127 Matching Annotations
  1. Oct 2021
    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on June 30 2020, follows:


      This paper addresses a critical issue in neuroscience: what's the question, and can we answer it? The questions the author proposes are ones that have been considered, in one form or another, reasonably often by experimentalists. And the author shows rigorously that there's a reasonable chance that they are simply not answerable.

      Essential Revisions:

      We believe that this is an extremely important issue, and the approach the paper takes is a reasonable one for addressing it. Our main worry, though, is that mainstream neuroscientists will ignore it, for two reasons. One is that it's not a message they want to hear. Second, the example circuits are sufficiently abstract that they can be dismissed as yet another musing by your typical uninformed theorists. (That is not, we should emphasize, our view, but it's not an uncommon one in the field.) Our goal, therefore, is to fix these potential problems, so that people will have to pay attention.

      The premise of the paper is that if you understand a neural circuit, there are certain questions about it that you should be able to answer. The author proposes six such questions, and then shows that in the worst case they are exponentially (in the number of neurons) hard to answer.

      The success of this program hinges on two things: a sensible set of questions, and a demonstration that answering those questions is hard. We're not ecstatic about the questions, but we believe that's not an insurmountable issue (more on that below). More problematic is the result that the questions are hard to answer. What's really shown is that there is at least one circuit for which, in the worst case, answering the questions is exponentially hard. While this is certainly correct, it doesn't make a convincing case that answering these questions will be hard in the brain. First, the worst case may not be the typical case. The 3 SAT problem, for instance, is NP complete, but is hard to solve only for a narrow range of parameters. Second, answering the questions for actual circuits found in the brain may not even be exponentially hard in the worst case.

      This brings us to two critical comments. First, it needs to be crystal clear that this paper does not demonstrate that answering the proposed questions is guaranteed to be exponentially hard, only that it might be. This was stated in the manuscript, but not emphasized. For instance, on lines 138-140, it says

      "Using techniques from Computational Complexity Theory, we ask what is the smallest number of experiments necessary, in general, in order to answer these questions, in typical experimental settings."

      Here "in general" means worst-case. For neuroscientists, though, "in general" means "most of the time". It should be clear that you mean worst case, and that the typical case may be very different.

      In fact, this needs an expanded discussion. Whether or not it will take an exponential number of experiments to answer the questions depends on the circuit. We might get lucky, and only a small number of experiments are needed. Or we might get unlucky, and a large number are needed. This analysis can't tell us that, and this should be clear in the paper.

      Second, what's really needed is the analysis of a more realistic circuit, ideally with both positive examples (for which it is possible to answer the questions) and negative examples (for which it isn't). This is hard, but we have a few suggestions, some of which can probably be done without a huge amount of work.

      a. Linear network, y=Ax+noise. For this (and possibly in all realistic) situations, "perform the task" needs to be replaced by "achieve a certain level of performance". For instance, if there's a true mapping y=f(x), then "perform the task" would be replaced with "<(y-y*)^2> below some threshold". The questions should be answerable in polynomial time for this network; otherwise, one should worry.

      b. In 2000, Hopfield and Brody came up with a simple circuit which we think of as "understandable" (Hopfield and Brody, PNAS 97:25, 13919-13924, 2000). It would be nice to determine whether the questions can be answered in polynomial time for this circuit. Again, if they can't, one should worry.

      c. Deep networks. Again, "perform the task" would have to be replaced with "performance is above some particular threshold". Here we suspect that the questions are not answerable; if that could be shown, it would be a huge step forward.

      d. A made-up model of a deep network. Assume that in a deep network, whenever you delete a neuron, performance drops. That's probably not so far from the truth -- and also not so far from what we think would happen in the brain. (With some exceptions; occasionally I hear talks where performance is better when two areas are ablated rather than just one, but let's ignore that.) How much performance drops depends, of course, on which neurons are deleted, so there's not a simple mapping between performance and which neurons are present in the circuit. Can the questions be answered in this case? This sounds like a problem computer scientists have considered, so possibly rigorous analysis could be done.

      We believe it's critical to consider a case that is not far from what one might find in the brain. Otherwise, it will be too easy to dismiss this work as irrelevant to real neuroscience. The above are only possibilities, and a and d may be pretty easy, but the author is welcome to come up with his own examples. Note that rigor is not absolutely necessary here, since there's already one rigorous example. Plausible arguments would be fine.

      Finally, "understand" needs further discussion. That's partly because the approach here is a little non-standard. Most people try to directly define "understanding". Instead, the statement is "if you understand a circuit, you should be able to answer these questions". This has to be made crystal clear -- especially since people aren't expecting it. In addition, a discussion of the more standard approach, a direct definition, should be included. The usual definition is something like "A short description of what is being computed, along with a description of an algorithm for computing it." It should be clear how this, more standard, definition compares to the one in the paper. For instance, under the standard definition it may be possible to understand a circuit without being able to answer any of the questions. For instance, I believe we can "understand" (by the more standard definition) the synfire chain circuit. This doesn't mean that one definition is better than the other, but their differences should be acknowledged.

  2. Apr 2021
    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on August 20 2020, follows.


      In this manuscript, Mughrabi et al reported a technical advance of long term vagus nerve stimulation (VNS) in mice. VNS has been used in clinics for treating certain patients with epilepsy and depression and pioneered in clinical trials for a number of disorders including inflammation. Yet, VNS has not been widely used in mice for mechanistic studies largely due to technical challenges dealing with the small size. Here, the authors developed a method for chronic implantation of VNS stimulator in mice, and tested the effectiveness of the method using measurements of heart rate changes and effects on inflammation. This method is potentially useful to investigate the therapeutic potential of long-term VNS in chronic disease models in mice. While reviewers were positive about the work performed in this study including that it was carried out by multiple labs, there are major concerns about certain points and additional essential experiments are needed. These include the need for robust data related to the LPS inflammation studies and histological analysis. There were also missing details of methodologies that decrease the enthusiasm for this study.

      Essential Revisions:

      1) At least two papers (PMID: 28628030, 32521521) have reported implants usable for the same application (long-term VNS in mice) although more extensive validation and characterization were performed in this manuscript. A comparison between those implants and the one in this manuscript needs to be discussed. As the authors stated, one technical challenge is that the vague nerve in mice is very small and fragile. However, it is unclear how the approach presented here is different from previous designs, and in particular, how mechanical damage is reduced using the reported apparatus.

      2) If the paper is going to be a resource, the authors should provide detailed descriptions of the materials and construction of the electrode. Currently the details are sparse and the photos of poor resolution. It is unclear how the custom cuff was built (no details provided in the method section), what materials were used, and whether these materials are bio-compatible. Also, it is not clear whether and how the cuff electrode is appropriately insulated to prevent stimulation of surrounding muscles/nerves. In addition, the touching point between the nerve and the cuff is very easy to be damaged. With the description of the implantation procedure, it should also be made clearer as to when the cuff electrode is place on the nerve. A clear description could prevent torsion or other injury to the nerve.

      3) LPS experiments: All reviewers thought the LPS experiment needed improvement. This study is under-powered and lacks a control group (saline + Sham stim). The LPS study is inconclusive due to a small number of animals. Increasing N to get conclusive data is important because this implant will be very useful to investigate the anti-inflammatory effect of long-term VNS in chronic disease models in mice. Related to this point, out of the 4 animals with bradycardia, 2 animals did not show a decrease in serum TNF. This raises a concern that using heart rate threshold may not be appropriate to deliver a consistent stimulation dose within/across animals if the goal is to get a consistent anti-inflammatory effect. It is likely that vagus efferent fibers responsible for HR decrease (innervating the sinoatrial and atrioventricular nodes) and those responsible for an anti-inflammatory effect are different populations. Those two populations might be differently affected by the implantation surgery and repetitive stimulation. In addition, performing VNS in awake animals is closer to the human situation.

      4) Please confirm that 0.1mg/kg is the correct dose, this seems low to induce this amount of TNFa.

      5) The histology of the vagus nerve raised questions and needs to be addressed. Here were relevant comments by reviewers.

      • In fig 4b, the vagus nerve in the cuff is quite clear, as is the carotid artery. But there are other nerve fragments and/or auto-fluorescent tissue immediately adjacent. What are these? Leads one to wonder if they only stimulated the vagus? The cervical sympathetic travels with the cervical vagus and care is needed to separate them from the carotid sheath. On the right side of fig 4b, the "control" side, they highlight a nerve nowhere near the carotid artery. This is intact tissue, so the vagus has to be next to the carotid artery. There is a big nerve next to the right carotid that I would bet is the vagus. I think they've got it wrong. It is not clear at what level these photos are taken, is it the cervical vagus? The authors should indicate the left and right carotid in these figures.

      • Figure 4. I do not see how fibrosis is determined. Is this actually collagen? Can the sections in B be stained with mason's trichrome. In "B" I am not sure that I see that the indicated regions are in fact the vagus nerve. It is hard to tell what other nerves would be present as there are few indications of the anatomical area these sections are from other than neck. Thus it Is hard to discern if this really is the vagus or not. I would have thought that the carotid artery should be visible in close proximity to the nerve bundle, this seems not to be the case and leads to uncertainty that this is the correct nerve.

      • Was there any difference in histology between mice with functioning and non-functioning cuffs? As stated in Discussion, left VN without surgery in different animals would be a better control than right VN in the same animals.

      6) In the data presented in fig 2 or any of the studies where the kent scientific pulse/ox was used, Did O2 saturation decrease with the change in breathing?

      7) Why didn't animals receiving awake VNS show visible changes in BR, which is in contrast to remarkable changes in BR in anesthetized animals?

      8) In video 1, it is unclear when the stimulation starts or stops. As a result, it is uncertain if the mouse scratching is due to stimulation. Is this a pain/nociceptive response?

      9) Fig 3 is presented in a confusing manner. In "A", I'm not sure why two mice are presented for different days post implantation and what this is showing. There is a clear effect of VNS on the heart rate and breathing (rate, and air flow), is this the minimum current for each day that was found to induce the heart rate threshold change. While I appreciate that the longer pulse widths are less susceptible to the effect of bio-encapsulation of the electrode over time, I'm not sure how one compares 100 uA at 100 us to 400 uA at 600 us. In B how is the HRT achieved without damaging the electrode as the ICIC is exceeded, or are we not understanding this graph correctly? In C there are days that seem to be missing given the legend. The supplementary figure also appears to have data points missing or obscured?

      10) Success rate tops out at 75% with a skilled surgeon, and ranges between 40-60% for your average player. I'd say this is not too good.

      11) It would be nice to show that the implant does not cause chronic inflammation as this would impact its usefulness as a method. The authors should measure tnfa 14 days Post implanted in cuff implanted and sham implanted mice.

      12) What behavioral experiments were done, and what were the results? These are mentioned in several places (line 172, line 279 etc) but not reported.

      13) The vagus nerve is critically involved in many essential body functions. Chronic implantation of the VNS stimulator may cause severe inflammation, nerve damage, and neuronal dysfunction. Therefore, it is critical to demonstrate that the chronic implantation does not alter nerve function. The chronic effect of the VNS stimulator implantation needs to be carefully monitored. For example, whether there is any change in body weight, food intake, as well as the sensitivity of diverse physiological reflexes such as the baroreflex, the Hering-Breuer reflex, and the stomach accommodation reflex.

  3. Mar 2021
    1. This manuscript is in revision at eLife

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


      PP1 and PP2A make up the majority of serine/threonine phosphatase activity in the cell. While substrate recognition has been studied for PP1 and PP2B, the substate recognition of PP2A holoenzymes are less understood. Here, Fowle et al. set to understand substrate recognition of B55/PP2A. Using a specific substrate of B55, p107, the authors identify a conserved binding motif (HxRVxxV) for recognition by B55 and show additional B55 substrates also contain this motif. This work incorporates many complementary structural and biochemical assays to delineate the binding and recognition of substrates by B55.

      Essential Revisions

      1) What is the evidence that this motif is only recognized by B5alpha/PP2A and not other B55 family members? Are the residues identified in B5alpha critical to the p107 interaction (D197 and L225) conserved among all of the isoforms? If they are, can other B55 family members bind p107?

      2) Have the authors looked for the HxRVxxV motif across the proteome? The author only state that they noticed that this motif was found in Tau, p130 and MAP2, but how many proteins contain these motifs? A list or understanding of the potential proteins which contain this motif could give researchers outside the field a link to understand the phosphatase important for their protein of interest.

      3) For the P107 deletion mutants has the expression of each one been confirmed in Figure 1 and is decreased binding to PP2A B55alpha been normalized to the expression of these mutants.

      4) Is the phosphorylation of p107 by CDK2 affecting the affinity of B55 binding to this substrate?

      5) Have the authors considered measuring direct binding affinities using ITC/SPR for example to look at the effects of these various mutants in a cell free / in vitro system?

      6) It would have been interesting to study the effects of the various B55 mutants on the endogenous phosphorylation of p107, Rb, and KSR?

      7) To gain insights into the physiological role of the identified domain of p107 in PP2A-B55 binding and in the dephosphorylation of this protein, new "in cellulo" experiments using the full length p107 mutant protein have to be performed and its impact in the temporal pattern of dephosphorylation analyzed.

      8) Figure 1D, it is obvious that in order to compare the levels of PP2A-B55 associated to each construct it is essential to normalize the levels of A and B55 signals to the quantity of protein that is recovered in each pulldown. As such, the levels of each GST construct in the pulldowns have to be measured by western blot and used to obtain the PP2A A our B55/GST-spacer ratio. Ratios can be then compared.

      9) The authors state that: "a mutant lacking residues C-terminal of R2 binds B55α similarly to the full construct, indicating that residues C-terminal to the R2 domain are dispensable for B55α Binding". Do "residues C-terminal of R2" mean full R2 region? If this is the case, this statement is not supported by Supplementary Figure 1B, where western blot of construct 2 and 7 display dramatically reduced B55 and A levels.

      10) The authors tested the effect of KR residue mutation in the R1 and R2 regions in p107 dephosphorylation. KR mutants used for the R1 are R621A/K623A, the two mutants that were tested in Figure 1D and that were shown to impact B55 binding. However, they select K657A/R659A for R2 region. These two mutants were not tested in Figure 1D. Why do they introduce these mutants and not R647A that was investigated in Figure 1D? If the authors think that these residues are important, why did they not test them for its capacity to bind B55 in Figure 1D?

      11) Other cdk-dependent phosphorylation sites on p107 that are essential for E2F binding have been described. Some of these sites are out of the spacer sequence. It will be interesting to know whether the dephosphorylation of these sites are dependent on PP2A-B55 and regulated by the mutants on the spacer sequence that decrease B55 binding.

      12) Figure 4A and B. Dephosphorylation pattern of R1R2 control construct is drastically different in Figure 4A compared to 4B. In the first case, complete dephosphorylation does only take place upon two hours of incubation compared with fifteen minutes in the second. This is very weird if the same purified phosphatase is used in both experiments. In this line, I would expect a timing of few minutes for a total dephosphorylation when a purified phosphatase is used. Does it mean that phosphatase in Figure 4A lost activity?

      13) "In vivo" experiments on the dephosphorylation of the non-binding p107 full length mutants have not been performed. To demonstrate that these residues are physiologically relevant for the physiological temporal p107 dephosphorylation pattern, these experiments must be done.

      14) In the same line, to really show the involvement of the pST-x(5-10)-(RK)-Vxx(VI)R in Tau dephosphorylation by PP2A-B55 a direct mutant of this sequence of Tau should be checked.

      15) What are the consequences of B55a-interaction mutants in p107 function? Is that mutant protein able to sustain cell cycle arrest?

      16) Since the authors propose a new model/motif, it would be great to add some statistics on to what extent this motif is present in the numerous hits found in recent screens for B55 targets during mitotic exit. Is this motif present in B55 targets involved in non-cell-cycle (TAU) or cell-cycle targets? Is it equally present in proteins dephosphorylated during early versus late mitotic exit? Any hint into these questions may facilitate the impact of the model proposed in the biology of PP2A/B55.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on February 15 2021, follows:


      The submitted manuscript presents an argument for a novel mechanism of action for the antibiotic colistin. The authors suggest that colistin kills bacteria through its action on lipopolysaccharides at the inner membrane. This is primarily supported by MCR-1 mediated colistin resistance conferring resistance only to cell lysis and not to outer membrane permeabilization. The authors extend this hypothesis to suggest that increasing the amount of LPS in the inner membrane should increase susceptibility to colistin. By inhibiting LPS transport with murepavadin, the accumulation of LPS in the cytoplasmic membrane increased. Combinations of colistin and murepavadin act synergistically to improve bacterial lysis and show efficacy in a murine lung infection model.

      Essential Revisions:

      1) 1) Observations demonstrating MCR-1 modification does not impact outer membrane perturbation and provides resistance to colistin induced lysis are supported by MacNair et al. They suggest that strengthened LPS packing provided by mcr-1 could play an important role in reducing the uptake and lytic activities of colistin. The author's should address that decreased colistin uptake could also result in reduced lysis. To support their hypothesis, the relationship between the amount of modified LPS in the inner membrane and resistance to cell lysis could be expanded on. https://www.nature.com/articles/s41467-018-02875-z

      2) The authors use the lack of change in susceptibility of mcr-1 spheroplasts to daptomycin and nisin to support that there is no change to the biophysical properties of the phospholipid bilayer of the cytoplasmic membrane. However, whether the sensitivity of daptomycin and nisin to changes to membrane charge or fluidity remains unclear.

      3) Murepavadin is used to increase LPS at the CM and as interpreted would support the hypothesis. However, it is also possible that in the whole cell assays, the OM disruption of colistin sensitizes the cells to the killing activity of murepavadin. Repeating the assays with a non-lethal OM permeabilizer like polymyxin B nonapeptide would eliminate this possibility and strengthen the authors conclusions.

      4) The authors suggest that mcr-1 provides protection from colistin through the modification of LPS at the inner membrane and that outer membrane modification has no impact on colistin activity. In contrast, it has been demonstrated that mcr-1 decoration is capable of preventing outer membrane perturbation by polymyxin B nonapeptide (https://www.nature.com/articles/nmicrobiol201728). This suggests that modified LPS at both the inner and outer membrane may play a role in resistance.

      5) Authors should discuss work in the synergy between novobiocin and colistin where novobiocin enhances colistin killing through the stimulation of LPS transport. https://www.ncbi.nlm.nih.gov/pmc/articles/PMC5990483/

      6) Hydrophobic NPN dye was used to explore the permeabilization of OM in this work. However, the uptake of NPN is not absolute proof that colistin is permeable. The authors should discuss this as a possible caveat of their mechanistic model.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on February 18 2021, follows.


      This paper is of potential importance to neuroscientists who study sensory representations and how they are learnt. It suggests that neural representations underlying human perception can be understood in terms of an optimal compression of the sensory input. While the attempt is indeed interesting, there are several shortcomings that should be addressed before this work could be considered as one that can contribute substantially to the understanding of tactile perception.

      Essential Revisions:

      1) There is a significant gap between the simulated data used here and the empirical data of material perception by touch. The vibratory signals were taken from recordings of surface exploration using a tool tip (Strese et al., 2017 ) whereas the ratings of the different materials are taken from an experiment in which participants used bare hand touch (Baumgartner et al., 2013). The difference is significant especially when material classification, and not only texture classification, is required. It is not at all clear how vibratory signals could code hardness, warmth, elasticity, friction, 3D, etc (see Baumgartner et al., 2013). The authors must provide a serious discussion about this gap and convince the reader that their simulations can indeed provide an access to the internal representations of natural haptic touch. In the same spirit, they should explain why, and demonstrate that, the pre-processing of the vibrotactile data (cutting & filtering) makes sense for natural haptic touch.

      2) The authors should provide good reasons to convince the readers that the compressed representation they found is indeed a good candidate for the biological representation. First, the nature of the AE algorithm is that it will converge to some representation in the minimal encoder dimension. Why is that a good encoding representation, and why is it a good model for the biological one? Second, the differences between the results obtained with the AE and those obtained with humans (Baumgartner et al., 2013) seem to outnumber the partial similarities found. The authors should list both differences and similarities and discuss, based on these comparisons, the probability that the coding found here is similar to the coding guiding human behavior.

      3) Notion of efficiency and compression. It was not demonstrated that the main result (figure 3A) is due to compression and efficiency of the AE. What will happen if no AE is used and the distance is measured in the raw input domain (e.g. between Fourier coefficients or principal components)? One could expect figure 4 to account for that, and also show that for a very wide AE there is some deterioration of the main result. Otherwise, the main result about correlation to perceptual data cannot be attributed to the compressive property of the AE.

      4) Biological correlates of the latent representation. On the one hand the authors claim that the AE latent representation aims to mimic a latent representation of the haptic space, which they assume to be compressed and efficient. On the other hand, they claim that the AE representation is similar to mechano-sensory representation, which is a first biological representation before any compression can take place (when hand movements are ignored, as done here). This needs to be clarified.

      5) Validity of the latent representation. The reconstruction error of the AE is large and systematic: only ~50% of the variance are explained and its high frequencies are systematically ignored. The resulting latent representation is such that classes are poorly separable (~29%) and it seems to be by far worse than the human level (around 70% in Baumgartner et al. 2013). It will be therefore interesting to see if the key result, i.e. relation between AE latent space and the perceptual distance, remains valid for a more advanced AE.

  4. Feb 2021
    1. This manuscript is in revision at eLife

      The decision letter after re-review, sent to the authors on February 2 2021, follows.


      The reviewers concur that this article offers an interesting conclusion regarding optimal foraging and chemosensory valence. However, they also agree that it would benefit from a second round of revision, aiming at an improved precision of language and a better discussion of the assumptions of the model and experimental conclusions.

      Public Review 1:

      The authors present experiments that demonstrate how C. elegans worms bias their foraging decisions depending on feeding history and sensory cues (here, called pheromones) that reflect the density of worms. Navigational preference for these sensory cues is found to change from attractive to repulsive depending on the time at which worms leave a food patch, and additional experiments that condition worms under different combinations of conditions (with/without the sensory cues, with/without food, with/without repellent) indicate that associative learning is involved in this inversion of preference. A mathematical model is provided to argue that this inversion represents an optimal foraging strategy that is also evolutionarily stable.

      Public Review 2:

      The authors use the nematode C. elegans to reveal how animals associate social signals with specific contexts and modify their behaviors. Specifically, they show that C. elegans leaving a food patch are attracted to pheromonal cues, while those leaving later are repelled from pheromones. The authors using a behavioral model to suggest that the switch from attraction to repulsion is likely due to a change in learning. This study links learning with social signals providing a framework for further analysis into the underlying neuronal pathways.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on January 29 2021, follows.


      This paper builds on recent studies that have made the connection between chronic endothelial damage and cellular senescence among endothelial cells in PH. Here, using a transgenic mouse that expresses in endothelial cells a dominant negative form of the TRF2 protein needed for telomere maintenance, the authors induce cellular senescence in the endothelium and show that these mice demonstrate worse PH characteristics following exposure to chronic hypoxia. They go on to test the effect of this dominant negative protein on human pulmonary artery endothelial cells in vitro and show that transfected ECs increase expression of secreted and surface-bound signaling molecules, and that when co-cultured in direct contact with pulmonary artery smooth muscle cells the SMCs increase their proliferation, an effect blocked by pharmacologic inhibition of Notch signaling. Notch blockade in vivo attenuates pulmonary hypertension in both transgenics and wild type controls. These data provide an intriguing framework for understanding how endothelial damage alters signaling to neighboring cells in the vascular wall and provides further evidence that Notch signaling plays a key role in the development of PH vasculopathies.

      Essential Revisions

      1) It's unclear where within the pulmonary vasculature the TRF2DN transgene is expressed, and therefore which vessels are effected by senescence. That the transgene is driven by a well-established endothelial promoter (VEcad) is not sufficient to demonstrate universal expression. Especially in the case of a transgene whose expression is intended to result in chromosomal abnormalities, DNA damage and a halt to cell proliferation, significant mosaicism is to be expected. In situ hybridization with probes specific to TRF2DN or an antibody stain that specifically recognizes the transgenic protein on lung tissue sections would address this problem. Both representative images and a careful characterization of the classes of arteries (subdivided by diameter, for example), capillaries, veins, and lymphatics that express the transgene and with which levels of mosaicism would be ideal.

      2) Validation of the EC expression changes, specifically of the Notch ligands identified as upregulated in vitro, need to be validated in situ to ensure they are upregulated in the endothelium of arteries where the PH phenotype (increased muscularization, increased SMC proliferation) is observed in this model. Whole lung dissociation followed by enrichment for CD146+ ECs will result in an overwhelming number of capillary ECs and a tiny number of artery ECs (Figure 3E). Similarly for the in vivo validation of Notch reception in SMCs through qPCR for indicators of Notch reception (Figure 3F, 4I) - this experiment was done on whole lung lysate and does not demonstrate increased expression of these genes in the artery wall. In situ hybridization with probes specific to TRF2DN or an antibody stain that specifically recognizes the transgenic protein on lung tissue sections would address this problem. Both representative images and a careful characterization of the classes of arteries (subdivided by diameter, for example), capillaries, veins, and lymphatics that express the transgene and with which levels of mosaicism would be ideal.

      3) The method by which PAs are identified (Figure 1D, 4F) and the metrics by which artery muscularization from images of tissue sections is quantitated (Figure 1F, 1H, 4H) are somewhat unclear and appear to be made from very few fields from an unspecified number of animals. There appears to be significant variance in artery response to hypoxia (comparing Figure 1E with vehicle in 4G), which is not a problem and very much to be expected, but means there must be absolute clarity in how the data for graphs summarizing imaging data were obtained. A supplementary figure with representative images demonstrating how arteries were scored would be very helpful. The number of independent mice for each analysis must appear either in the figure legends or in the relevant sections of the methods. A reader's understanding of how the PAs were identified in Figure 1D and 4F would be helped by using a vascular specific antibody stain. And a supplementary figure with a large panel of artery images from Tg and Wt animals before and after hypoxia exposure, with and without DAPT, so the reader can grasp the range of effects on vessels in each case would be immensely helpful.

      4) Please describe the in vivo relevance of endothelial progeria induced by decreased TERF2 function in patients with PAH.

      5) While endothelial senescence leads to decreased proliferation and apoptosis of EC, which have been shown to occur in PAH, clonal proliferation of EC is also a hallmark of advanced disease in PAH. The study does not comment on this varied phenotype of EC in the pulmonary circulation in PAH patients and the relationship of senescence of EC to SMC migration.

      6) Increased levels of Jag1 have been linked to excess proliferation in several cancer cell lines. In the context of senescence with decreased EC proliferation, increase in Jag1/Jag2 levels is surprising and the paper does not comment on this phenotype as being distinct from cancer cells.

      7) The mechanism for increased notch ligand expression in response to progeria was indirectly addressed with 5-Aza studies which presumably leads to inhibition of DNA methylation. However, it is unclear how this inhibits increase in notch ligand expression. In the discussion, the authors mention (Line 17, page 10) that DNA hypomethylation promotes specific transcriptional programs as a result of senescence. However, 5-Aza prevented the induction of Notch ligand expression in senescent EC (Suppl Fig 2). The discussion of these results needs further clarification. It is unclear what specific epigenetic modifications occur to increase the expression of Jag1/2 and Dll4 in senescence associated changes.

      8) The study did not report whether aorta and other systemic vessels demonstrate senescence changes in endothelial cells-endothelial progeria in the TG mice would involve all vasculature. Presumably, vascular remodeling was limited to the lung, given the unique response of the lung to hypoxia. However, examination of a systemic vascular bed would have strengthened the conclusions of the study. Do the EC and SMC derived from aorta or coronary vessels show similar responses in vitro compared to human PAEC with DN-TERF2 transfection?

  5. Jan 2021
    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on December 14 2020, follows.


      This study examined osmolarity-dependent dendritic signaling in oxytocin magnocellular neurosecretory cells (OT-MNCs). The authors show that repetitive depolarizations evoke larger calcium responses in proximal dendrites relative to distal dendrites. When these neurons were exposed to hyperosmotic stimuli, the distal calcium responses were found to be inhibited to a greater extent compared to proximal dendritic calcium responses. Propagation of glutamate evoked depolarizations from the dendrite towards the soma were also found to be reduced following increases in osmolarity. These effects of hyperosmotic stimuli are likely mediated by changes in membrane resistance of dendrites. A non-selective blocker of the channels, ruthenium red, blocked these effects of hyperosmolarity, indicating the non-selective cation channels (e.g. TRPV types) may be responsible.

      All three reviewers agreed that the finding is potentially important and could address fundamental questions about MNC dendritic physiology. However, the reviewers identified a number of technical concerns, as summarized below. These concerns need to be addressed for further consideration.

      Essential Revisions

      1) The title and abstract are not exactly reflecting what this study is about. The title of the paper is "Dendritic membrane resistance modulates activity-induced Ca2+ influx in oxytocinergic magnocellular neurons of mouse PVN". However, dendritic membrane resistance is never actually measured. As such, a title that does not mention membrane resistance may be more appropriate. Also, the purpose and rationale of this study are not clearly communicated in the abstract and introduction. The implication to the regulation of soma-dendritic release of oxytocin, but not hyperosmotic responses, was mentioned in Introduction, while the entire Results and Discussion sections are about hyperosmotic stress.

      2) Figure 3: The reviewers believe that stimulation paradigm is not physiological (neurons voltage-clamped at -70 mV with repetitive voltage steps to +50 mV for 5 ms). It is important to show that action potentials in the current clamp, instead of the +50mV voltage step in the voltage-clamp, can produce similar signals.

      3) A major focus of the manuscript is on Ca2+ elevations in MNC dendrites. However, the authors have not performed the essential experiments to identify what the Ca2+ entry/release pathways are. It is important to show that Ca2+ is through voltage-gated Ca2+ channels for their main conclusions. In addition, it should also be established whether dendritic propagation is active or passive.

      4) It is essential to report the effect of the osmotic stimulus alone on dendritic resting Ca2+, as this would affect the interpretation of the Ca2+ data.

      5) Figure 8: What is the effect of RR on proximal EPSCs? This information is needed to interpret the effect of RR on distal EPSCs. It would be required to also test the effect of RR on the modulation of Ca2+ responses in distal dendrites to see their effects on the dendritic conductance.

      Statistical handling:

      Please provide the statistical methods (t-test, 2-way ANOVA with Hom-Sidak corrections, 2-way repeated-measures ANOVA, etc.) used for each measurement in the text or figure legend (not just in the method section). For repeated measures ANOVA, please indicate how measurements were repeated.

      For the statistics of sex differences (Fig. 2-1, 4-1 etc), it is required to use 3-way ANOVA to assess variability by cells, animals, and sex. The number of males and females used is not clear in some cases, but it appears that only 2 females and 2 males are used (Line 203-204). If this is the case, the statistical comparisons between males and females are not meaningful and should be removed.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on January 12 2021, follows.


      In summary, this manuscript elucidates the function of Glypicans in Hh transport via cytonemes. The reviewers felt that that the manuscript describes convincingly that the fly glypicans Dally and Dally-like are required to maintain the expression of the Hh co-receptor Ihog, which stabilises cytonemes to establish the Hh gradient in the wing imaginal disc. A molecular analysis of Ihog domains was well executed.

      Although the manuscript provides an in-depth analysis, the reviewers believe that the presentation of the data is rather challenging for the readers. The authors need to clearly describe the different roles that have been attributed to the glypicans and for every experiment presented, a clear explanation of the impact of the results is needed e.g. Figure 5. In addition, the stability of Ihog and Boi by altered Glypican levels and their ability to stabilize cytonemes needs to be investigated. Finally, linking the Ihog analysis to cytoneme stability analysis needs improvement.

    1. This manuscript is in revision at eLife

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


      We feel that the major conclusions are right but the manuscript and story is not quite clear enough at present and there is a lack of deeper cellular and molecular mechanistic understanding of these phenomena to distinguish this work from the previous published studies. That ASC senescence impairs adipogenic differentiation capacity, has been previously reported in eLife in 2015 (doi: 10.7554/eLife.12997). For example, you concluded that adipose derived progenitor cells from older adults have higher potential to become senescence, which impaired adipogenesis. The percentage of senescent cells in adipose tissues is low, but the mechanism of how they could significantly affect adipose tissue functions is unknown. Is this through paracrine effects? or cross talk with other immune cells? etc.

      Essential Revisions

      1) Although the authors found that ASC senescence is associated with mitochondrial dysfunction and oxidative stress, it the nature of the links between these cellular events is unclear. It is well-known that mitochondrial dysfunction can directly lead to senescence. If the authors meant to prove that ASC senescence causes early adipocyte mitochondrial dysfunction, more evidence is required.

      2) It has already been reported that ASC senescence impairs adipogenic differentiation capacity, in Elife in 2015 (doi: 10.7554/eLife.12997). Furthermore, although the authors found that metformin prevents the onset of senescence and associated dysfunctions in ASCs, it has been shown in many publications that metformin is a senomorphic drug that can reduce the senescence-associated secretory phenotype. So it is not surprising that metformin can block the effects of senescent ASCs. Also regarding the increased adipogenesis by metformin, it has been reported that metformin can directly regulate adipogenic transcription factors, such as peroxisome proliferator-activated receptor (PPARγ), CCAAT/enhancer binding protein α (C/EBPα). As such, sufficient novelty is lacking at this point, and would require demonstration of causal links among these cellular events.

      3) Several conclusions need to be smoothed out and discussed in more detail. Methods must be described with more details, especially with regard to fat depot digestion (type of collagenase, concentration of collagenase, amount of tissue used for the digestion, are cell yields similar between young and old adipose tissue? Number of plated ASC?). The authors must consider that the term ASC is nowadays related to Adipose stromal cells and not Stem cells. As described in the introduction and method sections, ASC are stromal cells that adhere to plastic including fibroblast, smooth muscle cells, pericytes, endothelial cells, resident macrophages, preadipocytes and progenitors. This must be discussed since distribution and repartition of stromal cells are modulated with aging. The term "adipocyte" must be changed to "differentiated ASC" because adipocytes are characterized by unique lipid droplet (not the case here). The title must be modified. Senescence is related to ASC and not to adipocytes.

      4) Figure 1: It is unclear why the authors conclude about they are recapitulating in vivo aging. If so, one might expect that senescent "young ASC" phenotype may recapitulate the one of "old ASC" with a time lag, what is not the case for all the studied parameters. For example, the % of bgal cells is equivalent between P7 old cells and P11 young cells what is also true for P16, P21 and prelamin A but not for reactive oxygen species or mitochondrial potential. The authors must discuss this point.

      5) Figure 2: Was Cell number at confluency controlled and similar between "young" and "old" ASC? Since post-confluent mitosis are necessary for adipogenesis, one might speculate that the decreased adipogenesis might be related to less cell number and proliferation.

      6) Figure 3 and 4: Cells were treated from P3 with metformin. Do the authors consider potential "resistance" effect? When taking into account the large number of individuals treated with metformin, is there any evidence of an impact of metformin treatment on age-related loss in subcutaneous adipose tissue? Finally, inhibition of senescence may lead to cancer development. The authors must discuss this point.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on January 18 2021, follows.


      This is an exhaustive study of different phenotypes associated with Histone H3-G34 mutations in a fission yeast model. Because mutations at this site occur in certain human cancers, teasing apart their different phenotypes in a model system helps to understand their potential effects in pathology. The phenotypes vary widely, suggesting a key role for this residue in a variety of genome maintenance functions.

      The authors systematically examine histone modifications, transcription, and use genetic and cytological assays to measure genome stability. The phenotypes vary widely, suggesting a key role for this residue in a variety of genome maintenance functions. Direct extrapolation to human cells is limited due to the absence of multiple H3 variants in fission yeast, and the absence of the PRC1/2 pathway. However, this is balanced by the rapid and thorough analysis of numerous variants that is enabled in this model system.

      It is not possible to draw a simple model as there is little consistency in the phenotypes. This suggests that the G34 residue independently affects multiple activities. These will require laborious efforts to tease out.

      Essential Revisions

      This is overall a technically very well done paper with a variety of methods to examine different mutations in H3-G34. The strength is the consistent approach applied to numerous mutations. However, as there is no single response, it's rather descriptive overall. We have no major concerns about the data, but feel that the conclusions need to be tempered in two areas where the assays were not direct.

      1) In the absence of NHEJ repair assays it needs to be noted that conclusions about NHEJ proficiency based on drug sensiutivty are indirect.2)

      2) The authors imply that the H3G34 mutants affect the activity of the Set2 H3K36 methyltransferase. In the absence of an in vitro H3K36 methylation assay on the mutant histones with recombinant or affinity purified Set2 the authors need to note that this conclusion is speculative as they have not measured it directly.

