that was indirectly addressed by Sup. Fig 2. Although not required, it is recommended that the question of inflammation and/or effects on gene expression by the adenovirus be addressed more thoroughly, by sequencing or by a more thorough evaluation of gene expression changes. This is an issue as Adenovirus is known to incite pathological inflammatory effects. Finally, again not required by recommended, the authors are encouraged to assay for a correction of the UPR.

Essential Revisions

Please quantify the levels of collage protein. Please see the reviews for additional comments.

This manuscript is in revision at eLife

The decision letter after peer review, sent to the authors on June 12, 2020, follows.

Summary

In this study, Walls et al examine the role of PKM2 in NK cells. PKM2, the glycolytic enzyme that converts PEP to pyruvate, is expressed in NK cells and further upregulated during NK cell activation by Il-2/IL-12 stimulation. However, NK cells lacking PKM2 are activated normally in vitro and in vivo during MCMV infection, as indicated by proliferation, production of IFNg and TNF, expression of Granzyme B, and viral clearance. The authors attribute the lack of phenotype to compensatory induction of PKM1. The authors' findings also suggest that while in other cell types PKM2 may "moonlight" in a transcriptional role, any such role for PKM2 in NK cells seems not to influence NK cell activation, at least in the contexts studied.

PKM2, unlike PKM1, can form a tetramer with increased enzyme activity. In other contexts, such tetramerization is thought to enhance flux through glycolysis which disfavors glycolytic intermediates from being diverted to biosynthetic shunts like the PPP. The authors next asked how such tetramerization of PKM2 may influence NK cell activation, using a small molecule TEPP-46 that enhances PKM2 tetramerization. The authors found that TEPP-46 treatment during NK cell activation led to reduced cellular growth, reduced production of the PPP metabolites R5P and NADPH, increased cellular ROS, and reduced oxidative metabolism, as well as reduced production of IFNg and TNF and reduced expression of Granzyme B.

Essential Revisions

1) The authors should provide some mechanistic insight into how PKM2 tetramerization leads to reduced NK cell activation. Does treatment with ROS scavengers like NAC or cell permeable glutathione rescue the effects of TEPP-46 on NK cell activation?

2) Does PKM2 undergo tetramerization in a physiological context? Given the lack of a phenotype in the PKM2 KO in the in vitro or in vivo conditions that the authors analyzed, it seems like tetramerization may not occur (because PKM1, which is upregulated, is thought to not tetramerize). At the very least, the authors should discuss under what conditions PKM2 tetramerization can occur to suppress NK cell activation.

3) The authors should confirm that TEPP-46 has no effect in PKM2 KO cells.

This manuscript is in revision at eLife

The decision letter after peer review, sent to the authors on June 8, 2020, follows.

Summary

Cannabidiol (CBD) has been recently approved for treatment of epilepsy. Some of CBD anti-epileptic properties might be due to CBD inhibition of voltage-gated sodium channels but the molecular mechanism of such inhibition is unknown. Sait et al. studied the molecular bases of CBD inhibition using X-ray crystallography in application to the bacterial sodium channel NavMs. The authors solved NavMS structures in the apo state and in complex with CBD and based on structural comparison, identified CBD binding sites and proposed the molecular mechanism of sodium channel inhibition by CBD. The crystal structures are of high quality and among the best published structures of sodium channels, and the study is without doubt of high importance.

This is a solid manuscript from an experienced group that reports structural insights into cannabidiol interactions with the voltage-gated sodium channel NavM. The manuscript is easy to read, well-executed, and reveals interesting data.

Essential Revisions

The weakness of this study is the lack of functional data that would greatly complement the excellent structural results. Electrophysiological data showing the interaction of CBD with NavMs should be obtained and presented. This should be a very easy experiment to perform. CBD has been show to block the NachBac sodium channel, but there is no record in the literature that shows that CBD also blocks NavMs.

This is a fundamental experiment that should be included in a revised version of the paper. It will also be of great interest to test the results of their structure by mutating appropriate sodium channel residues (e.g. in Nav1.1) and measure changes in cannabidiol interaction.

Similarly, discussion of the different ways CBD and THC bind to NavMs (page 6) would greatly benefit from a comparison of the physiological effects of these two compounds. Does THC block NavMs and if it does, what is Kd/IC50 for THC compared to CBD?

Electron density observed at the CBD site in the apo state structure needs to be shown side by side with the density for CBD in the structure obtained in the presence of CBD (a supplementary figure would suffice). Along these lines, it might be a good idea to add a brief discussion on how physiologically relevant is the apo state density. For example, if this site is always occupied by a lipid in physiological conditions, the channel would never open.

This manuscript is in revision at eLife

The decision letter after peer review, sent to the authors on May 28, 2020, follows.

Summary

This paper describes a modelling and simulation project which utilises a mixture of data-sets to predict the likely concentrations (total blood) from the currently recommended hydroxychloroquine (HCQ) (chloroquine (CQ)) dose regimens for COVID-19.

Essential Revisions

Line 93: The NONMEM simulation code could not be found in the list of contents of the GitHub site. When searching for NONMEM in the Rmd file it does not appear. Please provide full details on how to access the PK modelling used.

Line 171: Please describe the model used to simulate the PK profile in order to obtain peak concentrations.

As not all regimens could be tested in the model, it would be highly informative to have the loading, maintenance and duration of dose used in the ~90 registered clinical trials summarised in a supplementary table. This would clarify how the wide range of chloroquine dosages currently being used relate to dosages modelled in terms of predicted exposure and mortality risk. This is needed to support the Impact statement that "Most chloroquine regimens trialled for the treatment of COVID19 will not result in life-threatening cardiovascular toxicity".

This manuscript is in revision at eLife

The decision letter after peer review, sent to the authors on May 29, 2020, follows.

Summary

In their manuscript entitled "Multiple Wnts act synergistically to induce Chk1/Grapes expression and mediate G2 arrest in Drosophila tracheoblasts," Kizhedathu and colleagues investigate the developmental regulation of Chk1 activation in larval tracheoblasts of the Dorsal Trunk segment tr2. They find that four Wnt ligands are required to achieve a level of active Chk1 (pChk1) needed to maintain tracheoblasts in G2 arrest. This regulation is achieved by autocrine signaling in which the canonical Wnt pathway is activated by 4 Wnt ligands expressed in the trachea at high levles. Wnt signaling is required for transcription of Chk1. None of the 4 highly expressed Wnts are dispensable. Release from G2 is required for activation of the dpp/tkv/pMad pathway that spurs continuing cell divisions.

This is a Research Advance manuscript following up on work reported in a prior publication entitled "Negative regulation of G2-M by ATR/Chk1 (Grapes) facilitates tracheoblast growth and tracheal hypertrophy in Drosophila." The current work makes several important contributions. Having initially identified a G2 cell cycle arrest dependent on Chk1 and Atr, but not upon DNA damage, the authors now show that the cell cycle arrest is maintained through a canonical Wnt signal that mediates transcription of chk1 mRNA. The authors identify 4 Wnt ligands expressed in the tracheoblasts and show that all 4 are required for G2 maintenance via chk1 transcription, although individually dispensable for fz3 transcription. The authors also show that the dpp pathway signal required to drive tracheoblast cell divisions cannot operate during G2 cell cycle arrest. Lastly, authors note that Wnt5 is thought to signal through a nonconical pathway, but in this instance contributes to canonical signaling.

Essential Revisions

1) Additional controls to confirm the requirement for 4 Wnts:

Is there any chance that there are off target effects from the RNAi that may cause this? Do the Wnt ligands impact each others' expression? Wnt ligand KD followed by qPCR analysis of the Wnt ligands could be useful. This issue is important to discuss, and test.

Test of second independent RNAi line where classic loss of function alleles are not available.

Test RNAi of the non-expressed Wnt ligands and addition of a supplemental table documenting the screen (Wnt and other pathways) with RNAi line numbers, drivers, temperatures and results.

2) Clarify ability of overexpressed Wnts to rescue, and determine the requirement for nonconical Wnt pathway:

Address whether derailed or doughnut are required in tracheoblasts.

Authors Wnt threshold model hinges on ability of overexpressed Wnt to compensate for loss of one Wnt ligand. However, this was only reported for one loss of function case (Wnt 6 RNAi), and only with one overexpressed Wnt (Wnt5). Authors should test ability of other Wnts to rescue, and should also address whether a conventional Wnt can substitute, when overexpressed, for Wnt5.

3) Address inhibition of mitoses during L2:

The authors show that downregulating the Wnt pathway in L2 stage does lead to the reduction of Chk1 mRNA (figures 3A and 2, respectively), but that this does not result in tracheoblast mitoses. This indicates that in L2, in contrast to L3, there must be some additional control which is lifted after L2/L3 metamorphosis. The authors should discuss this issue and present possible explanations. If they have any more relevant data, this should also be presented.

4) Move Figure 5S into results:

P. 14 lines 358-369. Minimally, it is not appropriate to introduce data in the discussion that is not discussed in the main results section. Moreover, the experiments and results are super interesting. I could be wrong because I am not an expert in the cell cycle, but I don't think the idea of a G2 arrested cell continuing to grow physically because it still expresses cell cycle promoting genes while in G2 arrest is really out there in the literature on cell and organ size control (although I think mammalian oocytes arrest in G2 and they get really big, but they also may have bridges to nurse-like cells to supplement growth). As such, I would strongly encourage the authors to make Fig 5-Figure supplement 1 part of the main figures and discuss the basic findings in the results section. Then it could be revisited in the Discussion section to put the result in the bigger picture context.

This manuscript is in revision at eLife

The decision letter after peer review, sent to the authors on March 4, 2020, follows.

Summary

In this study, Bennstein et al describe a T-bet negative ILC1-like cell population identified in cord blood. These cells lack the signature of NK cell genes and markers, and instead express genes and markers of T-cell lineage. In appropriate culture conditions these cells can differentiate into a complex repertoire of functional NK cells that express both NKG2A and diverse KIRs. The reviewers appreciated the attention to an important topic, but raised a substantial number of concerns about the manuscript as it currently stands. We therefore ask the authors to modify the manuscript according to the review recommendations.

Essential Revisions

1) The authors state that ILC1-like cells which are T-bet and CD56 negative and lack expression of perforin and all 5 granzymes develop into effector NK cells with de novo CD94, NKG2A and KIR2DL3 expression. The authors need to further phenotype the differentiated cells, showing evidence of essential NK cell markers, including CD56, NKp46, granzyme B and perforin. Additionally, they should demonstrate that inhibitory KIR expression in the differentiated cells is functionally inhibitory and leads to increased cytotoxicity in educated cells. Despite the ILC1-like derived NK cells having increased KIR expression compared to the CD56bright-derived NK cells, CD56bright-derived NK cells were equally functional and exhibited more target-specific degranulation compared to ILC1-derived NK cells.

2) The idea proposed in the discussion that CB ILC1 may be cells that have failed to convert into T cells into the thymus is an attractive one and perhaps the authors may wish to test it by looking at markers of recent thymic emigrants in CB ILC1 - if possible?

3) It is unclear if proper functional controls were utilized in this study. Target-specific degranulation needs to be shown instead of total degranulation in fig 5, as fig 7c makes evident. Additionally, the equation used to calculate cytotoxicity for the CFSE-based method should be included in the materials & methods section. For the ADCC assay, it is unclear what cells were used for the control. Individual controls (antibody negative) for each cell population should be included.