    1. This manuscript is in revision at eLife

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


      This paper describes very clearly a set of experiments to assess collateral sensitivity to certain antibiotics that is created by carriage of beta-lactam (incl carbapenenem) resistance plasmids in E. coli. This addresses one of the limitations of existing literature on CS, which typically focuses on the effects of resistance point mutations, which are clinically less significant. By documenting multiple ways that this CS is real and selectable and to a degree generalizable across genetic backgrounds, this is an important contribution in showing that CS is a real phenomoenon for clinically important resistance mechanisms.

      Essential Revisions

      1) The primary screen of 'antibiotics x plasmids' to identify collateral sensitivity, presented in Figure 1B, lacks an analysis of the statistical significance of results. Supplementary data shows that measurements of MIC are a little too noisy to robustly identify 2-fold changes with only 4 or 5 replicates. Defining "significant" as "mean more than 2x" is not adequate. Using a power calculation derived from the data in the manuscript, a sample size should be determined to have a 90 (or other high) % chance of detecting a 2x difference given the variability observed between assays, and then they should be done. Ideally this would be for all organism-plasmid pairs, but at least for the ones that the preliminary screen found a mean of 2x for.

      2) Recommendation (not required for acceptance, but please temper claims of clinical relevance if not done): The comparative killing data should be repeated in competition. This is technically more challenging but I believe not more so than the comparative growth curves. This would establish as proof of principle that a mixed population could be purified of plasmid-bearers by CS. Without this, the clinical relevance will still remain speculative. Also, two reviewers initially misread these as competition assays. The text and legend should emphasize that these are separate populations

      3) (Not required for acceptance but suggestion for future work:) The presented work is solid but, as pointed out by the authors, there is no mechanistic explanations for the observations. It would be highly interesting to know if the collateral effects are due to specific genes (OXA-48 would be a good place to start) and/or if the observed effects are due to the plasmid backbone.

      4) The experiment in Figure 3 demonstrates the exploitation of collateral sensitivity to preferentially inhibit plasmid-bearing bacteria. The terminology in this section refers to 'eradicate', 'mortality' etc, but in practice, the experiment defines survival as OD>0.2 after ~24 hours. It seems likely that in the 'non-surviving' conditions, waiting another day or two would show regrowth of some bacteria in these conditions.We don't think this requires any change to the experiment, only how the results are described: they show preferential inhibition of growth, not eradication. A more patient approach to identifying regrowth would be necessary to definitively state that these bacterial populations have been eradicated. Suggest tempering claims.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on January 11 2021, follows.


      Adiponectin is a key adipokine, and much of our knowledge about this molecule has come from the Scherer lab. It is well known that adiponectin promotes improved insulin sensitivity and glucose tolerance, along with anti-inflammatory effects, which can be followed by decreased fibrosis. In this paper the Authors use loss and gain of function mouse models to explore whether the beneficial effects of adiponectin on metabolism can be translated into greater healthspan or lifespan. They show that lifespan decreases in adiponectin KOs and increases in the transgenic (ΔGly) mice. The expected effects on glucose metabolism, insulin sensitivity, inflammation, and fibrosis are also demonstrated.

      Essential Revisions

      1) Given the known significant effects of adiponectin on metabolic fitness, the effects on healthspan which the Authors observed in their 2 models, was expected. However, while median survival time is definitely less in the APN-KOs and greater in the ΔGly mice, the effects are relatively modest compared to other longevity studies. Any increase in lifespan is a good thing, particularly when accompanied by a corresponding increase in healthspan. We would've hoped for greater effects on lifespan than those observed but even modest effects are worthwhile. The Authors should comment in their discussion on this point. In other words, it would be good to know the Authors' thinking as to why these impressive effects on glucose, insulin, inflammation, fibrosis, etc. do not lead to even greater effects on lifespan. Also, is there any information on the causes of mortality in the WT vs. KOs that might point to why lifespan is decreased?

      2) APN-KO clearly leads to impaired glucose tolerance, but it is a bit surprising why insulin levels aren't increased, which is the typical metabolic response to insulin resistance.

      3) Can the Authors please comment on adipose tissue mass in the KOs, particularly if they have any information on subq fat?

      4) In Figure 3, they show increased staining for ATMs with Mac2 in the KOs. What about the expression of other inflammatory gene markers, such as those shown in Figure 3G for the liver?

      5) With respect to hepatic effects, this paper shows increased inflammation in the liver in APN-KOs. However these gene expression patterns are in total liver tissue, and it would be helpful to understand the origin of these inflammatory markers. Are they from Kupffer cells, monocyte-derived macrophages, etc. In a similar vein, various fibrosis marker genes are increased in total liver from the APN-KOs. Most likely these expression differences reflect stellate cell effects. Do the Authors have any information on the effect of adiponectin on stellate cell function. Although fibrosis-related genes are elevated in the APN-KO, is there histologic evidence of increased fibrosis in the liver sections?

      6) The Authors suggest that the increased inflammation in the liver is the cause of the increased fibrosis. Presumably they think that the immune cells in the liver are signaling to stellate cells to produce this effect. Is this the scenario the Authors propose. If so, it should be made more explicit and corroborated by histologic staining of hepatic fibrosis.

      7) It would be of interest to know the extent of inflammation in the kidneys with APN-KO, beyond Mac2 staining (Figure 3D).

      8) In the results in the ΔGly mice, is the enhanced lifespan statistically significant. Unless we are misreading it, the p value suggests it is not. Also, why have only study chow fed mice and not HFD mice in the transgenics, as they did in KOs?

      9) ITTs are shown in Figure 4G, but the basal glucose values are different between the 2 groups. Can the Authors also present the data normalized to the basal value to determine whether the kinetics of the curve are different?

      10) The resulting changes in tissue fibrosis are clearly important when thinking about healthy tissue function. It would help if the authors could show histologic staining for collagen deposition in the various tissues, particularly liver and kidney. Although it might be asking for too much if the they don't already have this information, it would also be useful to know which cell types within the various tissues are responsible for the changes in inflammatory markers and collagen related genes. This could also be discussed.

      11) From an aesthetic point of view there is a certain lack symmetry in this paper, since some of the measurements made in the KOs are not performed in the transgenics and HFD was not utilized in the transgenics either.

      12) Much of the data could be predicted from studies by them or the other investigators in the field (Nature Med. 8, 731 (2002), J. Biol. Chem. 277, 25863 (2002), J. Biol. Chem. 277, 34658 (2002), J. Biol. Chem. 278, 2461 (2003), Endocrinology 145, 367 (2004), J. Biol. Chem. 281, 2654 (2006), Am. J. Physiol. Endocrinol. Metab. 293, 210 (2007), J. Clin. Invest. 118, 1645 (2008) . IT would be helpful if authors could provide insights into the life-promoting mechanism by adiponectin that has not been clarified so far.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on January 5 2021, follows.


      In this manuscript, Olive and colleagues used a genetic screen to identify Complex I (CI) of the electron transport chain (ETC) as a regulator of IFNg-mediated gene expression in macrophages. They attribute this role of CI to effects on the activity of the JAK-STAT pathway downstream of the IFNg receptor.

      While a potential link between CI activity and the activity of the JAK-STAT pathway would be interesting, the reviewers think that additional analyses are needed to substantiate this claim and rule out alternative interpretations.

      Essential Revisions

      1) Lines 204-205: The authors find that sgRNAs targeting other complexes of the ETC, including CIII and CIV, had no effect on the ability of IFNg to stimulate expression of cell surface markers. How do the authors interpret these findings, since CI does not work in isolation in the ETC and is rather dependent on CIII and CIV activity?

      2) How does IFNg stimulation affect oxidative metabolism as assessed by Seahorse? In order to corroborate the authors' conclusions regarding activity of individual ETC complexes (point 1 above), Seahorse analysis of individual complexes is also advised.

      3) The authors do some limited analyses in human MDMs to suggest that their findings in the mouse macrophage cell line can be generalized to other macrophage populations. It would be great if the analyses in the human MDMs could be extended to further strengthen the generality of their central findings.

      4) Fig 6D: Not clear whether similar exposures were used in different panels. Would be better to load samples in the same gel so that the same exposure can be used and a direct comparison between conditions can be made.

      5) Fig 6D: Does acute treatment with rotenone (but not inhibitors of other ETC complexes) have similar effects in reducing JAK-STAT signaling as knockdown of CI subunits? If not, then stable, long-term knockdown of CI subunits may have some effect independent of respiration in influencing JAK-STAT signaling (for example, on expression of some component of the JAK-STAT pathway). This interpretation could also explain why knockdown of other components of the ETC do not have similar effects to CI. Rotenone treatment could be tried (and compared with inhibitors of other ETC complexes), and if the data are different from knockdown of CI subunits, then related data in the study could be re-interpreted and conclusions modified.

      6) In Fig. 3H a key control is missing. What about survival of the cells when the import of the only energy substrate is blocked?

      7) The authors could consider placing their findings in the context of the broader literature. (As just one example, Ivashkiv Nat Imm 2015 described a role for mTORC1 and metabolism in IFNg-mediated transcriptional and translational regulation in macrophages.) This would increase the impact of their findings.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on January 7 2021, follows.


      In this study, Olive and colleagues used a genetic screen to identify new regulators underpinning the ability of the cytokine IFNg to upregulate MHC class II molecules, of relevance to our understanding of how macrophages are activated by IFNg to confer host defense during microbial infection. They identified the signaling protein GSK3b, and MED16, a subunit of the Mediator complex previously implicated in gene induction.

      Essential Revisions

      1) Experimental treatment with IFNg may not be physiological. In key experiments, authors should try co-culture with activated NK cells +/- IFNg neutralization. A dose and time response curve of IFNg treatment may be valuable in key experiments.

      2) Comparison to cells not stimulated with IFNg is needed in key experiments. Comparison to WT cells is needed in Fig 5A,B.

      3) Stimulation with Type I IFN and other PAMPs in key experiments, as comparison to the effects of IFNg and to broaden the relevance of their findings.

      4) More insight into how IFNg signaling interfaces with GSK3 and MED16 is needed (e.g. role of mTORC1 pathway in regulating GSK3).

      5) Can the authors extend their data to an in vivo setting?

      6) Can the authors clarify the relative roles of GSK3a and GSK3b? For example, how do the authors explain the lack of a robust phenotype in Fig 3B-F?

    1. This manuscript is in revision at eLife

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


      In the paper, the authors used metabolomics to identify Valine and TDCA as metabolites depleted in diet-induced obesity (DIO) and replenished after sleeve gastrectomies (SGx) in mice. Intraperioneal injection of these two metabolites mimics many of the benefits of SGx, including weight loss, reduced adipose stores and insulin sensitivity. These benefits are related to Val/TDCA's ability to reduce food intake without altering locomotor activity, leading to a negative energy balance. Val/TDCA injection eliminated the fasting-associated rise in hypothalamic MCH expression in obese mice, and central injections of recombinant MCH blunted weight loss induced by Val/TDCA. Overall, this paper reports interesting and surprising observations related to the impact of metabolomic disturbances in obesity, and suggests a role for Val and/or TDCA in regulating food intake through MCH.

      Essential Revisions

      1) It is unclear from the data whether the effects are derived from valine, TDCA, or both. Both reviewers felt that any reader would want to see experiments where either of these metabolites is injected alone.

      2) No quantitative metabolite concentration values are provided anywhere, making it difficult to evaluate the robustness of the data. How much do the levels of TDCA and valine change with SGx in mice and humans, and what levels are achieved with the injections of these metabolites in the mice?

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on January 10 2021, follows.


      The reviewers agree that this is an interesting and useful contribution for understanding LQ extinctions, and that it is generally well-presented. It shows that the factors that increase extinction risk are de-coupled from the factors that eventually lead to extinction and thus in its timing. However, the reviewers also note that although the modelling approach is novel, it is reliant on datasets that are biased and at times these biases are not well-accounted for. Because much of the conclusions drawn from the modelling could already be drawn from existing records and using literature that is glossed over here, attention to that literature should be improved and the contributions beyond the megafauna debate should be emphasized. Furthermore, the authors should take care to improve clarity in the framing of the models, the presentation and interpretation of results, figures, and discussion.

      Essential Revisions

      1) ADDITIONAL ANALYSES (no additional data collection). The reviewers had specific concerns about the effects of sampling on the extinction chronology and the influence of body mass on a number of things (recovery potential, life history/demographic correlates, etc). Specifically, the analytical issues that present the biggest problems revolve around sampling uncertainty and body mass correlation. The former could be addressed by introducing some sensitivity tests. These could be directed towards chronological biases (how does removing one date affect the confidence intervals?), as well as geographical sampling biases (how does removing a region affect the trends?). The latter in particular would be important in the claims of a continental trend. It is also possible that biases are a function of taxon sampling. There are an increasing number of small mammal Pleistocene extinctions being recognized in Australia, and it is unclear if these follow the same trends as the megafauna. If so, that would indeed remove the body size issues.


      (i) appears to assume that only human hunting will differentially affect demographically sensitive species. However, novel or extreme climate change can also affect such species (e.g. Selwood, K.E., McGeoch, M.A. and Mac Nally, R., 2015. The effects of climate change and land‐use change on demographic rates and population viability. Biological Reviews, 90(3), pp.837-853.)

      (ii) this mechanism is predicated on using a modelling result [ref. 25] as data. It also makes the bold claim that species inhabiting certain habitats are less accessible to human hunters without any consideration of the archaeological or modern record on this point (e.g. Roberts, P., Hunt, C., Arroyo-Kalin, M., Evans, D. and Boivin, N., 2017. The deep human prehistory of global tropical forests and its relevance for modern conservation. Nature Plants, 3(8), pp.1-9; Fa, J.E. and Brown, D., 2009. Impacts of hunting on mammals in African tropical moist forests: a review and synthesis. Mammal Review, 39(4), pp.231-264).

      (iv) many of the supporting references here do not seem like logical choices for this argument. E.g. [28] refers to coral-reef fishes. Moreover, this hypothesis conflicts with much modern data showing that extinction risk and body size are correlated under climate and environmental change (e.g. Cardillo, M., Mace, G.M., Jones, K.E., Bielby, J., Bininda-Emonds, O.R., Sechrest, W., Orme, C.D.L. and Purvis, A., 2005. Multiple causes of high extinction risk in large mammal species. Science, 309(5738), pp.1239-1241. Liow, L.H., Fortelius, M., Bingham, E., Lintulaakso, K., Mannila, H., Flynn, L. and Stenseth, N.C., 2008. Higher origination and extinction rates in larger mammals. Proceedings of the National Academy of Sciences, 105(16), pp.6097-6102. Tomiya, S., 2013. Body size and extinction risk in terrestrial mammals above the species level. The American Naturalist, 182(6), pp.E196-E214.)


      The major weakness in this manuscript is in the discussion. The authors should be very clear in their discussion that their model does not indicate that demographic factors had no part in extinct events per se, but rather that they don't explain extinction chronology. Extinction chronologies reflect a number of different factors and processes, but they don't take away from the fact that certain life history traits can make a species more likely to go extinct from those factors.

      The authors seem to argue that demographics don't explain the megafaunal extinction in the Sahul, but in fact, their results suggest that they do; the only thing demographics by themselves don't explain is the chronology. Extinction risk as determined by demographic susceptibility is highly related to body mass and generation time (which in turn is also affected by body mass) but differential survival (timing of extinction) is determined by factors such as geographic range size, dispersal ability, access to refugia, and behavioral and morphological adaptations against hunting, and the ability to survive catastrophic events. A reiteration of this point would be beneficial to the clarity of this otherwise well written manuscript.

      The authors clearly (and elegantly) show that extinct species, which were all large, and had long generation times, had demographic traits that made them more susceptible to extinction. This is evident in figures 3 and 4. However, in the discussion, in lines 301-303, they state that no demographic trends explain the extinction. This is not supported by the results. While the timing of when species go extinct doesn't correlate with demographic susceptibility, the peculiar nature of the extinction-a large size biased extinction-is explained by demographic factors, and is a phenomenon that has been explored in a global analysis by Lyons et al. 2016 Biol. Lett. Therefore, demographic trends DO explain why certain species go extinct, while others survive. The authors should be careful when they say that "that no obvious demographic trends can explain the great Sahul mass extinction event"; instead, they should re-iterate that no obvious demographic trend explains the extinction chronology.

      4) MORE CAREFUL DISCUSSION OF RESULTS RELATIVE TO LITERATURE. The authors further go on to suggest that their results suggest that the extinctions were random, but the size-selectivity clearly shows that the extinctions were in fact not random with respect to body size.Their analyses do show that the rate of extinction doesn't exceed background to the same degree that it's been suggested in prior studies, and this is something that researchers need to explore further. Also, the authors raise an important point in lines 309-311 that human hunting could have interacted with demographic susceptibility, something that Lyons et al. 2016 Biol. Lett. show, and the results of the present study should be discussed in light of the 2016 paper.

      They also raise an important point in lines 312-320 that behavioral or morphological adaptations may have allowed some seemingly "high risk" species to persist despite anthropogenic pressure. These model "mis-matches" have been reported by Alroy 2001 Science as well in a multispecies overkill simulation. It would be beneficial to discuss the present results within the context of other examples of model mismatches, such as those from Alroy 2001.

      In lines 353-358, the authors once again state that their results show no clear relationship between body-mass and demographic disadvantage, despite clearly showing these relationships in Figures 3 and 4, and even stating as much in the beginning of the discussion. The plots clearly show that large bodied taxa were at a demographic disadvantage. There is a difference between explaining why certain taxa go extinct vs. why they go extinct at a certain point in time, and this should be made clear. The authors are correct in stating that demographic factors don't explain the relative extinction chronology, i.e. when species go extinction relative to each other, but they do explain why large species go extinct, and why these extinctions take place after human arrival. Moreover, generation length, which is also correlated with demographic susceptibility, is highly correlated with body mass (Brook and Bowman 2005 Pop. Ecol), once again showing that body mass-related effects do help explain the extinctions.

      The authors rightfully point out earlier in the discussion that spatial variation, local climates, ecological interactions, etc. all influence how and why a particular population disappears. Extinction chronologies reflect a number of different factors and processes, but they don't take away from the fact that certain life history traits can make a species more likely to go extinct from those factors. Large proboscideans like mammoths had a high risk of extinction based on life history traits, but managed to survive on island refugia into the mid-Holocene. Similar other examples exist, and show that extinction chronologies can vary vastly.

      Therefore, the lack of correlation can be explained by these factors, and the authors need to expand on these in their discussion, perhaps if possible, by giving specific examples. They should be more careful in their discussion by clearly distinguishing drivers of extinction risk, and how these drivers can be de-coupled from timing, but at the same time providing a good explanation for the biological factors leading to the extinction. Here again the authors should consider the work of Brook and Bowman and Lyons et al.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on January 7 2021, follows.


      This manuscript describes a detailed investigation of the sigma-1 receptor, with an emphasis on the effects of membrane cholesterol content. The authors report that sigma-1 receptor clusters in cholesterol-rich microdomains in the endoplasmic reticulum (ER), contributing to its previously-described localization at mitochondria-associated ER membranes. A series of reconstitution experiments show cholesterol-dependent clustering of the sigma-1 receptor, an effect which is modulated by membrane thickness and drug-like ligands of the receptor. These findings are supplemented by an investigation of the effects of sigma-1 receptor on IRE1a signaling, leading to the finding that sigma-1 knockout attenuates IRE1a function.

      Essential Revisions

      The reviewers agreed that the manuscript was likely to be of broad interest and addresses important biological questions surrounding the poorly understood sigma-1 receptor. However, concerns were raised regarding a number of points that need to be addressed in order for the manuscript to be suitable for publication. Specifically:

      Most of the imaging experiments throughout the manuscript are interpreted only qualitatively, and many of these show relatively minor differences. See "MINOR POINTS" below for a list of specific examples. Objective quantitative analysis should be provided wherever possible. Any subjective assessments should be conducted using blinding to avoid introduction of bias.

      The connection between the biological effects on IRE1a activation and cholesterol-dependent clustering is relatively indirect. The reviewers agree that additional experimental data should be provided to further assess the validity of the authors' proposed model. For example, inclusion of rescue experiments in sigma-1 knockout cells using the cholesterol-binding mutants would help to strengthen the connection between IRE1a function and membrane cholesterol content. Similarly, disruption of cholesterol-rich domains by addition of beta-cyclodextrin could provide additional evidence to support the model. In addition, testing the effects of ligands in the cellular imaging experiments would strengthen the link between in vitro biophysical experiments and cellular physiology.

      A related issue is that cholesterol binding is not tested explicitly for certain sigma-1 receptor mutants, potentially confounding interpretation of experimental data. These include experiments where alterations were made to the S1R sequence, with results interpreted in light of S1R no longer being able to bind cholesterol. Two specific places where this issue arises are:

      1) Studies described on pages 6-7 and shown in Figure 3B where wild-type sigma-1 receptor is compared to S1R-Y201S/Y206S, S1R-Y173S, S1R-4G, and S1R-W9L/W11L. These mutations had differential effects on receptor distribution that were attributed to alterations in cholesterol binding without confirming the changes in cholesterol binding. This is particularly relevant for the explanation given for why S1R-W9L/W11L fails to cluster in both cells and the cholesterol supplemented GUV system, while the S1R-4G mutant exhibited cholesterol-induced clustering in the GUV system but not in cells (page 7, lines 27-31).

      2) Another example is the membrane thickness experiment described at the top of page 8 and shown in Figure 4A. Shortening the S1R by deletion of 4 aa in the TM region produced a sigma-1 receptor that exhibited a more diffuse distribution when expressed in HEK293 cells. The authors appear to be attributing this only to the decreased length of the sigma-1 receptor transmembrane domain. However, it seems feasible (based on their other data) that if this construct fails to bind cholesterol, the same result would be observed. Confirming that the truncated sigma-1 receptor does in fact bind cholesterol would strengthen the argument being made here.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on January 5 2021, follows.


      Your work analyzes the impact of the INPP5E inositol lipid-5 phosphatase on immune synapse formation and function. INPP5E is a cilium enriched protein. Although T cells do not display primary cilia, previous work by several laboratories showed that several ciliary proteins are involved in immunological synapse formation and in T cell activation and your work intends to further this view. Although the work has potential for publication in eLife, it requires essential additional data to support the central claims of the paper. Each reviewer raised substantive concerns (see below) that need to be resolved experimentally. For instance, experiments involving knockout in primary T cells will need to be performed. A better time series will also help deciding in what process the INPP5E protein is involved in. Moreover, imaging data should be quantified more precisely to assess spatial and dynamic differences.

      Reviewer #1:

      An important aspect of mature synapse formation is signal termination and ... effector responses, such as secretion of cytokines, exosomes and CD40L on synaptic ectosomes (Huse et al, 2006; Mittelbrunn et al, 2011). The demonstration of ESRCT function in both TCR signal termination and CD40L release to B cells on synaptic ectosomes likely involves inositol lipids that lack phosphorylation on the 5' position.

      It might make sense for the author to investigate a synapse effector function like degranulation of CD8 or CD40L transfer of synaptic ectosome in CD4 T cells as these effector functions actually link into synapse formation more directly than bulk IL-2 secretion.

      The ESCRT machinery is also highly entwined with ciliary biology and several ESCRT components important for signal termination and effector function will also require PIP metabolism.

      Reviewer #2:

      Interesting similarities between the primary cilium and the immunological synapse have been noted and investigated extensively over the last few years. In this context and beyond, the role of phosphatidylinositol lipids in the organisation of the immunological synapse and T cell function has been extensively investigated. Here Chiu et al. add to these topics by investigating INPP5E, a primary cilium-associated 5' phosphatidylinositol lipid phosphatase that can use PIP3, PI(4,5P)P2 and PI(3,5)P2 as substrates, in T cell activation. The authors show that INPP5E is recruited to the interface of a T cell with an activating antigen presenting cell. INPP5E binds to TCRzeta, ZAP-70 and Lck. INPP5E knockdown reduces TCR recruitment to the T cell/APC interface, clearance of PI(4,5)P2 from the centre of the interface, and TCR and ZAP-70 phosphorylation. These findings are consistent with the large body of existing work on the role of phosphatidylinositol lipids in the organisation of the immunological synapse and T cell function and, therefore, don't constitute a conceptual advance. Nor do they provide new mechanistic insight into phosphatidylinositol lipids in T cell activation. The data add another molecule to the existing body of work.

      In the first two figures Chiu et al. show that a number of cilium-associated proteins, including INPP5E are recruited to the interface of a Jurkat cells with a Raji B cell presenting superantigen. Such recruitment is not surprising. On the contrary, because of the reorientation of the MTOC to the centre of the cellular interface and the accompanying shift of the nucleus to the back of the T cell to create more cytoplasmic space at the interface, most proteins associated with vesicular trafficking shift their subcellular distribution towards the interface. Only data showing spatial or temporal distinctions in such recruitment within the small cytoplasmic space underlying the T cell/APC interface could provide interesting new insight. Reduced detection of INPP5E interface recruitment after INPP5E knockdown could be trivially caused by the worse signal to staining background noise ratio (Fig. 2A-E). The STORM data showing that INPP5E interface recruitment occurs in the T cell not the APC are welcome. However, spatial and temporal features provided by the higher resolution of these experiments are not explored.

      In the investigation of the contribution of different INPP5E domains to its interface recruitment the representative imaging data in Fig. 3A suggest that substantial quantitative differences exist. The '% conjugate with recruitment' metric doesn't capture such differences. Some form of a recruitment index as used in other parts of the manuscript would be more powerful. A more complex picture of INPP5E domain contributions to INPP5E interface recruitment is likely to emerge.

      The immunological synapse is a highly dynamic structure. TCR interface recruitment and PI(4,5)P2 clearance in response to various manipulations of PI turnover are only analysed at a single time point. A dynamic picture should provide more insight. For example, interface recruitment of the TCR may be consistently impaired, delayed or shifted in time. Reduced interface recruitment of the TCR upon overexpression of PIP5Kgamma (Fig. 5D, E) has already been described in the cited Sun et al. reference. This should be acknowledged.

      In Fig. 6E, the authors show a small reduction in IL-2 secretion in Jurkat cells stimulated with anti-CD3/CD28 upon knockdown of INPP5E. As INPP5E is expected to exert its functional effects through the control of the spatiotemporal organisation of the immunological synapse, activation of Jurkat cells with APCs would be more appropriate.

      The knockdown efficiency of INPP5E should be quantified.

      Reviewer #3:

      The work is fully performed in Jurkat cells, which a very good and widely used model to investigate T cell activation, yet, not perfect. Actually, in the case of events related with phosphoinositide function, Jurkat cells present a strong caveat. These cells lack the Phosphoinositide phosphatase PTEN, therefore having altered phosphoinositide turnover.

      Therefore, as a first critical point, the authors should confirm most of the central data of this work in primary T cells. They should also discuss this point, since it might bias some of their data.

      Additional points needing attention are detailed below.

      1) Regarding data in Fig 1D, the authors say the they find INPP5E localized with the centriole in the absence of SEB stimulation. The pattern shown is in the picture is very diffuse and blurry, not showing at all a centriole pattern.

      It seems to be more visible in Fig S1. The authors should replace Fig1D panel by a better "quality" picture if they wish to convey that message.

      2) What do the authors mean with "number of events" in the figures ? Please explain or replace by another term or means of quantification. If it means counting conjugates with INPP5E recruited "by visual observation", it would be much more appropriated to quantify fluorescence enrichment at the synapse making a ratio.

      It is also bizarre to plot "pairs" which are all at 100%. What does that mean?

      3) In Fig 2 D, E the authors observe by TIRF the presence of INPP5E at the planar pseudosynapse. They do in parallel TCRz. It would be interesting to better take advantage of that type of microscopy images to also quantify the impact of INPP5E on TCRz recruitment and to assess co-localization between INPP5E and TCRz using Pearse corelation on images with a very good resolution. From that image they look like they do not co-localize at all.

      4) The reasoning of the authors in Fig 2 H is somehow strange: "Since the distribution of INPP5E signals mostly appear at the T cell-APC contact site, it was necessary to examine whether INPP5E belonged to T or B cells" Although they use dSTORM the resolution of the image is not single molecule as they claim, but relatively large clusters. Moreover, they say that INPP5E is inside the T cell while TCRz is at the plasma membrane. In that image there are spots labelled far on the B cell. Moreover, it has been shown by several authors that TCRz largely occupies intracellular vesicular compartments. So the conclusion is not accurate. Finally, they claim that the overlap in some regions is suggestive possible interactions. The overlap is really minimal and in zones of clustering. So the comment is far from accurate. A proper colocalization analysis in TIRF_dSTORM images of INPP5E and TCRz quantified by Pearson correlation would be much more appropriate and accurate.

      By the way, the authors could use panel F of T cells transfected with Flag-INPP5E that relocalizes to the synapse to say that INPP5E in T cells relocalizes to the synapse.

      5) Fig 4A: The strongest interactor with INPP5E seems to be Lck, rather than TCRz. It would be interesting to also assess the effect of INPP5E silencing on Lck recruitment at the synapse.

      Is there a mistake in labeling IP in horizontal and IP in vertical. I guess one of them should be IB (immunoblotted / Western blot). Please clarify and correct if necessary. Same in B, there is labelled IP-Flag everywhere, is one of them input? Please clarify/correct if mistaken.

      The term INPP5E "interacted" with TCRz, ZAP and Lck in the text (line 168-169) is not fully correct here, since these molecules make complexes during TCR activation. The term "co-immunoprecipitated" would be more accurate here.

      Fig 4D Not clear here why the authors use cells transfected with TCRz-GFP while to conclude that INPP5E is required for exogenous CD3z clustering, they could just stain for endogenous TCR.

      Fig 6B: If the authors normalized the pProtein band density with respect to the total same protein, the Y axis should be expressed as band density ratio rather than "optical intensity (a.u.)"

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on January 4 2021, follows.


      In this manuscript, the authors have generated a new mouse model for the severe disease, Ataxia Telangiectasia (A-T). They introduce null mutations in Atm onto the background of mice that are somewhat sensitized since they also harbor mutations in the Aptx gene. The outcome is the mice show a set of phenotypes that are strikingly similar to symptoms seen in human patients. These include cerebellar degeneration, cancer, and immune system abnormalities. The also deliver small molecule readthrough (SMRT) compounds into tissue explants and show that such a manipulation can restore the production of ATM protein. The success in producing an Atm model with cerebellar degeneration is a compelling advance as this particular phenotype has been incredibly difficult to reproduce in animal models. The authors perform an interesting set of analyses to confirm that the other important features of the disease are also present in their mice. This paper has broad interest to multiple fields including neuroscience, cancer, and immunology.

      Essential Revisions

      1) It is not clear how progressive the cerebellar degeneration is. What is the spatiotemporal pattern of degeneration? Please consider the lobule by lobule effects over time.

      2) For the electrophysiology, what stage cells have you recorded from? That is, what was the structure of the Purkinje cells that you recorded? If the cells look really "normal" but fire abnormally, then please comment on how they are being affected. If the morphology is abnormal, then please explain what defects you see and how they might impact function. Essentially, the authors need to disentangle cell autonomous effects and non-cell autonomous effects with more clarity. That is, are you studying the "dying" cells or the cells that that escaped the genetic defect?

      3) Are both the Atm and the Aptx genes expressed in all (or the same) Purkinje cells? What is the experimental evidence?

      4) Please provide more context and rationale for Aptx in the abstract. As it stands, its mention comes out of nowhere.

      5) In the Introduction, please provide more information as to why previous studies/models might have failed to produce severe Atm-related cerebellar phenotypes.

      6) In the Introduction, the rationale for the choice of paring the Atm mutations with defects in the Aptx gene is unclear. Are they in the same pathway? Are the genes located in close proximity to one another? There are many issues that need to be discussed.

      Related to above, ATM and APTX, while involved in DDR, are involved in parallel pathways-ATM in DNA double stranded break repair, and APTX in single stranded break repair. Homozygous mutations in APTX causes human ataxia (AOA1), but there is nothing to indicate an intersection mechanistically between AT and AOA1. One could just as well call the AT-APTX double mutation a model of AOA1. As indicated above, please expand on the rationale of the experimental design.

      Also, are there more single stranded DNA breaks? Double stranded DNA breaks? Is there a sequestration of SS DNA break repair components including PARP1? How are the changes in PC firing related to DDR (it would be worthwhile for the authors to examine the following papers Hoch et al. Nature. 2017 Jan 5;541(7635):87-91, Stoyas et al. Neuron 2020 Feb 19;105(4):630-644) to give insight into studies that can explore mechanism for DDR and changes in cerebellar morphology/function.

      Therefore, the authors need to address whether single vs double stranded break repair is present and the authors could do a better job of linking the change in PC firing to DNA damage.

      7) Figure 2B: Apologies if I am missing something, but I do not understand the reason or explanation for what determines the probability of survival for the green, gold, and orange traces (the three severe cases in the graph). That is, why is the gold so strong?

      8) How come rotarod was not used as a test? This is a standard motor behavior test that is useful for comparing across animal models and studies.

      9) Related to above, why not use in vivo recordings? I can understand using slice recordings to tackle the biophysical and intrinsic mechanisms, although the authors did not do that. It seems to me that extracellular recordings would have been more informative in the in vivo, awake context.

      10) The authors picked specific regions of the cerebellum to target their slice recordings, which is perfectly reasonable. But why did you pick these regions? Please provide a full justification and discussion for the importance of these particular lobules in relation to what you are trying to solve.

      11) Given the use of slice recordings and that Purkinje cell degeneration is a key aspect of the phenotype, it would be very compelling if the authors showed some filled cells. As it stands, it is very hard to appreciate what the severity of neuropathology actually looks like, especially in relation to what the functional defects are teaching us.

      12) The authors state that "The largest differences were detected in the anterior [38.6{plus minus}3.4 Hz (n=187) vs. 88.1{plus minus}1.8 Hz (n=222)] and posterior [46.9{plus minus}1.9 Hz (n=175) vs. 84.1{plus minus}2.4 Hz (n=219)] medial cerebellum [1-way ANOVA, p<0.0001; Fig. 4B]." Okay, but what does this mean? What is your interpretation for why these regions were more heavily impacted (cell sensitivity based on circuit architecture, gene expression and protein make-up, neuronal lineage?) and how might it impact the phenotype?

      13) The authors state and reference "Previous studies in mouse models of heritable ataxia indicate that physiological disruption in PN firing not only includes changes in frequency but also affects its regularity (Cook, Fields, and Watt 2020)." I agree with having this reference, but what about other models of ataxia? There are a number of other excellent models that should be discussed.

      14) Purkinje cell firing data (figure 4B) should not be averaged across all of the ages, as this is not standard practice, and would be akin to averaging all behavior across ages. I think the data in fig. 4C suffices. If you want to compare across lobules on one graph, simply choose a particular age (perhaps when behavioral changes are first observed?) or at the oldest age.

      15) Why examine Purkinje cell firing deficits in different lobules but not make that distinction for Purkinje cell loss? The Purkinje cell loss analysis focussed on the areas with most pronounced firing deficits but this means that we don't know whether the cells that fire abnormally are the only ones that die. Also see point #2 above.

      16) Figure 4E and related text: Please provide a much more extensive set of images to show the cerebellar pathology. 1) Please show views of the different lobules to demonstrate the pattern of degeneration. 2) Please show different ages to show the progression of degeneration. 3) Please show higher power images of the Purkinje cells to clearly demonstrate their morphology.

      17) The authors need to need provide more data for what is actually happening in relation to cell death. Why not perform Tunel or caspase staining etc.? The authors must show that there are actually acellular gaps where cells have died, or some other indication that cell death has occurred or is occurring.

      18) Also in relation to the Purkinje cell degeneration, what do the dendrites look like? What about the axons? Do you see any torpedoes or axonal regression?

      19) In regards to the cerebellar degeneration, what happens to the other cell types in the cerebellar cortex? Are they intact? What about the cerebellar nuclei?

      20) The authors state "Of interest, APTX deficiency by itself had the greatest effect on the loss of DN4 cells...". Okay, but it is hard to see what this means for A-T as a disease. Interesting as it is, what is the relevance of this gene and these findings to the actual disease?

      21) Please provide a more extensive description and rationale for why this explant system was chosen.

  6. Dec 2020
    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on December 14 2020, follows.


      This study addresses an important topic of broad ecological interest and provides important insights into the role of local-scale processes in shaping patterns of species diversity, aiming to (i) assess if there is a global latitudinal diversity gradient (using alpha diversity) of rocky shore organisms and its functional groups and, (ii) whether there are any large scale or local environmental predictors of richness patterns. The strength of this paper is the global coverage of studies analyzed, showing for the first time that rocky shore richness does not appear to peak in the tropics - in contrast to many other studies of marine and terrestrial systems. These outcomes are not specific for rocky intertidal systems, with an increasing number of studies showing that the search for global ecological patterns may be elusive. While sampling in the tropics and the polar regions is poor (acknowledged by the authors), this should be viewed as a call for further research in these regions - not as a weakness of the paper per se. There are also some reservations on how the analysis has been conducted, including the lack of standardization of sampling effort and other details (e.g., size of sampling units) to derive a comparable measure of diversity across sites.