4) How do the authors explain the phenotypic and functional differences between the individual ILC1-like subsets as defined by CD5 and CD161 expression and how do these individual subsets contribute to their proposed NKP potential? This point should be discussed in more detail.

5) The authors state that ILC1-like cells preferentially differentiate into mature KIR+ NK cells compared to CD56bright NK cells in the OP9-DL1 differentiation setting in the presence of IL-2, IL7 and IL-15. Cytokine stimulation (IL-2 and IL-15) of NK cells leading to the induction of proliferation and results in CD56 and NGK2A upregulation, even in mature CD56dim NK cells. Hence it is not surprising that CD56bright NK cells retained high NKG2A expression while actively proliferating. The present experimental setup therefore does not support their statement on line 570-573 of a branched NK cell lineage model.

6) The authors clearly show that the CD127+ Lin- population is highly heterogenous, just by looking at CD161, CD5, CCR9, CCR4 and CCR7. Therefore, the transcriptomic and epigenetic data on the bulk population are not informative. Single cell analysis should be used to define the heterogeneity, considering that Simoni et al. have previously reported the heterogenous nature of human ILC1s (Simoni et al., Immunity, 2017) and questioned the nature of lineages included.

7) The authors claim that the cells do not generate T cells. However, they only use IL-7 and FLT3, while in other protocols the used IL-7, FLT3L and SCF.

This manuscript is in revision at eLife

The decision letter after peer review, sent to the authors on May 25, 2020, follows.

Summary

Using a combination of single and array recordings, and voltage sensitive dye (VSD) imaging, the authors demonstrate that neurons in awake macaque V1 show anticipatory responses to a smoothly moving object outside their classical receptive field (RF). This anticipatory activity builds up slowly and can lead to spiking. Combining theoretical modeling, VSD imaging and LFP recordings, they further demonstrate that the spatio-temporal properties of these anticipatory responses are consistent with the hypothesis that they are generated by intra-V1 horizontal and inter-areal feedback connections. These results are important because they challenge classical models of motion integration that are largely based on feedforward mechanisms. In contrast to these models, the work presented here demonstrates a role for horizontal and feedback mechanisms in motion processing, and that motion integration starts at the lowest level of cortical processing, within V1 itself. The authors use a variety of methodologies to corroborate this result.

Appreciation

The reviewers in general made positive comments about the work and found the findings interesting. They also made many critical remarks that require substantial and essential revision, data analysis and experimentation.

Revisions

1) The reviewers made many critical point about receptive field quantification, and the interpretation of anticipatory firing related to this.

(i) The anticipatory responses in the manuscript are assumed to be due to the smooth motion of the stimulus rather than an extra-classical RF effect. This is discussed by the authors, but not truly demonstrated in the manuscript. It is possible that the authors might have observed responses to bars placed outside the RF that are flashed rather than moving? The sparse-noise mapping that they used to delineate the RF might help to distinguish these possibilities as the authors could look at the responses to noise-flashes that fell on the trajectory of the bar (but outside the RF) to determine if these drove the cell.

(ii) The quantification of RF-sizes is not well explained.

• The reader would appreciate a plot of the (classical) RF boundaries and the starting positions of the 3 bar sweeps in the example cells shown in Fig. 1B-D.
• Since the conclusions of the study rely heavily on estimation of RFs, it would be important to show some examples of RF mapping with flashed squares, and to plot the activation profile with flashed squares for the same neuron as a function of DVA in Figure 1. The RF mapping is described quite briefly in the Methods and it is not entirely clear what it amounts to in terms of neural activation.
• Can the authors indicate at which distance from the RF the short bar sweep typically started?
• What is the latency of the response if aligned on the start of the short bar sweep? If it is close to 40ms, this might indicate that the bar actually started in the RF of some of the neurons.
• The finding that some neurons do not have anticipatory responses does not provide a control (in contrast to what is stated in line 184) because these neurons might have had smaller RFs. However, the data in Figure S2D-E might address this point, and could be presented in the main paper.
• We would like to see a distribution of RF sizes for the single units, the pixels of the VSD measurements and the spectral components for the MEA recordings.

(iii) The spatial extent of thalamic inputs arriving from the M- and P-pathway going into V1 differs (Lund et al., 2003, Figure 7). In particular M-pathway inputs have a wider termination zone. It is not clear whether this may account for a discrepancy between RF sizes mapped with moving stimuli and flashing stimuli. Moreover, since the RFs were mapped initially with flashing squares, it is possible that eye movements exhibited less variability in that condition, and that this leads to effectively larger RF sizes with moving stimuli. The finding of anticipatory finding might thus be explained by these factors without requiring recurrent connections. It is important to discuss this possibility and to address it with analyses.

(iv) If the bar would proceed to move after going out of the RF, is there also a widening observed there? This would be congruent with generally larger RFs for the moving stimuli.

(v) How did the authors compute the "time to peak" (line 191)?

• Line 244: time 0 is when the RF crosses the RF center and the peak response happens before time zero as shown in Fig 2C. This is worrisome, because the peak response for a moving bar is actually expected after the bar reaches the RF center, given the delay between retina and cortex (see e.g. Fig. 3 in Supèr and Roelfsema, 2005 Prog. Brain Res. 147, 263-282). Do the authors correct for the delay between the retina and V1 to compute time zero? How? Please specify this.
• Reviewers were confused in the methods section by lines 875-877. Is this where a correction for the response latency is described? If yes, please clarify this text (also in the main text) because such adjustments may have an large impact on the main result.
• There is a similarly confusion section in lines 893-898. It is not clear what happens here.
• Same in lines 907-910. What is "probability of anticipation"?
• Same in lines 912-921 what is "skp timing - 50"? What is the aim?

(vi) Is it possible to also show the retinotopic maps obtained with VSD imaging?

(vii) Overall, the authors should quantify RF size with the same methods used for flashes and bars and compare these directly with the same quantification; in addition correct for eye movements and delays.

(2) The reviewers made several critical remarks w.r.t. the relationship of the findings to trajectory prediction.

A main concern is whether the build-up activity demonstrated here is related in anyway to predictions of smooth motion trajectories or whether it is a passive spread of activity in cortex. Points 2.i and 2.ii are related to this concern. The spread of horizontal activity has been demonstrated previously and would reduce the novelty of the findings demonstrated here.

The reviewers agree that there are three aspects here that require further experimentation:

(i) The authors link their findings to psychophysical studies suggesting that we can use smooth motion to predict the upcoming location of the stimulus and improve perception on the leading edge of the stimulus. However, throughout the manuscript the activity triggered by the stimulus entering the classical RF is largely identical. Furthermore, there is no behavioral manipulation in the manuscript or any manipulation of the predictability of the motion path. This makes it difficult to determine if the build-up activity they observe has any functional significance or whether it is simply a passive spread of activity around the moving stimulus.

(ii) The lack of build-up activity for stimuli activating the ipsilateral cortex is an interesting finding which supports the authors' claims that these results are due to the spread of activity in (unmyelinated) horizontal connections. But doesn't this result also severely limit the functionality of this effect? If the prediction is unable to 'jump' across the vertical meridian, then this suggests it is more of a passive spread of activity around the stimulus rather than an active process providing cortex with a prediction of an upcoming moving stimulus.

• Is there psychophysical evidence that the effects of motion prediction on behavior (mentioned in e.g. lines 94-100) has a discontinuity at the vertical meridian?

(iii) The implication of these findings is that V1 neurons start responding to a moving stimulus before the stimulus reaches their receptive field. However, objects do not always move smoothly, and sudden changes in trajectories occur. Would V1 neurons, in this case, signal the "wrong" trajectory?

(3) The quantification of anticipatory firing needs to be substantially improved.

(i) Line 259: how was the "first significant change" estimated? Please specify here or refer to the relevant Methods section. In general, the data analysis section of the Methods is presented as a long list of metrics and statistical analyses without clear reference to which part of the results and figures each refers to. Vice versa there is no reference to any specific Methods section in the description of the Results or figure legends. This makes the manuscript somewhat difficult to read.

(ii) The representation of the data in Figure 1 is somewhat problematic, because the population average is shown only for neurons with anticipatory responses (n=26). In Figure Supplement 2, the number of cells is 22 (why the difference?). Are these now only the anticipatory neurons? Why did the authors not show the average population responses across all neurons before splitting into anticipatory and non-anticipatory neurons? It would be good to see the average PSTH.

(iii) Fig S2: The curves look less asymmetric there, and seems to show a general widening for the long bar condition.

(iv) Normalization is a concern for the group average plots, because an average PSTH can be biased by a few cells with high firing rates.

(v) line 386: there are no statistics for the anticipatory response here.

(4) The relationship of direction tuning to anticipatory activity requires further data analysis.

(i) It is unclear why the authors chose not to optimize the stimulus trajectory to the direction preference of the cells under study, at least in the single cell recording experiments.

(ii) The authors describe the relationship with direction tuning on line 276. They find that the anticipatory response is considerably stronger in cells where the direction of motion of the bar is aligned with the preferred direction of the cell. This interesting effect isn't quantified statistically and seems under-explored in the manuscript as a whole. It seems to be an extremely strong effect, to the extent that the reviewers wonder if the build-up effect is significant for cells with a non-aligned direction tuning? The effect is also not included in any of the later models and would not be predicted by their proposed model. The reviewers wondered whether the authors could also use the bar sweeps that they use for RF mapping, which move in 12 different directions, to further explore the relationship between direction-tuning and anticipatory responses?

(iii) Lines 274-281. Did neurons with preferred direction aligned to the stimulus trajectory also show shorter latencies of anticipatory responses? The authors speculate this could be the case in the following sentence, and present this as a result in the discussion section, but they never really showed any analysis addressing this.

(5) Motion speed:

The manuscript does not manipulate motion speed which limits the interpretation of the findings. One simple way to test the proposed model would be to vary the speed of the bar. At high speeds the feedforward drive would 'catch-up' with the horizontal and feedback spread and the anticipatory response should disappear. Do the authors have any data on this and would they agree with this prediction?

(6) Reviewers had concerns about smoothing in the data analysis.

Reviewers worried about the smoothing that took place in the analysis (e.g. line 856, 863) and the sliding window used for the computation of a power spectrum (line 928). Something similar may happen with detrending VSD signal in line 942. First smoothing the data in time can cause "responses" at earlier time points, but would be artifactual. Do the results also hold up if the data is not smoothed?

(7) Laminar differences:

Lines 260-266. The observed variability could depend on laminar differences. Do the authors have any record of laminar location of the recordings? More importantly, the variability could also reflect differences in the direction preference of the neurons. The authors should check this. It is possible that neurons with the direction preference matching the stimulus trajectory are facilitated while those with direction preferences unlike the stimulus trajectory are suppressed, or vice versa. This further analysis would provide additional insights into the underlying mechanisms.

(8) Analyses of frequency bands:

(i) Did the authors measure the RFs of the different frequency bands of the LFP? Low-frequency bands tend to be sensitive to changes in visual information over very wide regions of the visual field. The spatial precision of this effect may be very low and is not shown by the authors (did the low-frequency power drop simultaneously across the whole array at bar onset for example). It is hard to imagine that a coarse effect, which may be more related to arousal or attention, is related to a prediction about the precise location of an upcoming stimulus.

(ii) Reviewers would like to see the average power spectrum in Fig. 5.

(iii) line 455 Even though previous studies suggested that feedback influences have a spectral signature, this does not mean that changes in the power spectrum can provide causal evidence for the involvement of feedback connections. It can well be that subcortical inputs also decrease/increase power in particular frequency bands.

(iv) What is shown in Fig. 5B? Is this the evoked potential or some spectral measure?

(v) The authors should clarify in the main text how they normalized the power and determined statistical significance.

(vi) Line 475. The decrease in the low frequency band is actually preceded by a slight increase, as evident in both Fig. 5C and D. In the discussion, the authors only emphasize the decrease in power (which indeed is stronger), but they do not provide any rationale for why one would see a decrease, rather than an increase, in power. One would have predicted that an increase in feedback excitation would result in an increase in low frequency band power (and this would be consistent with published results indicating an increase in alpha/beta power when feedback processing increases). On lines 628-630 of the Discussion, the authors attempt to provide some explanation for such decrease in power, but the sentence is rather obscure. The authors need to clarify and expand this idea. Also, should the earlier increase in low frequency power be ignored?

(9) Results on the ipsilateral hemifield stimulation.

Reviewers did not understand the rationale for, and the interpretation of, this result. Surely callosal connections exist within about 2 deg of the midline and they would activate V1 neurons in the contralateral hemifield which, in turn, send horizontal connections within the contralateral hemifield. Also, in contrast to what stated in the discussion, reviewers pointed out that callosal connections are topographically organized.

(10) Discussion lines 677-678. The authors need to expand on these two concepts by clarifying to the broad readership of the journal what "diffusion of motion information" means, and how their results could underlie this phenomenon as well as enhance motion discriminability. Same comment applies to the sentence on line 688.

(11) Critique of the model:

(i) The model has many parameters that do not appear well justified. Such a model can provide support for horizontal spread but the authors should acknowledge that other models without horizontal connections in V1 could give rise to similar predictions. E.g. horizontal spread could happen in a higher areas that feeds back to V1. Arbitrary parameters appear e.g. in line 971; where does the estimate of 0.41mm come from? The same question can be asked about the choice of the model in lines 973-1006 and its parameters. Model choices, such as the function in equation 1 and the equation in line 993 are not well explained and make an ad hoc impression.

• Note that the equation in line 993 is not connected to equation 1, because the reader expects k_h to reappear in the equation in line 993 but it does not. It is also unclear why "h" appears twice in the equation in line 993 (within and after the brackets). Is h=k_h?
• Is there an equation of how the feedback influences k_h or V1?

(ii) It is unclear whether the speed of propagation beyond 2deg from the RF, which the authors attribute to feedback, is in fact consistent with feedback conduction velocities. On line 415, the authors seem to imply 0.02m/s is consistent with feedback (but feedback is much faster than this).

line 407: the authors arrive at a horizontal propagation speed of 0.06 m/s but the calculations that gave rise to this estimate are lacking. How strongly does it depend on the model with its many arbitrary assumptions ? Can they also provide a 95% confidence interval for this estimate?

(iii) Line 331. The model incorporates isotropic horizontal and feedback connections, but in real cortex these are anisotropic, and therefore only contact neurons having similar orientation and direction along the anisotropic axis. Incorporating real-life functional connectivity may help the model account for some of the variability in surround effects observed in the data.

(iv) Lines 978-979. What parameters values were used for this, and on what basis were these selected? More in general, all the parameter values used in the model (e.g. dh= 6 mm) need to be justified and appropriate references cited.

(12) Details about data analysis:

In general there are many details in the data analysis that are difficult to understand. The authors may first wish to consult with another specialist (not involved in the study) about the clarity of their descriptions because the reviewers found them insufficiently clear. Some of these have been summarized in the other points listed above and below. There are further points here:

(i) Line 273. Why was a 2-sample t test used here, given it is said that 3 trajectories are statistically compared? This should be an ANOVA. The T-test is used throughout the manuscript. From the Methods, it appears this may be justified by the fact that the authors pooled medium and long trajectories into a single group. IF so, this should be clearly stated in the Results and/or a reference to the relevant Methods section should be added to the Results. Moreover, what was the rationale for grouping the 2 longer trajectories?

This manuscript is in revision at eLife

The decision letter after peer review, sent to the authors on May 25, 2020, follows.

Summary

This work addresses the key question how the herpesvirus HSV-1 reactivates from latency in neurons and shows that neuronal excitability plays a major role for controlling latency and reactivation. How hyperexcitability might influence the behavior of a latent, neurotrophic virus was previously unknown, and the authors show that neuronal hyperexcitability induces HSV reactivation in a DLK/JNK-dependent manner. In additon, the authors identify the cytokine IL-1b as a stimulus that triggers HSV reactivation in neurons, dependent on neuronal excitability, which is also a novel finding and of great interest for the field.

Essential Revisions

The reviewers all agree that your work about the potential link between IL1b, neuronal hyperexcitability, and HSV-1 reactivation is very interesting. However, we think that the three experiments listed below would be needed to substantiate the conclusion regarding the link between these three elements.

1) To make sure that the results obtained with the inhibitors are not off-target effects, experiments with KO cells or siRNA knockdowns of DLK/JNK would strengthen the manuscript. Can you please specify in the manuscript the specific targets of the three inhibitors that were used - if they have discrete mechanisms of action, off-target effects may actually not be a problem. However, KO or knockdown experiments would validate the inhibitor results by an independent method and should be doable in these cultures.

2) To substantiate the very interesting finding with IL1b, an experiment with a neutralizing IL1b antibody should be performed to unequivocally show that IL1b induces reactivation (this would exclude that impurities in the cytokine batch such as LPS activate the cells).

3) To unequivocally show that IL1b induces reactivation through increasing neuronal hyperexcitability, calcium flux, which is induced by neuronal hyperexcitability, should be measured. A simple method to do this would be the use of Fura-2 AM or similar dyes. An advantage of this approach is that it could be measured what percentage of neurons are excited upon IL1b treatment and this could be correlated with the percentage of neurons that reactivate. This could also be performed in the presence of IL1b neutralizing antibodies to confirm that this cytokine induces neuronal hyperexcitability and HSV-1 reactivation.

These three additional experiments would make the report more robust and elegantly correlate hyperexcitability of neurons with HSV-1 reactivation.

Reviewer #2

This is an interesting paper that addresses and important and timely subject, namely identification of novel non opioid approaches to pain management. The authors direct their attention the CB2 receptor. Using perhaps the best characterized, and quite selective CB2 ligand, the authors implicated CB2 receptors in both neuronal and non neuronal cells in the spontaneous pain that occurs in a partial nerve injury model in the mouse. The studies largely used either mice in which the CB2 receptor was deleted in all cells only in neurons, or selectively in monocyte derived cells.

There are many intriguing findings in the paper, however, one is left with the feeling that there are hints at mechanisms, but nothing definitive is established. And major questions, which I believe could have been addressed with more selective Cre-mediated deletion of the receptor, are never answered. Hints here and there, but nothing definitive.

Major questions

The authors focus on sensory neurons and the non neuronal cells that surround the neuronal cell bodies in the DRG. How might the neurons in the DRG, which they appear to presume must be mediating the input that drives spontaneous pain, not be relevant to acute pain processing? The previous report of Soethoudt et al., 2017, which defined the specificity of JWH133, found that this compound is without effect on acute pain even at doses up to 100mg/kg. I am not sure how to translate that dose to the iv administration in the present paper, but my assumption is that the 100mg/kg dose is at least equivalent. Granted JWH133 is not potent, but then how does it affect spontaneous pain?

The most straightforward test of the DRG neurons is to delete the CB2 receptor from neurons, using one of several selective Cre lines (e.g. NaV1.8-Cre). This is particularly important as the authors highlight the apparent translocation of the CB2 receptor from non neuronal cells around the DRG to neurons. But they only used peripherin to mark the neurons, so that any change in myelinated afferents would be missed. As neurons are the only structure that can get information into the spinal cord, do the authors propose that it is this small 4% of DRG neurons that is key?

Perhaps the most glaring piece missing as to mechanism is the fact, acknowledged by the authors, that JWH133 has a significant action at TRPA1, which is expressed by sensory neurons. Most importantly, the authors found that the CB2R null only had 50% reduced nose poke for JWH133. Clearly, JWH133 must exert its effect, at least in part, on another target. In their Abstract, the authors are very careful concerning this finding, writing that ""While constitutive deletion of CB2r disrupted JWH133-taking behavior....". In other words JWH133 disrupted, it did not prevent or eliminate the behavior. So clearly, there is something else mediating JWH133's effects. Studying JWH133 effects in the TRPA1 mutant, and ideally in the mouse in which TRPA1 is selectively deleted from sensory neurons, is critical to understanding this drug's actions. Results from that study would add greatly to the authors study.

Also, as TRPA1 is expressed in sensory neurons, are they now proposing that TRPA1 only contributes to spontaneous pain? That is certainly not the case. In fact, a previous study did report that JWH133 blocked pain behaviors provoked by AITC, a TRPA1 agonist. A simple experiment would be to test the effect of JWH133 against 0.5% formalin evoked nocifensive behaviors. As for AITC, 0.5% formalin evoked behaviors are lost in the TRPA1 ko.

Another simple experiments that would get at mechanism is to examine the effect of JWH133 on nerve injury provoked microglial activation in the dorsal horn. If a decreased activation were demonstrated, the case would be much stronger that the drug is acting on sensory neurons.

Concerns about the immunohistochemistry: First, the images presented are not all that convincing, and particularly difficult to read given that the percentage of double labeled neurons is small. It is also very odd that the authors had to use TSA amplification. Also there is no mention of controls for antibody specificity.

Reviewer #1

This is a very interesting paper. While demonstration of CB2 receptor agonist self-administration in rodent models of chronic pain is not in itself novel, there is a sufficient body of additional novel and exciting work in this paper to set it apart from previously published work. In particular, the mechanistic dissection using tissue-specific KO mice, coupled with the demonstration of that CB2 receptor-expressing lymphocytes infiltrate peripheral neurons, and to a greater degree in nerve-injured versus sham mice. The anxiety-related results are also very interesting. The paper is well-written and the results, for the most part, are clear.

Major comments

1) While there are significant novel results and important conclusions that can be and have been drawn from the work, the mechanism underlying the increased self-administration of JWH133 in PSNL mice has still not been fully elucidated. The authors have shown it is CB¬2 receptor-dependent, but not due to CB2 receptors in neurons or monocyte-derived cells. Neither does it appear to be due to CB2 receptors on infiltrating lymphocytes. So the question still remains as to what mechanism or target is mediating the effect. I think the Discussion should address this limitation in more detail, and put forward some potential mechanisms.

2) Is it possible that there could be some involvement for CB1 receptors? JWH133 is relatively selective for CB2 over CB¬1, but to my knowledge it does still have some affinity for (and potential activity at) CB1. How can the authors rule out a potential involvement of CB1 in the self-administration of JWH133 after PSNL.

3) Given the anxiety-related aspect (and indeed the self-administration/pain aspect), why did the authors not look at whether lymphocytes expressing CB2 also infiltrate brain neurons? It would be very interesting to know if they infiltrate neurons in brain regions such as the amygdala, PFC, PAG and other regions known to be important in pain, anxiety and drug self-administration in pain models.