      Public Review

      The latitudinal gradient of diversity has been studied and confirmed in many aquatic and terrestrial habitats and species across the globe. In the vast majority of cases, richness increases towards the tropics. Using an impressive global dataset of latitudinal diversity gradients in 433 rocky intertidal assemblages of algae and invertebrates from the Arctic to the Antarctic, Thyrring and Peck show that rocky shore ecosystems may not follow this general pattern. The authors show that there is no clear latitudinal gradient for rocky shore organisms using alpha diversity - as posited by prevailing theories - although some functional groups exhibit contrasting patterns. Diversity within functional groups of predators, grazers and filter-feeders decreased towards the poles, whereas the opposite was observed for macroalgae. Correlation with environmental drivers highlighted the importance of local-scale processes in driving spatial patterns of diversity in rocky intertidal assemblages. The paper is well written and the many of the analyses are well done, but there is the concern, which the authors acknowledge, that sampling within tropical latitudes is sparse and needs to be carefully considered when interpreting the results of this paper.

      The work can be improved in the following manner:

      1) The relevant data to standardize species richness may not be available from the primary literature. However, it should be possible to employ relevant standardization methods within the 5{degree sign} latitudinal bands in which the data have been aggregated. An analysis based on standardized data, at least for the more data-rich latitudinal bands, must be added.

      2) Employ models that allow assessing unimodality, which is stated but untested. At the bare minimum, a quadratic relationship with latitude should be included in the GLMM. As implemented here, the GLMM employed to relate diversity to latitude can only detect linear trends, but not unimodal patterns and the mid-latitude peak suggested by LOESS for the northern hemisphere. To provide a formal test for unimodality, models with or without a quadratic term could be contrasted using standard model comparison procedures. Alternatively, GAM could be used to evaluate nonlinear effects.

      3) Clarify whether p-values are relevant or not. As is, it is confusing. For example, the legend of Table 1 mentions p-values, but these are not reported. Materials and Methods indicate that 95% confidence intervals are used to take decisions on null hypotheses, suggesting that p-values are not used in the analysis (lines 436-439). Nevertheless, p-values are reported in Table 2.

      4) Provide a rationale for distinguishing between canopy and other algal forms (the distinction is compelling, but it is not explained).

      5) We like the conclusion on the importance of local-scale processes. This should be placed in the context of previous studies that have quantified patterns and processes at multiple scales reaching the same conclusion.

    1. This manuscript is in revision at eLife

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


      This study combines high resolution imaging experiments with mechanical modeling to elucidate the energetics of flagellar propulsion and understand the role of internal dissipation in this system. The experiments use mouse sperm cells that are chemically tethered to a glass slip. For each cell, the flagellum shape is imaged over time and segmented into a mathematical curve. This data is analyzed based on a planar Kirckhoff rod model that includes hydrodynamic drag forces (based on resistive force theory), bending elasticity, and an unknown active moment density. An energy balance is written that also includes internal viscous dissipation generated inside the flagellum, with an ad hoc internal friction coefficient. By calculating the various terms in the energy balance based on the reconstructed filament shapes, the authors are able to estimate the active power density along the flagellum. This calculation leads to two unexpected findings: (1) the authors find that the active power density can be negative along some portions of the flagellum, meaning that along these portions the dynein motors act against the local deformation of the structure, and (2) the main origin of dissipation in the system comes from internal dissipation, which exceeds viscous dissipation in the fluid in magnitude.

      Essential Revisions

      1) It is not completely clear from the manuscript what the configuration of the sperm is with respect to the glass slide where the head is tethered. What is the orientation of the cells with respect to the slide, and in which plane are the deformations measured? (from above or from the side?) We would expect that different configurations may lead to slightly different waveforms. In particular, we are surprised that the mean shapes shown in figure 2(a) have a net asymmetry which is observed in nearly all the cells: could this have to do with the relative configuration of the flagellum with respect to the surface?

      2) The experiments are done with flagella very near a no-slip surface, since the cells are chemically adhered to the chamber boundary. Yet, the authors use resistive force theory for filaments in free space, without any reference to the nearby no-slip surface. As the rate of energy dissipation near the surface will be considerably larger than estimated by RFT, it is possible that some (or much, or perhaps all) of the additional dissipation found by the authors is actually within the fluid and simply not accounted for by RFT. Thus, all of the calculations must be redone with the appropriate Blake tensor for stokeslets near a no-slip wall before the results can be considered definitive. The paper must also more carefully illustrate and quantify the proximity of the flagella to the surface in order to make these calculations precise. Absent this analysis, the claims of the paper do not stand up to scrutiny.

      A related point is the need to understand the effect of tethering the cell on its kinematics and energetics? In other words, do the conclusions still hold for freely swimming cells?

      3) Is there any evidence of 3D dynamics? Some recent experiments with human sperm have suggested that sperm beats can take place in 3D (Gadelha et al., Science Advances 2020). As the model in the paper is 2D, this could also affect the energy balance.

      4) The authors should examine the work of K.E. Machin ["The control and synchronization of flagellar movement", Proc. Roy. Soc. B 158, 88 (1963)], which provided the first theoretical formalism to study active moment generation within beating flagella based on examining the difference between known force contributions from viscous dissipation and elastic bending. It seems that this same kind of analysis could be done here to identify directly the non-viscous contribution, rather than having to postulate a particular form.

      Stated another way: Why not try to estimate the active power density directly from the active moment density, which could be calculated from the moment balance of equation (4) where all the other terms are known? This would provide a direct estimate of the active power. The force balance could then be used to estimate the internal friction, which would then no longer rely on an assumed value for the internal friction coefficient. In fact, this could be used to obtain an estimate for that coefficient.

      5) The paper addresses in detail the use of Chebyshev fitting methods for the filaments, but does not appear to address the physical boundary conditions one would expect on elastic objects (particularly at the free end), involving the vanishing of moments and forces. Unlike, for example, the biharmonic eigenfunctions of simple elastic filament dynamics which are tailored to those boundary conditions [see, e.g. Goldstein, Powers, Wiggins, PRL 80, 5232 (1998)], it is not clear how the Chebyshev functions satisfy those conditions. Some explanation is needed.

      6) If indeed internal dissipation dominates, that would suggest that essentially all prior theoretical approaches to calculating sperm waveforms must be quantitatively in error by very large factors. It would be very appropriate for the authors to examine some of those theoretical works to determine if this is the case.

      7) The authors note in the Discussion that the beating waveform changes dramatically in fluid with higher viscosity. Yet, if external dissipation plays such a small role how can this be rationalized?

    1. This manuscript is in revision at eLife

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


      The manuscript from Perez-Garcia et al. follows up on a prior study by the same authors in which they identified the tumor suppressor BAP1 as a regulator of mouse placentation and trophoblast stem cells (TSCs) (Perez-Garcia et al., Nature, 2018). In their preceding work the authors showed that CRISPR-mediated knockout of BAP1 in TSCs results in upregulation of key stem cell markers Cdx2 and Esrrb and biased differentiation towards trophoblast giant cells at the expense of the syncytiotrophoblast lineage. Here the authors have expanded on these observations by demonstrating that BAP1 modulates the epithelial-to-mesenchymal transition (EMT) in TSCs and that a similar phenotype can be obtained by genetic deletion of Asxl1/2. Declining protein levels of BAP1 during differentiation of human TSCs into extravillous trophoblast suggest that the role of BAP1 may be conserved in humans. As the molecular mechanisms of trophoblast development, including EMT and invasive behaviors of trophoblast giant cells in the mouse and extravillous trophoblast cells in human are only beginning to be understood, this study provides an important advance.

      This is a well-written and technically sound study that clarifies the role of BAP1 in trophoblast development. Overall, the work presented is very important to the fields of EMT and trophoblast stem cell biology, and it warrants publication in eLife in principle. However, the claims in the abstract, the model in Figure 5, and the conclusions in the discussion are not well-supported. Therefore, additional experimental work will be essential for the manuscript to become suitable for publication in eLife.

      Essential Revisions

      1) There was consensus that the current manuscript lacks functional data to demonstrate conservation of BAP1/ASXL1/2 function in human TSCs. These are crucial claims in the abstract that are not supported, and some elements of these claims are necessary for the manuscript to have impact beyond the previous Nature 2018 publication. Currently, the studies in human TSCs are purely observational (Fig. 6D-E). The authors should employ genetic approaches to interrogate whether the functions of BAP1 in TSC self-renewal and differentiation are truly conserved between mouse and human.

      2) The main takeaway from Figure 2 is that BAP1 is dispensable for mouse TSC maintenance and that BAP1 knockout results in increased expression of stem cell markers Cdx2 and Esrrb. Both of these findings were previously reported in the authors' 2018 paper (see Fig. 4b in the Nature paper). Therefore, the statement that "BAP1 deletion does not impair the stem cell gene regulatory network" is not surprising and the authors should state clearly that these experiments confirm their prior observations.

      3) The overexpression data in Figure 4 is difficult to interpret. Vector transduced TSCs show a tight, epithelial morphology (Figure 3A), whereas the NT-sgRNA control cells look like they are undergoing EMT (Figure 4C). Why does the introduction of the NT-sgRNA induce EMT characteristics? Bap1 sgRNA1 cells seem less epithelial than the Vector transduced cells. Do NT-sgRNA TSCs have less BAP1 than Vector transduced TSCs?

      4) Moreover, all the data in Figure 4 are based on a single sgRNA that could activate BAP1 expression. To exclude off target effects, the authors should confirm the effect of BAP1 overexpression using another sgRNA or cDNA overexpression system.

      5) The authors need to examine the gene expression data more closely as well as the functional consequences of BAP1 overexpression on TSC proliferation and differentiation. In particular it would be important to compare the list of DEG in BAP1 KO and overexpression condition. Are they mirror-image or are there differences? For example, Zeb2 expression is strongly upregulated in BAP1 mutant line but not significantly altered in cells overexpressing BAP1. This should be discussed.

      6) In the abstract, the authors state that BAP1 function during trophoblast development is dependent on its binding to Asxl1/2/3. However, the data presented in this manuscript do not address whether BAP1 and Asxl1/2/3 are indeed part of the same complex in TSCs. Furthermore, the fact that Asxl1/2 KO increases expression of syncytial genes (Fig. 5) does not provide direct evidence of functional synergy between these proteins and BAP1. This conclusion could be strengthened by demonstrating that Asxl1 and BAP1 indeed have a protein-protein interaction in TSCs and/or by deleting the BAP1 binding domain in Asxl1/2. It would also be instructive to examine whether the phenotype of BAP1 overexpression in TSCs (e.g. gain of epithelial features and reduced invasiveness) is dependent on Asxl1. This could be examined by overexpressing BAP1 in Asxl1-deficient TSCs.

      7) In some cases, experiments are carried out to "confirm" and "corroborate" hypotheses rather than test them. For example, the similarity between the gene expression signature of Bap1 mutant murine TSCs is and Bap1 mutant melanocytes and mesothelial cells is shown and emphasized. One wonders how unique is this similarity? Is Bap1 expression modulation observed in other EMT processes during development or in cancer? This should be explored and discussed.

    1. This manuscript is in revision at eLife

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


      The study isolates bacteria from diverse Antarctic samples which utilise DMSP as the sole carbon source. It initially focuses on a Gammaproteobacterium, Psychrobacter sp.D2, which the authors establish lacks a known DMSP lyase enzyme despite having DMSP lyase activity (this needs to be quantified). Through RNA-seq and bioinformatics, they identify the gene cluster responsible for this activity and identify a novel DMSP lyase somewhat related to DddD in that it involves CoA, but critically also ATP, which distinguishes it from the pack of other known Ddd enzymes. This enzyme is a ATP-dependent DMSP CoA synthase required for growth on DMSP and its transcription is upregulated by DMSP availability. The novel mechanism of this enzyme is proposed from a strong structural component to the study. The authors propose the downstream pathway for DMSP catabolism, which we find to be oversold and requiring gene mutagenesis to confirm, and to be preliminary in comparison with the authors' other findings. Finally, the study attempts to show how widespread the enzyme is in sequenced bacteria, confidently showing it to be functional in other related Gammaproteobacteria and some Firmicutes.

      Essential Revisions

      1) Title: "a missing route", was it really missing? We would suggest a more precise title. Would be better to say "that releases DMS" or an alternative.

      2) This is a Ddd enzyme by definition and should be named as such.

      Line 27- We disagree with the use of a new gene prefix when there is a strong precedent for the use of Ddd for "DMSP-dependent DMS". If this enzyme is a DMSP lyase and is in bacteria then its naming should follow protocol and be called Ddd"X"-X-being a letter not currently utilised in known systems. Deviating from this convention causes confusion and is not appropriate. Furthermore, AcoD is already assigned in some bacteria to acetaldehyde dehydrogenase II.

      3) As presented, the bioinformatics-based evidence regarding the broad distribution of this enzyme (as claimed e.g. in the Abstract, line 33) does not stand up. Currently as presented in the manuscript, especially Fig 6, we are led to believe the enzyme is more widespread than can be demonstrated based on the authors' evidence (i.e., the authors allow a very low threshold of sequence identity and claim function outside of the groups they have tested). Either more work is needed to show that claims of such a wide distribution are merited, or the authors should limit their claims to what can be substantiated by their work. Specifically, the authors cannot comment on the "functional" enzyme being widespread outside of the Gamma's and Firmicutes that were tested, let alone the importance of the role in DMSP cycling. Only three "AcoD" enzymes were ratified in this study, which are relatively closely related to each (Psychrobacter sp. D2 Sporosarcina sp. P33 and Psychrobacter sp. P11G5 that are > 77% identical to each other). As can be seen in Fig 6, these three proteins cluster together and are far removed from all the other sequences on the figure, for which we have no evidence of their function (i.e., nothing can realistically be said on Deltas, Actinos or Alphas or the MAGS). Just to be clear, these other proteins shown in clades above and below the functional "AcoDs" in fig 6 are only ~30% identical to ratified "AcoD". Furthermore, only strain D2 was shown to make DMS; none of the other strains were tested. Far more testing of the diverse enzymes and strains are needed to make these statements as this study only tests one strain and three of the closely related enzymes (defined on Fig 6). Additional specific comments on this issue:

      Line 280. The sentence on MAGS and the environments containing them does not stand up for reasons summarised above. All MAGS shown on Fig 6 are not similar enough to "AcoD" to be termed as functional Ddd enzymes. More work has to be done on the strains and enzymes that are more divergent to true "AcoDs" before such a statement is supported. Please delete. Line 509-We agree with what the authors write about stringency. However, these parameters do not seem to have been utilised as stated here. Their stringency statement holds up for comparison between the D2 "AcoD" and two other tested "AcoD" enzymes and all those in the middle clade on Fig.6. But this is not the case for the proteins shown above and below this "AcoD" clade in Fig 6 which have at best around 30% identity to characterised enzymes. See below for examples. As the authors state in their methods, high-stringency methods are needed to exclude other acetyl-CoA synthetase family proteins. Thus, most of the genes shown on fig6 cannot be taken as having this Ddd activity.

      "To further validate that these AcoD homologs" the authors examined the activity of two closely related enzymes from a group of nine homologs with > 65 % sequence identity (starting line 283, Figure 6). It is not surprising that these enzymes have the same activity. Homologs outside this group of nine (Figure 6) are far less related to the characterized AcoD (< 32 % seq. identity). Conservation of the phosphate-transferring His (His292) and an active site Trp (Trp391) does not seem to be strong evidence for functional conservation. The manuscript does not provide any additional evidence that these less related enzymes also degrade DMSP. Either more experimentation is necessary, or the paragraph on the "Distribution of the ATP DMSP lysis pathway in bacteria" must be revised.

      For example: Psychrobacter AcoD (WP_068035783.1) is 31% identical to Bilophila sp. 4_1_30 (WP_009381183.1) in the below group of bacteria on Fig 6. Psychrobacter AcoD (WP_068035783.1) is 29% identical to Thermomicrobium roseum (WP_041435830.1) in the above group of bacteria on Fig 6. Line 283. This is not the case! The two sequences that were chosen to "validate" are far to close to the D2 "AcoD" than to MAGS and other potential "AcoDs" shown above and below the functional Ddd clade on Fig 6. This section design is weak and does not lend weight to the expansiveness of this family. More work on the more diverse enzymes and bacteria is needed to support the authors claims. Please delete or study the activity of the more diverse strains and their candidate "AcoDs". Fig. 6. This is a nicely presented figure that unfortunately slightly deceives the reader. The authors need to clearly show which strains they have shown to have Ddd activity (currently one as I understand it) and which enzymes they have shown to have the appropriate activity (currently three closely related enzymes as I understand it). If I am not wrong these are all confined to the middle clade of Gammas and Firmicutes. These stand clearly apart form the other strains (above and below) which have not been studied and which are only ~ 30% Identical to "AcoD" at the protein level. This is not clear on the figure and definitely misleads in the abstract and throughout the manuscript.

      4) We expect to see kinetics done on the new enzyme in line with what the authors have done in other related studies on Ddd and Dmd enzymes.

      This is important to place the work in context with previously identified Ddd and Dmd enzymes, many of which have been analysed by these authors in previous publications. The characterization of the AcoD activity remains entirely qualitative. The authors only provide relative activities measured at a single substrate concentration. This data does not support the following statement: "Mutations of these two residues significantly decreased the enzymatic activities of AcoD, suggesting that these residues play important roles in stabilizing the DMSP-CoA intermediate" (l.223-225).

      5) The manuscript does provide unambiguous evidence for the activity of AcoD and its function during growth on DMSP. On the other hand, the description of the "ATP DMSP lysis pathway" is less clear.

      Transcriptomics analysis (Figure 2C) suggest that growth on DMSP upregulate the genes 1696 (BCCT), 1697 (AcoD), 1698 and 1699. The function of the third and fourth protein remain unclear (line 253). Instead, a reductase (AcuI) encoded somewhere else on the same genome was shown to transform the acryloyl-CoA to propionate-CoA. What was the transcription profile of acuI acuH in the RNA-seq? were they induced by growth on DMSP? Is the 1696-1697-1698-1699 gene cluster conserved? What is the function of 1698 and 1699? These questions are only relevant if the authors plan to maintain the claim of having identified a new pathway. This pathway prediction component is very weak and could be supplemented by KO mutagenesis of the dddCB and acuI. Without such work this is speculation and needs to be written as such.

      6) Appropriate controls, units and quantification should be used:

      Line 102- Please give a normalised value for the level of DMS produced from DMSP per time and protein/cells.

      Figure 2. A. One would expect to see a growth curve of D2 on DMSP compared to acrylate, a conventional carbon source (e.g. pyruvate, glycerol or succinate) and a no carbon control. As "AcoD" is predicted to ligate CoA to DMSP it would be good to know if the strain grows on acrylate. It might be predicted to have different properties to e.g. Halomonas which does grow on acrylate. At least a no carbon and conventional carbon source should definitely be included.

      B. The units for this figure are not appropriate. It would be more appropriate to show the actual amount of DMS that is produced by the strain, ideally normalised to protein, cells or absorbance and time. Detail in the figure what the control is.

      C. Would like to see error bars on this figure. Also would have been sensible to colour code these to match panel D.

      Figure 3. B and C. as with Figure 2 we need to see levels of DMS normalised to cells/protein and time.

      Line 374 - No controls. Please include these as detailed above. No carbon, conventional carbon source, acrylate?

      Quantitative data supporting Supplementary Fig. 12 would be helpful. After all this route would have to explain that the bacteria can use acrylate CoA as sole carbon source (or at least alternatives would have to be discussed). Is the identified activity sufficient for this task?

      Line 388 - This method is/should be quantitative. It is standard practice to report DMS production normalised to time and cells/protein. Here we are only given peak area.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on November 30 2020, follows.


      The exact relationship between G6PD deficiency and malaria protection remains uncertain. This study provides evidence that the G6PD Med mutation (563 C>T) protects against clinical Plasmodium vivax disease. It uses a Bayesian statistical approach which specifically elucidates the particular protection which female heterozygotes versus male hemizygotes (or female homozygotes) for the Med mutation may experience. This is an important contribution to our understanding of the relationship between G6PD deficiency and P. vivax.

      Overall, the reviewers were positive about the work and its potential, but have some clear concerns that will require additional data, analyses, and interpretation. Below are the main points raised by the reviewers that would need to be addressed to for a revised manuscript.

      Essential Revisions

      1) The presence of mixed infections: although the work is focused on P. vivax, the majority (95%) of malaria in Afghanistan is caused by P. falciparum that means mixed species infections are likely high and P. falciparum infections may be obscuring P. vivax infections. It is not clear to what extent G6PD deficiency may impact the chance of being coinfected with both falciparum and vivax. Ideally, PCR verification of these samples would be performed to confirm the species for samples included in the analysis. Without this molecular data, the overall assessments of susceptibility to vivax malaria in association with G6PD Med is incomplete.

      2) The analysis relies on a number of assumptions made about Pashtun population genetics (e.g. is it reasonable to assume the same frequency of the relevant mutation throughout all the tribes in the study, and should this be at Hardy Weinberg equilibrium?) and it is not clear to what extent these assumptions are justified since little evidence/support is provided. In particular, the assumptions about Hardy Weinberg equilibrium of G6PD Med within the Pashtun population need to be justified and supported since the analysis is highly reliant on this assumption.

      3) The exclusion criteria does not appear to have been uniformly applied - in particular anemia was an exclusion criteria for only part of the data. This was not clear and may impact the overall significance of statistical results.

      4) While the manuscript makes a number of conclusions about female homozygotes, these are not strongly supported by the evidence. In particular, the study is likely under-powered with regard to clinical associations among female homozygotes with G6PD Med, but this is not addressed and the stated conclusions are likely stronger than what can be supported by the data/analyses provided.

  7. Nov 2020
    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on October 14 2020, follows.


      Injuries of the meniscus are associated with the future development of articular cartilage damage and ultimately osteoarthritis (OA). Prior work in this field has suggest that there are undifferentiated progenitor cells residing in the meniscus and it has been hypothesized that these cells could be harnessed to aid in meniscal healing after injury. The authors provide evidence that Hedgehog activation promotes meniscal healing and identify population of cells that are positive for Gli1, an effector protein in the Hedgehog signaling pathway. Using a combination of approaches, including lineage tracing, in vitro cell culture approaches and cell transplantation experiments, they show that this Gli1 populations contains putative meniscal progenitors involved in meniscus development and healing. Overall, the reviewers found this paper to have high potential and were particularly enthusiastic about the therapeutic potential of Purmorphamine to promote meniscal healing. However, all reviewers felt that the conclusions (and title) of this paper overstated the utility of Gli1 as a marker of de facto meniscal progenitor cells. It is specifically requested that the title of this manuscript be reworded in light of the previous work showing that Gli1 can be found in a number of cell types. In several places, additional work was requested to support the conclusions made in this manuscript. Please see the detailed comments below.

      Essential Revisions

      1) The authors describe many of their results as "novel". Gli1 reporter mice have been used extensively in other tissues to non-specifically describe progenitor cells (bone marrow, periosteum, peri-vascular spaces and others). Further, the role of Gli1+ cells in enthesis and and periodontal ligament (PDL) formation and healing has been previously explored. Gli proteins, which have a half-life of minutes-to-hours, may be a relatively unstable foundation for defining cellular identity. While the value of Gli1 as a general Hh reporter is clear, its utility as a putative stem cell marker (Title) does not seem adequately substantiated. The authors must temper their statements on novelty, exclusivity and utility of Gli1. The title of this paper also should be reworded.

      2) The Hedgehog (Hh) signaling manipulation conducted is rather straightforward and some overlapping studies have been performed in murine joints. Many of the experimental results could have been predicted. Other elements that contribute to the superficial nature of the studies are that Gli1 reporter activity is the only marker of Hh signaling examined (for example Gli2/Gli3 are not), and that the abundance and cellular source of an Hh ligand during development or repair is never entertained. Of note, these reporters for Ihh and Shh are available.

      3) It is a stretch to say that Gli1;tdTom labels meniscus progenitor cells (Lines 268-271). There is relative enrichment of Sca1/CD90/CD200/PDGFRa in Gli1+ cells (Fig 2B), yet the vast majority of cells positive for those markers are Gli1-negative (Fig S5). Positive outcomes during in vitro differentiation and scratch assays may primarily result from increased Hh-mediated proliferation. This logic extends all the way through the in vivo experiments (which are quite promising, translationally).

      4) The spatial profile of Gli1-expressing cells in the meniscus is beautifully described, however an interpretation for the superficially restricted zonation of Gli1 reporter activity is not given. Do these superficial cells have more or less cartilage antigen expression? Is there something clearly physiologically different in the Gli1-rich superficial layers that could be determined? Line 401 cites an osteoblast paper to set up the relevance of Gli1+ cells in development of musculoskeletal tissues. However, the meniscus is much more similar to the enthesis and the PDL. The authors should therefore lead with that literature. The PDL literature in particular is not cited and should be added. Also missing are recent enthesis development/regeneration papers (PMID: 30504126, 26141957, and 28219952).

      5) The characterization of Gli1+ and Gli1- FAC sorted cells could be expanded on a bit.

      6) CFU-F images should be provide in addition to quantification. The differentiation studies in Fig 2E are non-quantitative and not convincing. Further, it is a little contradictory that under certain contexts Gli1+ cells form more cartilage (2E), but under other culture conditions they have reduced cartilage markers (2F). These points need to be clarified.

      7) In Fig 5, changes in distribution or survival of Gli1+/- cells may underlie the difference, but survival nor Gli1- cell distribution were not assessed.

      8) Cartilage differentiation within the meniscus appears to be promoted with Gli1+ cell therapy and Purmorphamine. This could be assessed. Similarly, Hh signaling is known to induce osteogenesis. Osteoblastic antigens and/or presence of osteophytes should be assessed for in purmorphamine treated joints.

      9) One topic that is not covered in the paper is the role of Hh signaling in chondrocyte mineralization. This has been well studied in the growth plate (esp. related to PTHrP / IHH feedback loop) and may have relevance to the meniscus as well. The healing studies should consider this carefully, as ectopic mineralization is a possible negative side effect of Hh treatment.

      10) There are a number of places in the results where it is unclear if the authors are talking about Gli+ cells or Gli1-lineage cells. This should be clarified throughout, perhaps with specific nomenclature that defines "Gli1+" as cells that are positive for Gli and "Gli1-lineage" for cells that are descendants of Gli+ cells. Supplemental Figure 1A should be in the main document. Similar schematics in other figures are very useful for understanding the experiment.

      11) What are the temporal expression patterns of Gli1 and other Hh related genes during development and healing? It would be informative to see localized expression (e.g., in situ hybridization) or qPCR expression for healing tissues.

      12) The authors should clarify a number of things with meniscal cell isolation: (a) There are clearly differences in cell phenotype between superficial and deep areas and between attachment and midsection; was this considered for cell isolation? (b) I assume TAM injections were performed and then cells were isolated a few days later via FACS; please clarify details to show that Gli1+ (not Gli1-lineage) cells were characterized. (c) Fig 2: 3-month old mice were used, but again, Gli+ vs. Gli1-lineage cells is not indicated.

      13) The mechanisms by which Gli1+ and Hh treatments work is not explored. Some of the results are counter-intuitive. For example, why would Hh stimulate proliferation if Gli1+ cells if these are thought to be slow turnover resident stem cells? Furthermore, why would Hh stimulation lead to proliferation rather than differentiation, in contrast to what is know in growth plate biology)?

      14) The assessment of healing is qualitative/semi-quantitative (histomorphometry). The authors should perform a more rigorous assessment of healing to demonstrate the effectiveness of the Gli1+ cell and Hh therapies. This should include quantitative outcome(s) such as qPCR, mechanics, etc.

      15) The Gli1+ cell therapy histologic results are impressive. This is surprising because the delivery method was relatively simple. How much cell engraftment was there? Can the authors comment further (or add experiments to elucidate) on how long the cells were present and what their direct involvement was in healing?

      16) The authors show that native Gli1+ cells expand after injury. If this is the case, what is the rationale for adding more Gli1+ cells? Is the idea that the tissue has the capacity to heal but there aren't enough native Gli1+ cells to do the job?

      17) Figures and text jump between methodologies, making interpretation of results difficult. Fig1 shows that superficial cells of the meniscus generally have active Hh signaling 24-hours prior to a variety of postnatal-to-adult timepoints (A, B, E, F), and postnatal Hh signaling drives proliferation of early meniscus cells (C, D). It does not appear to report any long-term pulse/chase lineage tracing experiment as suggested in the text (Lines 223+). If this interpretation is incorrect, perhaps this could be addressed by increased clarity of figures and text (Methods, Results, Figure organization and captions).

    1. This manuscript is in revision at eLife

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


      Kang et al. eloquently describe the active suction organ that the larvae of aquatic insects of the Dipterian family Blephariceridae use to adhere robustly to complex surfaces. While the morphology of the mechanism has been reported previously, it's biomechanical adhesion function and performance across different substrates is unknown. The authors present three advances. First, they quantify the adhesion performance on rough, micro-rough, and smooth surfaces using an effective centrifugal setup. The ultimate adhesion tests show the larvae can resist shear forces up to 1100 times their body weight on smooth surfaces. Second, they visualize the suction function in vivo using interference reflection microscopy. This reveals that small hair like microtrichia can enter gaps in the surface. Because the microtrichia are angled inward, the authors surmise that the microtrichia's angle and small size helps increase adhesion contact area on rough surfaces. Finally, they compare the adhesion performance of the Blephariceridae larvae to other species, showing it is 3-10 times greater than found in stick insects. The finding that the larvae have such high attachment forces is impressive and the study offers new biological insights that may inspire engineers to invent new underwater suction mechanisms.

      Essential Revisions

      Although the reviewers were generally appreciative of the well-written manuscript and the remarkable performance reported for the active suction mechanism, the consensus is that the mechanism itself is not described in sufficient detail for the reader to fully appreciate the advance. Hence the main critiques focus on helping the authors to further flesh out the mechanism and report it in more mechanistic detail like how other adhesion mechanism are described functionally across the biomechanical literature. Further the presentation of the figures does not meet graphic design clarity standards essential to inform eLife's broad readership. To provide guidance, we list the following essential revisions.

      1) The introduction states that the suction organs have been observed, however, the manuscript does not communicate the observed mechanism as one would expect in the biomechanical adhesion literature. Instead it reports the measurements of the force and a suggestion that the microtrichia may be involved. We were hoping to find a quantitative report of the mechanism integrating the force data and microscopy images into biomechanical diagrams and to the extent possible, equations, that capture and communicate the mechanism as quantitatively as possible. Whereas we are not requesting further measurements, because the performance of the mechanism is well documented, we do ask a more in-depth biomechanical analysis that spells out the mechanism in a way it can be compared to the other classic mechanisms that the authors compare to. If this requires some additional measurements to inform the model, those efforts would be well worth it. In case the authors can use a mechanistic analysis lead, we recommend reviewing a couple of papers. E.g. Jeffries, Lindsie, and David Lentink. "Design Principles and Function of Mechanical Fasteners in Nature and Technology." Applied Mechanics Reviews 72.5 (2020). Or any other review or research paper that the authors find more useful.

      2) Please clarify if the experiments are done in air or underwater. We consider underwater as most appropriate; at minimum the surface should be wetted. The authors mention that the Stefan adhesion forces underwater would be higher than in air, but it's not clear if that statement pertains to the experiment. Please provide a full clarification, and in case the experiments were performed in air we would prefer to see them performed in water. If this is not possible, the manuscript should be entirely transparent on this matter so the reader can evaluate the precise merit of this study and its limitations fully.

      3) We found the images confusing at times. To resolve this we would like to see clear schematics (avatars) that ground the reader's perspective in all figures.

      4) Considering eLife's broad multidisciplinary readership and the appeal of this study for bioinspired designers and engineers, Fig 1d,e has to provide better anatomical readability. Please assume a Biology and Engineering undergrad level for the first figure, ensuring all definitions and anatomical names can be fully comprehended without reference to other literature. Please provide clear connections to the different views and perspectives presented in the panels leveraging graphic design to the benefit of the interested reader not familiar with insect morphology.

      5) Likewise, Fig 2 is also confusing. A schematic is in order to show the reader what they are looking at, how the images relate, and why they matter (significance) for understanding the main findings reported in this manuscript.

      6) Fig 3 clearly shows that course-rough surfaces provide far less adhesion force. We wonder, are there any images similar to Fig 6 showing that the microtrichia cannot enter the gaps? To comprehend what causes the differences, we would like to see a report of the length scale of the microtrichia compared to that of the gap's dimensions, both for the rough and micro rough surfaces. To clarify this in a universal fashion, please consider reporting gap size non-dimensionally based on the relevant microtrichia length scale. More discussion of the relevant length scales would help bring the force measurements and the observations of the microtrichia together.

      7) Fig 6 is an important figure, so it would help the reader to more easily grasp the viewing perspective using diagrams and avatars. I panel a, a schematic should clearly define the suction disc fringe and the perspective shown. What part is the suction disc and what is the length scale of this image compared to the suction disc? Also, it would be useful if the columns of the microstructure could all be aligned for clarity.

      8) Currently, the authors provide an estimate of the shear stress. It would be helpful to also include the normal stress based on the normal force data on smooth surfaces for lugubris. It would be informative for the reader to know if it exceeds 1 atm. If so, that is a very interesting finding. Please report and discuss what you find in the revised manuscript.

      9) Discussion: Please include a comparison of the magnitude of shear and normal stress that this suction mechanism creates with that of other organisms. Currently the comparison is done with force per body weight, which is biologically relevant. However, reporting stress provides an objective bio-mechanistic perspective on adhesion performance.

      10) Discussion, Ln 300: The suggestion that the inward-facing microtrichia may function to prevent inward slipping of the suction cup is interesting. Please discuss the tradeoff between smooth and micro-rough surfaces: is it possible that on micro-rough surfaces the microtrichia are better able to resist slip, but on smooth surfaces, the seal is better? And if so, this would suggest the effect of a better seal is more important than preventing slip, since performance is better on smooth surfaces? In-vivo visualization during failure would be very informative (in future work).

      11) Please discuss why there may be an intricate branching of the fan-fibres into the microtrichia. E.g. in the gecko, the branched tendons insert into the lamella, supporting the large tensile loads applied to the adhesive. However, here it is less clear if large tensile loads would be applied to the microtrichia. It seems logical that applying large normal loads to the suction cup should be done at its centre, resulting in decreased pressure if no slip occurs (as opposed to applying the normal force to the rim, which would not decrease pressure). So, this would not explain the intricate network of fan-fibres. However, for shear loads, it could make more sense: pulling in shear would engage the microtrichia on the far side of the cup, and the fan-fibres could help transmit this tension. It might be worth thinking this through and discussing the outcome in the paper to strengthen the mechanistic analysis.

      12) We would be excited to learn if the authors have thoughts on the slight curvature of the microtrichia and how it may be involved in the adhesion mechanism. In case this is purely speculative, this could go into the last paragraph of the paper, alternatively it could go into the biomechanical model of the mechanism.

    1. This manuscript is in revision at eLife

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


      The paper reports the involvement of isoleucine 553 in targeting Drp6 to cardiolipin containing nuclear membrane. The data are interesting, but there is no mechanistic understanding of how a single amino acid can target this protein so specifically to cardiolipin enriched membranes.

      Essential Revisions

      The authors are strongly requested to address the issues that were raised in the previous review. The authors state in their rebuttal that they plan to address them in a timely manner. The additional request of one reviewer that should be addressed is to test the involvement of residue 552 and 554 to highlight the significance of isoleucine in position 553 in targeting Drp6 to cardiolipin.

    1. This manuscript is in revision at eLife

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


      This manuscript presents new tool to detect and classify mice ultrasonic vocalizations (USVs). The tool (VocalMat) applies neural network technology for categorization of the various USVs to predetermined categories of pup calls. The paper in the form submitted seems to fit more as a methodology paper. Indeed, the authors state that the goal of their work is to: "create a tool with high accuracy for USV detection that allows for the flexible use of any classification method."

      The paper is well written and presents a useful tool to identify and classify USVs of mice. However, the reviewers think that the authors did not provide enough supporting evidence to claim that their method is significantly superior to other tools in the literature that attempted USV classification. For example Vogel et al (2019) - https://doi.org/10.1038/s41598-019-44221-3] - reported very similar (85%) accuracy using more mainstream ML approaches than attempted in this study with CNNs.

      Moreover, some of the reviewers were not convinced that the comparison to other tools was conducted in an unbiased and completely fair manner and that the approach described in this paper really represents a significant advantage over other tools. For example, two reviewers claim that the authors used DeepSqueak on their dataset without properly training it for this type of data, while their tool is specifically trained for it. Also, the reviewers expect to see a confusion matrix to assess model performance and establish whether the model does indeed replicate accurately classes (or how skewed it is with dominating classes).