Statistics: The authors should determine whether they need to adjust for multiple comparisons when doing repeated Mann-Whitney U tests, e.g. perhaps do a Bonferroni-Holm correction to control for alpha when doing multiple MW U test comparisons. Alternatively, they could perform a Dunn's test instead of the MW U test.

This manuscript is in revision at eLife

The decision letter after peer review, sent to the authors on May 1, 2020, follows.

Summary

Both reviewers found many positive aspects to your manuscript. However, although Reviewer #1 believes that the concerns could be addressed without providing additional experimental data, Reviewer 2 has identified some significant concerns that do need additional information. The specific experiments that are indicated address the underlying mechanism, including the extent to which receptor expression on sensory neurons is involved and most importantly, the contribution of TRPA1. We appreciate that the present COVID-19 pandemic will make it impossible to complete the requested studies within the normal two-month period, which will involve new mouse crosses, so we are willing to accept a revised manuscript when you are able to return to the laboratory and complete the studies.

This manuscript is in revision at eLife

The decision letter after peer review, sent to the authors on May 18, 2020, follows.

Summary

In this paper, the authors consider the problem of evolutionary transitions to multicellularity, and in particular the case in which aggregation drives the process. Inspired by the life cycle of Dictyostelium, they consider a model in which cells (moving on a grid) search for resources and can adhere to each other based on the match between ligand and receptors on their surfaces. All of this takes place in the context of a chemotactic march towards a local chemoattractant within one temporal "season", after which fitness-dependent reproduction occurs, the population is culled back to its starting size, and the environmental conditions are changed.

The reviewers all are of the opinion that this work provides an interesting perspective on a possible mechanistic basis of 'collective-level' function, that stems from physical interactions among cells in the absence of explicitly modelled costs and benefits of single cell's choices. At the same time, the reviewers were clear that there are many aspects of the model and the modelling approach that are not clear, unnecessarily complicated or not well justified. In light of these, major revisions to the paper will be necessary, as explained below.

Essential Revisions

1) Considering the paper as a whole, there are far too many things happening at once to draw any meaningful conclusions. There is the complexity of adhesion, the nature of the chemotaxis, the temporal switching between seasons, and the reproduction process. Each of these is explored to a limited extent, and it is unclear which are absolutely crucial to the conclusions reached and how sensitive the conclusions are to the assumptions made.

2) Regarding the definition of the model itself, the reviewers find it inappropriate to relegate so much of that explanation to the Methods section. The very large number of parameters (18) in Table 1 needs to be made clear (and that table should be referenced - it does not appear to be at present). Please explain more of the model in the body of the paper.

3) The reviewers are supportive of abstract models, but inasmuch as the authors have set up a physical/biological scenario with familiar processes (chemotaxis, adhesion) it would have been very helpful to have justified the kinds of dimensionless parameters that characterize the model in terms of real physical and biological features.

4) The essence of a Monte Carlo simulation is the definition of an energy function and a temperature, which together yield a Boltzmann factor that is used to decide if an attempted step is taken. The authors do not make clear in the main body of the text that they are performing a Monte Carlo calculation (that is only specified in Section 4, after the Discussion). They refer to MCS (Monte Carlo Steps) in the body of the paper without defining that term. But the larger question is why this kind of nonequilibrium biological system should have such an energy, and what would be the biological significance of the temperature? In addition, of course, the "steps" taken are those of Monte Carlo algorithm and have no direct interpretation in terms of real time.

5) The presentation of the model and the main results lack clarity in some key aspects: a. the relation between cell-cell and cell-medium adhesion and surface tension (line 136) is not explained, so it is not really clear what negative surface tension means. b. as surface tension pools two different kinds of adhesion, does it mean that in a certain sense adhesion to the surface can be traded off against adhesion between cells? This is important to know in connection to experiments. c. since the measure of sequence complementarity is symmetric, why does one need to suppose the existence of both a ligand and a receptor? Would it change anything if cells were characterized by only one sequence? If yes, it would be interesting to know if at the end of the numerical experiment ligand and receptor evolve to be the same or if 'molecular' diversity is maintained. d. the process of cell division/regrowth and the fact that cells do not change position from one season to the next should be more clearly explained in the main text. e. what is the initial spatial distribution of cells at the beginning of every season, and if this matters (many models assume aggregation-dispersal cycles, that does not seem to be the case here), should be specified or repeated in the evolutionary section. f. Figure 5 should depict a case of bistability: now it is not clear that different evolutionary outcomes are associated to differences in the initial surface tension, rather than in the initial cell configuration. It would by the way be interesting to see if the second also gives rise to bistability.

6) Cell migration (lines 394-404) is defined in terms of the actual direction of the cell over the past steps. This seems to build in persistence, and would appear to have a profound effect on the dynamics. Is this the case?

7) In general, it would be useful if statements like "In our case, aggregation leads to a highly efficient search strategy, guided by long-range, albeit noisy, gradients." (lines 272-273) could be made more quantitative. For instance, one would like to get a sense of whether the conclusions are robust to changes in (at least a few important) parameters. One would expect so from results in active matter physics, but it would be useful of the authors could argument it and indicate when they expect different conclusions to hold. Moreover, what is the role of the particular gradient chosen here in 'focalizing' the formation of multicellular groups (would an essentially 1-D gradient, where isolines are parallel, do the job?) and of its intensity/spatial variation (in the movie, one sees that the center of the gradient changes among four positions, does it matter?).

8) The authors claim that, in contrast to previous work, the increased fitness of the aggregates (better ability to perform chemotaxis) is an emergent property. The reviewers struggled to find a physical/mathematical explanation as to why such a relationship exists in the model but it appears that lines 424-427 contain the mechanism. The text speaks of the "center of mass of the perceived gradient". Unless we are mistaken, such a quantity averages over the individual constituent's contributions in such a way that larger cells will have more accurate measurements of the gradient. This is just the law of large numbers. If this is the case, then this feature is not an emergent property at all, but is part of the definition of the model. Please clarify. If the above critique is correct, then why bother with the complex model? The authors could just use the fact that larger aggregates are better at chemotaxis for the reason given and proceed from there.

The above suggests that the authors have basically put the answer in from the beginning. The model has the explicit feature that those that peform chemotaxis better reproduce more. So of course that will be reinforced. But multicellularity has costs and benefits, and the model does not appear to contain any costs associated with multicellularity. In real biological examples there are many - the increased metabolic cost of the structures that hold cells together, greater need for regulatory genetic networks, etc.

9) The referencing of the text to Figure 3 is all mixed up, leaving both text and figure hard to follow. -The authors should revise this section and make sure that they clearly state if higher chemotactic performance arises due to longer persistence of cell clusters only or due to longer persistence and higher chemotactic accuracy of whole cell cluster. Varennes et al PRL (2017) 119:188101 and manuscripts citing this work give measures for chemotactic accuracy within cell populations. - Fig 3d should show error bars. Annotation of Fig 3 f should be detailed, what is bar{X}? Is this the local gradient including noise or averaged on which scale.

10) The assessment time scale emerges as a decisive factor - it appears as a theoretical construct right now. What could it correspond to in the real world? Please discuss.

11) As for the particular details of the model, it is left unsaid in the main text but stated in the Methods section that there is a preferred cell size A_T and a harmonic energy around that size. As the target size is (Table 1) some 50 pixels, we are confused, as it seems that each "cell" occupies one lattice size. This energy would then clearly bias the system to aggregate already. Please clarify. The use of the term "pixel" for a lattice site is confusing.

12) The literature overview appears limited - please revise and consider recent work for example but not limited to Varennes et al PRL (2017) 119:188101; Jacobeen et al (2018) Phys. Rev. E 97, 050401(R). The authors should also discuss Guttal & Couzin 'Social interactions, information use, and the evolution of collective migration' PNAS 2010. And they should acknowledge relevant literature exploring, for example, similar issues in the Volvocales; "Multicellularity and the Functional Interdependence of Motility and Molecular Transport", C.A. Solari, S. Ganguly, J.O. Kessler, R.E. Michod, and R.E. Goldstein, PNAS 103, 1353-1358 (2006); "A General Allometric and Life-History Model for Cellular Differentiation in the Transition to Multicellularity", C.A. Solari, J.O. Kessler and R.E. Goldstein American Naturalist 181, 369-380 (2013).

This manuscript is in revision at eLife

The decision letter after peer review, sent to the authors on May 5, 2020, follows.

Summary

This study uses ontogenetic probes to activate the Raf and Akt pathways. This approach represents a powerful system to dissect signaling outcomes of these pivotal enzymes. Light-controlled activation of these two relevant signals is used to assess their ability to mediate axonal pathfinding, branching, and regeneration. The optogenetic tools allow for an examination of the sufficiency of either Akt or ERK pathway activation in these processes, in both PNS and CNS neurons. The result that both pathways play significant yet distinct roles in these processes is important and is of wide interest.

Several major and minor reservations were brought up by the reviewers. The major issues are to define more fully the upstream events that activate Raf-1 and Akt and the need for additional controls for the optogenetic probes. The kinetics of activation, as well as cell localization, requires attention. Another request is to examine if there is convergence in the two pathways. The major concerns are described below.

Essential Revisions

1) This study assumes that the tools trigger signaling pathways independently of upstream (neurotropic) signaling. However, whether these tools require some upstream signaling remain incompletely addressed. For example, activation of Raf1 requires upstream activation by kinases phosphorylating the N-terminal region (Y341 and S338). The phosphorylation of S338 is a commonly used read-out for Raf-1 activation (and mutants at this position show no activation). It would be very informative to examine the status of pS338 in optoRaf and to compare the optoRaf to a mutant S338A version, at least in Hek293 cells. Because these phosphorylations are linked to Raf dimerization, these studies would provide insight into whether Raf dimerization is required or possible in this context.

2) It would be also helpful to include more specificity controls for Raf vs. Akt signaling in Drosophila neurons to ensure the signals directly go to cells where the functional assessments are being conducted.

3) The kinetic experiments are interesting but somewhat incomplete, and it is unclear what the takeaway from these experiments should be. Importantly, it is not known how different pulsed light patterns translate temporally to signaling. It seems that from the data in figure 1, it is possible that in neurons patterns may maintain a constant activation of the pathway. Additional controls looking at the extent of signaling in neurons with these paradigms would be really helpful.

Minor Points

a) Recruiting optoAkt to the membrane does not make it independent of upstream PI3-K signaling, as PH-domain-containing kinases such as PDK1 are essential for Akt activation (by phosphorylating Akt on T308). Again, activation-specific phosphorylations on T308 could verify whether PI3K are involved in optoAkt function.

b) In one experiment, the authors tested the functional outcome of combining Raf and Akt activation, but it would be helpful if these were done in other experimental paradigms as well. Are these signaling pathways semi-redundant functionally or additive and able to further enhance the extent of regeneration? In this regard, what are the obstacles to utilizing optoRaf and optoAkt concurrently? Would synergism be expected?

c) The study suggests a lack of cross-talk between the two pathways. Given the ability of each pathway to achieve some regeneration on its own, the authors should discuss whether these pathways might eventually converge on common downstream effectors.

d) Given previous genetic studies, it is a bit surprising that Raf signaling plays a more pronounced effect than Akt in regeneration. It would be helpful in the authors could comment on this in the discussion, not just in the context of Erk/Akt but also the broader regeneration literature.

e) The Discussion points out the role of neurotrophic factor signaling, which is upstream of Raf and Akt. It should be acknowledged there is an absence of NGF family members and their receptors in Drosophila. This does not negate the results in the manuscript, but the significance of the findings should be clarified.

This manuscript is in revision at eLife

The decision letter after peer review, sent to the authors on May 7, 2020, follows.

Summary

In this study the authors have examined the role of TAZ in regulating hepatic gluconeogenesis. The authors show by genetically manipulating the hepatic levels of TAZ that TAZ acts as a repressor of gluconeogenic gene expression and in parallel this regulates hepatic glucose output either in response to a pyruvate tolerance test or to a bolus of glucagon. They go on to show that these effects are mediated via an interaction between the WW domain in TAZ and the glucocorticoid receptor that impairs the ability of the GR to bind to promoter regions. Intriguingly these effects were not observed with YAP another member of the Hippo pathway. These findings extend the expanding role of TAZ in hepatic metabolism. This is an extremely thorough analysis of the role of TAZ in hepatic metabolism involving a series of in vivo and in vitro studies utilizing different approaches to perturb the expression of hepatic TAZ levels. Much of the biochemistry is convincing and the data are well presented. The referees were less enthusiastic about the physiological implications of the data.

Essential Revisions

1) The effects of TAZ overexpression were much more impressive than its under-expression when looking at PTT. In fact if it weren't for the almost non-existent error bars for each BG measurement on the PTT I would almost doubt there is much of a significant effect of TAZ KO. How do the authors explain this? Is this because the mice were so fasted that hepatic TAZ levels are already so low that further reduction in its expression has little effect? This raises the issue of how physiological the level of overexpression of TAZ was. In Figure 3, if I am to interpret this correctly, the level of TAZ in total liver was 3-fold higher in overexpressing mice than controls whereas in the pericentral regions it was expressed at comparable levels to endogenous. Does this mean that there is much TAZ expression in other parts of the liver where TAZ would normally not be found? This needs to be addressed in the manuscript.

2) It would be important to measure TAZ protein concentrations in liver of diabetic mouse models i.e hyperglycemic (genetic or nutritional models of diabetes and/or insulin resistance). Does TAZ affect the binding of GR to gluconeogenic gene promoters under hyperglycemic/diabetic conditions?

3) Would the overexpression of TAZ prevent the hyperglycemia characteristic of db/db mice for example? It would help determine the potential role of TAZ in pathophysiology.

4) Why do the authors not consider - and discuss - the possibility of regulation of glycogenolysis by TAZ-GR? The reduction in liver mass with TAZ knockdown seems more consistent with promoting glycogenolysis (as glycogen will take up more space/account for more liver mass than gluconeogenic precursors) vs gluconeogenesis.

5) The interpretation of the ITT is questionable: the authors state that there was no difference in insulin sensitivity, but if we calculate the plasma glucose concentrations during the ITT based on the time zero plasma glucose concentrations in the PTT, we would expect plasma glucose in the ITT to drop to ~60 mg/dl in the floxed mice and ~70 mg/dl in the L-TAZ KO animals. Given this degree of hypoglycemia, not only insulin sensitivity, but also hypoglycemia counterregulation (which involves glucocorticoids!) would modulate plasma glucose. Please discuss.

This manuscript is in revision at eLife

The decision letter after peer review, sent to the authors on April 27, 2020, follows.

Summary

This paper presents a primary ovarian insufficiency (POI) case study, proband and affected family members with a unique genetic variant in HSF2BP. To examine the functional consequences of this variant, they generated a mouse mutant with the equivalent allele (S167L). Despite ostensibly normal numbers of follicles, Hsf2bp- S167L female mice showed reduced fertility in females. The authors also identify an interaction partner of HSF2BP named MIDAP and provide evidence that these two proteins function interdependently to facilitate BRCA2-mediated assembly of RAD51/DMC1 strand-exchange complexes.

Essential Revisions

Overall, while there are a lot of data in this paper, the quality of some experiments is questionable and lack rigorous quantification. The text is often inaccurate, sometimes not correct and requires major clarification and improvement.

Below are essential points and important point to revise, that include new data, formatting figures, text modification and reorganization.

1) One essential issue is to validate the conclusion that the case of human POI is caused by a variant of HSF2BP. Thus, the mouse mutant Hsf2bp167L requires additional analysis.

2) Another major problem is order and clarity of data presentation:

a) When presenting the phenotype of the Hsf2bp point mutant, the authors should clarify first the already published phenotype of the null mutant. They can add the data of their own null mutant as comparison.

b) Order of data: Males and female data are not presented in a consistent way for the analysis of Hsf2bp mutant (fig3, 4 and 5): Best would be to present male and female in parallel: Fig 3 (RPA), Fig 4 (DMC1, RAD51), Fig 5 (Mlh1). RAD51 data for female is required.

MIDAP localization in Hsf2bp mutants should be presented along with its colocalization with HSF2BP in wt.

Analysis of SPATA22 should be moved to main figures.

3) Removing poorly informative data: The in vitro assay fails to detect DNA binding activity of MIDAP or HSF2BP. This negative result obtained with non-purified proteins of undetermined concentration and molar ratio with the substrate do not allow to conclude on the DNA binding property of those proteins. Only part of the co-transfection analysis (Fig10) should be maintained.

4) The localization of HSF2BP/MIDAP at DSB repair foci is not shown in this study. This should be clarified either by referring to the previous study or by doing colocalization analysis (with RPA or DMC1 or RAD51).

5) Clarifying interpretations: Importantly the protein levels of HSF2BP and MIDAP is the mutants (Midap and Hsfp2bp) should be tested (in extracts from juvenile to avid confounding effect of cellular composition). Any coIP and western blot analysis from mouse testis to validate the interactions? And also the one with BRCA2? This would be expected given the Mass/spec data.

This manuscript is in revision at eLife

The decision letter after peer review, sent to the authors on April 22, 2020, follows.

Summary

Mutations in the five subunits of the eukaryotic initiation factor 2B (eIF2B1-5) complex cause a severe leukodystrophy called Vanishing White Matter (VWM) disease. In this study from the Bonkowsky lab, new mutants were either generated or imported and analyzed for CNS defects relevant to VWM. By studying growth, lethality, myelination, CNS cell development, and swimming behavior, the authors conclude that the new eif2b mutants phenocopy VWM patients. The authors also show that in mutants, a retained intron leads to expression of a truncated transcript, which they conclude acts in a dominant-negative fashion and suggest that this explains some pathology in human VWM patients.

Although modeling human disease in model organisms like zebrafish is important, there are several major issues with the study that dampen enthusiasm as outlined below.

Essential Revisions

Significance of model

1) For most of five the mutations most of them are heterozygous. Here the authors showed that only 2 out of 4 subunit mutants (eif2b5, eif2b2) exhibited phenotypes . Is it possible that other mutant alleles have mild phenotypes, such as increased ISR? More characterization of phenotypes in the other mutants (eif2b1, eif2b4) and the heterozygous siblings is needed to address relevance of this as a model of VWM.

Motor defects

2) It is unconvincing that the movement measurements in eif2b5zc103 mutants represent motor behavior deficits. Please address possible non-specific developmental delays cause the observed phenotypes. Can the authors perform the behavioral experiments at later stages or provide stage matched (rather than age matched) characterizations the mutants?

3) In Fig. 6, for the truncated EIF2B5 mis-expression experiments, it is unclear from the text and methods how the experiments were performed. If the truncated protein acts as a dominant-negative in the e1f2b mutants, why would expression of the wild-type gene rescue the mutant phenotype? The dominant-negative product would still be present. Also, Figure 6D: Compare motor behavior in actin:eif2b vs eif2b5 expression and clarify and address alternative interpretations of the data (See reviewer 3 comments).

Characterization of oligodendrocytes and myelin

4) Olig2 also labels motor neurons in the spinal cord and neural precursors in the hindbrain. Based on this marker alone it cannot be concluded they are only quantifying oligodendrocyte lineage cells in Figure 3. Please address.

5) Fig 3P-S: the TUNEL staining overlaps with Olig2 in the hindbrain but not in the rest of the brain. Please investigate which other cell types are undergoing apoptosis the optic nerve and optic tectum where the myelination and axon defects are evident in the eif2b5 zc103/103 mutants/

6) Fig. 3F-I:the eif2b2 and eif2b5 mutants show a striking change in proliferation pattern at 5dpf, including a loss of proliferation in the eyes and cerebellum and increased proliferation in the ventricles. To investigate which cell types are undergoing altered proliferation co-staining for cell-type-specific markers (eg: microglia, astrocytes, neurons) Is needed. See reviewer 1 comments.

7) The electron micrographs in Figure 4 are low quality and cannot be analyzed for G-ratio based on what is shown. Please address.

This manuscript is in revision at eLife

The decision letter after peer review, sent to the authors on April 18, 2020, follows.

Summary

This study investigates whether peroxisomal import is regulated by phosphorylation. The authors initially identify peroxide-triggered phosphorylation on Pex14 using PhosTag gels, then identify the sites, and use mutations to probe their importance. The key discovery is that S232 on Pex14 is phosphorylated (among other sites) in response to H2O2, that a phosphomimetic mutation of this site impairs catalase import, and that the reduced import of catalase during H2O2 treatment is important to maintaining viability during the stress. In vitro interaction studies suggest that the phosphomimetic Pex14 mutant can bind Pex5L, but does not form a stable ternary complex with Pex5L and catalase. The other phosphorylation sites seem to have less of an effect, but may affect other PTS1 import substrates. The primary conceptual advance here is that peroxisome import machinery can be regulated by phosphorylation to affect import of some, but not other substrates. The referees agreed that the conceptual advance of identifying a new regulatory aspect of peroxisomal import is appropriate for publication in eLife, but that the data are currently insufficiently complete to fully support the manuscript's claims.

Essential Revisions

1) The mechanism proposed by the authors for regulation of catalase import involves Pex14 phosphorylation. Yet it is Pex5 that recognizes catalase in the cytosol and is required for chaperoning catalase across the peroxisome membrane. Thus, to understand the mechanism of regulation, their crucial in vitro experiments examining substrate-Pex5-Pex14 interactions need to use the appropriate substrate-Pex5 complexes. Mammals have two Pex5's, a short Pex5 responsible for PTS1 import, and Pex5L, which binds to Pex7 and helps guide PTSII-containing proteins into the peroxisome. The authors do not provide any justification in the manuscript for why Pex5L was used in the in vitro binding experiments, and they do not provide any comparative experiments using the short Pex5. The authors must address this concern in order to justify the extrapolation of the in vitro experiments to the situation in cells.