      Overall, all the reviewers agree that they would like to see a more rigorous attempt to validate the findings presented (ideally also on an external database) and proper (unbiased) comparison with other similar software, to justify the claim that VocalMat performance in classification of USVs is indeed superior and novel to the methods already in use.

      If the authors wish to have the manuscript considered as a research paper and not in the form of a methods paper they should change the focus of the paper and provide more data showing a novel biological application of their pup calls classification findings. If not, we will be happy to consider a suitably revised version of the manuscript for the Tools and Resources section of eLife.

    1. This manuscript is in revision at eLife

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


      This work by Berger et al examined the process of De Novo infection by a model gamma herepesvirus, MHV68, using two complementary single cell approaches - CyTOF and scRNAseq. Using CyTOF and scRNA-seq, they characterize host and viral expression of protein and RNA during infection by the gammaherpesvirus MHV68. From CyTOF of numerous host proteins and one viral protein, they propose that the DNA damage marker pH2AX along with the viral protein vRCA are more precise indicators of progressive infection than a standard LANA reporter. Using a single viral (ORF18) and host RNA (Actin), they demonstrate that pH2AX+, vRCA+ cells uniformly express ORF18. To more closely examine viral RNAs, they performed scRNA-seq on infected cells and observe a high level of heterogeneity in viral gene expression.

      The manuscript is very well written and could potentially be a very welcome addition to the growing field of single cell virology. However, some concerns were raised regarding some of the conclusions and validation of the results. In particular, the variability in gene expression does not fall into existing models of kinetically regulated waves of viral transcription. This and their previous work convincingly argue that bulk measurements of protein and RNA are insufficient to represent the complexity of de novo MHV68 infection. However, in the absence of functional significance to the many clusters identified the impact of the conclusions is limited. With regard to validation, the authors must also consider that inherent variability in scRNAseq technology that could complicate the accurate measure of viral RNA. This should be discussed and addressed with additional data and/or experiments (see below).

      Essential Revisions

      1) The reviewers agreed that this article will be a very useful resource for the single cell virology community, but require further validation to realize that potential. As such, this article should be resubmitted as a "Tools and Resources" article. Furthermore, this revision should pay careful attention to the additional essential revisions that follow this point, in particular there are areas that require more data for validation. Ideally, existing data or experiments closely related to those conducted can be used.

      2) One of the more dramatic conclusions from the paper is that while the median infected cell expressed 52 viral genes, this ranges from 12 to 66 with only a handful of genes expressed uniformly. However, there are a number of indications that this may be explained instead by the stochastic failure to detect lowly expressed viral genes: 1) Figure 1A shows a tight distribution of the # of viral genes detected, which would be unlikely if there were multiple classes of infected cells expressing different subsets of viral genes. 2) Figure 1B shows a strong relationship between the average expression level and the frequency of detection, most easily explained by poor capture efficiency or another technical artifact resulting in undersampling. 3) These results fail to recapitulate known kinetic classes or uniform LANA expression. 4) Figure S3 indicates that even among host genes, the median cell had only a ~1,000 genes per cell detected, likely an insignificant fraction of expressed genes detected to assess viral gene number. These inconsistencies make it difficult to assess whether the observed heterogeneity is a true reflection of the gene expression profiles during infection or a reflection of the inability to detect lowly expressed transcripts by scRNA-seq.

      Given the inherent "noisy" nature of scRNA-seq, it is usually hard to quantify how much of a given mRNA expression variability among individual cells is due to technical limitations, and how much is due to biological differences. The authors could settle this question for at least a small amount of genes, by comparing the variability they see in scRNAseq to that they measure in PrimeFlow and CyTOF (although the latter has the added complication of comparing RNA to protein, but would still be valuable to discuss). If they compare the heterogeneity observed for the given proteins in CyTOF with what they observe for the corresponding transcripts in scRNAseq they will both validate their finding and will be able to estimate how much of their variability in scRNAseq translates to the protein level. They can do the same with their FlowPrime data, which would be even more informative as both measure transcripts. These approaches would be ideal as the data should be readily available. Alternatively, some of the expression should be correlated by RT-qPCR or by Northern blot or if single cell is necessary, then by in situ hybridization.

      The fact that the data do not pick up the established signatures of early vs. late gene expression goes against the bulk of work on viral gene expression control. More discussion about why this may be, including limitations of scRNAseq for less abundant transcripts is warranted.

      3) In figure 3A, the authors observe and note both pH2AX+, vRCA- and pH2AX-, vRCA+ cell populations; based on ORF18 or Actin expression, a significant fraction of these cells are infected. The proportion of cells in each gate is not quantified, but it appears that these single-positive cells represent a significant fraction of the total infected cells. However, in Figure 1C their appears to be no major single-positive populations, and the authors note that vRCA and pH2AX levels are highly correlated. This suggests that the cells are missing from the CyTOF analysis (perhaps lying outside of the two gates presented in figure S1A). These missing cells undercuts the value of the dataset and analysis and may lead to incorrect interpretations of pH2AX's value as a marker. Addressing this discrepancy in the FlowPrime/CyTOF data and some form of validation of scRNAseq (either by leveraging their protein data or via independent experiments) will be important for establishing the datasets as a reliable resource.

      Two related issues in the text: Line 217. "demonstrate that pH2AX+ and vRCA+ show progressive infection.." Progression implies that the study occurs over different time points, but the time parameter is not measured in these studies. It is not clear to me that these different phenotypes relate to different temporal stages of the infection or if they are different terminal outcomes. The authors should use another term than "progressive" in this context. Line 423 - the use of the work "progression" implies temporal studies which were not performed in this work. The study is a snapshot of a single time point and "progression" is inferred.

      4) Phenotype variation may be due to variation in cell cycle stage, cell viability and age, and asynchronous infection. To what extent are these variables controlled or considered in the analysis?

      5) In Figure 3, the authors show that ~20% of mock-infected cells are negative for beta-actin RNA. This seems quite odd for a house keeping gene, and the corresponding PrimeFlow data is not shown. I assume that this has to do with the authors gating strategy, or some technical issue with PrimeFlow that prevents all RNA molecules from being labeled. In either case, it would be helpful if the authors clarify this point and include the data for the mock cells in the figure.

      6) Could the authors explain their rational for including the CycKO mutant in the analysis and in combining the wt and KO data into one analysis? A-priori, if the mutant has no effect on the current question (de novo infection of fibroblasts) I would suggest excluding it from the paper and only showing the wt data, or to present the data for the mutant in a supplementary file, stating similar results were obtained with it. Although the authors states that only five genes were differently expressed between the wt and mutant, it seems wrong to aggregate the data from the different viruses into a single analysis.

      7) In Figure 6 and the accompanying text, the authors make a distinction between "virus-biased" and "host-biased" cells, based on the % of viral genes expressed in each cell. They go on to claim that "no significant difference in host gene expression among expressed genes" was found between these two groups. The statistical analysis for this result seems to be an ANOVA test, which I believe is not appropriate for this analysis. As the authors are comparing two distribution, something like a Kolmogorov-Smirnov test is needed. Additionally, in the text (line 314), the authors claim that no substantial difference is seen for cell-cycle genes between "virus-biased" and "host-biased" cell (Figure S6A). Looking at the data, it seems to me that G2 cells are highly enriched in the "host-biased" group. A formal quantitative analysis is needed to make this point.

      8) In line 316 the authors state that "host-biased cells expressed a number of interferon-response genes (Figure S6 and Table S3), suggesting a potential role in resistance to infection". I think this claim is not fully supported by the data. Since single-cell RNA-sequencing is a "zero sum" technique, cells with a higher proportion of viral gene expression are bound to show less host genes (as the authors have shown in Figure 6), including ISGs. To show that these cells are indeed expressing more ISGs than the "virus-biased" cells, would require sorting the different populations, as well as mock-infected cells, and measure ISGs (by methods such as qPCR, RNAseq, PrimeFlow, WB etc.), or at least have some analysis that takes into account the increased drop-off of host genes in cells with high levels of viral genes (something like a permutation test?

    1. This manuscript is in revision at eLife

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


      The referees agree your work on reconstitution of Drosophila septin hexamers into filaments on supported bilayers and their characterization and comparisin with the yeast counterparts is interesating and important. However, the referees raise a number of important points, all of which need to be addressed satisfactorily before publication.

      Essential Revisions

      1) In all sets of experiments different amounts of PS, PIP2 and septin concentrations are used. How can the obtained data be discussed in terms of these parameters, if they are not really comparable? What is the rationale of using the different conditions? For example: mEGFP-tagged fly septins are crowed with methylcellulose on neutral PC SLBs. Septin concentrations of 100-500 nM were used (Figure1). In Figure 2, however, 1000 nM septin is used without methylcellulose. AFM and QCM-D data were obtained with 20 % PS, no PIP2, and 10 nM septin concentrations. These conditions do not resemble the conditions in the TIRF experiments (as written). In the TIRF experiments 1000 nM septin was used. Cryo-EM data were obtained for 6 mol% PIP2, no PS. In the discussion a model (or several models) are proposed, which appear to be highly speculative. The results are compared to those with yeast septins reported in literature. As this comparison is the major point that is made in the manuscript it would be important to perform at least one of the experiments with yeast septin for direct comparison.

      2) The authors should create lipid bilayers on curved surfaces like glass rods to simulate the ability of the septins to create annulus structures as in vivo. Indeed it seems that on vesicles the structure of septin filaments hardly differ from the monolayer case. Adding topographica and geometrical cues to the septin assembly can potentially bring new insights in how they can assemble in rings or sheets.

      3) Examinations of septin hexamers only containing the short or long coiled coils or mixing two populations of septin hexamers (wt and ΔCC) to see whether the ΔCC are excluded from any filament stacks would be highly recommended to support the final model.

      4) Regarding the results in Fig.2D: A simple calculation explains why you find dense septin packing on SLBs at 10nM. Assuming a septin hexamer has the area of 4x24 nm2 and the flow chamber has an area of 5x20 mm2 and a height of 2mm, you would need about 1ꞏ 1012 septin hexamers to cover the SLB. This number of septins in the volume of the flow chamber would correspond to a concentration of about 8.7 nM. It is not clear why the authors did not check lower septin hexamer concentrations as this would simply require further dilution of the stock solution. These results seem to be also in conflict with the AFM results, where individual septin filaments are observed at 12nM and 24nM. The authors should clarify this difference.

      5) The comments about mechanical stability of the lipid bound septins are unsurprising and not very conducive as they describe GTA fixed septins. Studies of lateral stability don't have to relate directly to enhanced cortex stability. It would have been more powerful to compare the stability of septin decorated GUVs. Sorry, but the discussion about septin layer height limitation is very speculative and would be much better founded if the authors would have done some more experiments. The claim that the layer is self-limiting is not in line with the TIRF data that shows a steady increase of fluorescence intensity at 500nM septin. It would have been good to add AFM and QCM data on samples with higher septin concentrations, e.g. 500nM, to prove that the layer remains indeed within 12-21nm. It would also be insightful to either test mixtures of ΔCC septins with full length septins or to generate septins only lacking the long coiled-coils or the short coiled-coils to support the conclusions of the authors.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on October 30 2020, follows.


      Using a mouse model of melanoma, this report demonstrates the relevance of the CD300a immunoreceptor, specifically in dendritic cells (DCs), in tumor growth. It shows that the absence of CD300a is correlated with a higher number of regulatory T cells (Tregs) within the tumor microenvironment and therefore the tumor grows faster and survival decreases. Based on additional experiments, the authors propose a mechanism by which tumor-derived extracellular vesicles (TEVs) interact with CD300a in DCs, decreasing IFNbeta production which subsequently reduces the number of Tregs. In addition, data from melanoma patients show a correlation between overall survival and higher levels of CD300a expression in the tumor.

      Essential Revisions

      1) It is highly recommended to clearly demonstrate the role of IFNbeta in the proposed mechanism. In addition to using an anti-IFNbeta mAb in an in vitro culture (Figure 3D), other experiments must be performed, such as in vivo experiments with the anti-IFNbeta mAb. The authors have used this mAb in their previously published article (Nakahashi-Oda et al., Nature Immunology, 2016). Alternatively, in vivo experiments could also be performed with IFNAR1-like (IFN alpha and beta receptor 1 subunit) KO animals.

      In addition, is the observed increase in Tregs within the tumor in CD300a-/- animals due only to an increase in IFNbeta production by DCs? Are there other cytokines and/or cell-cell contact that may play a role? At least this should be discussed.

      2) Why are not all the experiments performed on CD300afl/fl Itgax-Cre mice instead of CD300a-/- mice? The experiments in Figures 2a, S2C, 3 and 4 should have been performed on CD300afl/fl Itgax-Cre mice. This is very important to state unequivocally that only CD300a in DCs is involved in the induction of an immune response capable of inhibiting tumor development.

      3) The authors found expansion of tumor-infiltrating Tregs in mice deficient in CD300a. However, no increase in Tregs was observed in tumor-draining lymph nodes. Did authors assess the expression of Treg activation and proliferation molecular markers, such as CD25, CTLA4, GITR, CD39, CD73 or Ki67? If indeed, Treg expansion as a result of CD300a-deficiency is the cause of enhanced tumor growth, authors should provide more evidence of Treg suppressive response. For example, authors can consider measuring the levels of co-stimulatory molecules (e.g. CD40, CD80 and CD86) on dendritic cells, which generally correlate with Treg activitiy and/or tumoral IL-2 concentration.

      4) PD-1 is the only marker analyzed to assess the exhausted status of CD8+ T cells infiltrating tumor lesion of CD300a-/- mice. Additional evidence of this functional status could be provided, such as for instance expression of CTLA4, TIM3 or other immune checkpoints, or low Ki67 levels. Indeed, particularly in reference of the human setting, PD-1 is also a sign of T cell activation, usually expressed in T cells infiltrating highly immunogenic and hot tumors. Hence, it would be useful having a broader characterization of immune effectors associated with progressing tumor microenvironment when CD300a is lost.

      5) Since authors have Foxp3-reporter mice, they should confirm their data in Fig. 3D with natural / freshly isolated Tregs, unless they are suggesting that CD300a mainly prevents in situ conversion of intra-tumoral CD4+Foxp3- Tconv cells into Tregs.

      6) Given that the interaction between CD300a and phosphatidylserine (PS) is critical to CD300a activation, PS co-localization with CD300a ought to be included in confocal microscopy. In addition, the binding of CD300a to PS and PE, which are both upregulated in dead cells, implies that apoptotic bodies could also be shuttling comparable signaling, Can the authors exclude that these particles are present in the EV preparations? Furthermore, does tumor supernatant lose any effect when depleted of EVs? The latter evidence could significantly strengthenthe exclusive involvement of exosomes in the process.

      7) Did authors validate the importance of PS in the context that they propose with an anti-PS blocking antibody? There are not many anti-PS blocking antibodies available and they might not block engagement with CD300a (see Nat Commun. 2016 Mar 14;7:10871). Nonetheless, this would be a good assay to demonstrate PS as the ligand that triggers CD300a to inhibit TLR3 and subsequent IFN-β production.

    1. This manuscript is in revision at eLife

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


      The idea of using DNA tags to enable tracking of protein and its subsequent handling is innovative and interesting. The manuscript is well written and some of the notions presented may help drive the field forward. There is a potential to revise the manuscript for eLife as a proof of principle for the approach of using scRNA seq to track an antigen in vivo.

      Essential Revisions

      While the archiving of the psDNA-Ova conjugate in lymphatic endothelial cells matches the earlier observations of fluorescently tagged Ova, the power of this method is to work with scRNAseq to be able to identify novel cells that interact the the complex. In this regard, it's clear that the psDNA-Ova may interact differently with various cell types due to the potential for recognition of the psDNA, particularly by TLR9 as suggested. Tracking the psDNA-Ova conjugate as an immunogenic adjuvant-antigen complex is an interesting starting point. You can address this concern by reframing the goal from tracking a protein antigen to characterizing the archiving and presentation of the barcoded psDNA-Ova complex. This doesn't require any additional work, just changing the way you set it up- that this if you immunogen is a DNA-protein complex- you can track it by scRNA-seq. The potential to study trafficking in a TLR9 KO mice in the future might open up using this method more generically for tracking the protein antigen, but this would require much more work to rule out other influence of the DNA on archiving and processing of the antigen.

      Your evidence that the psDNA really reflects the distribution of the protein is not sufficient. In Figure 1 c and d it's not clear how you measure the amount of protein? Is this the protein injected or the protein detected in a immunoblot or capture immunoassay? To extend the in vitro analysis in Figure 1c and d to actually visualize the native protein with anti-Ova and the psDNA by FISH would provide a high degree of clarity that the psDNA is not acting like a tattoo that outlives the intact protein. The FISH method could take advantage of any amplification step as long as it is consistent with detection by scRNAseq. Microscopy could demonstrate that the two signals remain in the same comparments. A particularly powerful way to show the direct association would be to perform a bulk IP-seq with anti-Ova and detection of the bar code with a test of the efficiency of depletion of the bar code form the cell lysate. A well-controlled experiment could be performed to map out the time dependent loss of protein (IP-western or capture immunoassay), and the free and protein associated psDNA. It would be ideal to include a macrophage in the analysis as a highly degradative cells in comparison to the dendritic cell and LEC, that maybe more specialized to regain intact proteins.

  8. Oct 2020
    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on October 6 2020, follows.


      The reviewers and editors were enthusiastic about the major conclusion of the study: that NusG-dependent pausing is an important factor that promotes Rho-independent transcription termination in Bacillus subtilis. Nonetheless, we felt that this conclusion can be strengthened with additional analysis and experiments that hopefully are not terribly burdensome. We believe that these additions would bring the paper to the level required for publication in eLife. The essential revisions are detailed below.

      Essential Revisions

      1) While we appreciated the careful follow-up work, we felt that the major conclusion could be strengthened by a more in-depth analysis of the genome-wide data, assuming those data support the role of NusG-dependent pausing in termination. Reviewers 1 and 2 give specific suggestions in their reviews. Some of these relate to the way comparisons are made between datasets, and others address specific scientific questions. Of particular relevance are analyses that test whether NusG stimulates termination at sites with (i) weak terminal base-pairs, and (ii) gaps in the U-tract. Any other analyses of the genome-wide data that support the importance of NusG-simulated pausing in termination would be valuable to include. For example, is there any evidence that NusG-dependent pause sites identified by NET-seq are associated with sites of termination?

      2) Termination sites in vitro are consistently downstream of those observed in vivo. While it is reasonable to hypothesize that this difference is due to trimming by exonucleases, there is no experimental evidence presented to support this. To test the hypothesis, we suggest mapping termination sites by 3' RACE in RNase mutant strains for one or two of the terminators characterized in the paper. B subtilis 3' exonucleases are defined, and mutant strains have been described (e.g., Oussenko et al., 2005 J Bacteriol 187:2758; Liu et al., 2014 Mol Microbiol 94:41).

      3) Add a figure showing the model described in the discussion (lines 332-84) for the proposed roles of NusG and NusA in intrinsic termination.

      4) Broaden the discussion of how the study relates to prior work on intrinsic termination.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on August 18 2020, follows. The decision letter below relates to version 1 of the preprint.


      This work has the potential to make an important original contribution to the aging biology literature and includes interesting new findings regarding the role of 17a-E2 in lifespan extension. The authors provide persuasive evidence of the role of classic estradiol receptor ERa in 17a-E2 signaling and mediating the metabolic effects of 17a-E2. However, far reaching and unsupported claims are made regarding the central tenets of this manuscript as is stated in their abstract: namely sex-specific differences and that of tissue specific mediation of 17a-E2 effects facilitating the therapeutic benefit. While the tissue specific data are suggestive that the liver and hypothalamus facilitate the beneficial effects of 17a-E2, these data do not appear to have been appropriately statistically analyzed. These need to be addressed prior to publication.

      The authors need to provide additional evidence for the tissue-specific nature of 17a-E2s effects on metabolism and lifespan, as well as correct/redo/undertake their statistical analyses using appropriate methods. Moreover, the experimental design needs to be more clearly documented and the data presented in a legible and interpretable manner. As such, the manuscript requires a complete reanalysis of current data and a complete rewrite, before we could consider its publication in eLife.

      Essential Revisions

      1) The experimental design needs to be more clearly documented, and the data presented in legible figures with detailed legends that alert the reader to the salient methods and findings. The authors should include a brief rational for each of the experiments used and their choice of cells and provide a concise description of the methods used, and sample size. The authors need to articulate how the significance for RNA-seq and CHIP-seq data was assessed.

      2) If the authors already have the complementary data on female mice on a high fat diet (rather than on normal chow) to facilitate a direct comparison with the male mice on a high fat diet and, thereby, support their sex-specific claims, it would strengthen the paper considerably, if not their claims on sex specificity should be removed from this paper as one cannot directly compare females on normal chow with males on a HFD.

      3) The authors state that their ChIP-seq data reveal nearly identical ERa binding patterns with17a-E2 and 17b-E2, however these have not been rigorously analyzed. The authors need to undertake actual statistical comparisons across groups rather than rely solely on qualitative assessments.

      4) The authors need to provide additional evidence for the tissue-specific nature of 17a-E2s effects on metabolism and lifespan. While they present convincing data that administration of 17a-E2 has direct effects on liver and hypothalamus, they have not provided definitive evidence that these tissues are directly responsible for the beneficial effects on metabolism and lifespan. The abstract and results section should be appropriately tempered.

      5) The authors claim that 17a-E2 reverses cellular senescence in the liver but provide limited conclusive supporting data. The authors need to provide additional evidence to support these claims.

      6) The motif comparison for the ChIP-seq data in Fig. 1B is not described sufficiently to allow for evaluation by readers. Moreover, the authors do not appear to have employed appropriate statistical analyses. Please describe the statistical tests employed.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on September 21 2020, follows.


      In this technical report, the authors use a previously-described mouse reporter construct to measure Cre-mediated recombination events, and repurpose it to examine Cas-induced double-strand break (DSB) repair gene editing events. All reviewers agree that the article will be of interest for the gene editing community and has the potential to make a significant addition to the field, in particular the delivery aspect in different experimental systems (cell culture, organoids, in vivo tissues). However, the reviewers also are in consensus that the manuscript is in need of additional experimentation to bolster the claims, in particular with regards to HITI and the complex events. Moreover, the authors need to address additional points as detailed below, many of which require only clarification, elaboration and text changes but not additional data. The claim in Figure 4 is not well corroborated and may be dropped unless a pilot screen and its results are presented in the revision. The claim in Figure 8 is not essential and may be dropped for better elaboration in an independent study. Below is a summary of the comments listing the essential revisions required for a revised manuscript.

      Essential Points

      1) The title should be changed. First, the use of in vivo may imply to some that the system is only for animals, which would short-sell its value. Second, given that the FIVER system is essentially the creative but simple use of dual CRISPR/Cas targeting on top of an already existing system (mT/mG Cre reporter mouse), the use of a novel acronym (FIVER) is not merited.

      2) The Abstract should include the fact that this represents a previously-described Cre/Lox reporter repurposed for gene editing analysis. This information is in the text, but more transparency is required. The repurposing of a previously-described LoxP reporter assay for gene editing does not constitute a novel reporter assay. Moreover, the abstract should highlight the gene delivery advance.

      3) The text requires elaboration and comparisons to other delivery approaches in the literature for each tissue examined. For example, it is unclear whether the efficiency of the delivery of Cas/sgRNAs to the retina in Figure 7H is expected based on other studies of gene delivery to this tissue. Namely, is it more difficult to achieve editing in this tissue, compared to introduction of a fluorescent transgene? If this has not been done, it does not need to be done here, but such comparisons with experiments in the literature will reinforce the utility of the approach.

      4) The HDR reporter presentation could be clarified and the assay has some limitations that should be discussed. Figure 1a is difficult to follow, because the repair templates are not shown. It is suggested to show at least the minicircle template and the targeted integration. In general, please strive that figures are understandable without consulting the text.

      Overall the frequencies of HDR are very low, but this is expected due to the design of the assay. Since two tandem DSBs are induced, NHEJ using the distal DSB ends causes loss of both cut sites, and hence is likely highly favored over terminal repair event. In contrast, most gene editing events involving HDR are induced by a single DSB, for which NHEJ recreates the cut site, and hence is a futile repair event. Namely, HDR is also promoted by the persistent nature of single Cas9-induced DSBs, which are inhibited in this assay by the second DSB. Also, the HDR event here requires a relatively long gene conversion tract, which is also not necessarily the goal of therapeutic gene editing. Accordingly, it is unclear whether this assay will be particularly useful for studying HDR.

      5) It is inaccurate to state this is the first in vivo gene editing reporter for HDR. The DR-GFP mouse was established and used to examine HDR frequencies in mouse tissues over 7 years ago (PMID: 23509290). The text should be changed and this information should be included in the manuscript.

      6) The validation of HITI editing and proposed applications are not at the level of Figures 1-3 validating endjoining or HDR events. NGS or equivalent quantitative techniques should be applied also here. This is especially true for the embryo editing application (Fig. 7) and the independent locus editing correlation (Fig. 8). For example, the very low levels of mosaicity during embryo editing is particularly surprising, since other papers have indicated that this is a major problem by sequence-based methods and phenotypic outcomes (e.g. tyrosinase editing for coat color). Have the authors validated the frequency of BFP+ events that are bona fide integration events at the target locus vs. random integration? This could be done, for example, by showing that the DSB at the target locus is required for BFP+ cells. BFP-minicircle transfections are used as negative controls, but do these also lack the DSB in the BFP-minicircle? Namely, the appropriate negative control should be BFP-minicircle + the DSB cutting the minicircle, but without the DSB cutting the target locus. This requires extensive new validation experiments that are essential for a revision.

      7) To improve the utility of the assay, the "unexpected outcome" of editing at the reporter locus (i.e. +tdTomato/+EGFP) must be investigated further with new experimentation to fully understand the structure of the event and potentially deduce the mechanism(s) leading to it.

      8) Figure 4 and associated main text. The claim that the reporter assay can be used in drug screens is not well supported. Either a proof-of-concept screen should be conducted or otherwise this claim should be removed.

      The small molecule SCR7 that has been reported to target DNA Ligase 4 (Lig4) is discredited (PMID: 27235626) and this should be discussed and indicated in any figure, if this section were to remain in the manuscript.

      9) The claim made in Figure 8 that editing at the reporter locus corresponds to editing at another independent locus requires further evidence. Controls for cutting efficiency are lacking and more loci need to be tested. In the context of the dual-editing (HITI at mT/mG and Zmynd10), it should furthermore be evaluated whether integration of the n.TagBFP occurs at the Zmynd10 locus and vice versa. The comments must be addressed experimentally, if this claim were to remain in the revised manuscript.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on October 2 2020, follows.


      There is consensus among the reviewers that this study provides an interesting and important advance in understanding the role of CEBP/b LAP in metabolism and response to a high fat diet challenge. The major discoveries reported here are fairly well supported by the data, including that male uORF KO mice show an increase in fat cell number as opposed to fat cell size, less inflammation, and improved glucose tolerance/insulin sensitivity.

      Essential Revisions

      However, all of the reviewers shared the major concern that it appears that only male mice were studied here, and that this fact - or the rationale for using only male mice - was not clearly articulated within the manuscript. This makes interpretation quite challenging, especially given that the authors previously published that lifespan extension in the uORF KO mice is much more pronounced in female compared to male mice. There was consensus that this is a substantial weakness to the current manuscript which limits its overall impact. It's possible the authors already have this data, and we would need to see inclusion of data supporting similar outcomes for the key experiments in female mice to recommend publication in eLife. If the outcomes are different in males and females, this is likely quite interesting and would need to be developed further.

      The other significant concern was related to the RT-qPCR data, which is indicative but not conclusive support for the authors' conclusions, especially since many of the changes are small in magnitude. It was noted that most of the relevant proteins have ELISAs available, and they all have antibodies which could be used to support the robustness and importance of the small but plausibly important differences observed. IHC against CD68 in the fat depots could be performed and the authors could strengthen their claims about adipose tissue inflammation by measuring the expression levels of inflammatory cytokines in adipose depots.

  9. Sep 2020
    1. Reviewer #3:

      The manuscript by Ishii et al focuses on understanding how cellular dynamics drive the spiral shape of the cochlear duct in mammals. The authors use live imaging of inner ear explants to follow dynamics of interkinetic nuclear migration (IKNM) and ERK activity (using ERK FRET sensor) to track some of the processes that give rise to tissue bending during spiral duct formation. On the imaging side, the manuscript presents a technical tour de force, showing remarkable two photon imaging capabilities that provide insights into the dynamics underlying cochlear extension. These experiments reveal several new observations: (1) Medial epithelial layer (MEL) tends to bend more than the lateral epithelial layer (LEL) despite being more proliferative. (2) That nuclei of cells in the curved region of the cochlea tend to stay in the luminal side, following cell division, rather than migrate back to the basal side. (3) The cells migrate towards the apical lateral roof. (4) That there are orchestrated ERK waves that correlate with cell migration. Based on these observations and on mathematical modeling, the manuscript has two main claims: (1) that nuclear stalling on the luminal side following cell division leads to increased curvature which gives rise cochlear duct bending, and (2) that multicellular flow mediated by ERK signaling waves pushes cells towards the growing apex, supplying the cells required for luminal expansion. While the observations in the manuscript are certainly interesting, I worry however, that some of the claims are not sufficiently substantiated, and also the connection between the two observations is rather weak. Here are the detailed concerns:

      Major concerns:

      1) The authors argue that cell cycle arrest results in a decrease in the curvature of the cochlear duct, which supports the hypothesis that luminal nuclear stalling promotes MEL bending. This is fine, but luminal nuclear stalling can be a result and not a cause. Since in a bent region, the basal side is more packed, this density gradient can be the cause of nuclei stalling at the luminal side. The fact that the curvature decreased but not diminished after cell cycle arrest could suggest that nuclear stalling is not required for bending, but rather reinforces it.

      2) Since the authors discuss both cell proliferation and nuclear stalling, and cell migration, as forces that can drive bending and coiling, it hard to interpret the results of the mitomycin C experiment. Could it be that the tissue is less curved because there are less cells to supply the elongation tissue rather than less nuclear stalling? The authors should consider inhibiting either cell migration or the cytoskeletal machinery required for IKNM to dissect these effects.

      3) The authors present a mathematical model to demonstrate that nuclear stalling in the luminal side results in bending. To model nuclear motion they use a parameter, gamma, which controls the degree of basalward movement after IKNM. Modeling in such way means that other than gamma=1, the nucleus never fully returns to the basal side, but if I understand correctly this is not the case, as even if the nuclei that stall at the luminal side, eventually return to the basal side.

      4) Furthermore, for luminal nuclear stalling, the authors tracked only the nuclei of dividing cells. This makes the data in Fig 2D' much clearer. However, in their model the authors show only these nuclei and not all nuclei. In addition, they show many crowded nuclei in the model, yet this is not observed in the images provided in the manuscript. Therefore, it seems the model does not represent the morphology of the tissue properly. The authors should model the process with non-dividing cells at the basal side.

      5) In lines 250-252 the authors claim that the higher volumetric growth measured at the MEL should cause an opposite curvature relative to the innate one. This is true if EdU intensity is proportional to volumetric growth, but cells in the MEL and LEL may not be the same size. For example, cells in the MEL could be smaller than cells in the LEL. The authors should therefore measure the nuclei number density and the volumetric cell density to clarify this. If the number density of the nuclei is indeed higher at the MEL, it may also explain the higher structural integrity of the MEL relative to the LEL demonstrated in figure 1C.

      6) The authors show the effect of ERK inhibition on tissue flow speed. This is a very important observation and raises several important questions. What is effect of ERK inhibition on curvature? On tissue length? On proliferation? These will provide a more complete understanding of the effect of RK inhibition.

      7) The authors should also test the effect of mitomycin C on cell flow and ERK activity. AS mentioned above, it is not clear whether the effect of mitomycin C is a result of less nuclear stalling or perhaps less cells that flow towards the apex.

      8) In Figure 3 the authors analyze the EdU distribution over the cochlear duct. This analysis is done using the maximum intensity projection of the stack. It seems that a more accurate way to quantify would be to use the summed intensity image rather than the maximum intensity image. This may reveal additional details that were missed by throwing away all other layers except the one at maximum intensity.

      9) In Figure 4 the colors used for the ERK activity analysis are very hard to see for color-blind people. It would be easier for this audience if the authors changed 1 of these color to green/red/yellow.

    2. Reviewer #2:

      The paper by Hirashima and colleagues shows some interesting cellular mechanisms they conclude drive the spiraling and outgrowth of the mammalian cochlea. The two cellular mechanisms they propose are supported by experiments and modeling. The spiraling ERK wave and the contrasting movement of lateral cells was very intriguing. However, the ERK wave and lateral cell movements seem disconnected from the bending forces discussed. Are the authors saying that the ERK mediated lateral cell movements are important for cochlear growth while the MEL is important for the bending? The two mechanisms they discuss seem insufficient to explain all of cochlear spiraling. Other cellular mechanisms such as cell proliferation and convergent extension are mentioned but their roles are not incorporated into their discussion. Are they not required? How do they complement their results?

      1) While the authors talk about bending forces, the paper has no measurements of the forces generated by different tissues. I also feel there are other cellular mechanisms that are mentioned but never incorporated into their proposed explanation for duct coiling such as convergent extension and actomyosin based basal shrinkage. Proliferation is discussed quite a bit but seems to be dismissed as a force. In the introduction they mention how Shh mediated proliferation is required for duct elongation while Fgf10 null mutants have a shortened duct yet normal proliferation. So what is the role for proliferation? Maybe they can answer this in the context of their interesting observation that there is more proliferation in the roof than the floor which would be predicted to bend the cochlea along that axis. When combined with the medial lateral bending could these two forces result in the spiraling? It also seems like this differential proliferation between the floor and roof was in more than just the epithelium correct? Could the cartilaginous capsule around the duct guide the bending as well? In their culture experiments, if too much of the capsule was removed then normal duct development was disrupted.

      2) Their demonstration that the bending forces are in the medial half is interesting but the only tissue whose mechanism is studied is the MEL. Could convergent extension in other medial tissues such as the prosensory domain (which Wang et al. showed was occurring in this tissue) and surrounding mesenchyme be the main force generator for the bending of the medial half of the cochlear duct? Does the MEL cultured by itself bend? They say that cell intercalation can drive ductal elongation but not bending (line 83) but can't convergent extension occur asymmetrically in the tissue? Such as by occurring in the overlying medial mesenchyme but not in the medial epithelium. It should be noted that the bending by the epithelium does not have to provide high forces as long as the force provided by other tissues are similar across the medial lateral axis, the bending in the epithelium could bias the mass of tissue to bend.

      3) The mathematical modeling for the luminal bending is less convincing than the mathematical modeling for the ERK and Cell flow coupling. The simulated curves in Fig. 2K are quite different from the Experimental measure in Fig. 2M, especially for the Mitomycin C condition. I feel that the values plugged in for the Numerical simulation, the standard parameter set were not well justified. What happened to the simulations as these values changed? Was the parameter space for acceptable values broad? In contrast the parameters for the numerical simulation of the ERK activation waves and cell flows were well justified. The parameters chosen might explain the big differences between simulation and experimental in figure 2.

      4) For the cell tracking experiments in the lateral region the resolution was 4-5 cells. The resulting cell flow patterns were very interesting but why didn't the authors track single cells? Segmenting individual cells via cytoplasmic labeling is much trickier but the nuclei are identifiable and the Imaris software they used in the paper has a cell tracking feature for such labeling. I would think that individual cell movements might provide more insights. In line 303 they say they can see cell contractions which I assume is for individual cells? How were cell contractions identified? Movie 5 was excellent and very informative. Do the cell flows correlate at all with the proliferation seen with Edu staining?

    3. Reviewer #1:

      This is a fascinating manuscript that explores for the first time the potential mechanisms underlying cochlear morphogenesis. The authors have used a combination of modeling, beautiful imaging and ERK-FRET reporter mice reporter mice to suggest at least two processes may be at play in cochlear shaping - differential interkinetic nuclear migration and a cellular flow that appears to correlate with ERK activation.

      I have no major concerns with this lovely piece of work. The imaging and quantification is meticulous, and the observations made by the authors are novel and will of great interest to cell biologists interested in morphogenesis, no just aficionados of the inner ear.

      The one suggestion I would make is for the authors to clarify the relationship between cell proliferation and ERK activation. When they reference the inner ear literature, they point out that FGF pathway mutants have deficient cochlear morphogenesis and proliferation, and they hypothesize that FGF-induced ERK activation may be responsible for their propagating waves. However, they also reference work suggesting that cellular extension during collective migration can also induce ERK activation and also suggest SHH-induced proliferation as another causative factor in promoting ERK activation through proliferation. I think the authors should try and clarify this - both in their explanation, but also by comparing the effects of the MEK inhibitor PD0325901 on ERK activity and tissue flow speed (Fig 4I and S3F) with the effects of the FGFR inhibitor SU5402, and also Shh inhibitors like cyclopamine. If the effects they see are directly due to FGF signaling, one would expect a change in ERK activation and cell flow with the same kinetics as with PD0325901. However, if Shh-induced proliferation is responsible, the change in ERK activation would take much longer to achieve. I think these experiments should be possible to do in a relatively short period of time.

    4. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on September 9 2020, follows.


      The mammalian cochlear duct is a spiral-shaped organ. This study investigated the mechanisms underlying the bending of the cochlear duct. Using two-photon live imaging and mathematical modeling, it was reported that the bending of the cochlear duct is caused by stalling of nuclei in the luminal side of the medial cochlear duct during interkinetic nuclear migration. Using FRET-based imaging, cochlear duct elongation is attributed to an oscillatory wave of ERK activity originating from the cochlear tip.

      All three reviewers were impressed by the imaging results. Although the reviewers and editors find the concept and approach interesting, blocking cell proliferation may be too crude a method to address the authors' hypothesis and many questions were raised by the results of blocking cell division. Second, the relationship between cell proliferation and ERK-driven migration is also unclear. Please see comments from Reviewer #2 and #3 for specifics. Third, what is the relationship between SHH-induced proliferation and ERK activation as suggested by the authors (see comments from Reviewer #1)? Additionally, it is problematic to illustrate a difference in the bending force between medial and lateral cochlear duct that is presumably occurring at E12.5 and E14.5 with a cochlear dissection at E17.5. The tissue architecture is completely different between E12.5 and E17.5. The surgery basically removed a specific region of the cochlear duct, the stria vascularis, rather than medial versus lateral halves of the cochlear duct.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on September 9 2020, follows.


      The role of extracellular vesicles (EVs) such as exosomes as factors potentiating metastasis by solid tumors has attracted considerable recent interest. The article by Ghoroghi et al is a very complete and thorough study of the role of 2 small GTPases, RalA and RalB, in extracellular vesicle (EV) release and breast carcinoma progression. The main advance of this manuscript is to describe a signaling role for the GTPases RalA and RalB in regulating phospholipase D (PLD) and multivesicular body function to regulate exosome biogenesis. They also show that RalA and RalB regulate expression of MCAM/CD146 on EVs, and that reduced levels of CD146 on EVs affects efficiency of lung cancer metastasis. Finally, they show RalA, RalB and CD146 levels are indicators poor prognosis for breast cancer patients. Overall these are interesting observations with clinical relevance. The study is extremely carefully performed, in general, with appropriate controls and conclusions. There are a limited number of weaknesses that need to be addressed.

      Essential Revisions

      1) Figure 3C shows that RALA and RALB have functions where they do not always act in series with each other. They may for exosome excretion, but not necessarily for proliferation. For Supp. Fig. 4C, this experiment needs to be longer than 72 hours for a proliferation assay to be truly convincing. While interesting that proliferation results differ between mice and growth on plastic, a 10 day growth experiment would lead to greater conviction that this is a sustained difference. Figure 3D better agrees with Supp. Fig 4C, where loss of RALB gives greater proliferation over control, albeit not as great as RALA loss. Was Fig. 3D performed at 12 days? The variable time points make it difficult to assess the role of RALA/B on growth.

      2) Figure 4 carefully describes why RALA/B deficient EVs fail to prime regions for metastasis. As the EVs are not directed to those locations, the contents fail to increase permeability of the regions. However, statistically significant does not mean biologically meaningful; specifically, looking at Fig 4f and 4g, knockdown of RALA/B had little effect on EV internalization. One question that is not answered is whether RALA/B are acting in series or parallel. Concurrent depletion of both RALA and RALB in the types of experiment performed in Figure 4 would help answer this question. If depletion of both isoforms is greater than either alone, then it implies they act in parallel.

      3) How are RALA/B activated in the context of 4T1 cells? The use of the RAL inhibitor in Figure 1B is most effective in cell lines without RAS mutations. Panc1 and MD231 cells have KRAS mutations, yet RALGEF inhibitors are least effective. At the concentrations used, all RALGEF activity should be inhibited. Is RAL expression levels similar between cell lines?

      4) The logic for targeting PLD1 seems rushed. There are several RAL effectors, and while the data on PLD1 are compelling, it is unclear why only this effector was selected. Were other effectors tested? The Hyenne paper, which is cited throughout, provided stronger logic for connecting these pathways. The statement in the discussion, "Our work further identifies PLD as the most likely effector acting downstream of RAL to control exosome section" is incorrect as stated. This work identified PLD1 as A downstream effector important for exosome secretion. To state that it is the most likely effector is an overstatement as no other RAL effectors were tested.

      5) The use of either PLD inhibitor at 10 uM will have significant inhibition of both PLD1 and PLD2 regardless which inhibitor is being tested, as well as additional off-target effects. Given both inhibitors have nanomolar IC50 values for their specific PLD isoform and low micromolar IC50 values for the related isoform, these experiments are inconclusive as presented. This section of the text should be reworked to account for the lack of isoform selectivity at the concentrations of inhibitor used. a. siRNA or shRNA could be used to validate the PLD1/2 inhibitor data.

      6) In all cases when using inhibitors, there are no western blots or additional validation showing target inhibition in any cell line. In this case, the use of such high concentrations of inhibitor likely resulted in inhibition of the target proteins. However, such high concentrations often result in off-target effects. Determining the lowest efficacious dose to inhibit target function should have been performed and used throughout the experiments.

      7) Would loss of MCAM expression, via direct knockdown, result in EVs that are unable to permeabilize HUVEC cells, as in Fig 4A/B? Alternatively, does loss of MCAM expression (or blocking via anti-CD146) result in decreased metastasis, similar to RALA/B knockdown? While Fig. 5g shows a decrease in EV localization to lungs on treatment with Anti-CD146, the rate of metastatic lesion formation was not assessed when CD146 was blocked.

      8) In a previous study (Hyenne et al, 2015) the authors already demonstrated a role for RalA and RalB in controlling MVB and EV secretion in the 4T1 breast cancer model, in a process evolutionarily conserved through nematodes. They also wrote a follow-up review article describing considerable evidence in the literature for RalA controling PLD and ARF6 function to control EV secretion. This diminishes the novelty and interest of the first part of the study, which could be reduced. The more novel and thought-provoking parts of the study are in the definition of the relationship between the RAL proteins and CD146, and the identification of unique properties of the exosomes produced in cells with manipulated RAL proteins (for instance, in regard to influencing exosome permeability). These could be better emphasized.

      9) Almost the entire mechanistic model is based on the work of a single breast cancer cell line, 4T1, which has been described by some as triple negative. This is a significant weakness, as there may be features of that line that make it uncharacteristic of breast cancer in general. At least some of the key conclusions should be functionally confirmed in an additional cell model.

      10) In addition, breast cancer cells fall into multiple different subtypes, which have different metastatic propensities and gene expression patterns. Is the functional relationship between the expression of RALA/B and CD146 in exosomes observed in just triple negative cells, or in other subtypes?

      11) In Fig 5h, K-M analysis of TCGA shows a weak relationship between MCAM expression and survival. Were the tumors analyzed segregated by tumor subtype? Were data corrected for tumor stage? This is important, as the MCAM staining pattern may reflect a propensity for MCAM expression in tumors at a late stage, or subtypes with a poorer prognosis.

      12) The authors provide observations suggesting that RalA and B control primarily the EV secretion pathway involving Multivesicular bodies, hence leading to exosome secretion. This is mainly demonstrated by observation of a decrease in MVBs upon knock-down of RalA/B, demonstrated by thorough electron microscopy analyses. This is correlative, rather than truly demonstrative, but the best one can do so far. In most experiments, the authors use EVs isolated by a relatively crude method, ultracentrifugation, that co-isolates non-specific components, and they do not analyse larger EVs that can be recovered at lower centrifugation speed, thus an effect of RalA/B on these non-exosomal EVs cannot be excluded. The EVs are only characterized by their number (NTA counting), which is not very precise, and not consistent with guidelines of ISEV (MISEV 2018, J Extracell Vesicles 2018, 7: 1535750).

      Maybe the authors can argue that they did perform more complete analyses of their 4T1 EVs in a previous article? Did they use the EV-TRACK website to verify their experimental EV isolation and characterization set up? Of note, the authors also perform quantitative proteomic and RNomic analyses, which gives a better characterization of EVs. The protein composition and its change upon RalA/B KD could have been used to try to confirm (or not) the MVB origin of the EVs controlled by RalA or RalB, but it is not crucial for the message. Alternatively, to demonstrate that the CD146-bearing EVs that carry the prometastatic function are bona fide exosomes, the authors could have shown its localization in the cells, upon or not RalA/B depletion, and show if a drastic change in ratio of localization in MVBs vs the PM occurs, but this would be an additional study, not necessary for the current paper.

      13) The authors insist that RalA/B control exosome secretion, and discuss the bases and limitations of their demonstration properly. The summarizing schemes (fig2f and fig5i) of their model show the release of RalA/B-depent pro-metastatic exosomes, and RalA/B-independent exosomes which are not pro-metastatic. However, EVs that are released in the absence of RalA/B could instead be formed at the plasma membrane, and correspond to ectosomes. Nothing in this study demonstrates the origin of RalA/B-independent EVs, thus PM-derived EVs should be represented in the scheme.

    1. Reviewer #3:

      The manuscript studies a theoretical model within the framework of reaction-diffusion equations coupled to signalling gradients to possibly explain the emergence of whisker barrels in the cortex.

      1) The model considered by the authors is identical to the one studied by Karbowski and Ermentrout (2004). The only new features are the extension of the original 1D model to 2D and the addition of an extra term to represent competition in axonal branching.

      2) The authors consider 2 guiding fields. What are their explicit spatial profiles? Notice that since these fields essentially guide the emergent pattern and hence their profiles, in relation to the geometry of the 2D domain, are crucial. A different profile would certainly lead to a different pattern. I feel that it is not enough to say '...linear signalling gradients aligned with the anterior-posterior and medial-lateral axes....' since the domain is 2D and of non-rectangular shape.

      3) The justification for the introduction of the extra term for competition amongst axons (eqn (3)) is missing. Why that form? What is the reasoning for introducing axonal competition? What essential features of the resultant patterns are missed out if this term is absent? Or has a different form? In the discussion section, the authors mention, without any justification, that the conservation of branch density in each projection is a key requirement for the emergence of barrel patterns. This is totally unclear.

      4) Related to the above point, the authors mention that the axonal branch density is bounded by their dynamics. I presume that the integrations on the RHS of eqn (4) are spatial integrals over the domain. Then how come a spatial index survives in the LHS of this equation? How did the authors arrive at this equation? Is there a continuous-time version of this equation (like a conservation law), i.e., one that does not make a reference to the discrete time-stepping dynamics?

      5) A typical mathematical modelling study should explore the space of relevant parameters to demonstrate the possible range of behaviours that the model can exhibit. This is usually presented as a phase-diagram. The authors do not explore the parameter space (or the possible spatial profiles of the guiding fields) in their study.

      6) Throughout, the authors emphasize the spatial-locality of their mathematical model and conclude 'Hence the simulations demonstrate how a self-organizing system...'. A mathematical model with spatial-locality alone does not imply self-organized dynamics. With a sufficiently large number of spatio-temporal fields (N=42), and the concomitant parameters, and non-autonomous guiding fields, it is possible to reproduce any desired pattern. As such, it is crucial in the mathematical modelling of living systems to delineate the essential requirements from the incidental.

    2. Reviewer #2:

      This is an interesting paper that with a few assumptions shows that an old model for areal formation in cortex is sufficient to quantitatively reproduce the patterns of barrels observed in mouse S1. It would appear from the model that the key is the parameters gamma_ij that are presumably (hypothesized) to be assigned at the level of the thalamus. I have a few questions about the paper

      1) Does the same model work with respect to projections from the brain stem (barrelettes) to the thalamus (barreloids)? This would be a good way to check the ideas. Related to this, is it true that the barrelettes (barreloids) precede the development of the barreloids (barrels)? It would seem to be necessary? Or perhaps, starting with a double gradient in the thalamus and cortex and a prepattern in the barelettes, would the correct patterns emerge simultaneously?

      2) There seems to be a strong prediction in this concerning the development of the patterns over time. Panel C indicates that early on there are large distortioins in the shape of the barrels particularly in D,E rows. is this known to occur?

      3) It seems to me that without the chi, then possible connections plus axons are conserved which is reasonable. But with the necessary competition, there seems to be a flaw in the model if they have to renormalize at each point. If axons make connections should they not be lost from the pool forever (this is the -dci/dt the model). For example, since the gradient has noflux in the original K&E model, there is conservation of the total number of connections and axons of a given type. (int ai+ci dx = constant). This principle seems to make sense to me. However, the competition term chi_i seems top disrupt this. Is there a way to introduce the axonal competition in a way the prevents the unrealistic (or biologically implausible, at least) renormalization at each step? I'd be more comfortable with the model if there were a more physiological way to renormalize. For example, I dont know if the authos considered something like an additional flux of the form: \chi ai \nabla \frac{1}{N-1} \sum{j\ne i} a_j

      This makes the axons of type i move away from type j while at the same time enforcing conservation without recourse to some sort of postnormalization.

    3. Reviewer #1:

      This compact paper proposes a a self-organization model for formation of whisker barrels. The key idea is that reaction-diffusion dynamics can lead to the observed topology, in the absence of pre-defined centers for the barrels.

      The model is well presented and the motivation of mathematical choices is mostly clear. It may be worth expanding on the motivation for competition for axonal branching (equations 3 and 4).

      It is a little unclear how the misexpression experiment (Shimogori and Grove 2005) in Panel E was done. The simulation approach and outcome for this section is described very tersely.

      The authors also mention another easily modeled experiment, in which capybara brains lack barrels because they are big. It should be a simple matter to do this run.

      Overall I feel this study presents an attractive and compact model for the formation of whisker barrels, which has good biological motivation, and does a good job of reducing assumptions and molecular guidance cues.

    4. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on April 10, 2020, follows.


      This compact paper proposes a a self-organization model for formation of whisker barrels. The key idea is that reaction-diffusion dynamics can lead to the observed topology, in the absence of pre-defined centers for the barrels.

      Essential Revisions

      1) How do the authors obtain 41 pairs of gamma values (line 102)? Are these parameters or were they inferred from experiments? This must be better motivated.

      2) The competition term chi_i requires renormalization, which seems biologically implausible. The authors may wish to try a form such as \chi ai \nabla \frac{1}{N-1} \sum{j\ne i} a_j which does not need renormalization. Several other points about this competition term are unclear as mentioned in the reviewer comments.

      3) There should be more exploration of the model: some parameter exploration and sensitivity analysis, and some more predictions.

    1. Reviewer #3:

      General assessment

      The authors present a cool new idea: using a large parabolic reflector in combination with a macroscopic lens array and rapidly modulated LED array to enable fast image multiplexing between spatially separated samples. I believe that there may be interesting applications that would benefit from this capability, although the authors have not clearly demonstrated one. The paper is short, and light on discussion, details, and data.

      Major comments

      1) The manuscript does not discuss several standard, key topics for any new microscope paper: "objective" numerical aperture, image resolution, optical aberration (other than distortion, which is discussed), and camera sensor size.

      2) Why was an array of low-performance singlet lenses used? With that selection, the image quality cannot be good. Can the system not be paired with an array of objectives or higher performance multielement lenses?

      3) Fluorescence imaging is not discussed or demonstrated but would obviously increase the impact of the microscope. At least some discussion would be helpful.

      4) Actual HTS applications are almost always implemented in microtiter plates (e.g. a 96-well plate) to reduce reagent costs and enable automated pipetting, etc. I do not believe anyone would implement HTS in thousands of petri dishes. The paper would be strengthened substantially by a demonstration of simultaneous recording from all (or a large subset) of the wells in a 96-well plate. It's not clear whether this is possible due to the blind spot in the center of the parabolic mirror's field of view that is blocked by the camera.

      5) One of the primary motivations for this approach is given in the first paragraph as: "wide-field imaging systems [which capture multiple samples in one frame] have poor light collection efficiency and resolution compared to systems that image a single sample at a given time point." With a f = 100 mm singlet lens, the light collection efficiency of the demonstrated microscope is also low (estimated NA = 0.12) and the resolution is unimpressive with the high-aberration lens and 1x magnification. They demonstrated only trans-illumination applications (e.g. phase contrast), where light collection efficiency is not important. I believe a fancy photography lens mounted directly on a many-megapixel camera set to image all or part of a microtiter plate could likely outperform their system in throughput and simplicity, at least for the demonstrated applications of cardiomyocytes and C. elegans.

    2. Reviewer #2:

      Astronomers have spent centuries learning how to image the night sky with limited sensor hardware. Ashraf et al present an ingenious adaptation of a technology developed for telescopes-parabolic reflectors-for imaging biological samples. In principle, the approach seems like it could be incredibly useful across a wide range of applications where multiple samples must be imaged in tandem. By placing multiple samples under a single parabolic reflector, multiplexing of samples and imaging hardware can be accomplished without sample-handling robots or moving cameras. The authors highlight two applications: cardiac cells in culture and free-moving nematodes.

      The authors explain the theory behind their technique in a clear and convincing way. However, the biggest challenge in most imaging projects is making the theory work in practice. In its current form, the manuscript falls far short of demonstrating the practical usefulness of parabolic mirrors for imaging biological samples. The authors include only a small amount of image data-for the nematode work, this consists of eight images collected from two plate regions. Data of this scope cannot provide readers or reviewers with sufficient evidence with which to evaluate the quality of the technique.

      1) The images shown-are they typical or are they the best possible images that can be collected from the device? The authors do not provide any quantitative evaluation of the quality of their images, in absolute terms or relative to existing methods, with which to understand the practical performance of parabolic mirrors. The authors should estimate the spatial resolution and dynamic range that can be obtained in practice with the devices, and evaluate how such image quality metrics vary across the entire field of view. Does performance degrade towards the edge of the mirror? Does performance degrade over time, as devices become de-calibrated with use?

      2) The manuscript is additionally weakened by the absence of a non-trivial measurement made with the device. Pilot experiments are included, demonstrating that images can be collected. However, no evidence is provided to show that these images can be used to compare samples and draw biological conclusions from them. A more convincing proof-of-principle would involve the measurement of some non-trivial biological difference between samples measured with the device, either confirming previous work or discovering something new.

      3) The authors highlight the comparative simplicity of their method: it eliminates the need for motorized samples or cameras. However, this simplicity must come at some: for example a substantially increased use of space or perhaps an increase in delicate calibration required, or equipment price. If a 0.25 meter mirror is required to measure four C. elegans plates, how large a mirror would be required to measure 16 plates-the number that can typically be measured using a flatbed scanner? The authors could also expand greatly on other practical issues: for example, is a dedicated imaging table required to align mirrors and samples? Readers would benefit from a clearer evaluation of the practical trade-offs in deploying parabolic mirrors in a laboratory setting relative to other imaging approaches.

    3. Reviewer #1:

      Ashraf and colleagues describe an approach to perform high throughput screening imaging without moving parts. The setup is original and offers to experimentalists the flexibility to record quasi-simultaneously stacks of images of multiple samples at the full field of resolution of the camera. The optical aberration inherent to the use of a parabolic mirror are mostly overcome by collimating light from the objective lens. The images require a post-processing in two steps for taking into account the image stretching on the detector and the variation in magnification due to the variation of the distance between the mirror and the image. Two applications illustrate the potential of the solid-state HTS.

      To my opinion, the following points need to be clarified:

      1) How homogeneous is the field of illumination with a single LED? Especially for a large field of illumination, a non-homogeneous illumination would compromise the quantifications.

      2) The accuracy of this ssHTS is related to the robustness at keeping the distance F2 constant between samples. In other words, how sensitive is the image acquisition to the potential variation in the F2 distance between samples as well as within a single large field of view?

      3) The magnification Mc must be explained.

      4) Is the post-processing compensation applied only in the y-direction?

      Assuming that such publication aims to disseminate the use of an ssHTS setup to a wide scientific community, I find the description of the setup as well as the applied image post-processing rather succinct, even with the 3D printing and source codes information.

    4. This manuscript is in revision at eLife

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


      The reviewers all recognised the originality of your solution to perform high throughput imaging without moving parts. They do have some serious reservations, primarily regarding the evaluation of the quality and utility of the technique and in addition to the other points raised, and consider it essential that you address the following:

      1) The standard topics for any new microscope paper: "objective" numerical aperture, image resolution, optical aberration, and camera sensor size, together with the specific aspects related to this technique, including dependence on homogeneous illumination, and sensitivity to maintenance of F2 distance.

      2) A substantial expansion of the scope of the data presented, to provide readers with sufficient evidence with which to evaluate the quality of the technique, including proof of principal with a 96-well plate assay.

      3) A direct quantitative comparison with existing HTS imaging solutions.

    1. Reviewer 2

      This work investigates the role of autophagy in the migration of neuroblasts in the forebrain of adult mice. The authors provide evidence that activity of the autophagic pathway is related to the ratio of the migratory / stationary phase. They also provide evidence that activity of the autophagolysosomal pathway is related to the ATP/ADP levels and that autophagy targets the focal adhesion molecule paxilin. Autophagy is emerging as a central pathway in the regulation of neuronal development and the manuscript adds interesting and new evidence to this concept. Overall I consider this an important and well designed study.

      Major Comments

      1) In order to support the central notion that ATP/ADP levels control the autophagolysosomal turnover of paxilin, which in turn regulates migration the authors should investigate the localization and expression of paxilin in their experiments using the analysis that was applied in figure 3.

      2) The data presented in Figure 1-4 is sound and directly related to the central point of the paper, i.e., that ATP/ADP levels control the autophagolysosomal turnover of paxilin. The data presented in Figure 5 is circumstantial and except for showing that different pathways that have been linked to migration processes (not specifically migration of neuroblasts in the adult RMS) modulate expression of autophagy-related proteins. The data does not contribute to the key message of the paper and I would suggest to remove the data entirely.

      3) I am convinced that the paper carries an important and novel message but the order of how the results are presented seems not ideal to me. I believe that the order: analysis of autophagolysosomal activity in relation to migratory phases, analysis of metabolism with a focus on ATP/AMP ratios, and finally analysis of Paxilin as a potential target of Autophagy would be more stringent and convincing.

      4) Data presentation: in many instances the authors provide sample images of only one experimental condition e.g. Fig 2 M-O, R, W. While this may provide an impression of how the data was collected I think that it would be more convincing if the authors provided example images of all experimental conditions to illustrate differences. In addition the figure legend for Figure 2 M-O does not clarify which/ whether the sample images are from WT or mutant mice.

      5) The authors write that "...An Atg5 deficiency led to the accumulation of neuroblasts in the RMS close to the SVZ (582.7 {plus minus} 72.5 cell/mm2 in WT mice vs. 846.7 {plus minus} 72.7 cell/mm2 in cKO mice; p<0.05, n = 4 animals per group), with an accompanying decrease in the density of neuroblasts in the rostral RMS (RMS of the OB) and the OB. The graphs in figure 2P do not support the statement. that the density of neuroblasts in the rostral RMS and the OB are lower in ATG5 KO conditions. Please correct the statement and provide an explanation of how the numbers of neuroblasts can be stable if a higher number is observed in the more caudal portions of the RMS.

      6) The authors use CRISPR/Cas9 to knockout Atg12, if possible I would like to ask the authors to confirm the loss of Atg12 protein.

      7) The authors use the RFP GFP LC3 reporter which allows estimation of autophagic flux in vivo. In their analyses of autophagolysosomal activity (Figure 1I) they only estimate the RFP punctae. determining changes in autophagolysosomal activity would be stronger and more convincing if the authors performed the GFP+RFP/RFP punctae ratio.

    2. Reviewer 1

      In the last few years the role of ATP metabolism at the synapse and in neuron development has become a topic of growing interest for the field of neuroscience. Autophagy is a prominent cellular process that has important roles in axon degeneration, cell death and nervous system disease. Importantly, the role of autophagy in neuron development has been less heavily studied than in disease contexts.

      The authors provide extensive quantitative datasets clearly indicating that genetic or pharmacological inhibition of autophagy results in reduced migration from the SVZ to the olfactory bulb. Indeed, a strength of the study is evidence showing that genetic effects on multiple autophagy components and AMPK (which activates autophagy) affect neuron migration. Another high point is extensive, quantitative time-lapse analysis of neuron migration in acute slice. This ex vivo approach is informative and makes for a compelling case regarding the role of autophagy in neuron migration from the SVZ to the olfactory bulb. While some in vivo data is provided more evidence on this front would further strengthen the study.

      While this is an interesting, high-quality study, the authors do not introduce an important body of prior literature on autophagy in neuron migration (Peng et al, 2012 JBC; Petri et al, 2017 EMBO; Gstrein et al, Nat Neuro 2017; Li et al, 2019 Cereb Cortex). As a result, it is unclear to the reviewer whether this is a significant step forward for the field, or a further valuable study solidifying the role of autophagy in neuron migration. At this point, the reviewer leans towards the latter view point. Below, are further details on this issue and several suggestions the reviewer hopes will improve what is a very nice piece of science.

      Major Comments

      1) The Gstrein paper is a very important piece of prior work, but is buried in the Discussion. This needs to be brought up in the introduction and noted appropriately. The manuscript also does not cite two other important papers showing that changes in autophagy can affect neuron migration in the olfactory bulb in adults in vivo (Petri et al, 2017 EMBO), and that molecular perturbations that affect autophagy impact neuronal migration in the cerebral cortex in vivo (Peng et al, 2012 JBC). Further recent work has shown that altered autophagy accompanies impaired neuronal migration in vivo in the cerebral cortex (Li et al, 2019 Cereb Cortex) and in vitro in a neuronal cell line (Li et al, 2019 Front Endocrinol). Placing the existing study's contribution more carefully and thoroughly within the context of this prior body of work on autophagy in neuron migration at the onset of the paper is critical.

      The attempted selling point of conflicting roles for autophagy in cell migration based on other cell-based studies and non-neuronal tissues is not particularly helpful and distracts from a major issue: There are already multiple studies indicating that autophagy affects neuron migration in vivo, and it is unclear how this work represents a major advance.

      2) The introduction does not comment on the role of ATP in neuron development and function; this has been an area of intense study in recent years. This type of background would be helpful for framing the context of the findings here.

      3) In vivo data indicating that autophagy influences neuron migration from SVZ to olfactory bulb is very important. Perhaps the reviewer is mistaken, but it seems like only Figure 2P shows quantitation of vivo data. This indicates loss of Atg5 results in increased cell numbers in the RMS. This an extremely important point. Hence, more evidence that other pharmacological or genetic manipulations of autophagy change cell density/migration in vivo would be valuable.

      The authors state: "with an accompanying decrease in the density of neuroblasts in the rostral RMS (RMS of the OB) and the OB". This is not supported by necessary statistical analysis, and looks likely to be insignificant. Statistics should be run here and commentary adjusted accordingly.

      4) In Figure 4B and C, quantitation of the ATP biosensor Perceval is shown. The authors claim a 20 fold change during migration. However, the Perceval ratio goes from 1.01 to 0.99 during one migration step and then 1.01 to 0.97 in the second step (Fig 4B). How is this a 20x change? To the contrary, this seems like quite a modest decrease in ATP ratio.

      How does this ratio change in a positive control where ATP production is reduced by impairing glycolysis or mitochondrial function?

      How does the role of ATP production by glycolysis versus mitochondrial stores influence migration?

      Presentation of data as a % change in Figure 4C is not ideal and gives the impression of artificially exaggerated effect sizes. Statistics are also notably absent from Figure 4C which makes a critical, quantitative point about migration and ATP consumption.

      5) The study emphasizes the point that AMPK senses changes in ATP levels and also activates autophagy. Both of these concepts are well known. Thus, pharmacologically blocking a known activator of autophagy like AMPK and showing effects on cell migration further supports the idea that autophagy is required for cell migration. This does not tie together that changes in ATP levels are affecting autophagy and, therefore, migration. Is there a way to directly manipulate ATP levels and then looks for impacts on both autophagy and migration? Is there a way to alter AMPK activation by ATP changes?

      6) In Figure 5D, treatments that increase and reduce the speed of migration show the same effects on autophagy as assessed by LC3II levels. How do the authors explain this? Wouldn't one expect opposing outcomes? Is this correct?

      7) Links between paxillin and cell migration are correlative, and not particularly convincing. Does reducing or increasing paxillin function affect migration? Does triggered specific heightened degradation/turnover of paxillin affect migration?

    3. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on March 30, 2020, follows.


      In this work you uncover the complex interplay between autophagy and energy consumption to regulate the pace and periodicity of the migratory and stationary phases in a prototypic model of migration in adult brain (the SVZ-OB). Both reviewers considered your work important as you provided evidence that 1) activity of the autophagic pathway is related to the ratio of the migratory / stationary phase, 2) activity of the autophagolysosomal pathway is related to the ATP/ADP levels, and 3) autophagy targets paxillin, a focal adhesion protein that is the direct target of LC3II.

      Essential Revisions

      The original reviews are attached below. Most of the major points can be addressed with minimal new experiments, but may require reanalysis of data or samples you already have. Based on these reviews, it is essential to address the following key points:

      1. Deepen the analysis of paxillin localization and expression
      2. Confirm the impact of Atg5 on the density of neuroblasts in the RMS (increased?) and the OB (unchanged?)
      3. Confirm the loss of Atg12 protein,
      4. Quantify autophagolysosomal activity (Figure 1I) by analyzing GFP+RFP/RFP punctae ratio

      In addition, while the science is strong, claims regarding the advance over previous studies should be toned down, since there is existing literature showing roles of autophagy in neuronal migration. The paper needs rewriting to accurately place your work in the context of prior research in the field. Specific recommendations include : i) rewrite the Introduction and Discussion to cite the literature appropriately: (ii), the second referee suggests that your Results could be presented in a different way in order to make better use of your data.

    1. Reviewer #2

      In their manuscript titled "SOX21 modulates SOX2-initiated differentiation of epithelial cells in the extrapulmonary airways" from Eenjes et al. the authors describe a new role for Sox21 in the developing and adult airway epithelium. Building on prior work they observe a unique distribution of Sox21 expression in the developing airways and through careful and elegant immunostaining and over-expression studies they suggest that Sox21 is downstream of a key airway development transcription factor Sox2. They suggest opposing roles for these genes based on analysis of Sox2 and Sox21 heterozygous knock-out mice whereby Sox21 prevents and Sox2 promotes differentiation of immature airway progenitors into basal cells. This raises interesting questions regarding the role of Sox21 in the biology of airway progenitors and the balance of cell types in the airways. In adult mice no obvious differences are detected in Sox21+/- mice in terms of regenerative capacity. In in vitro assays of adult mouse basal cell differentiation (ALI culture) failed to identify obvious differences in basal cell number of differentiation into specific lineages in Sox21+/- cells. The authors report an overall similar pattern of SOX21 expression in a human fetal lung organoid platform. Finally, in human ALI cultures the authors identify SOX21 expression most abundant in paranasal cells suggesting a similar possible role for this genes in differentiating basal cells in humans. Overall, the molecular mechanisms that control airway stem cell maintenance and differentiation are of great interest to the field.

      Major concerns:

      The development data is clear based on the studies presented. The immunostaining and figures are elegant. It does not appear the Sox21 is necessary for airway development. A key question raised by this work is how important and what precisely is the role of Sox21? For example, overexpression of Sox21 in the developing and adult airways might have been more instructive in answering these key questions rather than under the control of the SPC-promoter.

      The adult mouse data and human data seem to overall suggest that SOX2 and SOX21 are upregulated in differentiating cells in vitro and are expressed at lower levels in basal cells but real mechanism or phenotype related to SOX21 function is observed in the SOX21 het mouse cells.

      The attempt to assess human fetal airways is admirable. However, sections of fetal lungs would be more relevant. Can the authors address how similar fetal lung cultures are to in vivo airways and at what developmental time point ?

      Overall the relevance of SOX21 expression in the adult airways is unclear.

    2. Reviewer #1

      This is an interesting but also a bit confusing manuscript by Evelien Eenjes and colleagues.

      I was wondering whether the seemingly conflicting effect of Sox21 on basal cell differentiation could be due to an increase or decrease in Sox9 positive basal cells. These atypical basal cells have been described in a number of manuscripts.

      For example - https://www.ncbi.nlm.nih.gov/pubmed/26869074 - it appears from the figures that Sox21 may increase Sox9 expression. Can the authors look at the presence of Sox9 positive basal cells in the trachea of the different mutants?

      It would be important to quantify the % of club cells in the corn oil and naphthalene treated tracheas of the different mutants as these are the main cells that should be replaced upon naphthalene injury. I am not sure that people normally look at the number of ciliated cells reappearing after naphthalene injury as ciliated cells are not thought to be killed by naphthalene.

      The authors should also look at Sox9 positive basal cells in the tracheas of the corn oil and naphthalene treated ctrl and mutant mice.

      Are the intermediate para-basal cells in the human airway differentiation experiment club cells? Why do the authors think these cells are on their way to become ciliated cells? Doesn't Sox21 inhibit ciliated cell differentiation?

    3. This manuscript is in revision at eLife

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


      This is a comprehensive analysis of Sox21 in lung development, homeostasis, and injury, using wide array of methods including mouse human cell-based ALI cultures and organoids. The authors describe a new role for Sox21 downstream of the key airway development transcription factor Sox2. They suggest opposing roles for these genes based on analysis of Sox2 and Sox21 heterozygous knock-out mice whereby Sox21 prevents and Sox2 promotes differentiation of immature airway progenitors into basal cells. This raises interesting questions regarding the role of Sox21 in the biology of airway progenitors and the balance of cell types in the airways. In adult mice no obvious differences are detected in Sox21+/- mice in terms of regenerative capacity. In in vitro assays of adult mouse basal cell differentiation (ALI culture) failed to identify obvious differences in basal cell number of differentiation into specific lineages in Sox21+/- cells. In human ALI cultures the authors identify a similar possible role for Sox21 in differentiating basal cells in humans. Overall, the molecular mechanisms that control airway stem cell maintenance and differentiation are of great interest to the field. However, in its current form the studies remain primarily descriptive and several data inconsistencies remain, which makes it difficult to draw impactful conclusions at the current stage. The potential suitability for eLife would significantly increase with additional mechanistic experiments and data.

      Essential Revisions

      In particular, the following major points require additional experimental data (details are outlined below):

      1) The functional Sox21 role in the adult lung is not clear.

      Mouse studies would benefit from inclusion of overexpression of Sox21 in the airways

      In human airways and the models used (organoids and ALI cultures) gain and loss of function studies are not performed and would also behelpful to further determine the phenotype of the intermediate para-basal cells in the human airway.

      2) Evidence for genetic interaction between Sox21 and Sox2 in the adult lung needs to be expanded.

      3) Presence of Sox9 positive basal cells as additional atypical basal cells needs to be further investigated.

      4) Quantification the % of club cells in the corn oil and naphthalene treated tracheas of the different mutants as these are the main cells that should be replaced upon naphthalene injury.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on August 24 2020, follows.


      The current and widely accepted model how nuclei are positioned in the cell proposes that their anchorage is mediated through nuclear membrane spanning SUN and KASH domain containing proteins which connect the cytoskeleton to the nuclear interior. This study presents evidence that this model needs reconsidering. The authors follow up on their previous observation that nuclear positioning differs between mutants in SUN (UNC-84) and KASH proteins (ANC-1), where anc-1 mutants display a more severe phenotype. The study nicely combines structure-function analysis of ANC-1 with the readout of nuclei positioned in the syncytial cell hyp7 in fixed samples and by live imaging, and the mutant analysis correlates well with the fitness of the whole organism. The authors also show that the expected regions (the KASH domain or the actin binding domain) play rather minor roles in nuclear anchorage. Instead, anchorage is mapped to a portion of the transmembrane domain and to spectrin-like repeats in the cytoplasmic localised region of the protein. Mutating those protein domains not only leads to irregularly positioned nuclei but also to disorganisation and fragmentation of the ER, which also appears unanchored as evidenced by in vivo imaging. Consistently, the authors find ANC-1 prominently associated with the ER and that this association is independent of the KASH domain.

      This paper will be very interesting to a wide readership as it challenges current models of nuclear positioning and shows that mis-positioning and loss of connectivity can have severe consequences to the development of the organism. However, the reviewers felt that some of the conclusions required additional data to support the statements made, in particular to strengthen the proposed the ER link, as well as some other points that require clarification as detailed below.

      Essential Revisions

      1) The data shown in Figure 6 suggesting ANC-1 targets to the ER was not convincing and was also very hard to contextualise as no other markers for other organelles or the nucleus were present, and no merged images provided. Given that the authors also repeatedly draw conclusions relating to mitochondria, including a mitotracker in the far-red channel would be important. The ANC1 signal appeared rather diffusely localised in all cases (WT and TK/KASH mutants; noting that the KDEL signal is very low in the TK mutant image compared to the others) and it could be argued any potential overlap might be coincidental rather than specific. No other evidence for ER targeting was provided but would be required to support the current conclusions. The authors should also at minimum calculate the co-localization index and provide examples of line scans to show a correlation between signal intensities. Also the sentence "The slight discrepancy between localization of mKate2::ANC-1b and GFP::KDEL could be explained by the distance between the ANC-1 N terminus and the ER membrane" will need to be modified. This is highly unlikely due to the resolution of the microscope used to acquire this image. The discrepancy might be due to differences in the focus plane of the two light channels. Please remove or edit this speculation.