2) The phospho-serine rich site identified by the authors is predicted to be a PEST sequence by bioinformatic searches using the sequence for rat Pex14. PEST sequences are typically found on short-lived proteins and act as a signal for turnover by the proteasome or calcium-dependent calpain proteases. In several instances, Fig 1B, Fig 2A, Fig 2D, etc. it appears that oxidative stress results in a reduction of Pex14, consistent with a hypothesis that this proline and serine rich site is functioning like a PEST sequence. In Fig 4F, phosphorylated Pex14 is detected in the cytosolic fraction, which the authors claim is non-specific. An alternative explanation is that Pex14 is being extracted from the peroxisome and turned over upon H2O2 treatment. The dynamics of Pex14 turnover and its contribution to peroxisome import dynamics is not explored by the authors, but has important implications for their hypothesis. The authors should carefully consider the possibility that phosphorylation regulates Pex14 turnover, which impacts import dynamics. If the authors have data on the turnover of Pex14 and its mutants under different conditions, this would be important to include. At the very least, this alternative explanation for regulation should be discussed in a revised manuscript.

3) The microscopy experiments present in Figures 3 and 4 are not very convincing and are incomplete. It is difficult to see catalase in the cytosol in the S-to-D mutants. The control images stained for SKL are not shown, confounding the analysis. Further, the localization of the Pex14 mutants, while appearing punctate in the images, was not confirmed by colocalization with another PMP. Finally, equal expression of the different mutants relative to wild type was not verified (e.g., by SDS-PAGE analysis of parallel transfections). To make the experiment more complete, control SKL images need to be presented, the subcellular localization of the Pex14 mutants verified by colocalization with another PMP, and equal expression of the mutants verified by either quantification of the microscopy or SDS-PAGE.

4) Loading controls for the experiment in Figure 4D are needed to make this fully interpretable. Quantification of EGFP-PTS1 and HA-catalase in Figure 5C would be helpful to a reader.

5) Figure 4F is not convincing because the differences claimed are not very easy to appreciate and the degree of reproducibility of the small effects is not clear. To be convincing, this experiment needs to be quantified from multiple replicates and should be accompanied by Total samples to show the levels of the proteins in each sample before fractionation.

6) The anti-His blot in Fig. 2D is of poor quality and cannot be interpreted with confidence. The Pex14 blot is clear, but is complicated by co-expression and partial co-migration of endogenous and exogenous Pex14 species. This experiment would be improved by either improving the quality of the anti-His blot, or perhaps if the authors preformed a His-pulldown followed by blotting to selectively visualize the exogenous proteins. The other option is to perform the experiment in cells lacking endogenous Pex14. Regardless of the approach taken, the authors should improve the quality of this important figure.

7) The claimed role of Pex13 is not clear from the results in Figure 5A. This experiment can be improved if the authors perform IP with phospho-specific antibody to substantiate the claim that Phosphorylation of Pex14 alters it complex formation with Pex13. Alternatively an IP via Pex13 could also be performed and show that the pS232 is coming down with Pex13.

8) The conclusion that phosphorylation is ERK mediated has been shown with a single inhibitor and should be extended to show this more directly by checking Pex14 in ERK KO or siRNA cells.

This manuscript is in revision at eLife

The decision letter after peer review, sent to the authors on April 12, 2020, follows.

Summary

The authors explored the processes involved in the fate of LY6Chi monocytes and the factors influencing this process under TLR7-induced inflammation. They show that the Ly6Chi monocyte conversion to Ly6Clo monocytes is dependent on cell intrinsic Notch2 and Myd88 pathway as selective invalidation of Notch2 bias the differentiation of monocytes in steady state and more extensively in inflammatory condition toward circulating macrophages. This is an interesting paper and the presented experiments are of good quality. This study uses a variety of conditional genetic deletions, cell transfers and cell culture techniques to track these cells in vivo and in vitro.

Essential Revisions

While the editors and reviewers all agreed on the interest of the study, several points need to be addressed to strengthen the study.

The transcriptome analysis presented in Fig. 4 is important, but missing Ly6Clow monocytes from wt and myeloid Notch deficient cells under steady state conditions. It would be important to compare the profiles of untreated and IMQ-treated Notch2-deficient cells to dissect the treatment effects from the steady state condition caused by Notch2 deletion.

The authors should provide deletion efficiency in both monocyte subsets, for instance by qRT-PCR for the deleted exon. There is experimental proofs that the Cre lox system is not fully efficient in classical monocytes, usually associated to their short life span and likely partial in the ncMo (as confirmed in Gamrekelashvili et al Nat com 2016) and others. This could explain why the PCA analysis detects minimal difference in the Ly6Chigh subset as well as no impact on numbers in Notch2-mutant mice. Hence it is dificult to support the main conclusion that Notch2-mediated decision occurs at the Ly6Chigh level as it is still mostly present. Notch2 could rather regulate the survival of Ly6Clow Mo. This point is slightly discussed on p13. The efficiency of Notch recombination in Mo subsets after the different treatments must be presented (even if previously published at steady state) to better apprehend this limit.

Lineage tracing is always challenging, and it is difficult to assess whether notch signaling is requested in the differentiation toward a specific lineage or is requested for cell survival. Notch regulated monocyte survival is a well taken point, since also Bcl2 is strongly decreased in notch2-/- monocytes. Therefore providing absolute numbers for the in vivo and in vitro experiments (cell numbers instead of %) is absolutely required. In fact, most of the study is based on % (often unclear among which population) which could lead to misinterpretation. The authors should provide absolute numbers per organs along with per mg, whenever possible. For example "By comparison, the TLR4 ligand LPS also increased Ly6Clo cell numbers and expression levels of Nr4a1and Pou2f2. However, the absolute conversion rate was lower under LPS and there was no synergy with DLL1 (Figure 1D and E)". The numbers are not evaluated here neither the conversion rate as long as survival difference cannot be excluded.

The 'unrestrained inflammation' part either should be experimentally proven our should be completely rephrased (or deleted). The authors state in the abstract that "the absence of functional Notch2 signaling promotes resident tissue macrophage gene expression (...) resulting in unrestrained systemic inflammation" that could be interpreted as an overstatement. The inflammatory response shows perturbation in Notch-deficient mice, but not a clear pro-inflammatory shift (see also point below). Accordingly, it is not clear, if the splenomegaly or the "unrestrained systemic inflammation" is directly caused by monocytes. LysM-Cre is also active in neutrophils, which similarly express high levels of Notch2 according to immgen and can contribute to the observed phenotype. If the authors want to keep the link of 'Notch2-deficient monocytes cause unrestrained systemic inflammation' then the authors should perform monocyte (anti-CCR2 treatment) and neutrophil (anti-Ly6G treatment) depletion experiments in IMQ-treated wt and Notch-deficient mice. If the observed splenomegaly in Notch2-deficient mice is reduced to wt levels when treated with CCR2 (but not after Ly6G treatment), it is likely that monocytes are the direct cause.

T0 purity and flow analysis (F4/80, Ly6C,CD43, CD11c CD11b and GFP) of the sorted monocyte from all mouse strains should be provided. Working with bone marrow monocytes can be precarious, as the bone marrow may be contaminated with progenitors (and should be mentioned in the text).

In Fig. 3 the authors perform t-SNE analysis based on the Ly6C, CD43, MHCII, F4/80 and CD11c marker set and according to this identified 5 monocyte 'subsets' (Fig. 2c). Please also show the corresponding flow cytometry analysis (dot plots) (especially for PB) to identify these 5 subsets by regular gating and to see intensity of especially F4/80 and MHCII staining in Ly6Chigh and Ly6Clow monocytes in all conditions. In addition, in the gating strategy Fig. S1c the authors used F4/80 to discriminate CD115+ MF from monocytes. Rose et al., 2011 in Cytometry A showed that splenic monocytes also express F4/80 and that this antigen can be used to identify monocytes. Therefore it is possible that MF cells in the authors' gating strategy are contaminated by (probably aged) Ly6C low monocytes that up-regulated F4/80. To counter argue this please show their gated MF in a FACS plot with Ly6C vs CD43.

Consistent with the working hypothesis: Notch deficient LY6Clo monocyte phenotype drastically changes following IMQ Figure 3. Why were Ly6Clo wt and N2 deficient monocytes not examined without IMQ Figure 4? It is important to know how these cells alter from baseline and help distinguish if the effects are IMQ alone, Notch alone or IMQ and Notch.

The conclusion from these studies is in the presence of IMQ and absence of Notch2 LY6Chi cells become more of a "macrophage" compared to the natural progression towards LY6Clo monocytes Figure 5a/b. In Figure 5b, c and F what is the phenotype without IMQ. At present, without the controls, it is hard to comment on these experiments.

This manuscript is in revision at eLife

The decision letter after peer review, sent to the authors on August 26 2020, follows.

Summary

This study investigates the relationship between maternal cortisol levels (measured from hair) and infant amygdala microstructure in a cohort of 78 mother-infant dyads. The neonates were a mix of those born at term (n=42) and those born prematurely (n=36) but all were scanned at term equivalent age. The authors demonstrate sex-stratified relationships, with a strong relationship between cortisol and amygdala microstructure in males and a relationship between amygdala and other temporal/subcortical regions in females.

The reviewers agreed that the manuscript is both interesting and timely. The imaging methods are well performed. However, we shared a series of concerns that should be addressed before we can consider publication.

Essential Revisions

Sample:

-- The incidence of preterm birth is ~10%, while in this cohort the incidence is much higher. Were the women recruited from a high-risk pregnancy clinic (which may be a high stress population) or do the gestational ages largely reflect twins included in the sample?

-- All infants were imaged at term for this protocol. However, NICU-related procedures occurring between birth and scan (primarily days of mechanical ventilation and infection) are associated with alterations subcortical development in preterms. Was the preterm cohort a critically-ill cohort? Were these clinical variables available?

-- Maternal education is an important predictor of brain development and outcome. Had the authors considered to adjust for this variable in their analyses, particularly for the volumetric analyses?

Stress and cortisol:

-- The last line of the abstract implicates that the amygdala cortisol relationship gives an insight into the relationship between maternal stress and child outcome. Cortisol levels are shown here to covary with microstructure but do they reflect actual maternal stress in pregnancy in this sample? Are there any maternal stress (anxiety or depression) questionnaires that could be reported to address this?

Sex Divergence:

-- It's not just one sex that is affected but rather sex-specific effects dependent on the outcome examined (amygdala microstructure in male babies and microstructure of connecting white matter from the amygdala in female babies). The abstract doesn't describe this divergence, focusing on results only with respect to female neonates but actually the interaction effects both sexes in different ways / regions. It would also be very helpful to have plots to illustrates the relationships (residualised for covariates).

Interpretation of measures:

-- The major conclusions concerning HCC, the interaction with infant biological sex and the diffusion measures revealing evidence for alterations in "dendritic structure, axonal configuration, and the packing density of neurites..." aren't entirely supported by the findings based on the results from volumetric analyses. The alterations in ODI seen with HCC should be paralleled by changes in the volume data.

Given that brain volume differences are also believed to underlie alterations in dendritic structure, the authors' conclusions wouldn't entirely be supported. Modifying the central claims would be recommended but more data aren't required to support the findings.

-- The lack of a significant association between macrostructural changes in the amygdala and HCC was surprising. This is in consideration of previous work in the area in the GUSTO cohort, which focused primarily on amygdalar volumes. The discussion of the results related to the volume data should be expanded upon.

-- How inter-related were the measures - e.g. is there a negative association between amygdala microstructure and amygdala connections that could explain the split in sex associations and directionality.

Discussion:

-- What potential biological mechanism do the authors propose underlies these sex specific results. There are only really two vague sentences on this but the complex results need more.