      2) A further concern is the lack of any cytoskeletal network analysis in the paper; the authors (somewhat extrapolated) conclusions are focused on the concept that nuclei and the ER are detached from any sort of cytoplasmic structural network in anc-1 mutants, but this is not tested in the study. It would be very helpful to provide this evidence, but we recognise that analysing the cytoskeleton in detail may prove impractical given the current restrictions. However, if experimental data cannot be provided, it would be important to tone down such statements given the lack of formal evidence provided for this model.

      3) ANC1b-del6RPS and del5RPs appear to be expressed at much lower levels than other mutants (or WT protein) eg: Fig5; is this the case and if so, might the nuclear positioning defect just be due to this (ie: as the animals are more like anc-1 null)? It would be important to understand relative stability of these mutant proteins to interpret this data. Please provide more information on the relative intensity levels of each mutant and if they are similar, provide more representative example images.

      4) The authors put forward the claim that ANC-1 anchors other organelles besides the ER. There are a lot of markers available for different organelles, and it would be important for the authors to provide some staining in the most significant mutants (delta 6rps, delta tk), for mitochondria or other organelles. On page 11 the authors also write "Nuclear shape changes were observed during live imaging in anc-1 mutants consistent with a model where anc-1 mutant nuclei are susceptible to pressures from the cytoplasm, perhaps crashing into lipid droplets that corresponded with dents in nuclei.". It is not clear why the authors suggest "crashing into lipid droplets" and not any other organelles in the cell (mitochondria, endosomes, etc). Is there any evidence for this statement that can be provided?

      5) p. 14: ...was not enriched at the nuclear envelope...". it would very important to include pictures of the ANC-1 staining together with a marker for the nuclear envelope in Figure 5 to support this statement.

      6) Page 6, Figure 2A,B. it is not clear in the text that two of the four nonsense mutations that were analysed only disrupt isoform a and c (w427 and w621). If these mutations only affect isoform a and c, and not the shorter isoform b, then the authors could explain this better, so that this result goes together with the RNAi data.

      7) Figure 1c and Figure 3C - the dataset of WT and anc-1(e1873) seems to be the same in both these figures. Although duplication of the same data in multiple figures should not typically occur in publications, the duplication should be indicated clearly in the figure legend for transparency. Ideally, the duplicated data should also be shown in a different color/format in the figure so that they are immediately obvious. Other duplications of data in the manuscript should also be indicated. Why was unc-84(n369) data repeated three times on the graph in Fig 3C but with different values?

      8) The percentage of touching nuclei in unc84(n369), KASH mutants (fig 1C), and anc-1(dF1)(fig 3c), are around 20%. However, the authors classify the KASH mutants as "mild nuclear anchorage", whereas anc-1(dF1) on fig 3c was classified as "severe nuclear anchorage". The authors also used the term "intermediate nuclear anchorage" for other phenotypes. The authors should use the same classification (clearly described) throughout the manuscript.

      9) Figure 4A - the authors described the image of GFP:Kdel of hyp7 syncytia as a "branched network". It is very difficult to observe any branches and a network in these images. We recognise the authors want to use the same terminology that is used to characterize ER in other cells, but it is difficult to understand what the authors mean by a branch. Diffuse staining with dark round objects in it is visible, but branches are not clear. The authors should provide a better example, more similar to unc-84(n369) mutant, where branches and a network are more distinct and annotate these properly to support this statement.

      10) Figure 4C and D; movie 1 and 2- In these figures and the authors compare the dynamics of ER in WT and anc-1 mutant. The authors also provide representative movies. The WT animal appears to be crawling significantly less than the anc-1 mutant, making it difficult to directly compare the anchorage of ER in WT during crawling in the representative movies. Moreover, - Supp Movie 1 appears to be far shorter (fewer frames) than Supp movie 2 - ideally, equivalent time scales should be provided for WT animals to be comparable with the mutant.

      11) Figure 6A - in this scheme and through the manuscript, the authors refer to the c-term region of ANC-1, after the TM domain, as the KASH domain. However, by definition, the KASH domain includes part of the neck region, the TM domain and the c-term region after the TM domain (see e.g. Fig4 of Wihelmsen et al. JCS 2006, or PFAM definition of KASH - 10541). Therefore, the neck region of the KASH domain plays a role in nuclear positioning. Furthermore, labelling of Figure 6A should be changed accordingly to standard definition.

    1. This manuscript is in revision at eLife

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


      The manuscript by Silva-Garcia and colleagues addresses an interesting aspect of BRCA2 biology: the regulation of its steady state levels in response to DNA damage. It has become clear that BRCA2 level are subjected to change in response to a number of different environmental challenges, including the induction of various types of DNA lesions. This manuscript identifies the serine protease DPP9 as cleaving off the first two N-terminal amino acids of BCRA2 to target BRCA2 towards the N-degron pathway. The DPP9-mediated turnover of BRCA2 regulates the BRCA2-RAD51 stoichiometry and appears to promote RAD51 focus formation.

      Overall Evaluation

      The biochemical data are generally solid and support the conclusions, but the interaction has not been tested with the endogenous proteins and the affinity is low (~17 uM). The cell-based assays reveal a potentially significant problem in the BRCA2 construct. Overall, the physiological relevance is far from certain. To be conclusive, the PLA would need single primary antibody-only controls to ensure specificity. More importantly, although it seems possible that DPP9 has an effect on RAD51 foci, it is not clear from the results whether this is directly connected to BRCA2 or is an indirect effect. In particular, the results with the truncated form and full-length BRCA2 are done in overexpression; however, the levels of the two proteins are different and it is known that BRCA2 overexpression is toxic for the cells. Stable expression or equal transient expression would have been more convincing to draw these conclusions or at least rescuing the phenotype of full-length with the truncated form and/or with WT DPP9 would have been more adequate. The overall model needs to be significantly toned down in light of available data from cBioportal and DepMap that are inconsistent with the overall model that DPP9 cleavage is essential for BRCA2 function.

      Essential Revisions

      1) As the authors recognize, that there is a conceptual problem with the model that suggests that BRCA2 cleavage and degradation is required for RAD51 focus formation, when it is BRCA2 function that is required for RAD51 focus formation, as shown by genetic studies. How can the degradation of an essential factor for RAD51 focus formation be required for RAD51 focus formation? If, as the authors suggest, the BRCA2 : RAD51 ratio is critical, RAD51 overexpression should be detrimental. The authors may want to consult the literature on RAD51 overexpression and its effects and discuss this.

      2) Figure 1: Based on the data presented in Figure 1 panel A, it is concluded that DPP9-BRCA2 PLA signal is detected in the nucleus. However, that is hard to assess, as the visualized dots localizing in the DAPI stained areas could easily be on top of the nucleus. In addition, is there any evidence that DPP is actually a nuclear protein?

      The PLA experiments seem to lack the single antibody negative controls that require to account for nonspecific signal.

      Fig. 1D: This figure reports the results from the SPR as (partial) binding isotherms based on equilibrium analysis.

      Include the SPR sensorgrams (for example in supplemental figure 1) to show that equilibrium analysis can be performed on this dataset, thus if: • Observed response is due to specific binding of peptide to enzyme (methods section does not explain if reference surface subtraction has been performed and how much specific binding occurs). • Binding actually reaches equilibrium after 4.5 minutes association phase (rather than continuing to rise). • Dissociation occurs during dissociation phase of 7 minutes, at least for majority of signal, to make sure reaction is reversible (expected for micromolar range).

      Would it be possible to add inhibitor to the association phase to verify specificity of observed interaction?

      Saturation is far from complete. The uncertainty of the fits themselves (as reported in Graphpad analysis) are probably much larger than the reported variations between triplicate KD determinations, especially for the shorter peptide where not even 30% of the enzyme seems to become occupied at the highest peptide concentration. The uncertainty from extrapolation of maximum observed 50% and 25% binding for the different peptides towards 100% response plateau will have major influence on apparent KD. The uncertainty of the fits has to be considered in deciding whether the shorter peptide binds significantly weaker than the intact peptide.

      The enzyme on the chip surface will cleave the peptide and will retain the dipeptide but release the rest of the peptide (according to the observed electron density in the crystals). The intact peptide (40 amino acids) will results in an approximately 20-fold higher response in the SPR assay than the dipeptide (2 amino acids). Depending on the kinetics of peptide binding, the chemical conversion and product release, the observed signal in the sensorgrams will be mostly substrate, mostly product or a mixture of these, the composition of which changes during the experiment. Even if a steady-state binding level is observed in the raw data, the obtained parameters are probably not reflecting equilibrium binding constants. An active site mutant may be helpful here (and might return a much stronger affinity for the intact peptide). If that is not possible, a more qualitative reporting of the data could be considered rather than trying to obtain affinities.

      Fig. 1 S2: DPP9-BRCA2 PLA signal seems to increase with MMC in siBRCA2 treated cells. This potentially indicates that the PLA signal does not report on the DPP(-BRCA2 interaction.

      Why does removing FLNA reduce the BRCA2-DPP9 interaction? Is the BRCA2 pool bound to FLNA targeted by DPP9?

      Fig. 1B, G. It is unclear what is shown on the Y-axis, total fluorescence, number of foci?

      Fig. 1C, D: The affinity found for the interaction between BRCA2 and DPP9 is ~17 uM which seems too weak for a physiologically relevant interaction. Nonetheless the interaction appears to be real as they find it also with purified fragments. An immunoprecipitation with endogenous proteins with and without MMC treatment would be necessary to complement these findings in cells as the PLA is not sufficient.

      Fig. 1G: Please provide the statistical analysis of the (-) and (+) 1G244 samples under MMC treatment. This is the key control and not the comparison to -MMC.

      3) Figure 2: Fig. 2: If DPP8 and DPP9 crystals with the BCRA2 peptide are so similar, why is there a phenotype of DPP9 mutants? Why is DPP8 then not providing redundancy?

      Fig. 2: While the disorder in the DPP9 crystals is clear from the average B-factors (Table 1), what are the local B-factors for the active sites in both structures? Is the quality of the electron density in the active site of DPP8 actually good enough (~3 Å) to establish that the identity of the two amino acids are methionine and proline? Can it be ruled out that coincidentally one might be observing 2 residues from only partially ordered longer peptide? What other information from previously determine enzyme-inhibitor complexes (Ross et al 2018) and active site geometry is maybe used in concluding that the density corresponds to the N-terminal dipeptide?

      4) Figure 3: Fig. 3 A-D: The DNA damage sensitivity assays lack a control with siBRCA2 cells to show the sensitivity compared to knock-down of DPP9, without that it is difficult to interpret the results. This is especially relevant if the point is to show that DPP9 is required for the function of BRCA2 in DNA repair. The observed sensitivities to DNA damaging agents are very mild (plot axes are 1 log). Given that for example sensitivity of BRCA2 mutants to PARP inhibition is extreme, can the effect of DPP9 on survival be indirect?

      Fig. 3 E. The interpretation and description of these results do not appropriately reflect the data. HeLa DPP9 KD cells start with a higher constitutive level of gammaH2AX but the overall kinetics of the increase and decrease appears very similar. The statistical analysis, hence, is not appropriate to test a repair defect. How do normalized curves look like with 0 hr set to 100% and what is the statistical analysis of normalized curves?

      Fig. 3F. Same problem as in Figure 3E, although the increase in gammaH2AX signal is more dramatic. However, in the present illustration, it remains unclear, whether there is a defect in repair as measured by decrease of the gamma H2AX signal.

      5) Figure 4: Fig. 4A: Please provide statistical analysis of siDPP9 +/- MMC and siNT versus siDPP9 + MMC. The analysis provided -MMC siNT and +MMC siDPP9 is not helpful.

      Fig. 4 C and Fig. 4S1: When comparing the signal labeled BRCA2 in, for example Figure 4 panel C, with that in Figure 4 - figure supplement 1, it is difficult to understand that the signal represents the same protein, as in one blot the signal is a collection of bands, while in the other it appears to be a defined band.

      Fig. 4C: Is vinculin a proper control for quantitation of the levels of BRCA2, given that its signal appears out of linear range?

      Fig. 4I, J, line 373: The levels of BRCA2 1-1000 are different compared to BRCA2 3-1000. As this is a transient transfection the difference in the levels might be due to the quality of DNA of one plasmid versus the other. It is not clear that it can be concluded that BRCA2deltaMP is less stable than the unmodified N terminal BRCA variant. This is because the expression levels of the two variants is so different and both seem to decrease (relatively to their starting signal to the same extent). See overall evaluation.

      Fig. 4S2: What is the rational for using a different control protein to measure levels of RAD51 and BRCA2?

      Fig. 4S2: The scheme in G cannot relate to E and F, as RAD51 is analyzed there. Does it maybe relate to Figure 4 I and J. If so this should be indicated in the figure legend to Figure 4I/J and corrected. I suggest moving Figure 4S2G to Figure 4 as part K. What is the evidence that the ubiquitin is cleaved and how efficient is cleavage?

      6) Figure 5: It was very surprising that the WT BRCA21-3148 plasmid was not functional at all with the level of RAD51 foci being equal to the no plasmid negative control. Is it because of a construct problem? One would expect the WT construct can still rescue RAD51 focus formation but with a lower level than the mutant BRCA23-3148, as in Fig. 5C there are some RAD51 foci in siDPP9 cells under 300 nM MMC treatment as well as in Fig. 5-figure supplement 1F. If WT BRCA21-3148 is not functional at all without DPP9 catalysis (as suggested by Fig. 5F and 5G), how do the authors explain that N-terminally tagged BRCA2 variants are still functional, for example GFP-BRCA2, 2xMBP-BRCA2, which could not be processed by DPP9 as the dipeptide Met-Pro is not at the desired positions? This is a potential red flag and questions the validity of the central conclusion. The complementation activity of the constructs must be tested in a BRCA2-deficient background with proficient DPP9. The experiment in Figure 5F lacks a positive control to evaluate the level of complementation by the 3-3418 BRCA2 construct. This should be easy by omitting BRCA2 siRNA and using a scrambled control and no siRNA.

      Fig. 5A. The difference in RAD51 bound to chromatin is not clear and there is no quantification.

      Fig. 5B, please provide statistical analysis of the comparison of siNT versus siDPP9 + MMC. Also, the description in line 453 does not appropriately reflect the data, as there is a RAD51 focus signal in DPP9 depleted cells.

      Fig. 5B, D, F: it is important to show the real number of foci to determine whether the RAD51 foci per cells correspond to what is known from the literature and to find out the effect of the DPP9 KD alone to the number of RAD51 foci. For Fig. 5F this data is presented in Figure 5 suppl. 1 F.

      Fig. 5C: The detection of RAD51 foci is of poor quality. In addition, why under some conditions there is a strong cytoplasmic signal? The effect of different treatment on nuclear size is perplexing. The scale bar indicates 10 µm in every panel, yet nuclear size varies by ~2-4 fold.

      Fig.5. S1E. The levels of BRCA2 WT vs BRCA2delta MP are different, even if the amount of plasmid transfected is the same this does not mean the quality of the DNA is the same so the differences in the levels could be due to this. The quantitation is missing. Is this result reproducible?

      Fig 5 Suppl. 1F. This panel shows that the number of RAD51 foci is increased in cells complemented with a plasmid expressing 3-3418 compared to the full-length BRCA2. However, there are several possible issues in this experiment. A WB showing the control that the siBRCA2 worked in the same cells that overexpress BRCA2 and BRCA2deltaMP. The levels of BRCA2deltaMP is reduced compared to FL-BRCA2. The BRCA2 cDNA is big and its transfection is rather toxic for the cells so a reduced transfection efficiency could lead to higher survival and possibility of repair leading to increased RAD51 foci. What are the levels of gH2AX foci in both cells? If there is a difference in the amount of damage this could also lead to differences in RAD51 foci. The number of RAD51 foci in cells depleted of BRCA2 seems rather high compare to the ones reported in the literature. It remains unclear if the small difference in RAD51 foci between the two BRCA variants could be related to difference in their expression or heterogeneity in expression in the cell population.

      To assess the relationship of DPP9 and BRCA2 in DNA repair the phenotype of BRCA2 1-3418 should be rescued by WT DPP9.

      There is no convincing evidence to suggest that DPP9 regulates RAD51 filament formation by processing the BRCA2 N-terminus as stated in line 474. The authors examine RAD51 foci not filaments.

      7) In Figure 6 S1, the authors show a correlation between low DPP9 expression in breast cancer and patient survival. These data support the significance of DPP9 in breast cancer. However, a quick database analysis in cBioportal reveals that DPP9 and BRCA2 deficiency co-occur, which is not expected from the model presented here. Moreover, cBioportal also shows that DPP9 is often deleted in ovarian cancer but amplified in breast cancer. Again, these data are not consistent with the simple model presented here. Finally, analysis in DepMap shows that DPP9 in not essential whereas BRCA2 is an essential gene. These data do not support the model that DPP9 is essential for BRCA2 function. The authors should consider these available resources and refine their interpretation.

      8) There is a concern about the use of fragments. This appears acceptable for the structural analysis but in Figure 4I and J it is problematic for the stability experiments. In Fig. 5S1E, the full-length BRCA2 behaves consistently, but the analysis is very limited and not quantified. Is this finding reproducible? The reason this could be a bigger issue is the concern about the BRCA2 construct and the absence of complementation activity discussed above.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on August 24 2020, follows.


      In this paper, Brunet and coauthors show that various species of choanoflagellates have the capacity to switch from the typical flagellated stage to an amoeboid, non-flagellated stage. They show these amoeboid cells move using blebbing migration. The paper makes four major points:

      1) Several species of choanoflagellates make dynamic protrusions that appear similar to blebs in DIC when confined. This claim is well supported by nice quantitative analysis of blebbing using a diversity of choanoflagellate species.

      2) The blebs made by choanoflagellates, like those of animal cells and Dictyostelium, involve breakage and healing of the actomyosin cortex. This is the weakest part of the paper (see below further details).

      3) Choanoflagellate cells can use this blebbing motility to escape the confinement, a concept supported by movies of cells doing this. This is supported by movies of cells doing this.

      4) Amoeboid motility is homologous in choanoflagellates and animals. In particular, the authors postulate that epithelial and crawling cells in animals differentiated by exploiting the switch from the flagellated to amoeboid stages that existed in unicellular opisthokonts. Although this is an interesting hypothesis, we believe the data is not conclusive and both the implications and the conclusions need to be better explained in the general context of eukaryotic evolution.

      Below we define what we believe should be done to improve the manuscript.

      Essential Revisions

      1) The idea that amoeboid morphology and blebbing motility is older than animals is not particularly controversial: blebbing has been documented in various microbial lineages for some time, and blebbing motility uses a contractile actin cortex, which are also widely distributed. This, combined with a lack of engagement with alternative hypotheses weakens the conceptual significance of the paper. Fleshing out what the alternative hypotheses are, and/or providing context for how this work provides new insight into the evolution of blebbing would improve the paper. Furthermore, the introduction should include more background information to distinguish blebbing motility from actin pseudopod based motility. Also, the use of the term "actin-filled" to discuss bleb retraction is confusing; do the authors mean actin-encased? Also a clear definition of what a "retracted bleb" is should be provided. In general, some information in the results that could be better incorporated in the introduction as it explains the authors' motivation for the work.

      2) Similarly, the idea of homology between the amoeboid cells of choanoflagellates and animal amoeboid cells seems not well supported or at least no more than a potential homology of many eukaryotic amoeboid cells. This needs to be toned-down and/or discussed into the context of the potential ancestral eukaryotic feature. The same with the related idea that epithelial and crawling cells in animals differentiated by exploiting the switch from the flagellated to amoeboid stages that existed in unicellular opisthokonts.

      Finally, the authors say that the switch between flagellated and crawling cells in choanoflagellates is triggered by particular size-related stress. However, it is difficult to imagine that animals evolved under such a type of stress. It may be interesting to discuss whether the authors have tried to see if alternative sources of stress induce transition to amoeboid states or, alternatively, discuss particular hypotheses about which kinds of stress might trigger this response. When discussing this, it may be worth considering an alternative: that choanoflagellates might be a side phylogenetic group having evolved specific characteristics and virtually lost amoeboid stages except for extreme situations like the ones shown here. The ancestor of metazoans would then had simply retained an ancestral (eukaryotic) capability to transition from flagellated to amoeboid states during the opisthokont life cycle without this capability being in any way related to volumetric stress but rather to particular environmental clues.

      Overall, all these ideas should be discussed in the context of eukaryotic evolution and toning down the potential implications.

      3) The authors use the standard definition of blebbing: actomyosin cortex breakage and healing concomitant with production of round protrusions devoid of actin. The paper provides insufficient data to support the claim that choanoflagellate cells defined as "amoeboid" based on the lack of microvilli undergo this form of blebbing. Providing additional examples and/or quantitative analyses of the data would strengthen the paper. Specifically:

      a. Only a single cell with lifeact is shown (Fig. 2C, with what looks to be the same cell in Video 7). Additional examples would be welcome. However, this cell has high levels of septin overexpression: could this be interfering with the native phenotype? Fig. 3K looks very different from Fig. 2q. Is septin localizing to the membrane? The WT cells shown in P do not show cortical actin. It seems likely worthwhile repeating this experiment with lifeact but without septin overexpression. Additionally, linescans to quantitate the cortical actin levels before, during, and after cortical breakage would provide quantitative support, particularly with a membrane stain, or at the very least, the septin localization.

      b. The phalloidin staining in Figures 2 and Figure 2-figure supplement 1 is not particularly convincing in terms of the presence of cortical actin. Why do the cells in Figure 2P and 2W look different? The additional examples also show weak actin staining.

      c. Figure 2, Panels S and V show myosin staining which does not appear to be localized to the cortex. More than a single cell should be shown, along with quantitation by line scan analysis to support the claim of cortical localization. d. Definition of amoeboid seems problematic as many of the images show "amoeboid" cells with what look to be microvilli: 2C-K, 2U-W, 3A-F

      e. The text describing the phalloidin staining is a bit circular as it assumes blebbing to interpret the staining patterns, but then uses the staining pattern as confirmation of blebbing.

      4) The authors indicate that the actin in amoeboid choanoflagellates undergo retrograde flow. The authors show a single cell imaged with widefield fluorescence (Fig. 3 F-G, Video 9). Typically retrograde flow is visualized using TIRF microscopy to show the movement of individual actin filaments within a network. The data presented makes it difficult to evaluate whether this is the retraction of the entire cortical network, or flow of actin filaments within a network. To support a claim of retrograde flow, additional data and analysis should be provided. Moreover, the concept of retrograde flow in the context of blebbing motility needs to be explained more fully in the text.

      5) The microtubule inhibition experiments involve treating cells for 36 hours with a non-standard microtubule inhibitor. Due to the possibility of off-target effects, the authors should repeat this experiment with a second microtubule inhibitor to cross-validate the result. A second, orthogonal approach would be to stain cells and look for anti-correlation between microtubule density and bleb formation.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on August 10 2020, follows.


      The work establishes that mouse osteocalcin is O-glycosylated at Ser-8, independently of processing and gamma-carboxylation. Human osteocalcin was found not to be O-glycosylated, but mutation to Ser-8 allowed that process to occur. If increased stability of osteocalcin in vitro as a result of O-glycosylation is real, it could be of interest. The paper was found to be well written with figures illustrating the findings. With that said, several key experiments are required that would considerably strengthen the conclusions. Notably, without information on the biological outcomes of O-glycosylation, the paper is seen to be of limited interest.

      Essential Revisions

      1) Regarding the ELISA (ref. Ferron et al 2010b), capture antibodies can distinguish between carboxylated and non-carboxylated OCN. For the present work, it is essential that the authors show that OCN with or without O-glycosylation at Ser-8 is measured identically in this ELISA. The authors should specify what capture antibodies were used. This query applies also to data with human OCN and the Ser-8 mutant that is O-glycosylated. Furthermore, does the commercial ELISA kit measure glycosylated mutant and normal hOCN as identical?

      2) Figs 3H-J show a statistically significant difference in levels of glycosylated and non-glycosylated mouse OCN. These experiments however do not measure "half life" as claimed in the title and abstract. The in vivo half life of injected O-glycosylated vs wt ucOCN should therefore be compared using timed estimations during the declining phase.

      3) A feature of OCN that interested the authors was the remarkable difference in circulating amounts - more than 10 times higher in the mouse. This work appears to be part of a search for mechanisms to explain this, although they might consider that these are evolutionary changes, including the fact that there is only 65 % conservation of sequence between mouse and human , and the human OCN is not O-glycosylated, whereas the mouse OCN is. The biological significance of this difference in O-glycosylation thus needs to be established. While knocking-in a mutation to abolish O-glycosylation will provide the most definitive answer, the reviewers consider this not to be feasible during the pandemic. Therefore, at the very least, a cell-based assay should be used to compare biological activity. Examples are the dose-dependent increase in insulin mRNA in mouse pancreatic islets (Ferron. et al, PNAS 105: 5266, 2008). Very low dose ucOCN was shown in that work to promote insulin expression in islets in a dose-dependent manner. An alternative approach, arising from the same paper, would be to show at slightly higher doses, a dose-dependent increase in adiponectin expression in mouse adipocytes. The authors might have other possibilities of cell-based assay.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on August 20 2020, follows.


      The reviewers agree that the paper has been improved and is now easier to read. The findings were judged fascinating but there are still issues. The authors delineate a linear story (one pathway) but some elements could affect the system independently. The reviewers agree on a set of recommendations that should be addressed during the revision of the manuscript.

      Essential Revisions

      1) Resistance to parasitoid wasp.

      The authors provide an extremely important body of work. However, the reviewers have a concern about the physiological significance of the phenotype. It is appropriate to hypothesize that an increase in lamellocyte production will yield a more potent immune response against parasitoids, as seen in other Drosophila species (i.e. D. suzukii). However, genetic perturbation that increase lamellocyte numbers, or perturbs the immune system in any manner, does not necessarily mean that the immune response mounted will be successful. The authors should provide experiments monitoring resistance to parasitoid wasps when the pathway they discovered is perturbated. The should monitor the impact of feeding larvae on WOF on resistance and how disturbing Or49A, Gat and Ssadh affect resistance to parasitoid wasp.

      2) RNAi effectivity and using one line.

      The reviewers questioned the validity of the study as some results are based only one RNAi and their knockdown efficiencies were tested by using a ubiquitous and not in the actual tissues. They however recognize that the model is supported by the fact that they are testing different players affect the pathway. The reviewers however ask to repeat the experiments with Gat and Ssadh using another RNAi line to reinforce their conclusion.

      3) Sima staining.

      Figure 3: There are discrepancies in the Sima staining which put question into the specificity of this staining/back ground. For example, some LGs showed a punctate expression of Sima in the posterior part of the LG (Fig 3f, g, and h which is not seem in the other LGs). Pictures in Fig3b, k and m are not in agreement with quantifications in 3o. The same comment holds for Fig 3f-I and quantifications in j. Expression of Sima in lamellocyte is also not convincing. The specificity of the Sima antibody has to be checked. Sup Fig 7B is the difference in sima mRNA levels significant? The reviewers recommend to address this point or at least to prepare a supplementary figure showing replicated of the picture they use of their graph.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on July 9 2020, follows. The preprint has been revised in response to the comments below.


      This paper is an important extension of the authors' previous publication in eLife (Hawkins et al. 2017) that presented novel data suggesting that CO2/H+-mediated vasoconstriction in the brainstem retrotrapezoid nucleus (RTN) supports chemoreception by a purinergic-dependent mechanism. Here the investigators provide new data indicating that CO2/H+ dilates arterioles in other chemoreceptor regions (cNTS, raphe obscurus- ROb), thus suggesting that the CO2/H+ vascular reactivity in the RTN is unique compared to some other brain regions. The investigators significantly advance their previous work by applying a number of new experimental approaches to provide evidence that P2Y2 receptors in RTN vascular smooth muscle cells are responsible for the purinergic mechanism mediating the vascular reactivity and specifically contribute to RTN chemosensitivity. Importantly, pharmacological blockade or genetic deletion of P2Y2 from smooth muscle cells blunted the in vivo ventilatory response to CO2, and virally-driven re-expression of P2Y2 receptors in RTN smooth muscle cells rescued the ventilatory response to CO2, suggesting that these receptors are required for the normal ventilatory response to CO2. New pharmacological evidence is also presented that activation of RTN astrocytes is involved in purinergic signaling driving the RTN vasomotor responses. Overall these results advance the concept that specialized vasoreactivity to CO2/H+ in the RTN contributes to respiratory chemoreception.

      Essential Revisions

      1) Although authors are given leeway in the format of a Research Advance, this paper would benefit from more structure including delineation of Introduction, Results, and Discussion sections. The manuscript would be substantially improved in particular by including a more thorough, dedicated Discussion section with explicit elaboration on limitations of their experimental methods and conclusions, and including discussion of how the important P2Y2 receptor knockout and re-expression experiments represent a fundamental advance considering that the authors had already implicated (although not completely established) these receptors in their previous publication.

      2) Presentation of the RT-PCR data of purinergic receptor expression profiles can be improved, particularly by providing a more convincing validation of this data such as giving supplemental data of raw numbers for GAPDH levels across areas to prove that GAPDH actually is a valid reference. The authors could also use 3-4 such genes as many investigators do for expression profile calibration. The reviewers note that for the argument it is not necessarily that important how the levels of receptors look in relation to a house keeping gene, but whether P2Y2 is the only receptor which is relatively highly expressed in RTN smooth muscle cells compared to other regions. Looking at Fig. 1B, it seems that relative to the two other areas, P2X1, P2X4 and P2Y14 are also much higher in RTN smooth muscle cells compared to NTS. The reviewers agree that an important aspect is the remarkably low expression of P2Y2 in endothelium which in theory should oppose constriction by possibly releasing NO.

      3) Additional information on measurements of vascular diameters would be useful. Have the authors obtained measurements from multiple vessels at each time point in the chosen field(s) of view for individual experiments? If so, how do such measurements compare to the representative single vessel measurements for a given experiment presented in the figures? How many vessels per experiment are included in the group summary data? Please explain more completely why it was necessary to induce a 20-30% vasoconstriction by the thromboxane A2 receptor agonist before the measurements.

      4) Some additional validation of the specificity of the AAV2 used for the P2Y2 re-expression experiments would be helpful since this is not a well characterized virus and may lead to receptor overexpression. Additional nice clear images with proper co-localization would be good to see and additional details about non-smooth muscle cell expression should be provided.

      5) The experiments showing unstable breathing in vivo produced by injecting a thromboxane A2 receptor agonist vasoconstrictor (U46119) into the cNTS and ROb under conditions of mild hypercapnia (2-3% inspired CO2) are intriguing, but these experiments lack the proper control of U46119 injections into the cNTS and ROb under normocapnic conditions to determine if this alters blood pressure and produces breathing instabilities independent of any "gain-up" of RTN activity. It would also be of interest to know whether the authors have tested if larger instabilities occur with cNTS/ROb vasoconstriction at higher levels of hypercapnia.

    1. This manuscript is in revision at eLife

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


      Garcia-Marcos et al describe a method to study the activity of heterotrimeric G-proteins. These switches are usually activated via GPCRs and play very important roles in cellular signalling. Investigating their function is often difficult. Therefore the authors have designed an optogenetic tool that activates Gi proteins by blue light based on an engineered LOV2 domain. They demonstrate that activation is specific and that the dark state has a much lower affinity than the light state. The optimization is quite impressive. Overall, this is an interesting and useful tool but some experimental verifications are required.

      Essential Revisions

      1) Figure 1 shows binding of the G protein to permanently on or off mutant versions of LOV2GIV. Since the G protein is purified, abundant and bound to GST-LOV2GIV, why is it not visible in the ponceau S stained gel?

      2) This figure needs additional controls. Is the interaction with WT LOV2GIV induced by light as shown in the cartoon? Does the interaction lead to increased GTP binding, as shown in the cartoon? Is the binding blocked by GIV residues known to be important for G protein binding as shown in the cartoon structure? Whether or not these controls have been used in the past, they should be done here as well for this particular fusion.

      3) Figure 2A shows binding association (not dissociation as indicated) for the same constructs as in Figure 1. Figure 2B shows GTP hydrolysis but the function of GIV is to stimulate GTP binding, which is just as easy to measure. Again, this figure needs additional controls to show that it is activated by light and relies on key residues.

      4) Figures 3 and 4 shows G protein activation in yeast and HEK293 cells. GIV leads to increased GTP binding but the cell assays do not measure G-alpha-GTP signaling but rather measure release of G-beta-gamma. A direct assay for G-alpha-GTP should be used. The yeast legend and figure do not match and the yeast assays in Figure 3 and 4 use different readouts when both could be used in parallel. A single concentration of a single agonist as a reference is not sufficient when the authors could easily do a concentration-response experiment with an antagonist as a negative control.

    1. This manuscript is in revision at eLife

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


      This current study builds on previous work from the same group published in eLife. This past work focused on the mechanism that renders lateral line hair cells of pappaa mutants more susceptible to the ototoxin neomycin. This work found that mitochondrial dysfunction was the underlying cause for neomycin susceptibility. This current study expands on the previous work and suggests that not only defects in mitochondria, but also the ER are involved in neomycin susceptibility. The authors use a variety of approaches including TEM, live imaging, pharmacology and RT-qPCR in their present study. Using TEM the authors show that mitochondria - ER associated are more numerous. Furthermore, similar to disrupting mitochondrial calcium pharmacologically, disrupting ER calcium also renders Pappaa-deficient hair cells more susceptible to neomycin. The authors suggest that this ER dysfunction manifests in several ways. They use live imaging to show that in pappaa mutants hair cells are unable to properly package neomycin into autosomes. In addition, via RT-qPCR they show that pappaa mutants have an increased unfolded protein response (UPR). Currently the relationship between all of these pathological issues is unclear, but this work does reveal additional mechanisms that could render loss of Pappaa detrimental to hair cell health. Although the work is well written and presented and statistically sound, there are several experiments that are needed to strengthen the claims presented in this study.

      Essential Revisions

      1) Location of TEM micrographs in hair cell. The morphology of organelles can vary based on location within the cell. For example, in hair cells the ER near the nucleus can be distinct from the ER present near the contacts made with efferent neurons or afferent neurons. (https://pubmed.ncbi.nlm.nih.gov/1430341/; https://physoc.onlinelibrary.wiley.com/doi/10.1113/jphysiol.2013.267914).

      Can the authors indicate what direction the sections (apical-basal or transverse) were taken, where in the hair cells are the sections were taken and how they determined this location?

      2) Quantification of mitochondrial fragmentation. It is clear from the TEM cross sections that the mitochondria in hair cells (Figure 3 A) are quite different between pappaa mutants and controls. Whether there are mitochondria or ER networks are present is not apparent from these TEM images. Nor is it entirely clear that the networks are fragmented. The authors use plugins developed for confocal imaging to estimate fragmentation base on circularity and area/perimeter measurement. It is unclear if these measurement translate to hair cells or TEM. In addition to fragmentation in TEM images, the fragmented mitochondria in pappaa mutants are also hard to see in the live, max-projected mitoTimer images.

      The mitochondrial networks and fragmentation may be clearer or be better quantified by acquiring super resolution images of hair cells labeled with mitoTracker. In addition, it is possible that the fragmentation may also be visible or more convincing in movies of Z-stacks of mitoTracker label compared to in the max-projected images provided.

      3) Examination of hair cell ER morphology. The previous work on Pappaa in zebrafish hair cells focused extensively on the mitochondria while the currently study the shifted the focus to the hair cell ER. While the ER-mito distances are convincing, a more wholistic picture of the amount or distribution of the ER in wildtype and mutant is lacking.

      This could be accomplished either using a transgenic line that labels the ER or a KDEL antibody (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC4007406/).

      4) It qualitatively appears that pappaa mutant hair cells are taking up a greater quantity of fluorescent Neo faster than WT i.e. the fluorescent intensity is greater in more hair cells. Did the authors quantify Neo-TR uptake?

      5) Specificity of the pharmacological treatments. The authors perform numerous pharmacological experiments to disturb ER calcium. The authors suggest that that their pharmacological manipulations trigger hair cell death due to the alteration in the interplay between ER/mito calcium in hair cells. What concentration of either of these drugs does it take to kill WT hair cells? Dose-response curves comparing WT and mutant would help support the idea that hair-cell death observed is a direct effect of the drugs on hair-cell ER-mitochondria calcium signaling.