-- The authors present an extremely comprehensive overview of the connectivity of the amygdala. Given the authors' conclusions regarding future social cognition assessments, it's surprising to see that the subcortical gaze pathway was not examined (amygdala, thalamus, superior colliculus) as this pathway rapidly processing eye/face processing. Examining connectivity with midbrain structures might be infeasible in the neonatal brain; however, including a discussion of this pathway would be useful for future research in the area.

-- For the HCC relationships with microstructure, maternal HCC values for the preterm infants reflects exposure during (coarsely) a different trimester to the term-born infants. The subgroup analyses (term/preterm) indicate that the results are largely independent of this so does this implicate that the influences on amygdala development are from early gestation?

[Note: this preprint has been peer reviewed by eLife. The decision letter after peer review, based on three reviews, follows. The decision was sent on 19 May 2019.]

Summary

This paper describes five cryo-EM structures of ribosomal complexes apparently representing different stages of RF2-catalyzed translation termination. The novel observations here are that the tip of domain 3 of RF2 undergoes a rearrangement from an a-helical conformation to a b-hairpin conformation during termination that likely facilitates exit of the newly synthesized protein from the ribosomal polypeptide exit tunnel and that the ribosome can undergo two thermally activated, spontaneous conformational changes, a relative rotation of the ribosomal subunits and a swiveling of the 'head' domain of the small subunit, during termination that likely facilitate dissociation of RF2 from the ribosome. These are interesting observations that significantly extend our understanding of how class I RFs and ribosome conformational changes drive important steps during termination and, as such, all three reviewers recommended publication provided the following comments are addressed adequately.

Essential Revisions

1) The maps provided through the eLife system seemed to be unsharpened, as they showed very little detail. However, even after sharpening them with a B-factor of -100A2, they still did not show the expected features for their respective resolutions. My suspicion is that FREALIGN has been used to overfit the data. This should be addressed in the revision. It should be indicated whether gold-standard separation of halves of the data sets were used in the final refinements, or whether those were limited to a specific spatial frequency (like was done in the classifications). If the latter, those frequencies should also be stated in the manuscript, and they should be significantly lower than the claimed resolutions.

In addition: a lot of basic cryo-EM information is missing: the authors should include: a) at least one micrograph image b) some representative 2D class averages c) local resolution maps of the five structures. Also, because the density of important parts of the maps seems to be a lot worse than the resolution claimed, it would be good to explicitly mention the local resolution of the important features discussed in the main text. d) for each structure, some zoomed-in figures with the density on top of the molecular model. These figures should be chosen as to validate the resolution claim. For example, in structures I, II and V, the RNA bases should be well separated (they do so at 3.6A), and in structures III and IV beta-strands should be well separated, and many (larger) side chains should be visible. In addition, some panels with density for the most important features of each structure should be shown. e) FSC curves between the refined PDB models and the cryo-EM maps are missing from the manuscript. These should be included. In addition, to evaluate potential overfitting of the models in the maps, for each structure, the authors should also include the FSC curves between a model that was refined in half-map1 versus half-map1, as well as the FSC curve between _thesame model versus half-map2.

2) There appear to be many self-citations, and there are also a few places where relevant citations are missing or are mis-cited. There are too many to list individually, but, just a few examples: Page 4: the only citation for the phrase "recent biophysical and biochemical findings suggest a highly dynamic series of termination events" is a Rodnina paper. There are many, earlier papers from Ehrenberg, Gonzalez, Puglisi, Green, Joseph, etc. that should be cited here. Page 5: The only citation for the sentence "By contrast, biochemical experiments showed..." is a Green paper. There are earlier papers from Ehrenberg characterizing the effects of the GGQ-->GAQ mutations on the ability of RF3 to accelerate the dissociation of class I RFs from termination complexes that should be cited here. Page 5: There's a sentence that refers to X-ray, cryo-EM, and smFRET studies, but only provides citations to two smFRET studies (Casy et al, 2018 and Sternberg et al, 2009); Page 5: Moazed and Noller, 1989 identified and characterized the P/E hybrid state, but they didn't report that a deacylated P-site tRNA 'samples' the P/E hybrid state 'via a spontaneous intersubunit rotation'--that was later work from Noller and Ha; etc. There are several other instances of missing citations or mis-citations. We would ask that the authors review their citations with an eye for excessive self-citations and for missing citations or mis-citations. In this context, "Ensemble-EM" is also cited as a specific method in the introduction (Abeyrathne et al., 2016; Loveland et al., 2017). However, this method is more commonly known as (3D) classification of cryo-EM images, and there are many older, more appropriate citations.

3) The sample imaged is a model sample generated by in vitro assembly with purified components of a termination complex. In order to mimic a bona fide termination complex, a short messenger RNA with a strong Shine-Dalgarno sequence followed by a start codon and immediately after by a stop codon was used (mRNA sequence: 5'-GGC AAG GAG GUA AAA AUG UGA AAAAAA-3'). Similar constructs were used to crystallize termination complexes in the past and it has been proven by smFRET experiments that, at least regarding ribosomal inter-subunit dynamics, this model sample behaves similarly to a real termination complex with a peptide linked to the P site tRNA. However, the nature of this model sample should be apparent for the non-specialist reader, highlighting its similarities with a real termination complex but also its possible limitations, especially regarding the "artificial" nature of having a stop codon so close to the Shine-Dalgarno sequence, a situation that never happens in real mRNAs. The authors should explicitly acknowledge this and discuss its implications in the main text.

4) The authors set up a couple of somewhat 'strawman' arguments in claiming that: (i) there are discrepancies in the X-ray, cryo-EM, and smFRET literature with regard to whether ribosomes can undergo intersubunit rotation while bound to class I RFs or whether the non-rotated conformation of the ribosome is stabilized by bound class I RFs and (ii) class I RFs are able to terminate translation and dissociate from the ribosome without the aid of RF3. In the case of (i), it is obviously possible for class I RF-bound ribosomes to undergo intersubunit rotation while still favoring the non-rotated conformation of the ribosome. Moreover, there are enough differences between the cited studies, both in terms of the experimental conditions as well as the technical limitations associated with the various experimental techniques, that it is easy to rationalize differences with regard to whether the class I RF-bound ribosomes would be expected to undergo intersubunit rotation and/or whether the researchers would have been able to capture/observe intersubunit rotation. In the case of (ii), decades of biochemistry from Buckingham, Ehrenberg, Green, and others had already demonstrated that class I RFs are able to terminate translation and dissociate from the ribosome without the aid of RF3, and that the role of RF3 in termination is to accelerate the spontaneous dissociation of the class I RFs. If the authors want to highlight discrepancies in the literature, they should frame them in the context of differences between the studies, experimental design, limitations of the approaches/techniques in the cited papers that might account for such discrepancies. Re-writing this paragraph also in the light of addressing the missing citations and mis-citations pointed out under (2) will further help in toning these arguments down, which would strengthen the manuscript's scholarship.

5) Class I RFs are post-translationally methylated at the Q residue of the GGQ motif of domain 3 and Buckingham, Ehrenberg, and others have shown that this methylation accelerates and/or facilitates class I-catalyzed termination both in vitro and in vivo. Nonetheless, Svidritskiy et al do not report whether and to what extent their RF2 is methylated. Was RF2 overexpressed in a manner that ensured homogeneous methylation or lack of methylation? If they are overexpressing prfB and not overexpressing prmC, it is likely that they have a mix of methylated and unmethylated RF2. Assuming they are using the wt E. coli prfB gene, then the residue at position 246 is a T, rather than an A or S, and Buckingham has shown that, in the wt T246 background, a lack of methylation at Q252 is either seriously detrimental in richer media or lethal in more minimal media. It was felt that a discussion of this issue was not needed in the main text, but that it would be helpful if the authors would include the important/relevant experimental details in the Methods section, for example, did they use the T246 wt E. coli variant of RF2; and did they overexpress prmC along with prfB?

6) Structure I is denoted and treated as a pre-termination complex, but that does not seem at all possible given that the sample was prepared by incubating a pre-termination complex for 30 min in the presence of excess RF2, conditions that Figure 1-Figure Supplement 3 suggest results in robust termination. Structure I is more likely the non-rotated conformation of a post-termination complex that is in equilibrium with its rotated counterpart, Structure V. Based on my reading of the manuscript, it is likely that the authors understand this point, but are nonetheless using this structure as a mimic/analog of a pre-termination complex. If so, I think this is fine, but the authors should explicitly state that this is what they are doing. Related to this, the authors should clarify the description of their activity assay, show the raw data, and/or report 'Released [S35]-fMet (%)' instead of 'Released [S35]-fMet, CPM' on the y-axis of Figure 1-Figure Supplement 3; as the activity assay is currently described, reported, and plotted, it is impossible to determine whether RF2 is 1% or 99% active in termination.

7) The final sentence of the manuscript reads: "Translation termination and recycling of the release factors and the ribosome therefore rely on the spontaneous ribosome dynamics, triggered by local rearrangements of the universally conserved elements of the peptidyl-transferase and decoding centers". There are a couple of problems with this sentence as written. First, smFRET experiments by Gonzalez, Puglisi, and Rodnina have previously shown that "Translation termination and recycling of the release factors and the ribosome therefore rely on the spontaneous ribosome dynamics" and the relevant articles should therefore be cited here. Moreover, given the data are static structures solved using a sample that is at equilibrium, it is not clear how the authors determined that these spontaneous ribosome dynamics were "triggered by local rearrangements of the universally conserved elements of the peptidyl-transferase and decoding centers". Isn't it equally possible, given the data presented, that the local rearrangements were triggered by the ribosome dynamics?

[Note: this preprint has been peer reviewed by eLife. The decision letter after peer review, based on three reviews, follows. The decision was sent on 24 May 2019.]

Summary

The manuscript from Munkley, Elliott and colleagues shows that the epithelial splicing regulator ESRP2 is transcriptionally upregulated by the androgen receptor (AR), an observation based on a previous study of gene expression changes in response to androgen in the androgen receptor positive LNCaP prostate cancer cell line by some of these investigators. ESRP2 upregulation leads to a series of changes in alternative splicing, including switches with potential effects in disease relapse and metastasis which correlate with disease outcomes. Prostate cancer is driven by androgens via AR, and therapy involves androgen deprivation (ADT) to slow progression. However, it has also been reported that ADT promotes epithelial mesenchymal transition (EMT) (e.g. Sun et al, 2012), which might be related to the common progression to castration resistant prostate cancer following ADT. Munkley et al show that levels of ESRP2 are reduced after androgen deprivation in 7 prostate cancer patients. A number of other analyses using additional cell lines, a xenograft model, and data from other published prostate cancer samples leads to a general proposal that a decrease in ESRP2 expression (but not ESRP1) and some splicing changes associated with its depletion following androgen deprivation may be associated with prostate cancer progression and worse outcomes. One highlighted example is exon 30 in FLNB, skipping of which is associated with metastatic progression in breast cancer.

A number of papers describing roles for ESRP1/2 in various cancers including breast, colorectal, lung, and ovarian carcinomas have yielded conflicting conclusions on the role of ESRPs or epithelial-specific isoforms it regulates, such as CD44, in cancer progression and/or patient outcomes. In some cases ESRPs are proposed to be tumor suppressors, whereas in other cases they are proposed to promote more aggressive cancers (see, for example, Zhang et al., Genes and Dev 33: 166-179 and references therein). As cited by the authors, a recent manuscript reports that duplication and increased expression of ESRP1 (which would largely promote the same splicing events as ESRP2) is associated with more aggressive human prostate cancers. Thus, a central question is whether the current manuscript can provide further clarity regarding the general role of ESRPs (including ESRP2) in cancer, including prostate cancer.