      Pharmacology is non-cell autonomous and the authors do not present evidence that these compounds specifically impact hair cell ER or mitochondrial calcium. Alternatively, these compound could impact supporting cell ER (https://elifesciences.org/articles/52160) as well as the ER in the innervating afferent or efferent neurons.

      More direct evidence show that hair cell mitochondria or ER calcium (measurements using mitoGCaMP such as in the previous study) are impacted by these treatments would make the author's claims more compelling.

      6) The disconnect between IGFR1 and results in the current study. The identify and location of IGFR1 and the IGFBP are still undefined in this system and therefore it remains unclear exactly how IGRR1 or Pappaa impact sensory hair cells. In previous work on pappaa mutants (enhanced startle response, defects in photoreceptor synapse formation, defects in hair cell mitochondria) the role of IGFR1 in these processes was validated. In the current study, the link with IGFR1 is implied throughout.

      It is true that the relationship between IGFR1 and Pappa is well characterized and that currently the only known substrates of Pappa are IGFBPs. Despite this work, it is still possible that given the range of phenotypes in pappaa mutants, that Pappa has other protein substrates that have not yet been identified, or other has biological functions unrelated to the IGF system.

      To verify IGFR1 in this current study the authors could use NB1-31772 to stimulate IGF1 bioavailability and test whether this rescues either the autophagy or UPR defects in pappaa mutants. Being able to rescue these phenotypes also makes the study more compelling.

      7) The authors state that there is not more spontaneous hair cell death in pappaa mutants compared to controls (line 443). Previous work has shown in zebrafish that Usher mutants (cdh23, ush1c, myo7a) also have an early UPR (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC4007406/). Similar to pappaa mutants usher mutants have the same # of hair cells compared to controls, indicating no spontaneous hair cell death. But interestingly Usher mutants do have more TUNEL positive hair cells compared to controls, indicating that more hair cells in Usher mutants are in the process of apoptosis. Based on this new finding implicating the UPR response in pappaa mutants, could pappaa mutants, similar to hair cells in Usher mutants be more fragile (neomycin susceptible) as they are more likely to be in the process of apoptosis? A TUNEL label in pappaa mutants could reveal this. In addition, this paper on UPR in Usher mutant hair cells could be a useful paper to add to the discussion.

      8) Line 445-451: "Together, these findings suggest that Pappaa may regulate ER-mitochondria associations by promoting ER homeostasis. It is important to note that the ER and mitochondria are engaged in a constant feedback loop." This line of reasoning seems rather circular, considering that the previous study showed Pappaa regulates mitochondrial function. If mitochondrial function is impaired, it seems likely that ER homeostasis would be disrupted as well.

      9) Methods: Overall, the methods section needs more detail. All experiments that were not previously performed by the author or the author's lab should have a concise description of what the authors did next to the reference (e.g. fish were imaged under Lab-Tek Chambered Coverglass (Fisher Scientific) where they were immobilized under a nylon mesh and two stainless-steel slice hold-downs (Warner Instruments) per Stawicki et al, 2014) A detailed description of how individual pappaa170 larvae used in experiments were genotyped is needed. A comprehensive description of how mitochondrial circularity was measured using the "mitochondrial morphology" plug-in in ImageJ is needed.

      10) Statistics: how did the authors determine the power of the experiments were sufficient to avoid Type I and Type II error?

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on August 16 2020, follows.


      The manuscript entitled "Increasing heart vascularisation using brain natriuretic peptide stimulation of endothelial and WT1+ epicardial cells" by Li et al. reports data of myocardial angiogenesis in mice subjected to experimental myocardial infarction. The study indicates that repeated intraperitoneal injections of synthetic BNP or oral treatment with Entresto, a drug inhibiting neprilysin-mediated degradation of the endogenous natriuretic peptides, possibly improves cardiac vascularization after ischemia.

      Microvascular dysfunction after acute myocardial infarction (MI) is a major clinical problem. Although primary percutaneous coronary intervention (PCI) has markedly improved patients' survival, despite epicardial reperfusion more than 30% of patients show signs of microvascular dysfunction leading to adverse left ventricular remodeling and heart failure. Impaired angiogenesis can contribute to myocardial tissue damage. Based on experimental studies, several clinical trials aimed to improve myocardial angiogenesis via intracoronary administration of vascular growth factors, gene transfer or bone marrow mononuclear cells, in patients who had successful primary PCI, but the results were disappointing. A better knowledge of the cellular pathways regulating myocardial (re)perfusion after ischemia is necessary to search for therapeutic strategies capable to restore the microvascular network and flow. The here presented study aimed to elucidate whether B-type natriuretic peptide (BNP) can improve myocardial postischemic angiogenesis in as well as the potential pharmacological, therapeutic implications. Hence, this experimental, „preclinical" study addresses an important, clinically relevant question.

      Overall this study follows a very original question. But it includes many different data sets in somehow incomplete way, many of them generated with "NMC". It would benefit a lot by concentrating in a clean way on some concrete aspects. Mechanistic studies should be preferentially conducted with sorted or cultured endothelia instead of a mixed cell population (NMC, containing fibroblasts, pericytes, inflammatory cells, besides endothelial cells).

      Essential Revisions

      1) Certain parts of the study should be completed. For example, why don't the authors present a fine and extensive analysis of cardiac function in animals treated with BNP? In the same way, the authors should complement their experimental approaches with an analysis of all parameters of cardiac remodeling and in particular infarct size and interstitial fibrosis.

      2) Conversely, the authors made the effort to analyze cardiac function in animals treated with LCZ696 (Figure 9). However, there is no statistical analysis of these data? or the differences are not significant? in this case, what is the interest of a treatment that increases capillary density without modifying cardiac function? It is however likely that an analysis of cardiac function beyond 10 days post-MI could give significantly different results.

      3) The authors should analyze whether or not LCZ696 directly stimulates the proliferation of resident mature endothelial cells and/or that of WT1+ cells.

      4) Results, page 5, para 1: the authors state that "first they determined whether ip BNP acted directly or indirectly on cardiac cells". But there is no single data set in this manuscript allowing to conclude that the observed effects are directly derived from endothelial actions of BNP. As they mention before, BNP acts on many types of cells and organs, and the observed effects could also be "indirect".

      5) Results, page 5, para 3: plasma cGMP levels are a poor index of cardiac actions of BNP. It would be more meaningful to measure cardiac cGMP levels.

      6) Results, page 5, para 4: it is strange to use the phosphorylation of phospholamban (PLB) as index of BNP activity. This manuscript focuses on angiogenesis. PLB is a regulatory protein in cardiomyocytes. Where is the link to endothelial regeneration?

      7) Page 6, top: BNP increased phosphorylation of PLB by nearly 200-fold in "non-myocyte cells" from the heart. Which cells are these? Is this fraction contaminated by cardiomyocytes? Which non-myocytes have such high PLB levels?

      8) How were BNP plasma levels in BNP versus vehicle treated mice after MI? Did Entresto increase BNP plasma levels and to what extend?

      9) Most in vitro and ex vivo studies were performed with NMCs. How many endothelial cells are contained in such heterogenous populations?

      10) Some basic parameters are missing: how did BNP administration affect cardiac contractile functions as well as the infarct area and area at risk? Did exogenous BNP lower arterial blood pressure?

      11) Page 9: how does BNP, via NPR-A/cGMP-signaling, increase MAPK pp38? What is the signaling pathway and do the authors have any hint that this signaling pathway was also activated by BNP in vivo (in endothelial cells in situ)?

      12) Page 11 presents a section entitled "Increased vascularization in infarcted hearts after LCZ696 treatment". But in the corresponding Figure 9, there is no single data set showing „statistically significant effects of entresto". The figure just shows some preliminary data and trends obtained with very few mice.

      13) Figure 1C: it is surprising that the basal levels of pPLB were so low (-). Normally, after MI in mice the endogenous ventricular expression levels of ANP and BNP significantly raise. Was there a difference in pPLB between sham and MI mice (vehicle treatments)?

      14) Figure 1D: which types of non-myocyte cells express such high pPLB levels and what is the functional meaning?

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on August 9 2020, follows.


      Overall this is an interesting paper whose ssRNA seq dataset and experimental analysis of phenotypes provides a valuable resource for investigating gene expression differences associated with key phases of skin development and repair. The enhancement of HF regeneration upon Lef1 overexpression is a striking result and will be of general interest to many fields including developmental, stem cell, and epithelial biologists. The work is well conducted, the results are new, and significant for skin wound healing and HF regeneration, and in sum a good fit for eLife.

      Essential Revisions

      The overall tone of all reviewers is enthusiastic and favorable, however with very important points raised:

      1) Dermo1-Cre seems not specific to fibroblasts (and it is non-inducible). Ideally this should be addressed by using an inducible/more specific Cre mouse line. However, as the enhancement of HF regeneration is an exciting finding by itself and a new mouse model is likely out of scope of a revision, this point could be addressed textually by changing the conclusions to reference stromal cells instead of fibroblasts specifically.

      2) The interpretation of the scRNA data should be bolstered with additional analyses. It is important for the authors to revisit the data and figures (including making some improved analysis), and carefully state the actual results and conclusions supporting their claims and following next steps in the manuscript.

      a) ScRNA-seq analysis was superficial in relation to regeneration versus repair, especially comparison of the time points that model regeneration and scarring. Does velocity analysis predicting Lef1, or other genes, driving differentiation of one population of fibroblasts into a papillary fibroblast or DP-like state? Do multiple fibroblast subsets follow this trajectory? How do these finding compare between the two wounding time points? Does gene ontology suggest differences within one subcluster of fibroblasts between two conditions or are the major differences in the gene expression profile/function associated with each subcluster? A more complete analysis of this could shed more light on the involvement of fibroblast lineages in regenerative versus reparative healing.

      b) From the ssRNA seq analysis the authors state "we identify Developing papillary fibroblasts as a transient cell population that is defined by Lef1 expression.", but this is not clear from the ssRNA seq analysis. In Figure S2, Lef1 expression seems to be largely excluded from cells within the Dpp4 expression cluster (cluster 2), and Dkk1 (Cluster 0), which define the major papillary FB clusters. Can the authors expand upon how the Velocity Analysis identifies different genes than overlaying relative expression levels on the UMAPS?

      3) Surrounding the claim of a transient papillary fibroblast population (which is an important part in their paper), several parts are unclear;

      I.e. they could/should explore the fibroblast populations of all conditions to compare regeneration vs scaring and regeneration vs development (e.g. R2Q2, R3Q5).

      Which of the two papillary fibroblast population(s) is/are transient? How to explain the rather minor overlap of Lef1 expression with these two papillary fib populations? Where are the two populations in situ in developing and in regenerating skin?

      4) Given that the WIHN generates a significant amount of cysts, the authors have to down-tone their statement of "without adverse phenotype". As the authors also refer to Hedgehog-pathway induced de novo HF formation (a model giving rise to tumors and new HFs), they likely meant that their model does not induce apparent tumors (the cysts look different compared to the obvious BCC-like lesions trough Hh-pathway activation) - however the authors totally neglect the fact (don't mention) that the mice apparently develop cysts in addition to HFs in wounds.

      Figure 5e,g,j. The regenerated HFs appear very abnormal and cyst-like. The authors state several times in the paper that Lef1 overexpression enhances regeneration without other adverse phenotypes, but these regenerated structure are very abnormal. Are they cancerous? P90 wounds appear to generate a significant amount of cysts; is this representative for all conditions or something more specific for the P90 timepoint?

    1. This manuscript is in revision at eLife

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


      This manuscript uncovers an unexpected role for myogenin in muscle stem/progenitor cells in adult zebrafish. Further analysis of a previously characterised mutant makes novel contributions to the field of muscle growth. The authors show that Myog helps keep MuSCs quiescent and provide mechanistic insights into how Myog controls MuSC activation. Intriguingly, their work suggests that Myog mutants have increased differentiation markers compared to wild-type siblings. They also offer new models for MuSC positioning within a fiber.

      Essential Revisions

      1) In their previous publication (Ganassi 2018), the authors showed that the differentiation index of cultured adult myoblasts does not differ between WT and myog-/-, but in the current study myog mutant cells show a much higher degree of differentiation compared to their wild-type siblings. Please clarify why these findings differ.

      2) The authors claim that the pax7a:GFP+VE cells represent bona fide MuSCs, which can only be determined by co-label of GFP and an anti Pax7 (or Anti Pax3+7) antibody. Although the authors do provide this co-label in one panel, they only show one cell per genotype. Please provide quantification of how often the GFP+VE cells are also positive for the anti-Pax3/7 antibody. Unless this co-label is extremely common in both genotypes, or confirmed in each experiment, the authors should soften their language abut the GFP expressing cells being verified MuSCs.

      3) Related to the previous point: The authors show that MPCs behave differently in culture and although they show increased pax7a and pax7b expression they also express higher levels of differentiation markers and enter terminal differentiation. This is puzzling and inconsistent with the reduced number of myonuclei and smaller myofibres that are seen in the mutant fish. Furthermore, it is not clear how the increased number of MuSCs per fibre is reached. A plausible explanation for both observations (fewer myonuclei/smaller fibres & more MPCs), is that these cells are myocytes that do not fuse efficiently. The authors raise this possibility in the discussion, however, this should be better assessed and either excluded or supported.

      4) The surface area domain size measurement in Figure 1 is a strange proxy for myonuclear domain. which is best thought of as a volume, as shown in Figure 2. However, figure 2 omits all pax7:GFP+VE cells, some of which may have fused recently enough to retain their GFP label. Please replace the SADS calculation in Figure 1 with a volumetric calculation. This will be important for interpreting and comparing the two findings.

      5) Culture of mononucleated MPCs from plated fibres was used to investigate whether lack of Myog enhanced MPC proliferation. The relative proliferation rates were not significantly different, however, EdU pulse experiments suggest that mutant MPC are more readily entering S-phase. Overall the authors suggest that lack of myog accelerates MuSC transition into the proliferation phase. At present this is not supported convincingly. Indeed, the data shows reduced proliferation and AUC (4E) in mutants. An additional EdU pulse at an earlier time after plating (day 1) should be included to potentially strengthen this idea. Alternatively the statement should be modified and toned down.

      6) The authors want to assess whether there is an earlier onset of differentiation of MPCs in culture. However, they only show expression of mef2d and mylpfa at day 3 (Fig 4H) and day 2 should be included here as well. Overall the differentiation index of MPCs is increased, can they comment on whether the cells remain mononucleated.

      7) In the discussion the paragraph (292 ff) regarding the niche is very speculative and should be toned down/amended. In particular, (Line 318) the conclusion that that Myog is required for assembly of the MTJ MuSC:niche complex is not well supported, there are no MTJ markers shown.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on July 6 2020, follows.


      Sando et al. extend on previous work by the same lab to delineate the neuronal mechanisms that control UV-light / ROS suppression of feeding and evoked spitting behaviors. They provide a nice characterization of pharyngeal behaviors that are involved in feeding and spitting, showing that upon UV-light stimulation feeding pumps are modulated to evoke spitting instead. M1 neurons are central to the spitting reflex; they sense light, integrate inputs from light sensitive I2 and I4 neurons and transmit the information to the anterior pharyngeal muscles pm1/2 and the anterior part of pm3. The conceptual advances of this paper are twofold:

      1) The hourglass circuit motif as a means to transform ingestion movements into spits.

      2) Local activation of pm3 muscles via a compartmentalized calcium signal that ensures opening of only the anterior part of the alimentary tract.

      Most of the behavioral experiments are well done and the paper could be of potential interest to a broad audience. However, the reviewers raised some concerns that should be addressed prior to publication in eLife.

      Essential Revisions

      1) A major concern is that all three reviewers are not convinced that the data presented here support the conclusion of local calcium dynamics in the anterior pm3 muscles. Since this is one of the major aspects of this study, it is essential to provide more experimental evidence. The authors used a pan-pharyngeal driver to express GCaMP. The imaging resolution seems not good enough to distinguish calcium transients in pm1/2/3 and the most straight forward interpretation of the results is that the anterior calcium transients are derived from pm1/2 but not pm3. It seems otherwise to rest on the claim that pm3 is sufficient for spitting and that, in the absence of pm1/2, local contraction of pm3 is the only way to hold the valve open during expulsion. Same for Fig 4F.

      To substantiate the claim, these experiments should be repeated using a pm3 specific driver.

      Alternatively, if pm3 specific drivers are not available, the experiments could be repeated upon laser ablation of pm1/2, to ensure that the signals are indeed specifically derived from pm3.

      Perhaps, if imaging resolution and interference by emission light scattering permits, an overlay of a good DIC with GCaMP fluorescence may settle this more easily since pm3 stops at the base of the buccal cavity whereas pm1/2 line the cavity.

      Individual recording traces of the different regions along with ethograms of the pharyngeal behaviors should be shown.

      2) The authors use a calcium imaging assay in immobilized worms to record UV-light evoked muscle activity- and pharyngeal neuron activity. While pumping and spitting behaviors occur at a frequency of up to 5Hz in the behavioral assays (e.g. Fig 1D,E), calcium dynamics in muscle and neurons were observed at 1-2 orders of magnitude slower (e.g. Fig 1 H,I; Fig 4H-M). However, the authors state that these dynamics would match well the time-scale at which light evoked pumps are observed. This is confusing. While it is possible that pharyngeal neurons encode the rate of pumping/spitting, muscle activity should correspond to the motor rhythms.

      What is the pumping rate under the imaging/immobilization conditions? Do the animals spit? The behaviors under imaging conditions need to be better characterized and documented.

      Individual traces should be shown throughout (like Fig 4H), importantly next to ethograms of pharyngeal behaviors.

      The image acquisition rate should be stated in the methods? Was this also 2Hz like the flickering rate?

      Only with this information at hand it is possible to properly interpret the imaging results. Are the measurements convoluted by low acquisition rate and slow on/off kinetics of GCaMP, or do light evoked pharyngeal behaviors occur at such a slow frequency in immobilized worms?

      3) The purported movements of the metastomal filter appear to be based solely on the observation of particle flow with a particular concentration and size of beads. At times this may be misleading. For example, the authors report that 25% of normal pumps are associated with openings of the metastomal filter. However, it is possible that the beads do not always become jammed in the buccal cavity, even if the metastomal flaps remain in position. Direct imaging of the metastomal flaps would address this question; if this is not possible the limitations of the assay should at least be acknowledged.

      4) The opening of the metastomal flaps during spitting is interpreted as a "rinsing" of its mouth "in response to a bad taste". This interpretation is problematic since the animal is "rinsing" its mouth with the same particles that have presumably induced the spitting. It would make more sense if the animal increased rather than decreased selectivity of the metastomal filter; this would allow water to enter the pharynx while excluding potentially toxic particles. If the authors insist in their interpretation they should at least discuss this issue.

      5) Line 183 - What is the basis for believing the sufficiency of pm3 is based on "contraction of a subcellular region"? And Line 188 - where is this "uncoupling" shown? There are few figures/data here. Is it deduced that this must be so because the pharyngeal valve is open while the lumen closes during spitting? Is local contraction of pm3 the only possible explanation for this? In the WT condition, for example, could pm1 and/or pm2 contraction overcome a global relaxation of pm3 to hold the valve upen during lumen closing? Although spitting apparently persists after ablation of pm1/pm2, these events should be documented in the same detail as WT events to demonstrate that pm3 is truly sufficient for "normal" spitting (i.e. continued pumping of lumen while the valve and filter are held open, local Ca++ events in anterior portion of pm3). This section seems to take a leap to a precise muscle mechanism based only on the ablation.

      6) At the cellular level, the authors note that calcium waves in muscle can cause local contraction patterns that lead to peristalsis, but that their observations seem to be of a different kind in terms of spatial and temporal patterning (long sustained local Ca++/contraction in one domain while rhythmic Ca/contraction occur in another domain). How input strength might create such a pattern is difficult to envision, given the simplicity of the M1 pm3 innervation pattern. What is the proposed cellular mechanism here?

      7) Figure 4J-L: these panels lack quantifications. Please show also individual traces; is the little initial bump in lite-1 mutants' response consistent across multiple recordings? Is the reduction in lite-1;gur-3 statistically significant?

      Why is this initial transient signal so much stronger when gur-3 is expressed in I2 in the double mutants (Fig 5D)?

      8) Line 422-424: this statement is not supported by data in Fig 6B-F; only I4 ablated animals show a robust defect and there is no synergistic effect in the double ablation.

      9) Fig 6G: this result lacks quantifications. Appropriate statistics should be performed. Show also individual traces.

      10) Line 210 - "data not shown"... the correlation between spatially-restricted contraction / Ca++ signals and spitting is a central claim of the paper...it needs to be quantitatively documented in a figure.

      11) Line 104 - Is the experimenter blinded to strain/condition? If not, what steps were taken to detect or correct experimenter bias? This is a major pitfall of manual behavior coding.

    1. This manuscript is in revision at eLife

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


      This work describes a novel approach to address the important and still open question of the extent of negative selection in cancer and the potential implications. The authors use data from the catalogue of somatic mutations (COSMIC) and a straightforward approach comparing synonymous, nonsynonymous and nonsense mutation counts to separate genes into Oncogenes, Tumor suppressors and Essential genes. The authors conclude that negative selection plays an important role during tumor evolution.

      Essential Revisions

      The reviewers agreed that this work is timely and relevant, but also agreed that there are several important aspects that need revision/improvement before it can be accepted for publication in eLife.

      Structure of the paper:

      1) The reviewers agreed that there are various aspects of the structure of the paper that require especial attention. The introduction is a bit lengthy and very focused. It introduces different questions, e.g. hallmarks, prediction of oncogenes and tumor suppressors, prediction of selection, etc and it reads like multiple introductions to different articles. Many parts (e.g. the discussion of cancer hallmarks) could be shortened substantially, which would make it easier to read the paper. One suggestion is to mainly introduce the models of cancer evolution with respect to the SNVs and indels, and the different models and limitations in the estimation of negative selection in cancer and why it is difficult to detect, see e.g. (Zapata et al. 2018, Lopez et al. 2020, Tilk et al. 2019).

      2) Additionally, it will be important to include citations to previous work on the detection of negative selection in cancer that has been omitted. For example, in Line 353 they should add the work from (Zapata et al. 2018, Van den Eynden et al. 2017, Martincorena et al. 2017, Pyatnitskiy et al. 2015).

      3) Both reviewers agreed that the Results section is repetitive and unbalanced with respect to the Methods section. The work would benefit from streamlining the Results part and moving details to the Methods section.

      4) Regarding the discussion, it is also very lengthy and lack focus. The authors should make clearer the main results and take-home messages from their work. At the moment, this is not very clear.

      5) For simplicity and to improve readability of the manuscript, it was suggested that the authors focus on 2 standard deviation through the manuscript, instead of describing repetitively the results with 1SD and 2SD.

      6) Regarding the presentation of the results, the reviewers suggested to redesign the figures in such a way that they describe the methodological approach, present the major results of their analysis, and show a comparison of these results with previous methods, and lastly (currently as a table) show the association between the identified genes and the hallmarks of cancer.

      Comparisons with previous studies:

      7) One of the problems with the present work raised by the reviewers is that the authors did not performed sufficient comparisons of their results with previous studies. The authors used a seemingly simple approach to measure selection, dividing fractions of frequencies of different mutation classes by each other, with relatively arbitrary cutoffs, e.g. 1 or 2 standard deviations from the mean, to define gene sets. The manuscript does not show the advantages of this method over previous approaches. The authors should clearly show that there is an advantage of their approach by comparing with previous approaches.

      8) The authors should also compare their results with previous publications. One of them, which is cited in the manuscript, is Weghorn & Sunyaev. In fact, this work seems to be misquoted. The authors claim that Weghorn & Sunyaev "identified 147 genes with strong negative selection" (line 371), but that study in fact found very few genes under significant negative selection (<10 applying a q-value cutoff of 0.1) and Weghorn & Sunyaev concluded that "the signal of negative selection is very subtle". Zapata et al 2018 identified stronger signals of negative selection. The identified genes and functions were partly the same as in the here presented work (eg GLUT1). The authors should compare their results to these and other previous results.

      9) Furthermore, there is recent evidence that correcting for mutational signatures and nucleotide-context composition has a large impact when quantifying selection (see e.g. Zapata et al. 2018, van den Eynden et al. 2017, Martincorena et al, 2017), and this is a relevant aspect in the current lines of discussion in the context of negative selection in tumor evolution (see for example Van den Eynden et al. Nature Genetics. 2019). The authors should show that their main observations hold when the mutational signatures and/or trinucleotide context is taken into account.

      10) Related to this, the authors described a clustering-based method to detect genes that deviate from an average proportion of mutations (nonsynonymous, nonsense and synonymous) to infer selection. However, by only using the observed mutations (nonsyn, syn, nonsense), the underlying base-pair composition is ignored. Genes that have a high likelihood of acquiring nonsense mutations will show a deviation from the rest of the genes due to their composition and not due to selection. The authors should recalculate their metrics by performing this correction before reaching the conclusion on the number and identity of the genes.

      Use of controls:

      11) The reviewers also indicated the lack of sufficient controls. To improve the robustness of their method, it was suggested to assess the results after varying several of the conditions. For instance, to circumvent the limitation of the lack of mutations to detect negative selection, the authors study only transcripts with more than 100 mutations. The authors should compare their results using different cut-offs for the minimum number of mutations (50,100,500), and check the performance of their method and whether their results are robust.

      12) Other variations that the authors should consider is to stratify data based on tumor type and mutation burden, since mixing samples with different evolutionary histories might confound the signal of negative selection. As an additional control, a reviewer suggested to perform the same analyses using the germline mutations to separate the genes into cancer specific or cell essential.

      13) An additional control to be performed by the authors was related to the origin of the mutations. The file CosmicMutantExport.tsv contains both mutation data from targeted and genome- / exome-wide screens. Targeted data should be excluded (if the authors didn't do so already). Otherwise their analysis will be highly biased towards well characterized cancer genes.

      Statistical tests:

      14) The reviewers also agreed that there is a general lack of statistical tests in the results. For instance, "the mean parameters of TSGs differ markedly from those of passenger genes in that rNS and rNM values are higher" (line 529), but these comparisons should be done with appropriate statistical tests to assess the significance. Similar tests should be performed throughout the manuscript.

      15) A very interesting idea in the paper highlighted by the reviewers is that by combining their proposed metrics they can differentiate between oncogenes and tumor suppressors. It would be convenient to have a visual interpretation on how different genes can be only oncogenic, only tumor suppressors, or both, depending on which sites are hit. It is important to note though that similar classifiers have been developed (Schroeder et al. 2014), so it would strengthen the claims of the study to provide a comparison with those methods.

    1. Reviewer #3

      The focus of the manuscript by Nicolas-Boluda et al. is timely as it has been shown by this team and by others that dense collagen fibers and other features of the matrix architecture surrounding tumors may form a barrier for T cell infiltration into solid tumors. Despite the authors' claims, however, the data in this manuscript fall short of definitively demonstrating that response to anti-PD-1 therapy and T cell migration into tumors is improved upon reduction of collagen cross-linking. I have a number of concerns that would require additional substantive experiments to be adequately addressed. Below I list major and minor points that should be addressed before further consideration for publications.

      Major points:

      1) BAPN is used as a covalent inhibitor of LOX activity however the authors provide no evidence that the drug is having the expected effects in vivo. In order to draw specific conclusions about these studies the authors would need to provide measurements of collagen cross-links (DHLNL, PYP, DPD).

      2) Imbalance between the mechanical characterization of multiple tumor models with little space for defining the effect of tumor stiffness on anti-PD-1 efficacy and T cell distribution, motility and activation.

      3) Rationale for selected tumor models relative to human tumors was unclear.

      4) Sample sizes, # independent experiments and statistical analyses were inadequate across multiple figures.

      5) Measurements of stiffness, collagen structure and T cell speed should be provided for all treatment conditions (control, LOXi, PD1i and combo) rather than just for LOX inhibition.

      6) Lox inhibition was performed in a preventive setting. Do the authors think LOX inhibition would be as effective in changing tumor stiffness and matrix architecture if the treatment started at the same time point as anti-PD-1?

      7) In Figure 1 the correlation of tissue stiffness/collagen accumulation with tumor volume in clinical samples should be provided in order to attribute collagen cross-linking to tumor progression.

      8) The efficacy data in Figure 6 should be accompanied by survival data.

    2. Reviewer #2

      In this manuscript, the authors provide a thorough analysis of the ECM architecture and stiffness in 4 murine tumor models. They then attempt to correlate ECM architecture and mechanics with T-cell migration and PD-1 efficacy. Substantive concerns are as follows:

      1) The study is highly correlative with inadequate sample size to be conclusive. The authors attempts to draw conclusions about when stiffness does and doesn't affect migration by attempting to interpret data across 4 very different tumor types. In two tumors the migration changes with BAPN and with 2 it does not. It is not possible to draw a conclusion based on 2 points.

      2) Data regarding the relationship between collagen organization and stiffness has been reported previously (as cited by the authors).

      3) Sirius Red staining is referred to and described in the text but no images are shown. Likewise, no SWE images are provided to show the relative heterogeneity described in the text. This is important since so much of the conclusions rests on this data.

      4) The results section discussing figure 1 emphasizes heterogeneity in stiffness, however none of the data shown depict spatial stiffness heterogeneities.

      5) The rationale for the choice of cancer models is not clear.

      6) Why is mPDAC measured and reported differently in figure 2A than the other tumor types?

      7) Why is 40kPa chosen as the cut-off for "stiff?"

      8) Mean-squared displacement is the more appropriate metric to describe cell path (and more conventional) rather than "straightness"

      9) How many cells were studied for each parameter in each condition in Table 2?

      10) The authors study migration of cells on slices, but isn't the more appropriate metric to study cell invasion into the tissue?

    3. Reviewer #1

      In their article entitled "Tumor stiffening reversion through collagen crosslinking inhibition improves T cell migration and anti-PD-1 treatment" Alba Nicolas-Boluda and co-authors analyze the stiffness and collagen distribution in different tumor models implanted in mice. They show that treatment with an inhibitor of collagen crosslinking modifies the collagen network in these tumors and that this correlates with changes in their stiffness. They then analyze the motility of T cells in the different models and show that this motility is modified by the treatment and correlates with the stiffness of the tumor. In the last part of their study, the authors show that treatment of the mice with the inhibitor of collagen crosslinking changes the immune infiltrates in the tumors characterized by a more abundant presence of CD8+ T cells. They finally show that interfering with collagen stabilization leads to increased efficacy of anti-PD-1 blockade on tumor growth.

      Relevance of the study: T cells are excluded from a large proportion of solid tumor. This represents an obstacle to T-cell-based immunotherapies. The authors make the hypothesis that this can be, at least partly, due to the organization of the ECM in the tumor that would oppose physical resistance to the infiltration and migration of T cells. The results are sound and important for the community since 1) they describe thoroughly some of the mechanical aspects of several models used in the literature, 2) they thoroughly analyzed the effect of an inhibitor of collagen crosslinking on these mechanical properties 3) study the effects of these modifications in T cell motility and 4) test in one tumor model the effects of the combination of an inhibitor of collagen crosslinking with anti-PD1 immunotherapy. The results are convincing and I only have minor concerns.

      In the first part of their study, the authors analyze the structure heterogeneity of 5 different carcinomas, i.e. subcutaneous model of cholangiocarcinoma (EGI-1), subcutaneous (MET-1) and transgenic model (MMTV-PyMT) of mouse breast carcinoma, orthotopic (mPDAC) and subcutaneous (KPC) models of mouse pancreatic ductal adenocarcinoma.

      They measure the tumor stiffness during tumor growth using Shear Wave Elastography (SWE) and analyze the organization of the collagen fibers in these models. To my knowledge, this represents the first characterization of different tumor models classically used to study tumor immunity and is thus very useful for the scientific community. In particular, the authors show a correlation between high tumor stiffness and accumulation of thick and densely packed collagen fibers.

      Minor modifications: The authors should indicate more clearly the number of mice and tumors investigated.

      In the second part of their study, the authors treat the mice with beta-aminopropionitrile (BAPN), an inhibitor for LOX enzymatic activity in the drinking water and analyze the stiffness of tumors and collagen fiber organization in tumors. They show the heterogeneity of response in the different models in both stiffness modulation and collagen fibers remodeling. Mostly this treatment reduces the stiffness of tumors without affecting their growth.

      Minor modifications: The authors should clarify how "normalized tumor stiffness" indicated in the legend of figure 2 is calculated. Indeed, this is an important point since tumor stiffness is associated to the sizes of tumors. Moreover, they should also indicate more clearly the number of mice and tumors investigated. Concerning collagen fibers orientation, authors should use a dot plot representation instead of bar histograms in order to show the distribution in the different tumors.

      The authors then analyze how BAPN treatment modifies the migration of T lymphocytes in the tumors. Because of the different models used, the authors either added activated purified T cells from human donors (EGI-1model), or mouse activated T cells (MMTV-PyMT tumor model) or followed the motility of human resident T cells in mPDAC and KPC mice tumor models. Although the models are very different, the correlation between tumor stiffness and T cell speed and T cell displacement is specially striking in tumors from BAPN treated mice. It seems that T cell motility responds to two different regimens in tumor from untreated or BAPN treated mice. This might be due to difference of stiffness in untreated and treated mice but might also results from another parameter.

      Minor modifications: The authors should discuss this point. Indeed, the main conclusion of their work and short title of their study is that the main parameter involved in T cell motility and access to the tumor is tumor stiffness but then the slopes should be the same as in the spontaneous MMTV-PyMT tumor model. There are probably other parameters involved in the regulation.

      The authors then investigate the effect of BAPN treatment of tumor bearing mice on response to PD-1 immunotherapy. They perform experiments in KPC tumor bearing mice and show that BAPN treatment alone significantly decreases the number of neutrophils, increases the presence of MHCII+ TAMs. Yet, the combined therapy (BAPN and PD-1) is necessary to expand the percentage of GrzmB CD8+ T cells and the ratio of CD8+ to Treg cells and is associated with an increase in cytokine production. The combined treatment also leads to a decrease in the tumor sizes. Although these results are convincing as they are, confirmation of the results in another model would strengthen the results.

    4. This manuscript is in revision at eLife

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


      The work analyzes the stiffness and collagen distribution in different tumor models implanted in mice and shows that treatment with an inhibitor of collagen crosslinking correlates with changes in their stiffness. This results in a change in the motility of resident T cells. The inhibitor of collagen crosslinking increases the number of tumor-infiltrating CD8+ T cells and leads to increased efficacy of anti-PD-1 blockade on tumor growth. The reviewers have discussed the reviews with one another and the Reviewing Editor and their views concur. Although the work has potential for publication in eLife, it requires essential additional data and statistics to support the central claims of the paper. Each reviewer raised substantive concerns (see below) that need to be resolved experimentally. To quote a few, you should provide a measurement of the collagen crosslinking in mice treated by BAPN to confirm that this drug has the expected effects. The combined BAPN plus anti-PD-1 therapy needs also to be confirmed in another model. Measurements of stiffness, collagen structure and T cell speed should be provided for all treatment conditions (control, LOXi, PD1i and combo) rather than just for LOX inhibition. Importantly, several important conclusions are based on inadequate sample size to be conclusive (see below). Along that line, the number of mice and tumor cells plus corresponding statistics need to be indicated in all the figures.

    1. This manuscript is in revision at eLife

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


      This manuscript describes a laboratory evolution experiment designed to explore effects that may shape evolutionary trajectories in a native host environment. The model system is E. coli nitro/quinone reductase NfsA, a promiscuous FMN-dependent oxidoreductase that reduces toxic compounds and has the basal ability to reduce the antibiotic chloramphenicol. This function was used to select for improved detoxification by mass-mutagenizing eight active-site residues and isolating variants with up to tenfold higher tolerance against chloramphenicol. The five best variant proteins were purified and characterized, showing that their kcat/Km was only marginally improved, with worse kcat but improved Km, indicating that the improvements in detoxification were driven by enhanced substrate affinity. For the top two variants, all possible evolutionary trajectories were recreated and their EC50's tested to determine the most likely possible step-wise paths from NfsA to the final variants. The authors found that iterative evolutionary strategies could have generated similar variants, but that there were only few accessible pathways, indicating epistatic effects. The analysis also showed that for both variants, elimination of arginine at position 225 in the first step enabled further improvements to take hold and played a role in the loss of wildtype 1,4-benzoquinone activity. The sensitivity to four out of five tested prodrugs was however unchanged. Turnover of the fifth prodrug, namely reduction of metronidazole, which yields a toxic product, was on the other hand increased in the evolved variants, and could be used as a counter-selectable marker. This was briefly tested showing the potential of such an application.