Munkley et al raise the clinically-relevant point that current treatments for prostate cancer might have undesirable side-effects by inhibiting ESRP2 mediated splicing events. Overall, the manuscript is clearly presented. The data documenting the ESRP and AR regulated splicing program, and the restriction of tumor growth by ESRPs (Figs 1-4, 6) are very clear with very nice correlations between responses to ESRP overexpression, knockdown and androgen stimulation.

Essential Revisions

1) A key concern relates to the relative levels and effects of ESRP1 and ESPR2 under conditions of androgen induction or ADT in prostate cells. The authors do a good job documenting that ESRP2 is under transcriptional control of the androgen receptor, while ESRP1 is not, and that there is a 2-fold reduction in ESPR2 expression post-ADT in cancer samples. On the other hand, a) both ESRP 1 and 2 seem down-regulated at the protein level in androgen receptor-negative prostate cancer cells lines (probably by different mechanisms), b) both ESRP1 and 2 mRNAs are up-regulated in tumor samples compared to controls, c) both ESRP1 and ESRP2 are up- regulated in a cohort of metastatic patient samples, d) the correlation between ESRP levels and recurrence free survival is a more significant for ESRP 1 than 2, and e) a number of functional assays from this manuscript and other publications argue that both ESRP1 and ESPR2 can contribute to regulate overlapping targets relevant for epithelial-specific splicing. Therefore one key question that remains is to what extent the androgen-mediated transcriptional regulation of ESRP2 does contribute to splicing regulation in the context of the relative levels / activities of ESRP1: while a number of the results presented show that androgen treatment can promote splicing towards a stronger "epithelial" pattern, the authors should make additional efforts to demonstrate that ablation of ESRP2 alone (in the presence of ESRP1) leads to substantial changes in splicing that would be expected to explain the association of a loss of ESRP2 with worse outcomes, which is an essential point for the validity of their model. For example, an analysis similar to that of Figure 1A for ESRP1 should be included, as well as other experiments aimed to determine whether the activity of ESRP1 can buffer the effects of ATD on ESRP2.

2) There is also a need for clarity in terms of the coherence of the predicted biological effects of the alternative splice site switches and at least one proof-of-principle demonstration that they are relevant for any property of prostate cells relevant to cancer, as it is difficult to draw firm conclusions from the data presented as to whether the regulation of ESRP2 by androgens is definitively associated with prostate cancer progression or outcomes in a positive or negative manner.

a) Figure 5A shows exons that are more included or skipped in prostate cancer vs normal using TCGA data. But only 6 of the 44 ESRP-AR regulated events are highlighted on the plot, two of which do not change significantly, including FLNB which is highlighted in the abstract and is the only event used to test the response to the AR antagonist Casodex. All of the events from Fig 3 should be highlighted in Figure 5A, with ESRP activated and repressed exons clearly distinguished by colour or symbol. The authors should explain -when known- the nature of the differential activities of the isoforms and whether the isoform switch observed in the presence of androgens / mediated by ESRPs is predicted to contribute, repress or be neutral to tumor cell growth, apoptosis, motility, metastasis, etc. and therefore whether a functionally coherent program of alternative splicing is coordinated by ERSPs or whether various contrasting contributions are predicted whose relative significance will depend on context, etc. If not, is it possible to stratify the data e.g. by tumor grade, or by ESRP expression level? Would this for instance, reveal different classes where events such as FLNB do show a difference between cancer and normal in some classes?

b) In Figure 6, why is FLNB e30 the only splicing event monitored for response to Casodex - especially since this is one of the events that is not altered between prostate cancer and normal tissue-? This Figure should be more systematic with more splicing events.

c) Increased inclusion of exon 30 in FLNB (which occurs for example upon androgen stimulation) is consistent with inhibition of EMT (something that could be stated more clearly in the text). But there is no mechanistic model presented as to how a change in FLNB splicing (or other targets) impacts prostate CA. What about the other alternative splicing events highlighted in Figures 4 / 5? Even if FLNB splicing switches have been shown to influence expression of EMT markers in breast cancer cells (Li et al 2018), it will be essential to show that the degree of switch observed in prostate cancer cells (for FLNB or any other gene) has a relevant biological readout.

[Note: this preprint has been peer reviewed by eLife. The decision letter after peer review, based on three reviews, follows. The decision was sent on 21 May 2019.]

Summary

Masachis, Darfeuille et al. analyse a type I toxin - antitoxin (TA) module of the major human gastric pathogen Helicobacter pylori (Hp). Expression of toxins encoded by Type I modules is controlled by small, labile, cis-encoded antisense RNAs and often also by complicated mRNA metabolism that envolves conserved mRNA folding pathways and/or mRNA processing. Using a combination of elegant and robust in vitro and in vivo methods, the authors first show that that the aapA3/IsoA3 TA system of Hp is regulated in a way very similar to that of the homologous aapA1/IsoA1 system from the same organism (Figs 1 and 2). This initial part of the manuscript sets the stage for the next step, where the authors employ a powerful genetic screen combined with deep sequencing to identify single nucleotide changes that abolish production of the AapA3 toxin (Fig. 3). This principle, which was invented by the authors, is technically robust, intellectually attractive and very powerful, and may yield novel insights that at present cannot be reached by other approaches. In particular, the authors discover that single point mutations outside the toxin gene reading frame suppress toxin gene translation. Focusing on the translation initiation region, they discover two mRNA hairpin structures that, when stabilized by single base changes, reduce translation by preventing ribosome binding (Figs 4-6). They propose that these structures are metastable and form during transcription to keep the toxin translation-rate low, as explained in the model figure (Fig. 7).

Essential Revisions

All of the reviewers thought the quality of the experimental work in the manuscript is outstanding and the conclusions are justified. However, all thought it would be nice to have additional evidence of the proposed metastable structures in the nascent toxin mRNA. While the reviewers understood this might be technically difficult, they agreed that it is worth a try and had the following suggestions.

1) Phylogeny (i.e. nucleotide co-variation in sequence alignments) was previously used to deduce the existence of stem-loop structures not only in ribosomal RNAs but also in mRNAs (e.g., hok mRNAs). Did the Authors consider using this approach to support the existence of the proposed metastable structures in the nascent toxin transcript? This possibility depends on the actual homologous sequences available and is not possible in all cases. If phylogeny indeed supports the existence of the metastable structures, the Authors could look for coupled nucleotide covariations that would support a conserved mRNA folding pathway (that is, one mRNA sequence elements pairs with two or more other elements during the fife-time of the mRNA) . The Authors state in the Discussion that "these local hairpins were previously predicted to form during the co-transcriptional folding pathway of several AapA mRNAs (Arnion et al., 2017)." However, they authors did not explain how these hairpins were predicted. It is worth explaining this central point.

2) Although transient structures are by definition hard to detect, the authors could try in vivo structure probing (DMS) of truncated mRNAs 1-64 and 1-90 to demonstrate the existence of the first and the second metastable structures, respectively.

3) It is preferable to carry out 2D structure predictions on the naturally occurring transcript, not a sub-sequence. 2D structure prediction generated by algorithms such as RNAfold (or Mfold) that are guided by delta-G stability optimisation are sensitive to the sequence context, so the correct sequence needs to be used to be able to draw conclusions. Additionally, the findings presented in Figure 3D could be analyzed a bit further to produce significant, independent evidence for some structure features. Specifically,

Figure 2 caption:

• lines 184 - 186: "2D structure predictions were generated with the RNAfold Web Server (Gruber, Lorenz, Bernhart, Neuböck, & Hofacker, 2008) and VARNA (Darty, Denise, & Ponty, 2009) was used to draw the diagrams."
• Please state clearly whether any of the results of the experimental 2D structure probing were used as input to RNAfold (i.e. as additional constraints to the prediction algorithm).

Figure 3D:

• Please add coloring to the peaks depending on which codon position they overlap (1, 2 or 3) and carefully discuss the corresponding results, also in the context of the 2D structure elements.
• Given that you have a decent number of pair-mutations, analyze them to see whether any correspond to RNA structure base-pairs (and whether any of the pair mutations rescue the base-pair and thus affect the system differently). This would serve as additional, independent evidence of 2D structure probing and predictions.

[Note: this preprint has been peer reviewed by eLife. The decision letter after peer review, based on three reviews, follows. The decision was sent on 17 June 2019.]

Summary

Natural Killer (NK) and the ILC1 subset of innate lymphoid cells share related functions in host defense but have been argued to arise from distinct pathways. Park et al present new evidence challenging this concept. They show that murine Toxoplasma gondii infection promotes the differentiation of NK cells into an ILC1-like cell population which is stable and long-lasting, even after the infection has been cleared. These T. gondii induced cells, unlike Eomes+CD49a- NK cells, are Eomes-CD49a+T-bet+ and therefore resemble ILC1 cells. The authors additionally show that their differentiation involves Eomes down regulation and is STAT-4 dependent, However, in common with NK cells and distinct from ILC1 the T. gondii induced "ILC-like" population circulates to blood and lungs. Finally, the authors employ single cell RNAseq to examine the heterogeneity of the major T. gondii induced innate lymphocyte populations and their NK vs ILC relatedness as assessed by gene expression. Together, their observations establish a previously unappreciated developmental link between NK and ILC1cells in the context of infection.

The 3 reviewers and editor agree that this is an important contribution that sheds new light on the developmental relationship of NK and ILC1 cells, a scientific issue that has received considerable attention in the innate immunity field. Although extensive, most of the criticisms raised can be addressed by revisions to the manuscript. One additional experiment is requested to provide a missing control.

Essential Revisions

All reviewers had a major concern about how this new population of T. gondii induced innate cells should be referred to in the manuscript. Based on the single cell RNAseq data, these cells (cluster 10) are still closer to NK cells than to ILC1s (Figure 5f and Suppl Fig 4e) despite their loss in Eomes expression and acquisition of CD49a expression. Thus, one could easily think of them as "Eomes negative NK" or "ex-NK" cells rather than ILC1s, and to simply refer to them as Eomes-CD49a+ ILC1 cells may be misleading . For this reason, the authors should modify the title of the paper and change their designation throughout the manuscript. We suggest "ILC1-like" as a good descriptor. In addition, although it is clear that the "Eomes negative NK" cells that are generated during T. gondii infection are transcriptionally and epigenetically distinct from the NK cells in the steady state and NK cells after infection (Figure 7 and suppl Figure 6), these "Eomes negative NK" cells referred to as "T. gondii-induced ILC1s" were not directly compared with classical ILC1s. Based on the single cell RNAseq data, these cells may not express many of the ILC1-related signature genes. Therefore, again, the authors need to be cautious in referring to them as ILC1 cells.

A second concern was that the NK 1.1 depletion shown in Supplemental figure 1 was performed with a PBS rather than isotope matched immunoglobulin control which is considered unacceptable. The authors should repeat at least once with proper control Ig to make sure this is not issue. It is not necessary to repeat entire survival curve just experiments shown in A and B and initial survival to make sure there is no death in controls vs. antibody treated.