      Essential Revisions

      This study presents a wealth of data, and is well reasoned, carefully executed and clearly laid out. However, although it states that its aim was to study the evolution of a promiscuous function within the native host environment and thus under metabolic interference of the native substrate, this was not the approach taken. Instead, a fitness peak for the promiscuous function was identified through mass mutagenesis at eight positions followed by selection, and then two potential evolutionary paths leading from the wild type to this peak were inferred based on an analysis of all possible mutant combinations at the mutagenized positions. The authors need to make clear throughout the paper that the variants able to detoxify chloramphenicol were not evolved and did not arise against metabolic interference of the native substrate. This is an important point as the considerable potential of endogenous metabolites to shape evolutionary outcomes (Abstract) is purely inferred from the observation that the first mutation in both reconstructed evolutionary paths appears to have been a mutation at R225, which led to a substantial drop in the turnover rate of the endogenous substrate. From this the authors conclude (very prominently throughout the paper) that the evolution of a new activity is only possible after loss of activity against the original substrate.

      From the data presented, it is however not clear to what extent this conclusion is supported.

      1) According to the data in Figure 4 and Table S1, mutation of R225 alone is accompanied by a ~2-fold increase in kcat/Km for chloramphenicol. This seems to be sufficient to explain the ~2-fold increase in EC50 for chloramphenicol without invoking loss of quinone reductase activity. The control experiment in Figure 5, showing that substitution of R225 has no effect on most promiscuous activities of NfsA, also seems to indicate that the loss of native activity is not required for the evolution of chloramphenicol resistance. It would be important to determine the kinetic parameters of 1,4-benzoquinone reduction for NfsA and the purified R225V and R225D mutants in order to establish the loss of quinone reductase activity in the postulated first step of the evolutionary path. It would also be useful to study the effect of 1,4-benzoquinone competition on the chloramphenicol reductase activity of the mutants, at least the first ones along the proposed path, in order to show that they rapidly become insensitive to the native substrate.

      2) After the initial screening of the transformed library of NfsA variants, 0.05% of gene variants are reported to be more effective in chloramphenicol detoxification than the wild type. In the next steps, this number is reduced to the top 30 variants, as characterized by their improvement of chloramphenicol EC50 values (Fig. 1D). However, it is not clear from the presentation whether these observations were controlled for the expression levels of the different NfsA mutants. Protein variants are often expressed at different levels in vivo, which can have a significant effect on the activity measured. Fig. 1D was used for selection of the "best" variants for the rest of the study and to support this choice and the conclusions of the manuscript, relative enzyme expression levels should be reported (and if significantly different, should be corrected for). Such expression levels are reported later on for the 36_37 and 20_39 variants, but are missing at this early stage.

      3) While mutation of R225 appeared to be required for improved chloramphenicol detoxification in this study, the authors only considered the effects of substitutions at eight positions. This is probably the main weakness of the combinatorial mutagenesis approach used here. It seems plausible that substitutions at other positions could also increase chloramphenicol tolerance, possibly opening a path without loss of quinone reductase activity. If the authors were able to perform one round of error-prone PCR on NfsA with selection for improved chloramphenicol resistance and obtain mainly variants with substitution of R225, this would substantially strengthen their claim that evolution of increased chloramphenicol resistance can only occur through loss of quinone reductase activity.

      4) Even with additional experimental support for the main conclusion of the article, it seems fundamentally problematic to extrapolate from two instances to a general principle of evolution. The authors should tone done the claims that improved chloramphenicol detox activity is ONLY possible after elimination the native activity and instead comment on the two characterized mutant pathways as examples of this phenomenon, within the limitations of the experimental setup.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on July 11 2020, follows.


      In this article, the authors sought to identify interacting partner(s) of Zc3h10, a transcription factor that activates expression of UCP-1 and other brown-adipocyte-specific genes. They identified the H3K79 methyltransferase Dot1L as an epigenetic modifier that interacts with Zc3h10 and facilitates its action on UCP-1 and other brown-adipocyte-specific genes. The strength of the manuscript is that the hypotheses were examined by a wide range of approaches, including protein-protein interaction assays, cell culture studies, and animal models. The present data provide solid evidence for an important role of Dot1L in the regulation of brown-adipocyte-specific genes. At the same time, all of the reviewers believed that the mechanisms involved in the epigenetic regulation of gene expression by Dot1L need to be investigated in more depth. Because the roles and the regulation of H3K79 methylation are still not fully understood, it would advance the field if the authors could provide additional data along these lines.

      Essential Revisions

      1) The protein expression of Dot1L appears disproportionally specific to brown adipose tissue compared with the mRNA expression. Is there a protein-gene difference? Is the identity of the band correct? Can the author see the loss of the band in the BKO tissues?

      2) Most of the experiments appear to have been performed under basal conditions (e.g. unstimulated cells, room temperature mice). Dot1L expression increases with cold exposure and in their previous study that Zc3h10 is recruited to thermogenic gene promoters by p38 MAPK phosphorylation in response to adrenergic activation. The present study would benefit from additional experiments demonstrating a dynamic role for Dot1L in thermogenic gene transcription during cold exposure. Does cold exposure/adrenergic activation modulate Dot1L-Zc3h10 interaction, Dot1L recruitment to thermogenic gene promoters, H3K79 methylation, etc. in a p38 MAPK-dependent manner?

      3) The authors conclude that "these results show that Dot1L methyltransferase activity is required for thermogenic gene expression and other Zc3h10 target genes for the BAT gene program (line 175)" and that "Dot1L enzymatic activity is critical for activating the thermogenic gene program in vivo" (line 255). These statements are not yet strongly supported. The involvement of H3K79 methylation was implied through the use of a chemical inhibitor EPZ5676 (figure 2c and figure 3) and the reduction of H3K79me3 levels in whole-cell lysates (figure 3b). Can the authors confirm the change of H3K79 methylation at brown-adipocyte-specific genes by conducting ChIP-QPCR in the experiments where they modulate either expression or enzymatic activity of Dot1L? In addition the authors could compare the effect of the overexpression of wild-type Dot1L (figure 2d) with a mutant Dot1L in which critical residue(s) are substituted in the enzyme catalytic core.

      4) In Figure 4D, ChIP-qPCR shows the reduction of H3K79me2 and H3K79me3 enrichment on thermogenic gene promoters in Dot1L knockout BAT. It would be informative to examine changes in Dot1L and Zc3h10 binding on the same regions in BAT.

      5) Although not absolutely required, it would be ideal to look at global epigenetic changes following induction or inhibition of Zc3h10 and/or Dot1L. Of particular interest is whether Zc3h10 plays any role in tethering Dot1L and modulating H3K79 methylation at brown-adipocyte-specific genes and whether the epigenetic changes induced by are specific to brown adipocyte function or not. The authors should consider performing ChIP-seq for H3K79me2/3 and Zc3h10. The use of tagged protein is an alternative if the antibody is not available for the latter. H3K79me2/3 reportedly marks a subset of enhancers (2019 Nat Commun, 10.1038/s41467-019-10844-3). It is also of interest whether such H3K79me2/3-marked enhancers are enriched in the vicinity of the brown-adipocyte-specific genes.

      6) The raw ATAC-seq data show very high background (figure 5A). How many peak calls were obtained? Improvement is necessary to discuss the qualitative differences. Please consider the use of culture cells if the technical hurdle is caused by the use of tissue samples. Further, the pattern of the aggregate plots (figure 5A left upper) does not obviously match that of the heatmaps (figure 5A, left lower). Please describe exactly what is shown in the figure. Are the scales the same for each panel or the heatmaps zoom in the area indicated by the red dotted boxes in the aggregate plot? What do the red dotted boxes mean? What does color scale bar in the middle heatmap mean?

      7) Also related the ATAC data, Figure 5C suggests that loss of Dot1L alters chromatin accessibility at far more genes than is represented in the "Shared processes" pathway analysis. It would be helpful to see a more comprehensive analysis of the ATAC-seq data (is thermogenesis one of the top pathways, what other pathways are affected, is the Zc3h10 binding motif overrepresented at sites of increased chromatin accessibility? etc.) and discussion about why the ATAC-seq changes might be more general/less specific than the RNA-seq changes.

    1. Reviewer #3

      This paper reported that estrogen can accelerate mammary involution by exacerbating mammary inflammation, inducing programmed cell death, and promoting adipocytes repopulation, that the effects of estrogen on the expressions of genes during mammary involution are majorly mediated by neutrophils, and that estrogen promotes mammary LM-PCD independent of neutrophils by inducing the expression and activity of lysosomal cathepsins and other pro-apoptotic markers such as Bid and Tnf. These findings are potentially interesting, and could expand the functions of estrogen. However, there is a lack in mechanistic insight into these observations.

      I. The mechanism underlying estrogen-induced cell death needs to be further explored. For example, what kind of player(s) connects estrogen with cell death? Whether TNF-alpha plays a role in linking estrogen to cell death? Is there any enrichment of cell death genes associated with the estrogen treatment in RNA-Seq data? Why the artificial MCF-7/Caspase-3 cells were used? The results about MCF-7/Caspase-3 cells showed that estrogen promoted TNF-alpha-induced apoptosis, rather than lysosomes-associated cell death. Maybe the authors should try MCF-10A cells as the model.

      II. Based on the data on Figure 4, it is not so convincible to conclude that neutrophils are involved in adipocytes repopulation during mammary involution normally, please see also Issues#3. The authors need to re-consider the relationship between these data and the conclusion. Maybe they should re-describe these results or modify the conclusion.

      III. The most interesting finding is that estrogen does not trigger the similar biological actions in age-matched nulliparous mammary tissue. However, this study does not figure out the molecular mechanism underneath the difference between the functions of estrogen in involutional and nulliparous mammary tissues. At least, the author should discuss about the potential possibilities.

      Other issues:

      1) Quantification in Figure 1B should indicate the fractions, for example, No. cells of total or area. The data in Figure 1C, except Csn2, were not described in the content, and these data should be associated with adipogenesis. As for Figure 1D, no any description was presented about Ly6G, and in fact, it was described in the second part of Results section. Supplemental Figure 2 was mentioned in the content before Supplemental Figure 1. The first part of results was very important for readers to understand the paper, but these problems confuse the readers.

      2) In Page 13, Line 219, "E2B treatment alone without the antagonist (E2B+DMSO) lead to an expected 1.57-fold increase (p=0.0082) in mammary neutrophils as compared to the Ctrl+DMSO". Should "1.57-fold" be "2.57-fold" or something other? It is not the case based on the data in Figure 3Ci.

      3) In Figure 4B, upon neutrophil depletion, Cebpb and Cebpd were already increased, which could limit their further enhancement when treated with E2B. As for Adig and Egr2, it seemed that they also apparently increased. In Figure 4D, the data had the similar problem to those in Figure 4B. No description about Figure 4E and 4F was found in the content. Overall, these data put it in question that estrogen-induced adipocyte repopulation is associated with the induction of adipogenic and tissue remodeling genes through neutrophils.

      4) In Page 19, Line 305, "This suggests that the up-regulation of Ctsb expression by E2B is a direct event independent of STAT3 activation". These data in Figure 5B could not demonstrate that Ctsb expression is the direct event of E2B. In Figure 5D, why the lysosomal pellet fractions showed no lysosomal proteins, such as catheptins. In Figure 5A, at least the protein level of TNF-alpha should be measured, because it was very important for the functions of E2B, based on the data in Figure 6.

      5) In Figure 6, TNF induces p-STAT3 while Fig 5A shows E2 induces TNF expression (mRNA), but no p-STAT3 was increased in Fig 5B. The increased mRNA does not mean the increased protein. Please measure the TNFa proteins in Fig 5A (See Issue#4). The MCF-7/Casp3 model seems not to well support the conclusion. The data in Figure 6 are about typical apoptosis not the lysosomes-associated cell death involved in the functions of estrogen as revealed in this study.

    2. Reviewer #2

      In this study, Chew Leng Lim et al determined the diverse effects of Estrogen exposure on neutrophil infiltration, inflammation responses, cell death and adipocytes repopulation in mice models. While the authors revealed some new findings, this study suffers from obvious defects, including overdependence on the use of chemical inhibitors, lack of in-depth mechanistic investigation as well as unfocused research topics.

      Major concerns:

      1) In addition to neutrophil, estrogen exposure also induced macrophage infiltration, while "neutrophil" deletion by using anti-Ly6G antibody obviously reduced the infiltration of macrophage (Fig S1). Therefore, the role of macrophage in Estrogen exposure-induced biological responses should be deeply determined.

      2) Since anti-Ly6G antibody also reduced macrophage infiltration significantly, it is very likely macrophage play a pivotal role in Estrogen exposure-regulated gene expressions and cellular phenotypes. Therefore, the conclusion that 88% of estrogen-regulated genes are mediated through neutrophil is not solid. This point should be addressed by specific deletion of macrophage and neutrophil, individually.

      3) The source of CXCL1/CXCL2 upon estrogen exposure should be further investigated. In Fig 8, the authors indicated that CXCL1 and CXCL2 are produced by existing neutrophil. Further evidence to support this should be provided.

      4) Many biological and small molecule inhibitors, including anti-Ly6G antibody, PAQ (S100a9 inhibitor), CXCR2 antagonist SB225002, etc, have been frequently used in this study. However, the effects and specificity of some of these agents have not been well validated during the study. The use of genetic mice models for critical signaling pathways is highly suggested.

      5) Figure 5, The critical role of CTSB in the activation of CTSD/CTSL and induction of LM-PCD upon E2B treatment should be validated by downregulation of CTSB expression pharmacologically or genetically.

      6) The data presented in Figure 7 based on the analysis in a single cell line is not reliable.

    3. Reviewer #1

      Dr. Valerie Lin discovered some interesting links between estrogen signals and the differentiation and programmed death of mammary cells, as well as the formation of pro-inflammatory microenvironment, which facilitate post-partum mammary involution and presumably parity-associated breast cancer. They also demonstrated that mammary gland-infiltrating neutrophils emerge as a major immune cell participant during this process.

      1) Dr Shengtao Zhou reported that ERβ has potent antitumor effects, which suppress lung metastasis by recruiting antitumor neutrophils to the metastatic niche. It is recommended to carefully address whether estrogen specifically target ERα or ERβ on post-weaning mammary cells and infiltrating neutrophils in this setting.

      2) Perhaps a missing point is whether estrogen-induced mammary cell death subsequently cause inflammation (presumably augmenting neutrophil accumulation), since several cell death modalities has been associated to inflammation via the release of danger molecules.

      3) Besides lysosome-mediated PCD, can estrogen induce other cell death modalities, such as pyroptosis, necroptosis, ferroptosis, which are all caspase 3/7/8-independent? It is important to make a clear conclusion.

      4) Since the synthetic estrogen regulate the differentiation associated genes of fat cells and accelerated LM-PCD. Does estrogen affect lipid metabolic pathways? How does this metabolic remodeling affect cell death and differentiation of adipocytes and the function of neutrophils? By carefully going over the Seq data, the authors may add more important discussions.

    4. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on April 30, 2020, follows.


      Lin and colleagues aim to explore how estrogen promotes post-partum mammary involution and increases the risk of parity-associated breast cancer. Previous studies have unraveled different molecular mechanisms of mammary gland involution (see a previous summary PMID: 30448440). The authors highlighted that estrogen causes mammary involution by stimulating the accumulation of neutrophils, sculpturing the pro-inflammatory microenvironment, facilitating adipocytes differentiation, and causing lysosome-related programmed death of mammary cells. These findings are interesting, but further efforts are needed to nail down some of the major conclusions and to clarify the underlying mechanisms.

      Essential Revisions

      1) A major concern is about several discoveries on neutrophils. The contribution of neutrophils during estrogen-induced mammary involution should be cautiously defined with solid experimental evidence. Do other immune cell populations, such as macrophages, actively participate in this process? Does Ly6G antibody efficiently deplete neutrophils, rather than masking the labeling of Gr1 antibody (for validation)? As neutrophils have short half-life, secret lots of inflammatory mediators, and quickly replenish from BM progenitors, this point is important. The possible coordinations between neutrophils and other immune cells (e.g. macrophages, monocytes), and their relative importance at different stages of mammary involution can be examined and discussed (see a previous summary PMID: 24952477). In addition, more evidences are needed to prove whether the recruitment of neutrophils depends on a positive-feedback loop of CXCL1 and CXCL2. Quality controls are needed for the application of inhibitors.

      2) Another major concern is about estrogen-triggered mammary cell death. How do ERα, ERβ or death receptor-mediated signals contribute to this process? Does estrogen-induced programmed cell death exclusively rely on lysosome leakage and related effector molecules? Have the authors tested the existence of other cell death modalities? Does estrogen-induced cell death augment local inflammation and perhaps the accumulation of immune cell populations?

      3) The authors may consider to rephrase/weaken some of their claims and reorder the display of some of their results.

    1. This manuscript is in revision at eLife

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


      This report provides significant new information about the mechanisms of neurosteroid enhancement and inhibition of GABA-A receptor (GABAR) function. This study builds on an earlier investigation by the same group (Chen et al. PLOS Biology 2019) showing that photoactive NS ligands can bind to three distinct sites on α1β3 GABARs - the canonical intersubunit site at the interface between the transmembrane domains (TMDs) of adjacent subunits and additional intrasubunit sites located within the TMDs of the alpha and beta subunits. In the current study, combining [3H]muscimol radioligand binding assays, site identification by photoaffinity labeling, and electrophysiological analyses of steroid modulation of wildtype and mutant α1β3 GABARs, the authors suggest that the overall functional effect of a given NS molecule is dependent upon which binding sites are targeted, with binding to the intersubunit site causing positive allosteric modulation (PAM), whilst occupancy of the intrasubunit sites appear to promote desensitization and negative allosteric modulation (NAM). Given the physiological significance of neurosteroids, elucidating how these structurally similar compounds can act as positive, negative or null modulators is clearly important.

      Essential Revisions

      1) The electrophysiological data presented (changes in steady state desensitization current magnitudes) is insufficient to conclude that NAM steroids inhibit GABAR function by stabilizing a desensitized state. Additional experiments such as co-application of agonist + NS and monitoring desensitization kinetics would be informative. Measuring the rate of recovery from agonist-induced desensitization in the presence of neurosteroids might also be helpful. While the data presented can be interpreted as changes in desensitization, the authors should discuss that alternative models are also possible. For example, it has been proposed that selectively stabilizing a pre-active state can result in changes in macroscopic desensitization (Gielan and Corringer, J. Physiol. 2018).

      2) Mutant receptors were not assayed for their sensitivities to agonist before measuring effects of neurosteroids. The functional assays and binding experiments need to be done at a consistent fractional EC value for each mutant construct being analyzed. For example, if the apparent Kd for muscimol has shifted substantially, the observed potentiation of muscimol binding by a neurosteroid will be artificially high or low. The is also true for experiments measuring neurosteroid potentiation/inhibition of functional activation by GABA.

      3) In the result section, there are concerns about quantitatively comparing electrophys data and [3H]muscimol data (measured at different agonist concentrations and time periods). Are the methods reliable enough to infer that the small changes in Popen and Pdesensitized are real? In some cases, data are not shown. Inherent methodological limitations of two-electrode voltage clamping (e.g. slow ligand exchange) raises concerns that authors are over interpreting the data. As it stands, the comparison seems to be a bit of a reach and in this reviewers' opinion does not significantly add to the paper.

      4) While having three distinct sites for NS binding to GABARs does fit with aspects of the data, it's noteworthy that with the suggested model, there are three ligands that bind to all three sites, 3a5aP, KK148 & KK150, but each has a distinct functional profile, PAM, NAM via stabilizing desensitization, and competitive antagonist, respectively. This implies that divergence in function is dependent upon differential binding/efficacy at these three sites, presumably due to the ligand sitting in each site in a different orientation. While the observation from the [3H]muscimol binding experiments suggests that 3a5aP binds to the b3 intrasubunit site with lower affinity, the data presented in Fig 6B also suggest that binding of 3a5aP to the intersubunit and a1 intrasubunit sites works synergistically to increase muscimol binding. The reasoning being because with both sites intact, the Emax for muscimol binding is 374%, whereas mutating these sites individually causes similar decreases in Emax (to 159% and 146%). This implies an allosteric interaction between these binding sites, a conclusion which the authors also reach in their previous publication (Chen et al 2019). This makes interpretation of the effects of mutations in these two sites (and possibly also the beta intrasubunit site) difficult to interpret and to use to specifically dissociate a mutations effects on NS actions to binding to one particular site. The authors need to thoroughly discuss this concern/limitation.

      5) The demonstration that steroids apparently enhance [3H]muscimol binding affinity without changing the number of sites (Fig 6 supplement 1) is in contrast to past reports from multiple labs that [3H]muscimol binding (to brain membranes) is characterized by high and low affinity components and that steroids and other GABAR positive allosteric modulators increase the number of high affinity sites with little effect on their binding affinity. Please discuss. In addition, we would like to see presented in supplementary material representative experimentally determined [3H]muscimol binding curves (total and non-specific vs [ 3H]musc concentration, not just the calculated Bspec of fig6 supp fig 1). In their methods (p.25) they say that they determined [3H]muscimol binding isotherms from 0.3 nM to 1 uM [3H]muscimol at a radiochemical specific activity of 2 Ci/mmol. It is surprising that they can go to micromolar concentrations with such small uncertainties, and it is crucial to their claim steroids produce only shifts of affinity, not shifts of Bmax.

      6) [3H]muscimol binding is measured on cell homogenates over a time scale of hours. There seems no reason to "infer" that 3α5αβP increases [3H]muscimol binding by stabilizing an active state while 3β5αP stabilizes a desensitized state. By my reading, the previous studies (13,14) report that the αV256S mutation removes the "inhibitory" effects of sulfated steroids and 3β5αP, not the "desensitizing" effects, this should be more clearly articulated in this manuscript. This report will be strengthened by avoiding unnecessary overinterpretation, and leave it for future studies to determine whether there is any measurable quantity of receptors in an active state under the conditions of the [3H]muscimol equilibrium binding assay.

      7) Given the expectations that some of the neurosteroids stabilize a desensitized state, do they "fit" in the proposed intrasubunit sites in, for example, one of the published presumed desensitized-state structures of the α1β3γ2 receptor?

      8) A more thorough discussion of why recently solved GABAR structures have not resolved intrasubunit neurosteroid binding sites is warranted.

    1. This manuscript is in revision at eLife

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


      The manuscript by Fournier et al. highlights the importance of acetylation in the ChAM domain of PALB2 in regulating nucleosome binding and DNA repair. The text is well-written text and the experiments are well-designed. We read the manuscript, the reviews from Review Commons, as well as the rebuttal and plans for a revision. We believe the revision and the proposed added experiments will be needed to cement the conclusions.

      Of the 5 experiments, #1 and #2 are critical, and we believe #4 and #5 are also important as BRCA1 is a key factor for PALB2 (#5) and the effect on HR (#4) should be documented experimentally. We do not consider experiment #3 (PALB2 foci) as critical. We encourage the authors to plan and execute this revision as they outlined with the above exception of experiment #3. You may want to consider combining KAT2A/B depletion and/or using KDAC inhibitors in the experiments with the 7R and 7K mutants, but we leave that suggestion to them.

    1. This manuscript is in revision at eLife

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


      The revised paper presents a better-fitting analysis, and does a more nuanced job in discussing the results than the original manuscript. However, there are still a few major criticisms that we have for the analysis, detailed below.

      Essential Revisions

      1) Brain-wide, multiple-comparison corrected tests comparing auditory versus visual decoding are still lacking. The authors have now provided vertex-wise Bayes factors within areas that showed significant decoding in each individual condition. Unfortunately, this is not satisfactory, because these statistics are (1) potentially circular because ROIs were pre-selected based on an analysis of individual conditions, (2) not multiple-comparison corrected, and (3) rely on an arbitrary prior that is not calibrated to the expected effect size. Still, ignoring these issues, the only area that appears to contain vertices with "strong evidence" for a difference in neuro-behavioral decoding is the MOG, which wouldn't really support the claim of "largely distinct networks" supporting audio vs. visual speech representation.

      The authors may address these issues, for instance, by (I) presenting additional whole-brain results - e.g. for a direct comparison of auditory and visual classification (in Figure 2) and of perceptual prediction (in Figure 3). (ii) presenting voxel-wise maps of Bayesian evidence values (as in Supplementary Figure 3) for the statistical comparisons shown in Figure 2D, and Figure 3D (iii) in the text included in Figure 2D and 3D making clear what hypotheses correspond to the null hypothesis and to the alternative hypothesis (i.e. auditory = visual, auditory <> visual).

      2) As noted before, the classifiers used in this study do not discriminate between temporal versus spatial dimensions of decoding accuracy. This leaves it unclear whether the reported results are driven by (dis)similarity of spatial patterns of activity (as in fMRI-based MVPA), temporal patterns of activity (e.g., oscillatory "tracking" of the speech signal), or some combination. As these three possibilities could lead to very different interpretations of the data, it seems critical to distinguish between them. For example, the authors write "the encoding of the acoustic speech envelope is seen widespread in the brain, but correct word comprehension correlates only with focal activity in temporal and motor regions," but, as it stands, their results could be partly driven by this non-specific entrainment to the acoustic envelope.

      In their response, the authors show that classifier accuracy breaks down when spatial or temporal information is degraded, but it would be more informative to show how these two factors interact. For example, the methods article cited by the authors (Grootswagers 2017) shows classification accuracy for successive time bins after stimulus onset (i.e., they train different classifiers for each time bin 0-100 ms, 100-200 ms, etc.). The timing of decoding accuracy in different areas could also help to distinguish between different plausible explanations of the results.

      Finally, it is somewhat unclear how spatial and temporal information are combined in the current classifier. Supplemental Figure 5 creates the impression that the time-series for each vertex within a spotlight were simply concatenated. However, this would conflate within-vertex (temporal) and across-vertex (spatial) variance.

      3) The concern that the classifier could conceivably index factors influencing "accuracy" rather than the perceived stimulus does not appear to be addressed sufficiently. Indeed, the classifier is referred to as identifying "sensory representations" throughout the manuscript, when it could just as well identify areas involved in any other functions (e.g., attention, motor function) that would contribute to accurate behavioral performance. This limitation should be acknowledged in the manuscript. The authors could consider using the timing of decoding accuracy in different areas to disambiguate these explanations.

      The authors state in their response that classifying based on the participant's reported stimulus (rather than response accuracy) could "possibly capture representations not related to speech encoding but relevant for behaviour only (e.g. pre-motor activity). These could be e.g. brain activity that leads to perceptual errors based on intrinsic fluctuations in neural activity in sensory pathways, noise in the decision process favouring one alternative response among four choices, or even noise in the motor system that leads to a wrong button press without having any relation to sensory representations at all."

      But, it seems that all of these issues would also effect the accuracy-based classifier as well. Moreover, it seems that intrinsic fluctuations in sensory pathways, or possibly noise in the decision process, are part of what the authors are after. If noise in a sensory pathway can be used to predict particular innacurate responses, isn't that strong evidence that it encodes behaviorally-relevant sensory representations? For example, instrinsic noise in V1 has been found to predict responses in a simple visual task in non-human primates, with false alarm trials exhibiting noise patterns that are similar to target responses (Seidemann, E., & Geisler, W. S. (2018)). Showing accurate trial-by-trial decoding of participants' incorrect responses could similarly provide stronger evidence that a certain area contributes to behavior.

    1. This manuscript is in revision at eLife

      The decision letter after peer review, sent to the authors on April 16, 2020, follows.


      Using a clever genetic system in the budding yeast Saccharomyces cerevisiae the authors test whether R-loop can form in trans, meaning that a transcript from locus A could lead to R-loop formation in locus B. Moreover, they test whether R-loop formation is dependent on Rad51, the eukaryotic RecA family recombinase. Using their genetic system and cytological analysis of Rad52 foci and the S9.6 antibody to detect R-loops in wild type and strains with mutations known to affect R-loop, conclusive data are shown that R-loops only form in cis and that R-loops in this genetic system are independent of Rad51. Overall, this work significantly enriches the discussion in the R-loop field and provides an alternative view point of an earlier publication that suggested R-loop formation in trans being catalyzed by Rad51.

      Essential Revisions

      1) The pGal promoter induces very high transcription in the presence of galactose (often 500X or more induction). The level is likely very different (much less) for the tet promoter, which is generally only induced 2-3X upon addition of doxycycline. This could significantly affect the results - e.g. the cis vs trans effects could really be a matter of different transcription levels. Transcription levels from each promoter really need to be determined- this is a very important control. The exact induction conditions used, including concentrations and induction times, need to be spelled out in the methods and should be consistent with those used during the RT-PCR experiment to test transcript levels. In the absence of being able to do the experiment on the constructs used (which would be optimal), at least it could be cited if this lab has used the same promoters and induction conditions in the past, and a caveat inserted if transcription levels are different. It would also be good to switch the promoters and make sure the result holds, as there could be issues of differences in timing of transcription as well.

      2) In Figure 2 the authors relate recombination frequencies in their assays to RNA:DNA hybrid formation without measuring hybrids directly. This is a major weakness that significantly limits data interpretation. For instance, I am very surprised that the "cis" recombination frequency of the inverted LacZ reporter is essentially as high as the regular lacZ construct. This result implies that hybrid formation is insensitive to the orientation of the reporter when in many reported cases, R-loop formation is strongly orientation-dependent. Of course, another hypothesis is that (stalled) transcription itself triggers recombination, not R-loops. Without data on R-loop formation, one cannot disentangle transcription from co-transcriptional R-loop formation. The authors must use DRIP-based assay to quantify R-loop levels in the various sequence contexts and under the various genetic backgrounds to establish that their assay is reflective of R-loop levels. Using bisulfite-based readouts to measure R-loop distributions and lengths across the LacZ region would be even better. Without this data, the claim that this new genetic assay can "infer the formation of recombinogenic DNA:RNA hybrids" is unsubstantiated.

      3) Source data. The source data file should be labeled better. Missing are:

      • what the numbers in the table are (rates of Leu+ x 10^-4?)
      • which data goes with which Figure panel
      • average and SEM numbers should be shown in the data table

      The exact p values not reported and could be added to source data file. N values can be discerned from the source data file but it would be nice for them to be stated in the figure legends.

    1. This manuscript is in revision at eLife

      The manuscript was reviewed by Review Commons. eLife's decision letter, sent to the authors on April 18, 2020, follows.


      In this manuscript, the authors study the transcriptional regulation of HOXA9, a transcription factor that plays a central role in homeostasis of immature hematopoietic cell types and in the development of leukemia. They use the CRISPR/Cas9 technique to introduce a fluorescence reporter cassette into the endogenous HOXA9 locus of a human MLL/AF4-rearranged B-ALL cell line. After validating this engineered cell line, they perform multiple genetic screens to identify potential transcriptional regulators of HOXA9 and to delineate essential transcription factors in this cell line. They identify USF2 as new transcription factor that modulates expression of HOXA9.

      Major Revisions

      If the authors can commit to adding the following data, as they indicate in their rebuttal, the manuscript would be greatly strengthened and could be considered acceptable:

      1) The authors should include their data on the independent loss-of-function CRISPR transcription factor screen in SEM HOXA9-P2A-mCherry MLLr reporter line ectopically expressing HOXA9-MEIS1 to overcome the possibility that key regulators could be missed in the CRISPR/Cas9 screen due to survival dropout.

      2) The authors should include supporting data for the key observations in the manuscript in other cell lines; for example, as indicated by the authors, the data gathered using an additional HOXA9 MLLr AML reporter cell line established in OCI-AML2 cells to further support findings from the initial in SEM MLLr ALL reporter line.

      3) The authors should perform USF2 knockout experiments in multiple non-MLLr cell lines according to the reviewer's suggestions. As an example, the authors should repeat the competitive proliferation assay to determine the effects of the single knockout of USF1 and USF2 vs the double KO in SEM cells and other MLLr leukemia cell lines with proper controls.

    1. This manuscript is in revision at eLife

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


      This manuscript presents a new agent-based model of coral reefs that is designed to answer questions about the response of coral reefs to multiple stressors in a mechanistic, bottom-up way. The model uses traits and functional types of corals and algae to represent not only taxonomic but also functional diversity. The manuscript includes a very impressive description of the design, calibration and testing of a coral reef model. The authors have used the ODD protocol (to some degree), calibration of 12 model parameters for three empirical locations in the Caribbean, hierarchically structured validation, and global sensitivity analysis. Spatial interactions between corals and algae are represented in detail and allow to analyze relations between traits and functional responses and thus to depict realistic trajectories of reefs under different scenarios of external forcing.

      Agent-based models are often criticized because of their complexity, which makes them difficult to parameterize, calibrate, test, and understand. This manuscript is an impressive demonstration of how it is possible to combine all relevant existing data in a systematic way, test a model at multiple levels, and thus demonstrate that, yes indeed, trait-based agent-based models allow us to model the role of diversity (see also this review: Zhakarova et al. 2019).

      Essential Revisions

      1) The Introduction takes a lot of space in discussing challenges to coral reefs. I guess virtually all papers about coral reefs start like this. It should be shortened, also because it raises the expectation that you are going to tackle these questions, which is not the case. Rather, this is a methods paper and you should come to this point more directly and perhaps list the challenges to ABMs for exploring diversity (see above) as the key challenge addressed in this manuscript.

      2) If you say, in the Abstract, that the model "provides a virtual platform": Where can we download the software? Is there a manual describing the workflow needed for running the model and all its data scripts? Is the model description in the supplements complete? If not, this article would not really provide a tool. You might have a look at two examples where ABMs were presented, in journal articles, as tools. In both cases there was a full model description, a manual, and a download site: Becher et al. (2014) and Hradsky et al. (2019).

      3) Section 2.1: It is impressive to see all those packages and tools you used, but, ideally, you would also provide all, or the most important, scripts you wrote to run these packages and tools. If others are to use your virtual laboratory, they very likely would fail immediately because they would not know how to actually handle all those tools and data sources. I know that there is no culture yet to provide all relevant scripts, but I think we should go there.

      4) The ODD model description in the main text is not bad, but just a verbal summary description while the intention of ODD is to provide all information that is needed to re-implement the model. I understand that much of these details are in the Supplement, e.g. about Initialization and Submodels? It would be good if this link would be made more explicit by having a full ODD in the supplement, as a separate file. It would contain an augmented copy of the ODD of the main text and then just provide, in all detail, the information required for the seven elements of ODD. Why? Because the point of a standard is to follow it exactly so that readers, who either know the standard or learn about it, can easily find certain kinds of information at certain places in the model description. Currently, this is finding of relevant information is made unnecessarily complex. Examples of complete ODDs of complex model are provided by Ayllón et al (2018) and Nabe-Nielsen et al. (2019).

      For producing a complete ODD, please note that a new version of ODD has been published, which in particular has very detailed guidance, in the supplement, about ODD itself, summary ODDs, model narratives, etc.: Grimm et al. (2020). All that said, please note that we certainly do not require that you use ODD (because I am the main proponent of ODD), but any format, that compiles all information needed so that it is easy to find the kinds of information listed in ODD protocol, would be acceptable.

      5) Scales: The model applications relate to a space of 5x5 m (25m2). I am not sure if such a small space allows for realistic dynamics if single corals grow large (> 2-3 m diameter) as then only a very low number of individuals would be present in the simulations potentially leading to artifacts in results. It is a pity that the spatial output of the model is not shown (except one specific figure in S5). I also see a discrepancy between the very high spatial (1cm) and the low temporal resolution (6 month). The time span within half a year could e.g. cover a mild bleaching event or other disturbances as well as processes of reef recovery leading to a different species composition and thus change the reef trajectory without being considered in the present model. I do not see that it is an argument, that the field data are only available in a low resolution of approx. 6. month. A comparison with model processes stays possible even if it is resolved higher.

      6) It is apparent that all model runs cover only a very short time span of around ten years (21 simulation steps). This is extremely short for coral reefs which frequently undergo dynamics based on larger time scales. Thus, emerging dynamics and states, e.g., resulting from the sensitivity analysis, should be discussed with much care.

      7) Overfitting? The model is very impressive, as it is possible to very closely possible represent the dynamics of measured reefs. However, I am not sure if this actually results from some overfitting. The model (runs) include some very strong and very specific influences of external drivers. For example, at the end of a time step certain values for grazing or sand cover are enforced. At least the impact of grazing results from a feedback with different reef processes. Thus, at least much of the trajectories in the model are the result of external drivers and it becomes difficult to analyze self-organization processes in the reef. In short: you cannot claim that a model is producing realistic dynamics due to a realistic representation of its internal organization if in fact the match between model output and observations is imposed by external drivers. A similar case occurred with honeybee colony models, where often the yearly time series of colony size was compared to data to claim that the model was realistic, but that time series was largely driven by the time series of the queen's egg-laying rate (Becher et al. 2013).

      8) A major question thus is whether the authors believe that their model can better address large scale questions about coral reefs, such as their resilience to regime shifts from disturbances and climate change, than 'minimal' models, such as that of van de Leemput et al. (2016)?

      9) In Carturan, Parrott, and Pither (2018) coral functional traits are classified as 'resistance' and 'recovery'. In the current manuscript, the terms 'stress tolerant', 'ruderal', and 'competitive' species (Grimes' classification) is used. Do 'resistance' species a